Political Science and Public Policy
Author's Note: In the introductory chapter, I wrote about the influence on me of Max Weber's views on the imperatives of the academic vocation. These views are spelled out and elaborated here. The occasion for the essay was a request to address a plenary session of the American Political Science Association on the relations of political science to public policy—probably because I was at that time a political consultant in Washington. The editor of the book in which the essay appeared, being himself active in political consulting, no doubt expected a much different argument. At any rate, he wrote an introductory note dissociating himself from my views. But experience in Washington had convinced me that Weber's views on the essential separation, though intersection, of the policy maker's and social scientist's vocations were, if anything, understated.
I place the essay first in this section because it augments points made in the chapter on background and because most (certainly many) political scientists probably are drawn to the field because they want somehow to affect the political world. But they rarely achieve clarity about the natures of the scholarly and activist vocations. This essay clarified the matter for me. I hope it will for others.
As pointed out in chapter 1, I omit from this section on political science what are (for me, but not others) my most important articles on the field of political science: "Authority Patterns: A Structural Basis for Political Study," American Political Science Review 67 (December 1973): 1142–1161,
and "On the 'Science' of the State," Daedalus 108 (Fall 1979): 1–20. A more marginal paper on an aspect of political science is "A Critique of the Area Studies from a West European Perspective," in Political Science and Area Studies , ed. L. W. Pye (Bloomington: Indiana University Press, 1975). Chapter 8 might also have been included in this section.
Relating political science to public policy making poses many problems, but perhaps the least of them is to interest political scientists in policy questions and political activity in the first place. To be sure, some academic students of politics have recently been accused of fiddling while Rome burns—and not even knowing that they fiddle or that Rome is burning. The charge may hold for those at whom it is directed. I do not think it does, but that is of no consequence here. The essential point is that the great majority of contemporary political scientists, regardless of special interests or methodological persuasion, devote much time and effort to a concern with the world's problems and transactions, both those peculiar to our times and situation and those that arise permanently and ubiquitously in politics. Publishers' lists, journals, the mass media, congressional records, and the files of administrative agencies and bureaus teem with their researches, reflections, and recommendations on pressing practical issues; and the issues they tackle run the gamut from small details of administration to the great and ramified questions of peace and war, the public welfare, political stability, development, and insurgency. Even when not directly concerned with such matters, the source of political studies in the world's alarms is apparent and acknowledged. In comparative politics, for example, almost everything that has happened since the Second World War reflects, more or less directly, an attempt to adjust theoretical and practical understanding to four decisive experiences: the malfunctioning and low survival value of many democracies, the rise and spread of totalitarianism, the decline of colonialism and appearance of new states professing large aspirations and lacking settled institutions, and new forms and magnitudes of protest and revolutionary violence.
Relating political science to public policy is not, then, a problem of political "mobilization." On the contrary, the most pressing questions about that relationship stem precisely from our very considerable concern with policy and involvement in the policy-making process, at virtually all levels and both extramurally and intramurally—in public media and agencies as well as in policy-oriented classes, seminars, conferences, and research projects. More than exhortations to participate, we need clarity about the relevance of academic political studies to policy; about the
problems of strain and compatibility that may arise between the two distinguishable roles political scientists play when they seek to influence choices of policy in their professional capacities; about how political scientists can effectively influence policy processes; and about the extent to which they should, as academic specialists, attempt to influence them in the first place.
That the professional student of politics needs some detachment from political activity and commitment is unlikely to be disputed. Neither, however, is anyone likely to argue that choosing professional political study as a career incurs civic disqualification or that political scientists do not possess any special knowledge relevant to policy problems or that, possessing such knowledge, they should, as a professional duty, provide it only through normal professional channels. But this is just the problem: both sets of premises granted, where and how to draw the line between detachment and involvement?
Few political scientists base their own political activities, or inactivity, upon much reflection about that problem. This is easily explained. They have other work to do. And more important, the question itself has so many facets, so difficult to resolve into a clear result, that drifting by simple inclination into some implicit position on it is all too tempting. Among the considerations affecting any reasoned position on it are first, of course, personal matters: career motivations (which, for most political scientists, surely include being fascinated by, and believing in the crucial importance of, public authority and wishing to understand and influence it in some way out of the ordinary); conceptions of civic obligation; conceptions of proper demeanor, particularly as to matters of arrogance, pride, ambition, modesty, and a sense of limitations; and more prosaically, but no less important, routine difficulties of allocating scarce resources, above all time and energy, which never suffice for playing adequately every open role and, like it or not, enforce choices based on priorities. These choices, although to a degree ineluctably personal, can hardly be made without confronting certain abstract considerations, concerning the inherent nature, demands, and capabilities of the scientific and academic vocations and the impact they may have on one another. And these abstract considerations must be related to particular contexts—social, political, and academic. One wishes to know not only what science can abstractly contribute to policy but also how much one's particular science, at a given stage of development, can actually help in working out practical commitments. And political contexts are no more equal than scientific fields. Differences among them raise not only moral questions but also complex practical questions of access and influence, of how one can use politics and avoid being exploited by politicians.
The Tension Between "Science" and "Politics" in Max Weber
How then can the affinities and tensions between political science and political activity be defined? What boundaries separate and what areas of overlap join them? Although, as stated, this question has been more often avoided than confronted, we are not without guidance in regard to it. A handful of social scientists (and their critics) have explicitly dealt with it and worked out positions that may serve as reference points—among them Max Weber, to an examination of whose position on the subject the rest of this chapter is devoted.
There are reasons for this emphasis on Weber, quite apart from the fact that concentrating on his position is one way to limit discussion of so widely ramified a problem and to proceed critically or with approbation from what has been said about it. Most important is the unrivaled intensity, extensiveness, and clarity of Weber's confrontation of the issue. Whether one agrees with his views or not, one must at least recognize that they are devoid of platitudes, laziness, wishfulness, ambiguity, mere exhortation, or vainglorious pretense. In many essays, letters, and speeches, spanning his life from student days to the twilight of his university career, his "powerful mind . . . strove restlessly for clarity [about this issue] at levels where his contemporaries were satisfied with ambiguities and clichés," fully living up to his demanding conception of maturity as "trained relentlessness in viewing the realities of life and the ability . . . to measure up to them inwardly." These qualities of his reflections have given them great influence, to the extent that some of his views, fresh and challenging when first stated, may now indeed seem commonplace—an influence evident most of all in the more thoughtful positions differing from his that have been stated since his time, for in the main these have been worked out with Weber's arguments as a frame of reference and constant counterpoint.
To deal as intensively and influentially as did Weber with the relations between social science and public affairs required more than intellectual force. Two other factors above all contributed to that intensity and influence, both of which may make Weber especially relevant to us: his personal orientation to the scientific calling and his temporal location in the development of social science and its social and political context.
In regard to Weber's orientation to science as a career, the most essential point is that his attitudes are typical, even if in an enlarged form, of those of political scientists for whom the topic of this chapter appears as a problem: those who know a tension between the politics of the study and those of the hustings and corridors of power. Weber, even if not a political scientist in the narrow departmental sense, was preeminently what Gerth
and Mills call a "political professor." Like many of us, he engaged in scholarly work, "not in order to seek . . . a quietistic refuge . . . but rather to snatch from [it] a set of rules which would serve him in his search for political orientation in the contemporary world." Like many of us, too, he soon experienced that science and scholarship were not so easily turned to a mere instrumental purpose, so readily made subservient to political activity. They imposed imperatives of their own, as does any special calling, made special demands on personal resources and moral conscience, and like other specialized vocations, had both peculiar capabilities and peculiar limitations. Being political scientist and politician appeared to him, first as identical, then separable but complementary, then separate and in certain senses even antithetical roles. Yet as his closer friends (Troeltsch, Jaspers, Michels) invariably stress in their remembrances, the desire to join the two in some manner never left him, even as the sense of their separateness deepened and the academic vocation, through its own demands, came to consume his time and energies. Aron puts it precisely in saying that in his life and work he "both separated and united politics and science," a phrase that would surely serve well also as a general characterization of political science and its practitioners.
Some biographic details will clarify these points. The larger setting in which Weber was formed was a new nation, in which life, especially for educated men and precocious youngsters, had many characteristics familiar in the more recently new polities, not least a pervasive political cast. A political event, unification, was the decisive experience of his generation, coloring all other experiences. A powerful leader who had unified the country was devoting himself to the task of endowing it with international status and power and was using political means to help Germany rapidly catch up economically and socially with more advanced countries. Highly organized structures of political competition existed, and previously inactive groups were becoming mobilized in politics; the political system was, however, greatly skewed in favor of executive domination, both formally and as a result of a lack of political skills, ideological and parochial dissensions, and sterile romantic aspirations in the movements and parties. Under such conditions, it is natural that "all ultimate questions without exception" should seem, as they did to Weber, "touched by political events."
Later he was to develop an elaborate intellectual basis for his perception of life as political in every aspect, hence for the primacy of politics, which anticipated totalitarianism with the prevision of a Tocqueville. I refer to his argument that political "development" is a process of continuous public expropriation of private spheres, beginning with the gradual expropriation by the "state" of means of violence, proceeding to the expropriation by the power monopolists of economic means, and culminating in the public
expropriation of education and artistic creativity, the whole becoming subject to the caprices of unfettered charismatic leaders and the routines of servile bureaucrats. That vision was based on historical sociology, but even more fundamentally on the tenor of life in the national macrocosm of his youth.
To this add the intensely political atmosphere of his domestic microcosm. Weber's father was simultaneously a councillor of the city of Berlin and a member of both the Reichstag and the Prussian Diet. The Weber house throughout his childhood was full of politicians and political intellectuals, engaging in constant discussion of questions that Bismarck's domination raised for party politicians and intellectuals alike: questions of the relations between political power and ideals, between unlettered men of action and scholarly men of ideas, between vocal political philosophies and mute objective forces, between the growth of democracy and that of bureaucracy and plebiscitary leaders. But there was also in the home a splendid historical and philosophical library to which the young Weber had full access and that represented a quite different pole of life. At fourteen he was writing historical essays so precocious that he was (unjustly) accused of plagiarism—essays mainly concerned with the ruthless appraisal of political sacred cows, like Cicero. At seventeen he was trying to formulate laws of history and reflecting on the sociology of religion, but doing so in order to obtain dependable bearings in life, not out of any "mere objectivity" (his own phrase). Objectivity for its own sake he considered then already an inadequate and truncated stance in life, just as he had already come to think of even the loftiest ideals as self-indulgence and self-corroding, when unrelated to realistic possibilities. Steeped in politics, immersed in books, youthfully cynical about the impotent ideologues, casuists, and political amateurs in the drawing room, his adolescent reflections were increasingly ruled by visions of the power obtainable through the scientific knowledge of life. At that point, politics and social science were certainly not seen as separate in any fundamental sense.
Only after finishing his legal and historical studies at the university did a note of conflict appear, and then only for the most mundane of reasons: Should he accept an academic job or make an extramural career? The latter deeply attracted him ("I have an extraordinary longing for a practical job"); becoming a scholar he found at least "congenial," although financially hazardous; and he began to see that the latter course, which relatives and mentors alike urged on him, might not satisfy his longing for practical activity. "Temporarily," he writes, "purely scientific work has lost all its excitement, because I live under the impression that practical interests . . . pose combinations not to be grasped by science." Nevertheless—because of an unsuccessful application for a legal job?—he continued abstruse scholarly research (on the legal implications of Roman agrarian history)
and joined a group dedicated precisely to the task of grasping practical combinations scientifically, the Verein für Sozialpolitik , a policy-oriented group of academics, civil servants, and businessmen, for whom he prepared a large study of agricultural labor in East Germany.
By 1892, at age twenty-eight, he was at work lecturing at the university in Berlin, and by 1893 appointed professor extraordinary and fully launched on an academic career. Yet he had made no final choice of science as against the active life, based on a sharp sense of any need for such a choice. If his work for the Verein was mainly a piece of research, then his inaugural professorial lecture was essentially a policy statement based on that research, and it has been published not in the volumes of his "scientific" writings but in a special volume of "political" essays. It dealt primarily with the need for public policy to arrest the drift of peasants from the East German estates into urban areas in order to maintain Germany's power position vis-à-vis the Slavic peoples; a second theme was the need to provide "political education" to those still largely excluded from power but politically on the rise. About the same time, too, Weber became involved in Naumann's Evangelisch-Soziale Verein , a somewhat amorphous group of well-intentioned, politically oriented theologians, professors, artisans, and workers. Naumann had been converted by Weber himself to the view that the state should pursue a "social" policy (i.e., welfare and development policies within a liberal political framework) and that such a policy presupposed national security and power, and even more, a socialism of administrable policies, not merely of theories, antipathies, and utopian aspirations.
Thus, at the very moment Weber was launching himself as a prodigy professor, politics and scholarship still seemed to him closely linked and the very fate of Germany to depend on political education and policies informed by relevant research. Nor had his mercurial rise as an academic allayed his doubts about whether he was "in the right place," not even after he had received, in 1896, the accolade of succeeding Knies in the chair of economics at Heidelberg and had there become immersed in the intense intellectual life of a circle that included Troeltsch, Jellinek, and Neumann.
In the same period, however, doubts and soul-searchings about politics and its relation to science—still mundane, but less humdrum than the mere question of choosing a job—appear. Mainly, they have to do with the world Weber had encountered in his attempts to play an active role in politics. That world seemed to him to consist largely of powerful, unscrupulous, and myopic Realpolitiker , lofty but impotent idealists, and servile, narrow-minded functionaries. Largely as a result of his involvement with Naumann's group, he came to realize that good intentions and objective knowledge were nothing politically without funds, organization, and special skills.
At the same time, no existing political machine attracted him. None stood for everything he considered essential: the national idea, democracy, liberalism, and a "social" policy; and they were all themselves populated by self-seekers, bureaucrats, and futile ideologues. Moreover, these concrete disillusions were accompanied by the first signs of profound abstract questionings. Did not the laws of morality lie beyond human reason, in the realm of the passions? Were there any absolute imperatives, or did not every special realm of life impose unique, perhaps contradictory, demands? Did not politics, as such a special realm, also require special aptitudes and attitudes, a special Sinn?
There has been much sympathetic and malevolent speculation about Weber's prolonged physical breakdown at this point of his career, the three-and-a-half years of almost total incapacitation that were never to be fully overcome. Such afflictions no doubt have deeper causes, but it is reasonable to think that the tensions which had accumulated between his career orientations contributed a share. Having drifted into the demanding work of teaching and research—"If I don't work until one o'clock, I can't be a professor," he had told his wife—he remained, despite prodigious success, emotionally ambivalent toward that work, convinced of the truncation of human life involved in "mere objectivity," yet unable to find solid bridges from objective reason to practical and socially creative activity.
These career tensions reflected, or were reflected in, other tensions. As a good citizen in a new state, he was a fervent patriot and nationalist, but repelled by the state's authorities and policies, and more important, deeply aware that science and scholarship transcended all political boundaries. As part of his conception of academic integrity, he was detached and reserved in the classroom, despite great oratorical gifts and an impulse to demagoguery, even poetic prophecy, that made him feel at ease haranguing a political meeting and panic-stricken at the very thought of a lecture. He wanted to train his students for more than a bookish life, but felt obliged not to impose on them anything not readily recognized as appropriate to responsible teaching. Underlying all was an ethical tension. Morally exacting on himself and others in a personal sense, Weber was becoming increasingly convinced that what is dignity in a man might be the height of irresponsibility in politics and quite indifferent to scientific judgment, He could not then, or later, take the easy ways out of becoming either an ethical absolutist or relativist. He had gradually become, and remained, an ethical pluralist , that is to say, a believer in the government of different life-spheres by different imperatives, so that even the mere business of choosing a job involved, in his own words, a choice among warring gods.
Whether or not this explains his personal calamity, the fact is that he emerged from it by squarely confronting the two most fundamental ques-
tions the social scientist as would-be politician can ask: What can social science contribute to the shaping of our personal and social lives? And what is our position in historic process, what forces shape and have shaped that position, and how can these forces be controlled? Although he remained interested in the minutiae of policy and was occasionally active in the congresses of the Verein für Sozialpolitik , the period from 1903 to World War I was mainly devoted to these questions and led to a vast output of historical sociology, as well as to the philosophic writings that will concern us later.
With the war, the Bolshevik Revolution, and Germany's defeat in 1918, he turned again mainly to immediate political questions, especially the impending political reconstruction of Germany and the probable course of communism in power. He also again became absorbed in political activities, including publicist agitation against the Imperial regime, participation as an expert consultant in the Versailles peace negotiations, a major role on the constitutional advisory committee that fathered the Weimar Constitution, a short-lived membership in the Munich workers' soviet, and an abortive parliamentary candidacy for the Democratic party (he still had difficulties finding political machinery to which he could unreservedly attach himself or that would accept his uncompromising and idiosyncratic contributions).
His intense return to immediate political affairs did not mean, however, that a new synthesis of the scientific and political vocations had been worked out during the long years of sociological study and philosophic reflection, and certainly not a regaining of his earlier innocent belief in the identity of politics and social science. On the contrary, he had only gained clarity (as it seemed to him) about their separate natures and requirements, their restricted areas of overlap and mutual relevance, and dignified acceptance, touched by pathos, of the boundaries of his own professional life-sphere. The position to which he had then come he elaborated in two gigantic lectures, "Politics as a Vocation" and "Science as a Vocation," delivered in 1918 before the students at the University of Munich—lectures requested (ironically?) by the students to obtain his guidance in their own choices of careers. They have since become two of his most celebrated essays and the best summaries of the views we shall sketch below.
Weber's ambivalent career aspirations—familiar in a milder form to most political scientists—thus help explain the intensity and extensiveness of his thought about our topic and these in turn explain his influence on others. Neither, however, would have been so great had he not worked during a
pivotal phase in the development of social science and its context which externally defined and heightened his inner tensions. This is important not only for understanding his questions and positions but also for judging their relevance to ourselves.
Most fundamental to Weber's outlook was an encompassing social prognosis based on a judgment of what was salient in his present and decisive for the future. Weber saw social life as in process of becoming characterized by an unimaginably complex "functionally specific" social differentiation, a rapid multiplication of specialized and bureaucratized compartments, with narrow expertise replacing wider-ranging knowledge and activity, special associational attachments in place of more diffuse identifications, and rationally devised routines encroaching widely on personal spontaneity. Creativity and broad self-realization in that specialized and bureaucratized world could only come genuinely, he thought, from extraordinary men in times of extraordinary stress and falsely to alienated individuals indulging sterile cravings for "personal experience," and even the works of the extraordinary men, the charismatic figures, could only punctuate the march of routinization. Politics and academic life themselves were instances in point. Politics in all its aspects was increasingly becoming administration, and administration bureaucratized; academic work, increasingly, a special professional role, subdivided into numerous still more special fields. Moreover, the relationships between politics and higher education were becoming governed by the requirements of the functionally specialized society. The university's raison d'être was less to cultivate broadly educated men than to train the higher functionaries. The scientist and scholar himself increasingly achieved access and influence in politics as a kind of occasional functionary, a "consultant," and less than formerly through spontaneous personal involvement in a prestigious social class that was also a ruling class in Mosca's sense. Weber thought that judgments about the relations between politics and social science, to be pertinent, must be predicated upon this general tendency—a tendency he considered farthest advanced in the United States, which, with Tocqueville, he regarded as an intimation of the future of all social life.
In other senses, too, Weber's work was done during a politically and academically pivotal time. He stood near the beginning of mass democracy and other forms of mass politics; in his lifetime, the politics of warring ideologies and doctrines was still fresh; the mass media were being developed, and he wrote presciently about popular journalists as a special political class, advertisers as hidden political influences, and sensationalism for the sake of sales as a source of political irresponsibility; he witnessed also the early stages of that further expropriation of private spheres involved in revolutionary socialism and the growth of welfare states and planned societies. As for the academic setting, his career came not long
after the emergence of a specifically methodological consciousness in social studies, attributable to the diffusion of natural science ideas to other spheres. When he began his work, an academic war was raging in Germany between those holding that the natural and social sciences were quite identical and those who utterly separated them (into Naturwissenschaften and Geisteswissenschaften ); at the same time there were embryonic conflicts over the nature of concept formation for purposes of social analysis, over basing social theory upon historical studies or logically deduced models, over the powers of statistical method, and over the question of the uniqueness or comparability of social phenomena. All this is familiar to us; the only differences are that the orthodoxies have changed and the revolutions have become routines. Just because of that, however, Weber is crucial for finding lines of continuity and points of change in the work and orientations, intramural and extramural, of social scientists.
Needless to say, however, these points do not imply that his ideas were not affected by peculiar aspects of his person and context which bear upon their cogency and pertinence. For example, numerous commentators on his work have pointed out, rightly, that, despite wide travels and even wider historical study, his vision could never quite transcend the Germany of Bismarck and William II: a new nation characterized by a rampant officialdom, by Machiavellian leadership succeeded by pathetic dilettantism at the top, by an impotent opposition of high-minded but impractical ideologues, by ingrained party bureaucracies (which we know best from Michels's work), and not least, by a certain political constraint upon professors who, after all, were paid functionaries of the state. But even more important to the shaping of his ideas, if only because less widely understood, was a personal factor: the profound effect of his Protestant background upon his outlook.
In his sociologies of religion and economics, Weber stresses the sublimation of religious forces and tensions in worldly activity. We have reason to think that this emphasis, central to his originality, grew out of inner experience. Weber's ambivalences and tensions probably stemmed, at bottom, from the influences of very different, and estranged, parents: a gpolitical, worldly, practical, temperamental, morally liberal but domestically authoritarian father; a deeply pious, warm, dutiful, emotionally contained, morally demanding mother, intensely active in typically Protestant religious-humanitarian work. Of these two, the pious mother's influence was much the greater at the deeper levels of personality, the worldly father's more discernible on the surface. Weber was never religious in the conventional sense. Condescendingly respectful toward the pious, he had a thoroughly disenchanted attitude toward church religion, despite contempt for the self-display of Promethean atheists like Nietzsche. His youthful letters, however, display deep religious longings, and in his own life
he compulsively acted out much of what he discerned in the Protestant ethic. Those close friends who saw in his somber dignity of bearing and the biblical force and imagery of his speech a secularized evangelism were certainly discerning.
The Protestant ethic ruled his life and colored his views on politics and science in several momentous ways. Most important perhaps were his distrust and fear of passion as against sober matter-of-factness and the rationally systematic organization of personal life—a distrust and fear all the deeper for not expressing an emotionally incapable person but one who recognized with dread the stultified life of rational automatons. Weber also derived from the Protestant outlook a tendency toward the absorption of his personality in a larger order: that of the "vocation." Choosing a career he saw as more than a superficial preference for a special line of work. He saw it as taking on a calling, and that meant, to the Protestant, the assumption of compelling duties. To have a Beruf , a profession, was to be a kind of cell in an ordained network of "mechanical solidarity," in which each segment, even the least spiritual, was regarded as a kind of priesthood, working with "worldly asceticism" ad majorem gloriam Dei . As is characteristic of the Protestant devotee, Weber felt a "need to be crushed under a load of work" and "took pride in belonging to a fellowship of self-forgotten workers, who knew nothing better than devotion to the work at hand." Even after his breakdown had softened him into greater tolerance for his own and others' weaknesses, he remained a worldly ascetic, oscillating between compulsively hard and scrupulous work and near-collapse, his energies incommensurate with his conception of duty. More important than the sheer effort demanded by the Protestant calling is, for us at any rate, its requirement of total commitment and the doctrine of separate ethical realms for different vocations, each equally ordained by transcendental authority and each attuned to a special function in the overall order of life. This especially made the choice of vocations momentous. At the same time, Protestantism greatly heightened the burdens of that choice, as of all choices, by enjoining total self-responsibility for it, as a good and a necessity. Neither ascription nor other authority could absolve one from such responsibility; and the vocation itself was not anything like the traditional corporation, a regulated community, but at most an abstract fellowship of atomic individuals who had heeded similar calls and were continuously responsible for themselves.
This is not said, however, to sociologize away at the outset what Weber said about the gulfs and bridges between the two vocations that attracted him. Although his thought on our topic was compounded simultaneously out of abstract intellectual factors that we readily recognize and considerations largely alien to us, it remains to be seen how much of it is, by virtue of special personal and contextual factors, dead intellectual history
and how much still vital, by virtue of its abstractness or pertinence to our own context. Toward this end, we must now sketch his position in some detail and then return to its setting and our own to help in an appraisal.
Weber on Politics and Politicians
The role of political scientists in policy making is, of course, always affected by highly variable considerations: by what they currently know, by who happens to be in power, by the opportunities at various levels actually available to contribute to policy. Weber, however, wisely relegated (anyway, tried to relegate) such desiderata to a secondary role in his reflections, concentrating on more constant factors that affect positions on the matter largely irrespective of time and place. What, he asked in regard to practical politics, is its intrinsic nature? What manner of men does one encounter in it? What are the conditions of operating effectively in the policy-making process, and what makes for political impotence? What, if any, are the special imperatives of politics and the conditions and functions defining them? With regard to scientific work, his questions have a similar cast: What are its characteristic ends, techniques, capabilities, and vocational demands? Absolutely noncontextual thought about such questions is probably impossible, and Weber's reflections clearly were tied to modern social science and modern politics in a general sense; but by that very fact, he avoided being either too abstract to be informative in any context or too concrete to be pertinent in a setting different from his own.
Weber's conceptions of politics, political efficacy, and political imperatives rest upon five predicates: (1) politics is a realm of power and violence; (2) it is (especially in modern times) a matter of managing, and working in, complex organizations; (3) it is (again from the modern standpoint) a professional, not avocational, sphere, in which the crucial actors are political careerists and entrepreneurs; (4) it is a life of choice and commitment, hence for passionate men; and (5) since its choices are nothing if not systematically implemented, the passionate men must be not mere sentimentalists but "men of perspective" who harness ardor to judgment and calculation. These premises need elaboration.
Politics as Violence . "Politics as a Vocation" begins with a sober definition and ends in an impassioned sermon, but the beginning and ending form a unit because both concern the central role in politics of power, force, and violence. As for the definition: Politics, says Weber, obviously has ends and operates through institutions, but these are in no case distinctive to the political realm; what is distinctive to it is its instrumentality, the use of violent coercion, actual or potential, by political institutions in the service of political goals. In premodern societies, that instrumentality
was dispersed among many structures and used competitively; in modern ones, it has been expropriated and become concentrated in territorial societies by "states." Hence "all political formations are formations of violence," regardless of their purposes; the modern state is a special formation claiming a monopoly over the legitimate use of force in a territory. Coercive power, in that sense, is to politics what money or its equivalents are to economic life. Either may be used for good or ill; either may be accumulated with or without scruples; but purposes and restraints do not alter the nature of the currency. "'All they that take the sword shall perish with the sword' and fighting is everywhere fighting."
The definition becomes harangue when Weber reflects on what it implies for the relations between politics and ethics. Mainly it implies that certain ultimate ethical positions are simply incompatible with politics—above all those inspired by the Sermon on the Mount and, in a larger sense, all ethics of pure intention. Political ethics must not be sentimental but "responsible," in the sense that they must take into account the intrinsic nature of politics and involve willingness to adjust means pragmatically to ends, even at the likely cost of adjusting the ends themselves to available means. This call to moral trimming as nothing less than an imperative hardly expressed Weber's own sentimental preferences, shaped as they were by the more tender and exacting influences of pious Protestantism. On the contrary, it leads him to a bitter warning:
He who lets himself in for politics, that is, for force and power as means, contracts with diabolical powers, and for his action it is not true that good can follow only from good and evil only from evil. . . . Whosoever contracts with violent means for whatever ends . . . is exposed to its specific consequences. This holds especially for the crusader, religious and revolutionary alike. . . . The genius or demon of politics lives in inner tension with the god of love. . . . Everything striven for through political action operating with violent means and following an ethic of responsibility endangers the salvation of the soul. . . . [There] are inexorable consequences for [the politician's] action and his inner self, to which he must helplessly submit, unless he perceives them.
Not to face up to this imperative is to be doomed to a noble futility, like that of Bismarck's unworldly opponents, or worse, to supplying a facade of sublimity to diabolical men. The lesson is, of course, intended for moralists, not social scientists, but for the latter there is an added message: To work in politics is not only to contract with coercion but to face up to a theodicy, for in politics one will always also encounter undeserved suffering and unpunished injustice inflicted by the power wielders, and most important of all to the professional academic, "hopeless stupidity" among the high and mighty. Social scientists who act in politics must not only dampen sentiments but learn to suffer fools and to work
with them; they certainly ought not to expect that a scientific argument will be persuasive solely because of its scientific status. Power, justice, and sophistication are all too imperfectly correlated.
Access and Bureaucracy . Stupidity and his own scruples are, however, by no means the most important barriers to the social scientist's political influence. More decisive are questions of access: whether one can obtain it at all, the means required to get it, and what one has access to when it has been obtained. Most crucial to this matter is Weber's conception of politics as extremely complex, routinized organization, punctuated in some cases by the short-lived paroxysms of charismatic rule.
To influence policy one must, of course, have the attention of those who make it or themselves have influence. But just identifying the decisive actors in modern bureaucratized systems of government may be almost insuperably difficult. The difficulty arises only in part from the sheer complexity of bureaucratic systems, with their intricate internal specialization, involved methods of coordination, many-layered hierarchies, and confusions of formal competence and real power—although complexity and polycentricity are important. It is also a result of the defenses bureaucracies develop against external influence. These include obfuscating locations of responsibility by using the "official secret," a specifically bureaucratic invention that may also be used to establish an unwarranted air of superior knowledge vis-à-vis outsiders. Bureaucrats put outsiders at a disadvantage by overwhelming them with real and false mysteries and tend further to diminish their contributions by shunting them through, and often losing them in, the labyrinths of their routines. To these routines they are committed partly by habit and partly by vested interest, for narrow specialization chains them to their jobs. Weber thus clearly foresaw, indeed had some personal knowledge of, the not uncommon experience of government "consultants" whose uncertainties (about locations of power, about proper and feasible policy) grow with acquaintance.
Indeed, he felt that bureaucratic structures applied their defenses even to insiders—to other bureaucrats and, most of all, to their supposed political masters. Bureaucratic decision making he saw less as a process of imaginatively using pertinent information and expertise in the pursuit of clearly understood goals than as a more mechanical process of repetitively acting out routines and as an internally competitive process, the object of competition being to obtain for each segment a modicum of autonomous power. Overall, such structures were highly efficient, which is why they had everywhere replaced other modes of administration. They got things done (e.g., collected taxes well, applied regulations well, produced data and briefings efficiently, kept track of records, worked out sensible divisions of labor, engendered expertise), but their production, like that of
other machines, was only quantitatively impressive, not qualitatively creative.
The obvious alternative to working through bureaucratic channels is to be active "politically" in the conventional sense. That too, however, raises problems. One is the very power of governmental bureaucracies; a second is that the organs of political competition, parties and pressure groups, are themselves in modern states complex bureaucratic structures, having structural intricacies, mysteries, routines, and specialized vested interests of their own. Yet such is the efficiency of these structures, whether administrative or "political," that circumventing them altogether—for example, by activity in well-intentioned but weakly organized civic groups like Naumann's or the Verein für Sozialpolitik —was, for Weber, tantamount to opting out of politics altogether. One could not wish away the central importance of complex organizations in all phases of political life and to be efficacious one had to accommodate activity to them.
Politicians . What manner of men worked and controlled the political machines? Weber's answer to that question rested on a distinction between men who live "for" politics and those who live "off" it. To live for politics was, most simply, to be devoted to politics but not materially dependent on it—in other words, to be a political "amateur," one who loves politics for its own sake, the model of that sort of politician being the landed notables and other men of substance who constituted the main political class in representative oligarchies. Living off politics, per contra, meant being a "professional," that is, engaging in politics for the purpose of acquiring values (money, goods, status), even if not only for that reason. Political professionals had, of course, always existed. The princes who had built feudalities into states, for example, had used such men systematically in their struggles against ecclesiastic and secular corporations. But with the progress of political expropriation, the professionals had greatly multiplied and become much more than instruments. Modern politicians, whether bureaucrats or not, were largely men tied to politics not just for ideal rewards but dependent on it as well for safety (i.e., security), income, and deference, hence oriented to political spoils and booty—political acquisition—for their own sakes.
This had obvious and important consequences, two above all. First, it meant that the rational definition of political goals and means would be distorted not only by complexity and routines but also by the need of political actors to do things that would further, or at least not imperil, their personal command over values. Thus bureaucratic timidity grew out of a need for personal security no less than the institutional routinization of bureaucratic roles. Politicians had to calculate the gains and losses in popularity and financial supporters entailed by stances in politics. They
were impelled also to get out of political power what they could while power lasted and to ensure themselves against the possible loss of it by rendering services to those who could provide pantouflage: remunerative private positions when public careers had ended or been interrupted.
Closely related to this is the appearance and signal importance of new kinds of political entrepreneurs. The early entrepreneurs in politics had been robber barons literally speaking: expropriators and monopolists who, by ruining competitors, had built large kingdoms out of petty principalities. Their means had been military force and a surer justice and greater administrative efficiency. Rationalizing their staffs and armies, raising their outputs while lessening costs, giving the public what it wanted, they gradually drove out of the market less efficient or more scrupulous producers of political goods. Once power had been concentrated, however, political entrepreneurship took the form more of exploiting it systematically for other ends (e.g., economic ends) or establishing a kind of brokerage between political power and private aspirations. Its prototype, although not sole manifestation, Weber saw in the American "boss" who built up reservoirs of reliable voters, activists, and technicians and used them to place men in official jobs and to obtain through them politically allocated values for himself and his clients. Weber did not entirely frown upon that kind of entrepreneur or the systems of patronage and spoils in which he flourished, but indeed regarded him as a constructive counterweight to the petrified routines of bureaucracies. Truly innovative political entrepreneurship, however, he thought could come only through charismatic figures who, by mobilizing and channeling anxieties and fervors in troubled times, could thoroughly unsettle and perhaps reshape routinized political systems, even if their creations were themselves fated to fall into the hands of careerists and doomed to routinization.
Effective Politics . Coercive force, complex organization, careerists and entrepreneurs of power are, however, not all there is to politics. They are only instrumentalities and general aspects of its structural components. Each of the components may make a part of its business the attainment of autonomous power, the maintenance of routines, or the acquisition of material values, but the function of the whole is to make and realize a society's most consequential choices—to define the ends and means to ends in the service of which the awesome coercive powers and technical capabilities of states are to be mobilized. These choices are often cruelly difficult, partly because of the instrumentalities used to carry them out, partly because they are often compelled by circumstances rather than entirely voluntary, partly because they must often be taken hastily on insufficient information or reflection. What imperatives for political action, especially efficacious action, follow from this aspect of politics?
The most important requirement it imposes, in Weber's view, is that those who wish to work political effects have what he variously calls enthusiasm, Glauben (faith or belief), ira et studium (scorn and bias), and passion. In the first place, this is because of the fact that pure power politics is futile and senseless. It may create transient disturbances and ephemerally satisfy base appetites, but Weber saw clearly the mere destructiveness and inner weakness of the cultists of power (like D'Annunzio) and of the "braggarts and parvenus" who use it mainly for "vain self-reflection" (like McCarthy). Second, faithful enthusiasm is required also because defining goals entails, at some point, making moral commitments, and moral commitments, in Weber's view, cannot be worked out by technical calculations only. Third, it is required to reduce hesitation in the face of great pressures, responsibilities, and objective uncertainties. And it is needed because of the very instrumental and structural characteristics of politics. Willingly to use coercive power as means implies forceful convictions, not weak half-certainties, and attempting to move the complex, inscrutable machines of politics against the strong resistances of their routines calls for great energies that can come only from strong passions.
In these senses politics is most certainly a realm for sentiment. Indeed Weber, despite his somber passages on the generally petty routines and stakes of politicians, always regarded politics as the preeminent realm for human heroism and the highest area of human liberty, since it offered the greatest opportunities for making consequential choices and effecting them against powerful impediments.
Just as pure power is politically senseless, however, so also is pure sentiment—"sterile excitation," as Simmel called it. If choices are to be implemented by practical activity, including coercive power, choosing is not so light a matter as it is in print and talk. Passion may be requisite to it, but so is "responsibility," "judgment," "assessment"—dispassionate appreciation of relevant givens and genuine possibilities, rational calculation of the various benefits and costs of alternative ends and means, and pragmatic understanding of the real relations between ends and means, including understanding of, and willingness to accept, the "tragedy with which all . . . political action is interwoven," namely, that sublime purposes may be realized only if compromised and pursued by morally inconsistent means. Weber's efficacious political actor is, in essence, what President Kennedy called himself, an "idealist without illusions," a man of "tamed passion," there being also two corruptions of the species, idealists with illusions (excited romantics) and illusionists without ideals (pure careerists and entrepreneurs of power); but since the latter always exist, a condition of efficacious political action is learning to work with and through them, to some extent at least on their own terms.
Science Versus Politics
Weber's reflections on the relations of social science to public policy were worked out with reference to this model of political instrumentalities, structures, actors, functions, and conditions of efficacy and a similarly general model of social science. From these reflections two villains emerge: arrogant social scientists who overstep their role and pusillanimous politicians who do not live up to theirs. The essential thrust of Weber's arguments is not only to affirm a substantial role for empirical social science in responsible political action, but also to deny its sufficiency (or anything even approaching it) for the conduct of political affairs. In social scientists Weber wished to awaken mainly a sense of limitation vis-à-vis politics, indeed all "practical" life, and a sense of the distinctive demands of their chosen vocation; for politicians he emphasized responsibilities of which neither social scientists nor anyone else could relieve them; for both he wanted to define the distinctive characteristics of their callings and the dangers of identifying them too closely or separating them too widely.
To clarify why and how he proceeded toward these ends, the following matters now need discussion: (1) how Weber viewed the nature, capabilities, and limitations of social science; (2) what contrasts and strains he deemed to exist between the political and scientific roles; (3) at what points he considered these contrasts small enough to warrant the close identification of the roles; and (4) what perils he thought might follow from failure to grasp the nature of their differences and compatibilities.
Weber's social science was in most respects consistent with modern "behavioralism" in political and social studies. Many proponents of the latter indeed respectfully confess his inspiration in regard to their formulation of problems, modes of conceptualization, theoretical approaches, types of model building and hypothesizing, and the use of certain techniques for gathering and processing data. Just for this reason Weber is widely thought of as a man who glorified the work and capabilities of scientists and affirmed a close identity between the natural and social sciences. In fact, the contrary is the case. All of his writings on science are pervaded with a sense of its limitations, to a pitch occasionally verging on despair, and many of these writings are specifically concerned with drawing large contrasts between the natural and social sciences and pointing out the specially great limitations of the latter. To be sure, he did not revile science as do the professional antipositivists, and he most certainly did not glorify some nebulous unscientific "wisdom," "prudence," or "experience" as they do. But he was at the very least a positivist without illusions.
Weber, of course, did not think of the natural and social sciences as absolutely different. In many respects they were certainly similar, having substantially the same purpose (to discover trustworthy empirical generalizations about phenomena), using largely similar techniques (those of systematic observation, logic, and quantification), and requiring rather narrow specialization (if only because their methods demand hard and devoted work with voluminous minutiae: "brooding at one's desk" over "thousands of trivial calculations"). To this extent they also have similar power—and similar limitations.
The power of science is that it alone can provide valid knowledge of relations among phenomena, social or "natural." If one wishes to know what effects interest rates have on employment or productivity, whether and to what extent political campaign techniques affect voting turnout and voting preferences, whether upward social mobility creates mainly satisfaction or heightens perceptions of deprivation, in what ways changes in electoral systems may affect party systems, or any similar matters, "nomological" knowledge is indispensable. Men do have beliefs about such relations apart from scientific laws, based on individual common sense, folk wisdom, experience, intuition, or cosmological philosophies; but these beliefs are themselves nomological knowledge, in a cruder form and built on shakier foundations than those of science.
Weber summarizes the limitations of science in saying that it cannot, however much it may be perfected, discover "meaning" in life. Every epoch that tastes of the tree of knowledge is, in his view, fated to discover that the meaning of existence eludes it, except insofar as it creates such meaning for itself, in other ways; indeed, to the extent that life becomes "scientized" meaning recedes and men become "estranged" from the world. What did Weber mean by this?
First and best known, he meant that science cannot provide any guides to personal conduct or any means of choosing among "ultimate" alternatives. Before Tolstoy's questions—"What shall we do and how shall we live?"—it remains silent. Even when desirable ends have been chosen, it cannot solve or reduce such problems of conduct as whether such ends sufficiently sanction undesirable but unavoidable means, or whether in choosing and pursuing desirable ends the possibility of undesired repercussions should be taken into account, or how to deal with conflicts among conflicting desirable ends. To the medical practitioner, for instance, it offers a highly developed technology for relieving suffering and extending life, but it cannot tell him whether to do so is good and in what cases it may be justifiable to end life as redemption from suffering. To the political scientist, it may offer technical knowledge of how to maintain a certain system of rule, but it cannot provide guides to whether that system is intrinsically valuable or more so than probable alternatives. In the most
general sense, science may tell us much about what the world is like, but says nothing about whether its nature is sublime or diabolic and whether it is sensible to live in it at all. Not only how to live but even whether to live are ineluctably questions for choice and compromise. And as science advances, the "meaning" of life, in the sense of a moral orientation toward it and moral understanding of it, may recede in several senses: as a result of an overestimation of the powers of science and the surrender of responsibilities for creative choice to its technicians; as a result of the fact that science continuously discovers new facts and relationships to integrate into moral conceptions of the world; and most of all, because science offers ever greater and more fateful technical means for working effects, hence for defining choices of ends and means. Weber could not foresee specifically the concrete possibilities that exist for us—to destroy virtually all life, to prolong almost all suffering, to uproot, incarcerate, coercively police, or indoctrinate whole peoples—but he certainly saw the principle of the thing and realized that every new technical possibility imposes new burdens. He foresaw also the likelihood of technology being increasingly relied upon to define choices lying beyond it, for the sake of the semblance of choosing wisely.
In saying that science does not discover "meaning" in life, Weber had in mind, second, a characteristic of the very nomological knowledge it provides: the intrinsic transience and tentativity of that knowledge and the extent to which, as a result, it makes all individual contributions to science fragmentary and ephemeral. To be a scientist means to belong to a devoted company that proceeds gradually and with painstaking labors toward the objective of absolutely dependable empirical knowledge of the world, but never attains that objective. There are no ultimate and absolute tests for generalizations about observed data. New data constantly present themselves as scientific technology itself makes possible wider and deeper observation; in any case, there is no way to know when data have been exhausted. The generalizations of science themselves generate new generalizations, themselves become new data and sources of new actions that constitute new data, and may always be made more general, simpler, or more powerful. Science, therefore, knows no rest, only continuous striving. The scientist's judgment must be always in abeyance, every new finding being doubtful or a source of new mysteries, and he, as individual, is merely a figure in an endless collective process which is itself only a fragment of the whole of mankind's intellectual activity. "It is the fate of every scientist to see his work surpassed," says Aron, following Weber, who himself holds out to scientists the biblical injunction, "thousands of years must pass before you enter into life and thousands more wait in silence," as especially pertinent to them.
The endless progressiveness of science seems to Weber to denude life
of meaning because he agreed with Tolstoy that it makes death senseless. For men chained to an infinite progress, "life should never come to an end; for there is always a further step ahead for one who stands in the march of progress. And no man who comes to die stands upon the peak which lies in infinity."
Weber especially contrasted this transience of science with the permanence of art. Both are creative, but the creations of artists stand in the march of progress in a very different sense. Technical progress may offer new possibilities to artists, and, in a sense, "enrich" their work; many artistic innovations (e.g., the Gothic style, evolving orchestral composition) have in fact originated in technological advances as much as in aesthetic inspiration. But no work of art is ever surpassed, in the sense of being made aesthetically less valuable by new artistic techniques. All works of art are legacies, all accomplishments of science merely episodes.
Science is estranged from life also because of its extreme specialization. Scientific progress carves up the world of phenomena into ever narrower fields in each of which progress itself makes work continuously more taxing and more life-absorbing. Hence the scientist must pay in growing ignorance of the whole for every increment of knowledge of its parts. Synthesis may be possible, but may only create new special fields carved out of the margins of old specialties (e.g., "political sociology") or be bought at the price of inadequate knowledge of what is synthesized.
Finally, science cannot invest life with "meaning" because it is necessarily abstract and in that sense "unreal," even though its abstractions may be intended to capture the true blood and sap of life. Weber's science is certainly not Plato's philosophic sun, the reality of which is poorly reflected in the shadows of concrete experience, but just the reverse. Its concepts, models, formulas, hypotheses, indices, and correlations are themselves shadows of reality through which men try to make experience intelligible, if not meaningful. The abstract "concept," argues Weber, appeared to the Greeks as the key to eternal truth as against transient opinion. Reformation scientists still believed in science as a way to God, hidden and remote from us but revealed in His creations (even "in the anatomy of a louse"). Now, however, science is recognized as consisting of no more than heuristic devices, helpful in interpreting life but separated from it by an insurmountable barrier between abstraction and concreteness. The specialization of scientists is relevant to this point, too, since all their laws and regularities, as well as being abstract, capture only aspects of the complexity of concrete configurations.
Reading through such passages, one may get the impression that Weber tried to glorify the scientist as a kind of antihero, willingly engaging in consuming labors that can come to no end, no fullness, no foreknowledge,
and no moral guides to life. Up to a point this is probably so, and it corresponds to the Protestant's gloomy sense of vocation. But it is as well to reemphasize also the other side of his view of science: his belief that, whatever may give life "meaning," science is indispensable to any sort of technical mastery over it, so that the effective attainment of any creative aspiration depends to a large extent upon scientific knowledge. In stressing the limitations of science, Weber tried to affirm that human life retains large areas of genuine liberty and creativity regardless of scientific progress, while at the same time stressing the large extent to which free, creative choices may themselves be senseless without the technical knowledge that science alone provides.
All this pertains to every kind of science. Even with regard to that small slice of intellectual life constituted by the sciences, however, Weber was a pluralist. The social sciences particularly seemed to him to require distinction from the natural because of two characteristics, both of which make them less powerful in achieving nomological knowledge and the technical mastery it provides.
First is the fact that human acts, individual or in social aggregates, have "meanings" to the actors which vary among individuals and cultures. These meanings include intentions, that is, goals toward which actions are directed, normative expectations, and culturally peculiar attributions of significance. In that sense, "social facts" were not conceived by Weber à la Comte as mere objects, or even quite à la Durkheim as ways of acting imposed by external constraints, but as behavior inextricable from subjective, internal meanings, despite the possibility of a purely objective observation of human action and the undeniable role of external forces in conditioning internal meanings.
How does this affect the nature and weaken the capabilities of the social sciences? In the first place, it makes them more complex than other sciences because it adds a distinctive variable—and "meaning" is a variable, since it is not deducible (not fully, anyway) from universal psychological traits. This variable is omitted only with the gravest consequences, since subjective orientations do not always closely reflect objective circumstances, may independently have causal effects, and always intervene as intermediary forces between objective conditions and their objective consequences. Such orientations must, therefore, always play a role also in attempts to use the social sciences technically, that is, in social engineering: the same "policies" in different cultures may have vastly different effects, not so much because objective conditions differ but because the meanings of the conditions and policies may be variously interpreted. At the same time, however, meanings are extremely difficult to get at and one's formulations of them difficult to test when one thinks that one has got at them. Verstehen , or empathy—the power of projecting oneself into the
object of study—is important in social study, but adds to it a special problem not fully soluble by standardized techniques of inquiry and hence an added source of arbitrariness that widens the gulf between reality and scientific constructions.
The second distinctive characteristic of social science limiting its powers is that its subject, according to Weber, and again contrary to Comte, is not fixed and static but inherently "developmental." This is not to say that it is "progressive"; Weber in fact attacked all "scientific" theories of progress as assuming value standards not determinable by science. It means only that human history brings forth ever new social forms and patterns of action rather then merely repeating old ones. The processes of historic change, moreover, are hardly predictable by deterministic historicist cosmologies, precisely because men can, by means other than science, invest life with meaning and make, even if within limits, creative choices on the basis of their orientations. Weber wanted, according to Aron, to preserve the "drama" of history—its irregularities, accidents, and purposive strivings—against any thoroughgoing mechanical determinism. Even more important, he wanted to stress that social science theories cannot be cumulative in the same sense that the theories of natural science are. In the social sciences all the possibilities for infinite process previously mentioned exist, but in addition to them old observations and the theories they support may become irrelevant (not just enlarged, improved, transcended) through historic processes of creative innovation. In that sense, the social sciences are sciences "to which eternal youth is given"; at any point in time, social scientists may find that history demands of them a virtually fresh start.
One may ask how it is possible to be a social scientist at all when one holds such views about meaning and creative development in human affairs. Weber could be a committed social scientist despite these views because he believed in the plain necessity of science for efficacious creative action and because the special characteristics of social behavior seemed to him only to restrict the capabilities of social science in certain senses, not to make it futile. To an extent, one can indeed avoid all cultural and historical peculiarities in social science by developing very abstract and general theories (like models of "rational" optimizing actions or theories of the universal functional imperatives of social life), but only at the unavoidable costs of widening the gulf between theory and reality and being uninformative in regard to less general, possibly more important questions. These costs Weber himself would not incur; hence his own broadest generalizations are always middle-range theories pertaining to concrete historic processes and cultural systems of meaning. At the same time, he believed that a modicum of human experience could be grasped by universal scientific "laws" independent of history, such as those of psychology, and a larger portion by the study of proximate causality, even if still another
portion was amenable only to "interpretative understanding"; and he believed also that systematic comparative historical study, aided by psychological theory as well as a more nebulous empathy, could make motives and meanings understandable by tracing them to their origins (as he himself traced the motives of modern capitalists to Protestant beliefs). Social science to Weber consisted, in essence, of an admixture of laws, hypotheses about proximate causes and trends, and empathetic understanding, corresponding to the combination of determinism, probability, and choice—of necessity, circumstance, and creativity—that constitutes social life.
On the basis of these sketches of what is involved in being a politician or social scientist, one can readily see huge contrasts between their roles. Let us list only the most general and important.
First, since choice is the essential business of politics—choices of ultimate goals that require moral commitments and of immediate means that cannot be purely technical since they may have to be selected upon inadequate technical knowledge and may pose moral problems of their own—politicians need, and generally develop, passionate convictions and a sense of certainty, even personal infallibility. The social scientist's vocation, per contra, is morally silent and implants a zealous uncertainty, dispassion, and tentativeness, and a deep sense of the fallibility of all personal beliefs and labors.
Second, political work must always be done with reference to concrete, extremely complex social wholes, whereas social scientists work with abstract and simplified conceptions that concern only fragments of social experience. Both may be highly specialized, but they are specialized in different senses. Political specialization involves the distribution and coordination of tasks that are themselves highly complex, whereas scientific specialization involves splitting concrete complexity into abstract fragments. Scarcely a single special political task does not involve psychological, economic, administrative, and sociological considerations in complicated combination, but these are just what scientific specialization disjoins.
Third, political work is always done in large, substantially routinized organizations that must be moved and jockeyed if anything is to be achieved. The organizations, moreover, are not merely instrumental facilities to be adapted at will to any purpose, but to an extent ends in themselves, in that the politicians' careers may be bound up entirely with maintaining their positions in them and preserving their routines. Consequently, adapting means to political ends is not just a matter of impersonal calculations but entails also a host of personal stakes and considerations, large and petty. In contrast, social scientists work mainly as individuals, have to endure only a minimum of routine, and see the relations of ends and means principally as abstractly logical problems—not
least when pronouncing on political matters, with which their own incomes, safety, and deference are not bound up.
Fourth, political and scientific space and time have very different dimensions that make for contrary perspectives. Political space is parochial, tied to specific societies, whatever visions there may be to the contrary; scientific space is inherently ecumenical. The politician's time perspective is inherently constricted; the social scientist's is expansive and indeed, in a sense, infinite. Politicians must generally act expeditiously even if that entails making commitments upon little or no preparation; in any case, their work lies in the present moment or immediate future. Social scientists, on the other hand, may sit long and patiently making their myriads of trivial calculations, safely knowing that nothing will be impaired by the ticking away of time, except possibly self-esteem; and their work is free of temporal constriction also in that its end is always infinitely remote.
This list of contrasts could certainly be enlarged. For example, one could, and probably should, add to it contrasts between scientific and political communication, such as those entailed in teaching as against persuading and those between the religious openness and honesty of scientific communication and the compulsive mystifications and flimflam of politics. What has been said, however, should suffice to make the essential point, which is that the contrasts between the scientific and political callings are such that they will produce considerable strains when their practitioners encounter one another or cross vocational boundaries. Because they evolve different orientations—different vocational systems of meaning—professional politicians and social scientists are likely to be mutually unreceptive and antipathetic, as well as highly ineffective when engaging themselves outside of their accustomed spheres, although one should immediately add that this is so only insofar as they properly understand and practice their vocations. There certainly have been politicians who felt more at ease among scientists and scholars than in politics itself (Balfour, for example) and even more scientists and scholars who took readily to politics; but they have rarely been notable politicians or accomplished scientists.
Strain, however, does not imply irrelevance and the desirability of utter separation. Weber's thought about the relations of social science to policy making was certainly not intended to construct an elaborate rationalization for indulging that "craving of his soul for failure" which Leo Strauss has somehow detected in him. His aim, as I understand it, was just the opposite: to promote the potency of both social scientists and politicians by clarifying for the one what he can do in public affairs and for the other what he must do; by identifying clearly areas of overlap and complementarity between the two roles and equally clearly corrupting dangers that may arise when they are joined; and of course, by stating explicitly factors
that may make for strains in any case but all the more so when they are unrealized.
Certainly Weber's claims for the contributions social scientists can make to policy qua social scientists are far from inconsiderable. Although they cannot provide scientifically ultimate value standards, there is much they can do, at least potentially (i.e., to the extent that they actually possess scientific knowledge and can adjust themselves sufficiently to the ways of the political world). Given an explicitly stated goal, they can supply knowledge of technical means for its attainment. Even if they cannot measure the intrinsic ethical value of a goal, they can assess its "meaningfulness" in a given setting, that is, whether it makes sense to pursue the goal at all. They can help determine with precision the impact on other spheres of pursuing any special goal and hence the overall costs of a policy. Through logical analysis they can also make explicit the more general values implied by clusters of goals and judge the consistency of goals with one another. They can elucidate what data and theoretical knowledge are ideally required to choose among alternative means to ends. And they can study values and goals as empirical givens—for example, expose the preconditions and consequences of their being held and thereby help men to decide whether to hold them at all.
It is true that all this is only instrumental and that the political decision maker must take into account factors in no sense scientific, in ways not purely technical, in making even instrumental choices. But it is also true that social scientists can be especially useful in policy making precisely because their orientations are so different from, and complementary to, those of politicians. They can, for instance, serve to dampen passions where coolness may be essential, detect self-serving pettiness in political purposes and calculations, induce a sense of uncertainty where false conviction may be self-defeating, help politicians to see through comfortable but dysfunctional routines, provide a larger sense of space and time where narrowness and haste may have bad consequences—in short, help politicians to avoid the faults of their own virtues, always provided that they achieve rapport with them without assuming the politician's own distinctive orientations.
However, in stressing the complementarity of the scientific and political vocations, Weber was also necessarily insisting on their essential separateness. Most important, he saw two serious dangers in a too close identification of them, one pertaining to social science, the other to politics, but both expressed a single, more general fallacy, that of "scientism"—which means literally what it says, regarding science as an "ism."
The chief danger social scientists should avoid in regard to political activity is to play at being moral teachers, agitators, demagogues, and
"prophets" in their professional capacities, most of all in the classroom (although by no means only there). The fundamental reason for this is, of course, Weber's conception of the limits of empirical science. Weber did not accept Comte's vision of a scientistic ethics: the belief that as there is no room for free judgment in physics so there will be none in social life once the sciences pertaining to it are perfected. That view seemed to him simultaneously to misunderstand science and morality and to endanger human dignity. Nor did he subscribe to the attitude Jacques Ellul considers inherent in the technician's approach to decision making: the belief that all problems have unique solutions deriving from purely technical considerations, so that as technology advances the necessity for moral choice diminishes. Even in regard to instrumental decisions, let alone commitments to ultimate ends, scientific calculations leave room for other considerations and creative choices because of the inherent uncertainties, abstractness, finitude, simplifications, and fragmentation of science. For "values," then, science is irrelevant, for "evaluations" insufficient, even though its adequacy for the latter grows with technological advance.
There is an additional reason for ruling moral preaching and policy recommendations especially out of the classroom. This is the inherent asymmetry of the teacher-student relationship. After all, the teacher's authoritative position can easily be used to stifle discussion and contradiction on controversial matters. Students and teachers in any case do not enjoy "equal time" if they disagree on matters eminently subject to disagreement. Teachers can permanently harm students who make themselves obnoxious to them through examination marks and other means. Students tend to be respectful and impressionable anyway and to crave leaders and guardians rather than teachers, as well as being unaware of the fallibility of the petty gods who reveal themselves on the lecture platforms. And on the other side, teachers may be tempted to court easy popularity by generating sentimental excitements rather than demanding exacting empirical work and ruthless analysis, of both themselves and their students. Should teachers nevertheless wish to preach, plenty of less asymmetric channels are available to them for doing so.
It was said in Weber's time, and still is today, that moral teaching and the closely related academic concern with policy questions are justified because the end of higher education is the whole cultivation of men rather than specialized training. Weber, however, was strongly for the latter, not just because the specialized society requires specially trained experts, but, more important, because for him cultivated men do not surrender or fail to realize their moral autonomy, the right and duty of resolving problems of conscience in their own way. Moral men may, after all, be cultivated in two ways. One may teach them a particular version of morality; or one may sternly refuse to interfere with and lessen their sense of a creative
liberty of choice, which is the essence of moral personality. So strongly was Weber for the latter approach that he greatly preferred the heated moral histrionics of Treitschke and Schmoller to teachers who believed that it was permissible to parade values and policy judgments on the lecture platform provided they were presented with cool detachment; he preferred the outright demagogues because they were less likely to deceive anyone about what they were doing.
Contrary to common belief, these views do not connote that Weber was an ethical "relativist." Partly they stem from his ethical pluralism, that is, his belief that different realms of activity impose varying imperatives, the scientific vocation demanding a certain ascetic self-control in sentimental matters. Mainly, however, they reflect his fear of encroachment upon men's moral autonomy, without which no ethical life exists at all and which he considered the creative motor of human development. He saw the complete life as combining knowledge (science), conscience (morality), and will (passion), much as did Freud, and wished to keep each integral and intact.
His own reaction to the reception of Freudian theory by friends who used it to justify sexual promiscuity in the name of "healthy living" illustrates his position. Weber greatly admired Freud's scientific work but considered it potentially dangerous to moral life: (1) because there is no reason to consider healthy nerves a moral absolute as against other values, like self-constraint and heroic suffering; (2) because he foresaw, with rare prescience, the possibility that psychoanalytic clinicians would encroach on personal responsibilities by becoming a new species of directeurs d'âme; and (3) because he considered Freudian theory to be as transient and inadequate as any other scientific theory. He also feared that transforming it into a moral code would rigidity it in a still highly inadequate form, preventing the realization of its scientific promise and thus threatening both morality and science.
"Scientism" might also take a second form. If the need for choice is especially pressing and decisions are especially difficult to make, politicians, including bureaucrats, may become not too resistant to social scientists but just the opposite, too susceptible, abdicating to scientists their own responsibilities. They may themselves come to regard scientific knowledge and techniques as a surrogate "ism," a kind of revelation that obviates fateful choices. Weber loathed the surrender of moral responsibility in all men, but most of all in those who had chosen a vocation the very essence of which is decision making. He foresaw, however, that with the advance of political expropriation, with the growing complexity and momentousness of rule, a powerful tendency toward the "scientification" of politics and administration might arise, especially since scientific advance would occur simultaneously with "political development." This possible tendency he regarded simply as yet another kind of routinization of spheres in which
liberty and creativity had prevailed. He also regarded science as another potent weapon of mystification with which bureaucrats might overwhelm their supposed masters, especially if successfully joined to the already highly developed weapon of the "state secret."
Symbiosis and Separation
All the essentials of Weber's ideas on relating social science to political activity have now been sketched. As is often the case with his thought, however, summary is difficult. The alternate bursts of energy and inactivity that went into his work left much of it fragmentary, episodic, and in the end, inconclusive—all the more so since he died before his time, while almost all his major work was still in progress. By the time he gave his last lectures on politics and science, he had isolated and analyzed the chief elements of the problem of relating them, but although the lectures state with unparalleled clarity and vigor the nature of these elements, they do not present any final, clear-cut position on the problem. Perhaps this was because Weber had not come to any such position. But perhaps he simply would not state it because he felt that choices of career, and of ways to relate them to other choices, had in the last analysis to be his students' own moral burden—that he could only help them to be "responsible" by clarifying the inescapable commitments, limitations, and consequences their choices entailed. Whichever is the case, the two lectures take one to a crossroad, and only say, "You may go this way or that; if you go in this direction such-and-such will be your road, and if in that, it will be so-and-so; and there will be such difficulties in going from the one to the other and such paths between them; choose."
Yet although Weber's thought comes to no definite conclusion, it surely points to one. He sought most of all a symbiosis of free, creative moral responsibility and technical mastery, either being senseless without the other. This necessarily implied a symbiosis between politics, the preeminent realm of the first, and science, the chief source of the second. Yet either was all too capable of encroaching excessively on, indeed destroying, the other, making action merely technical or merely sentimental. Symbiosis could not, therefore, simply mean combination. Moreover, the vocational cultures, as it were, of politicians and scientists were so different that they could neither personally cross nor collaborate across the boundaries of their callings without considerable strains and a high probability of ineffectuality. And in addition to that, both callings were, if anything, growing more divergent, as well as more life-absorbing for their practitioners: politics more organized, bureaucratized, specialized, professionalized, demanding, and fateful; science, through its very progress, more abstract, segmented, and evanescent. Hence, one is left with the
impression that Weber considers a fruitful symbiosis most likely if politicians and social scientists work diligently and dutifully within their separate life-spheres, facing up to their quite different imperatives, keeping their distance, but recognizing the limitations of work in each calling as a condition to restrained and mutually sympathetic cooperation, if only at their margins.
For the social scientist this need be no counsel of resignation toward politics. Like anyone else, he can still be politically committed—provided that he acts out his commitments avocationally, not "in the name of science," in the usual market places of politics, and that he does not thereby neglect the stern duties of his vocational role, which he will, after all, have chosen freely and can freely choose to leave. More important, since the various vocations are all fragments of an interdependent whole, he can perhaps, in the final analysis, be more efficacious politically by doing as diligently as possible what he is most fit to do—which (unless he has mistaken his real bent) is the advancement and teaching of nomological knowledge—rather than by engaging himself intensely in a sphere so very different from his own. After all, social science can inform politics only to the extent that it can inform at all—that is, only to the extent that it has actually been developed.
That leaves the practical question of how social science, such as it is, might in fact inform political action, insofar as it has relevance. Weber says nothing specific about this. Perhaps he feels that if the pitfalls and vain pretensions afflicting their relationship are made plain, the problem will solve itself, which is surely improbable. However, here and there in Weber's writings there are hints as to how he would have social scientists influence politics in their professional capacities. They may do so through restrained publicist activities and equally restrained technical consultation. Best of all, they may do so by providing to students, who might choose politics as a career, decent specialized vocational training, provided that they do not delude them with any nonsense about there being a "science of policy." Weber considered this phrase an infelicitous result of the German universities' serving mainly as training schools for state officials and held categorically that there can be no special scientific preparation for policy making that differs from scientific training for any other purpose.
Anyone who wishes to treat this position as an intellectualized response to purely personal problems in a special social setting can do so easily enough through the materials earlier provided. Yet the fact that a position suits a man's temper and justifies his life does not invalidate it, nor is an argument made irrelevant by the mere fact of being two generations old, least of all if a man had some understanding of continuing social forces.
From an exposition of Weber's thought, we turn therefore to an appraisal of its present pertinence.
The Contemporary Relevance of Weber
Does anything in contemporary politics or political science compel a revision of Weber's arguments and apparent conclusions? In particular, have recent trends in either sector increased the capabilities of political scientists to contribute to policy making in their professional capacities, either by collaborating across or actually crossing vocational boundaries?
The principal development in recent political science has been the growth of what is generally referred to as the "behavioral" persuasion. This involves in essence a wider, more intensive quest for "nomological" knowledge as Weber thought of it, based on methodological precepts derived from the natural sciences and the more positivistic social sciences. Surely that development has increased the capabilities of political scientists to contribute to policy in at least this sense: it has augmented considerably their stocks of knowledge and skills relevant to policy questions. Useful and instructive work has been done by contemporary "nomologists" in political studies on such subjects as the origins and resolution of conflicts in general and violent political conflicts in particular; conditions of political stability, especially in democracies and new nations; the conditions and prospects of certain kinds of engineered political change, such as "nation building"; the general structure of international systems and their specific potentialities for war and peace; decision making in crisis situations; and many others in a similar vein.
As for the skills acquired for purposes of such work, it may suffice to say that it is easy from any point of view to see the good, and difficult to see the harm, in political scientists learning new procedures for obtaining reliable data, processing them into findings, and testing the findings; and surely the same applies to their increasing mastery of the exact disciplines (statistics and mathematics) and the languages, perspectives, and methods of other social sciences. Many possibilities Weber attributed only potentially to the scientific study of politics (or any other social science) are actualities now, even though the ratio of actualities to possibilities is still puny and despite the fact that ever more "knowledge" is transcended, ever more rapidly, by progress in political inquiry, in the manner of all nomology.
So far, so good. But what of opportunities to bring such knowledge to bear on policy? Surely these too have grown in many respects. The easy informal relations Weber knew between politicians and academics—based mainly on class position and an attendant coincidence of tastes, education, residence, and circles of friendship and kinship—assuredly have declined, but in their place have developed numerous functional equivalents. An unparalleled number and variety of formal channels bringing political and other social scientists into the governmental machinery now exists. These
include complex networks of consultantship, formal conferences, and task forces sponsored by governmental agencies; "in-house" research divisions of government departments that both carry out and sponsor professional study; research auxiliaries of such departments; and some full-time service by political scientists as departmental specialists. In addition, there has been a good deal of mobility, in both directions, between academic and governmental institutions, and in that sense at least a marginal fusion of the two vocations. The fact of that mobility is not unprecedented, but the amount of it certainly is. One should also note the growth of graduate training schools for the public service, providing opportunities to academics to devote themselves to policy-oriented teaching and research and to influence future "politicians" at an impressionable age and present ones in midcareer. Not least, as the business of government has become more complex and consequential, scientistic attitudes in politics and administration, as Weber expected, have concomitantly grown; and whatever the dangers of these attitudes, they do at least provide opportunities to social scientists to obtain a hearing among those who wield political authority. In fact, the channels between social science research and government are now such that, alongside in-house and auxiliary research establishments, there has even grown up a sizable industrial entrepreneurship of social science research tied to governmental contracts, as well as numerous academic social science research centers operating, in varying degrees, on public funds for public purposes. Over these preside a new bureaucratic species unknown to Weber, research administrators and promoters. Largely self-determining scholars, who are to science what the feudal nobles were in politics, still abound in the social sciences. But much more of the work of social research has been absorbed into bureaucratized research organizations, many of which depend on and promote massive governmental interest and subventions, and are, in the way of bureaucracies, highly efficient in turning out research and getting it into influential channels.
Thus far, then, even better. But there is another side to the matter which, in my view, is a great deal more important and strikingly bears out Weber's central arguments. The gist of it is that although policy-relevant political knowledge and formal channels for transmitting it to politicians have greatly increased, the cultures of politicians and political scientists have become so much more divergent and the demands of their separate roles so much more crushing that merely looking at the knowledge and the channels yields an altogether misleading picture of the actual relations between them.
The contemporary culture of political scientists is characterized, first, by a much greater sense of uncertainty than in the past. In part, this reflects their assumption of scientific attitudes along with scientific methods, and
it is likely to persist. In part, it also reflects the fact that "behavioral" political studies, being young and rambunctious, have so far done more to unsettle old beliefs, to raise questions, to reveal areas of ignorance and partial knowledge, and to open new, still unattained, possibilities than to settle anything. This may be a temporary state of affairs, attendant on a large shift in methods and perspectives. Yet, there is already evidence to suggest that as scientific methods spread in political studies they will be characterized increasingly by the evanescence of knowledge, hence by the permanent tentativity intrinsic, in Weber's view, to all nomology—most of all in social studies.
In addition, the recent development of political science, also in the manner of all nomological study, has made it more abstract, more shadowy. Political studies, as Weber foresaw, have become more specialized and fragmented. Beyond this one need not be a mean opponent of the so-called "behavioral revolution" in our own field to see that its very accomplishments are predicated upon a growing estrangement from the living phenomena of politics. What, after all, is it to employ "indicators" as data if not to use the reflection as the real object? Or to study behavior by "simulating" it? Or to construct "models" as sources of knowledge? Or to discard the common vocabularies of politics and their meanings for technical conceptual schemes? Or to bury individuals in correlations? Or to treat responses to survey questions as living attitudes? Or to construct ever more general theories in which ever more vivid detail is lost? One may suspect that some of the resistance to behavioralism is due to just this fact and that it is for this reason that we are so strangely accused of fiddling among the flames.
The fact is, however, that what is going on in political science is precisely what the advance of nomological knowledge, hence technical mastery, requires. Tentativity, specialization, and conceptual and theoretical abstraction do not reduce the relevance of political study to public policy in principle. If anything, the opposite is the case—again, in principle. In fact, however, the politician's culture, largely unchanged since Weber's time (except for the maturing of then-embryonic tendencies), militates powerfully against the proper reception and utilization of the fruits of such study.
Politicians, working in bureaucratized machines, dependent on conformity to them and on popular appeals for their careers, pressed to make decisions highly consequential for society and for themselves, upon quick diagnoses of and responses to concrete pressures and conditions, want, understandably, hard certainties immediately applicable to complex concrete pressures. They shy away from studiously tentative abstractions with all their excess baggage of ceteris paribus clauses and caveats. In fact, like physicians, they often develop a sense of personal infallibility as a necessary
defense against the inherent uncertainties and fatefulness of their work and therefore tend to be especially unresponsive to men with a carefully cultivated sense of their own and others' limitations. The resultant divergences in outlook are aggravated by growing differences in language and techniques of thought and work. And scientism in politics, being a corruption of the scientific culture precisely in regarding science as a solvent of uncertainties and necessities for choice, encourages mainly scientific quacks—persons who will produce a "system" for dealing with virtually any problem, if the customer is gullible and the fee is right; at least, it does so where there is no clear conception of the boundaries between what science must solve and politics must decide, of the sort that largely regulates the relations between politics and the natural sciences.
For these reasons, one may suspect that much relevant work in contemporary political studies gets no attentive political audience at all or gets it only at the margins of the policy process or only after intermediaries in or out of government have packaged (and distorted) it into a form more consistent with the politician's culture. And for the same reasons, it seems likely that political scientists least acculturated to the scientific culture get the most crucial and most attentive political audience.
Cultural strains affect not only the transmission and reception of messages from political scientists to politicians but also the very willingness of the former to use the channels of influence available and of the latter to grant different kinds of political scientists access to them. We have no systematic studies of the subject, but one's impression is that the willingness to become involved in policy processes (even if not a concern with policy in other senses) is unevenly distributed in the profession, with the behavioralists excluding themselves from direct involvement in politics more than other subcultures in the field. That exclusion, however, is not always self-imposed, but results also from the selectivity of politicians. This too is understandable, and perhaps inevitable. If it is natural for political scientists to opt out of policy processes on grounds of cultural strain, it is equally natural for politicians to recruit into their structures the more congenial, familiar, and supportive kinds of political scientists—not necessarily those who will nourish their biases, but those most like themselves in styles and modes of thinking and talking. Self-exclusion by certain political scientists thus is reinforced by the recruitment practices of the other side.
Exclusion does not always imply an absolute lack of access and participation. In many cases it manifests itself more subtly but with the same results: for example, in an unwillingness to continue interaction on one side or encourage continuation on the other, or in being put on a consultant roll but not asked actually to consult, or by one party making little effort to communicate intelligibly or the other little effort to understand
correctly. These days not many political scientists of consequence fail to have any contact with government, but not a few find that after the initial interchanges the silences, on both sides, become longer, more frequent, and at last permanent.
Weber's analysis clearly points to, and explains, these cultural strains and their consequences. It also clarifies a second major dimension of the problem: the tendency for politicians and political scientists to become estranged because their roles grow more burdensome and life-absorbing, compelling the awful single-minded absorption in their special callings that the Puritans voluntarily assumed as a sign of grace.
Being an efficacious politician today requires a more "slow and arduous boring of hard boards" than Weber could have envisioned. The scope and complexity of governmental activities have grown enormously through the continuous expropriation of private spheres. So, concomitantly, have governmental structures and structures of political competition. So has the need for politicians both to balance complex pressures and interests to work effects through bureaucratic machines become more cumbersome and inert as they have grown larger and more settled and to act so as to safeguard their careers as a condition of personal income, deference, and security. To be a contemporary political scientist is not much less burdensome, at least if one is seriously committed to the calling. One assumes onerous teaching and administrative duties. There are massive pressures for research, by increasingly taxing methods, in an ever-widening set of contexts. One must get through an awesome and constantly growing quantity of publications and other materials to "keep up" with a discipline expanding its knowledge ever more rapidly and making it obsolete ever more swiftly. Constantly there are new languages to be learned, methods to be mastered, and theories to be appraised and tested. And all this is bound up with the political scientist's own income, security, and status, no less than his professional commitments.
Between committed politicians and political scientists, then, interactions may become more voluminous, but the very volume of interactions adds to their being more casual and superficial, for cultural reasons and reasons of personal economy. The question today, therefore, is not just who will listen and understand across vocational boundaries, but who can: who has the time and energy to listen and comprehend, and who the time and energy to speak, and speak intelligibly?
There may be workable remedies for these difficulties, as there are for others. Weber in no way supplies them to us. By the end of his life, despite incessant groping, he had not even worked out a fully integrated orien-
tation toward science and politics for himself. But Weber's thought may help others to go further in that direction by laying bare, as it surely does, the more general and constant elements of the problem, identifying specific currents in politics, science, and their relations that any present position on the problem must still interrelate, and stating on these bases an explicit and thoughtful position against which to measure stances we take more implicitly and thoughtlessly.
This is not to say, however, that no further thought about the nature and roots of the problem is needed. One would like to see, as a condition for useful practical reflection, a considerable devotion of time and money by interested parties to the systematic study, with modern methods, of subjects like the following (about all of which we currently can only speculate and report impressions): (1) the nature of the professional cultures of politicians and political scientists , both of which vary over certain ranges; (2) the channels and volume of interaction among them; (3) who actually interacts in these channels on both sides, with what frequency and in what manner ; (4) the strains that arise in the interactions; (5) the nature and behavior of individuals and institutions that especially intermix the two vocations (such as political scientists in actual public service and politicians recruited into academic careers); and (6) the experience in public service of men who use training schools in public affairs as a springboard to their careers .
Weber's reflections about our problem, however incisive, remained essentially uninformed by "nomological" study itself, as do ours. In this respect at least, we certainly can and should go beyond him, devoting science itself to the groundwork needed for fashioning useful bridges between political study and political activity.
It seems to me that this agenda for research on the issue still applies, in its entirety, in the 1990s.
A Perspective on Comparative Politics, Past and Present
Author's Note: This essay took stock of the history and condition of comparative politics in the early 1960s. Almost all of it remains pertinent now, although the final section needs much updating.
I called the essay a "perspective" because it is, in a way, a history of comparative politics, without being in any way a survey of writings in the field—not even of the most important writings.
The object of the essay was to illuminate the condition of the field by discussing the main phases in its evolution and the forces that have affected it, in both the present and the past. Had it been written as a conventional history, I would have dealt at length with many more writers, especially such great writers as Tocqueville, Marx, Weber, Mill, and Bagehot. I would have dealt more briefly, or not at all, with minor writers whose chief virtue is that they can illustrate, in an exaggerated way, the character of comparative political studies in their periods and not that they have made any important contribution to such studies. I would have taken some care to distinguish national differences in styles of analysis in the same periods, rather than speaking of comparative political studies only in overall terms. Such national differences have always existed and exist today: English writers on comparative politics, for example, were much less affected by what I call here the formal-legal style than others and have been less affected, perhaps for just that reason, by the contemporary reaction against that style. Finally, I would have taken greater pains to show the extent to which the predominant style of any one period is still practiced, with less em-
phasis, in the periods that follow, although I try to make clear throughout that the development of comparative politics has not proceeded through mutually exclusive phases, but has involved instead a continuous heaping up of strata of analysis, if one may put it that way.
Since the distinction between comparative politics and other aspects of the study of politics is rather recent in origin, I should perhaps also point out that much of this essay provides a perspective on the whole study of politics, indeed of the social sciences, as well.
The field of comparative politics has a long and honorable past. That its pedigree reaches back as far as Aristotle is not unusual, since just about every discipline can, in one way or another, trace its origin to Aristotle. Comparative politics, however, has a particular right to claim Aristotle as an ancestor because of the primacy that he assigned to politics among the sciences and because the problems he raised and the methods he used are similar to those still current in political studies. From Aristotle stretches an impressive line of other Greats who can be numbered, without too much distortion, among the ancestors of the field: Cicero, Polybius, and Tacitus among the Romans; Machiavelli, among others, in the Renaissance; Montesquieu in the Enlightenment; and an imposing line of sages in the nineteenth century—Tocqueville, Marx, Mill, Bagehot, Mosca, and many more. The general analysis of political systems, the classification of their types, the study of the forms of their development, and the observation of the many varieties of actual political systems are concerns nearly as old as the history of recorded thought. These concerns have at least as timehonored a place in human thought as the concern with political morality.
Yet specialists in comparative politics seem today to be preoccupied, almost paradoxically, with questions we associate not with the maturity but with the infancy of a field of inquiry—questions about the fundamentals, the "first things," that govern the processes and ends of analysis. Such questions are raised only rarely in disciplines that have a highly developed tradition. If we are to understand the present state of comparative politics, we must know what these questions are and why they are being raised at this particular stage in the field's development.
The Present State of Comparative Politics
Let us begin with the questions.
First of all, a host of procedural—perhaps one should say methodological and epistemological—questions are raised by contemporary students of comparative politics. What, they ask, is the nature of comparative method: how is it used, and what sorts of studies are not comparative?
What can be learned by comparisons, assuming that we know how to make them properly? Is the comparative method in the social sciences, for example, really an adequate substitute for experimentation in the natural sciences, as has sometimes been claimed? Can it be used at all in a field like political science—that is, are political systems really comparable—or is each system unique, so that each particular political system is best dealt with by configurative rather than comparative analysis, by constructing a special Gestalt , a "profile" as Heckscher has called it? Even if this conclusion is not necessary, does not the comparative method operate usefully only within certain limits: at a relatively low level of theoretical abstraction, where analysis is not very broad in scale but confined, at most, to limited periods in time, certain geographic areas, or similar types of political structure? And what do we mean by concepts like uniqueness, abstraction, similarity? Not only are questions raised about such basic issues, but also about the proper use of specific devices for comparative analysis: for example, the proper uses of ideal and real types, sampling methods, scaling techniques, and so on.
A second set of questions concerns the use of concepts in the field. These fall primarily into two categories: questions regarding the classification of political systems and questions regarding the elements of such systems.
In political science a bewildering variety of classificatory schemes is available. The most venerable of these schemes is still much in use and was never discarded (only amended, simplified, elaborated) from the time of the Greeks to the nineteenth century. It classifies political systems according to the number of participants in decision-making processes into monarchies, aristocracies, and democracies. Since the middle of the nineteenth century, however, schemes for classifying political systems have multiplied helter-skelter, every man his own taxonomist. Today an almost embarrassing number of such schemes exists, requiring choices we do not really know how to make.
Some writers on politics use schemes consisting of two basic types, not, as in the classic case, of three. Some of these two-term schemes consist of polar types, limiting a continuum along which actual systems may be ranged, while others simply provide two "boxes" into which actual systems are placed. An example of the "box" approach is the classification of systems, now widely used, into Western and non-Western types. The continuum approach is found in a large number of schemes—for example, the division of political systems into constitutional and totalitarian, traditional and modern, or agricultural and industrial types.
Some students of politics choose instead classificatory schemes consisting of three basic terms. Weber, for example, classifies political systems, according to the legitimations of authority dominant in them, into tradi-
tional, rational-legal, and charismatic types. The Marxists classify them, according to the dominant economic class, into feudal, bourgeois, and proletarian systems. Coleman, departing less from the classic typology, characterizes them either as competitive, semicompetitive, or authoritarian. Dahl uses the terms democracy, hierarchy, and bargaining systems. (The last are added, presumably, to accommodate his interest in economic systems in which not "decisions" but, so to speak, mutual "accommodations" are arrived at.) Still another series of writers uses four-term schemes. Apter, for example, labels governments as dictatorial, oligarchical, indirectly representational, and directly representational. Almond once constructed a scheme typifying political systems, obviously on a variety of bases, as Anglo-American, Continental European, totalitarian, and preindustrial.
We can find in the literature schemes even more complicated than these. Edward Shils, for example, has recommended a five-term typology, constructed specifically to deal with the analysis of "new" states: political democracies, tutelary democracies, modernizing oligarchies, totalitarian oligarchies, and traditional oligarchies. Coleman, in another classificatory proposal, has gone Shils one better by dropping one of his categories (totalitarian oligarchy, which, presumably, would not be omitted in the analysis of established as well as new states) and adding two others, "terminal colonial democracy" and "colonial or racial oligarchy." And this is only a partial list, a sample.
We have here a considerable embarras de richesses . We can explain why it exists and why it should have come into existence after the middle of the nineteenth century, particularly in very recent times, for this variety of classifications is obviously a reflection of the rapid development of modern social theory and the broadening of the range of materials in the social sciences. The important point, however, is that such a disconcerting wealth of classificatory schemes inevitably raises some fundamental questions: Which scheme is more useful than others for any given purpose and, even more basic, what is the use of any classificatory schemes at all? How ought such schemes properly to be constructed, and how can one distinguish, in principle, a good scheme from a bad one?
The same questions arise in regard to the elements of political systems, taking "elements" to mean the parts into which such systems are divided and out of combinations of which they are, for analytical purposes, constituted. Following early modern usage, we used to think of these elements primarily as three: legislative, executive, and judicial structures and functions; but lately a large variety of alternatives have been proposed and used. Apter, for example, thinks of political systems as consisting primarily of government, political groups, and systems of social stratification. The last he considers the aspect of the social setting most directly and most
significantly related to politics. Each of these elements is then further divided and subdivided to arrive at a large series of components of politics, certain of which supposedly "cluster" in typical (frequently found) political systems. Governments, for example, are held to have a certain "format" and to depend for their very existence on five structural requisites: authoritative decision making, accountability and consent, coercion and punishment, resource determination and allocation, and political recruitment and role assignment. Lasswell presents a breakdown of political systems on the basis of seven functional variables (and explicitly because of his dissatisfaction with the classic separation-of-powers formula): intelligence, recommendation, prescription, invocation, application, appraisal, and termination. (The meanings of these anything but self-explanatory terms are immaterial to the present purpose.) Easton suggests that political systems have essentially two elements—inputs (demands and supports) and outputs (authoritative decisions)—while Almond provides a complicated breakdown of both inputs and outputs into seven so-called functional categories: four for the "input" function (political socialization and recruitment, interest articulation, interest aggregation, and political communication) and three for the "output" function (rule making, rule application, and rule adjudication—the classic formula, but restricted to only one aspect of political systems).
These also are only examples to which a good many others might be added, but they will suffice to illustrate the many different grounds on which a breakdown of political systems might be based—structural categories, functional categories, structural-functional categories, system requisites, elements of formal organization, elements of informal processes. They also show why questions should nowadays be in the air regarding the most basic aspects of such analytical breakdowns: their relative utility, their purpose as such, the "logic"—if there is any—of their construction.
To some extent, the answers to such questions depend on how one answers certain other basic questions that are also very much in the air these days. Is it, for example, more fruitful to treat political systems as autonomous systems or as systems embedded in other aspects of society? If we want to link politics with its larger setting, what aspect of that setting should we stress? Does social stratification really have the explanatory power Apter claims for it, so that we can safely dispense with the examination of other elements of setting? Or are the most significant links to be made with levels of economic development (as Lipset suggests), culture (as Beer implies), or personality (as political psychologists like Lasswell appear to argue)? Even more important for the way we break down and classify our data—and indeed also for our methods—what is a political system? What really is our subject matter? Is it "states"—governmental units possessing sovereignty—as the most venerable view in political science
has it—or is it any power relationship (Catlin), any influence relationship (Lasswell), any system that allocates social values? And if the last, are we really interested in any such allocation or only, as Easton maintains, in authoritative allocations? That is to say, does government, in the traditional sense, remain our focus, or do we act upon the recommendations of a whole host of men, from Catlin to March, and examine in the construction of a truly general and comparative political science almost any interpersonal relationship, whether conventionally thought of as political or not?
Once we have dealt with such questions, a host of others, equally basic, remain. For example, what unit of analysis should we use in political studies? Should we use impersonal units, such as "roles" (clusters of expected behavior patterns revolving about a particular function) or "interactions" (acts and the responses they engender)? Or should we use a personal unit—that is, concrete individuals? Or superpersonal units, such as groups, institutions, or organizations (taking these in the specialized senses in which they are used in modern sociology)? What "perspectives" or "orientations" should we use in analyzing these units? Should we still emphasize, as we have traditionally emphasized, the study of formal constitutional structure or apply instead group theory, structural-functional analysis, the decisionmaking approach, communications theory—to mention only a few of the possible analytical approaches available to us? And what sort of "theories" do we want to construct through these approaches: empirical "laws," models, causal explanations, functional analyses, equilibrium theories, developmental theories, or still other, as yet unexplored, types of theories?
These questions—about methods, concepts, definition of the field and its elements and boundaries, units of analysis, analytical approaches, and types of theories—will be recognized immediately as the most important metatheoretical and pretheoretical problems arising in any field of inquiry. ("Metatheoretical" refers to theory about theory—methodology, for example. "Pretheoretical" refers to operations that must be performed before the construction of theory proper—that is, before the formulation of testable hypotheses and their testing.) I have listed them here, not because I have any intention of answering them or resolving disputes about them, but solely because they can immediately tell us something important about the present condition of comparative politics.
In most fields of inquiry, such questions, despite their obvious importance, are either not raised at all or are raised only by the way and by men, like the members of the Vienna Circle, who have a special taste for philosophy and fundamentals—and men who are usually more influential outside their fields than in them. Why then are they raised so much in comparative politics today? After all, students of politics, as I have stated, have had many centuries to reach settled conclusions about them. What is more, preoccupation with such questions, fundamental though they are
(indeed just because they are fundamental), probably hinders more than it promotes substantive research. In a way such preoccupation involves a kind of vicarious experience of research. What then can explain the apparent paradox between the venerable age of the field and the infantile questions raised in it?
The answer is both simple and important. Some historians of science tell us that, despite the myth of steady scientific progress that we have inherited from the Enlightenment, the advance of science has not really been steady. Instead, it has been punctuated by revolutionary intervals in which the whole framework of scientific knowledge—all its basic, usually unspoken, assumptions—has come under heated debate: assumptions about the proper purpose of inquiry, about the nature of its subject matter, about what constitutes satisfactory scientific knowledge. Science always functions within a framework of such preconceptions, but the preconceptions are never opened to examination when a consensus on them exists; men do not argue questions upon which they are agreed. In such cases of consensus one may indeed get the impression of a steady unfolding of a shared perspective upon scientific work. When consensus breaks down, however—when a field is marked by dissent or is in transition from one framework of inquiry to another—the fundamentals always come to the forefront; the silent major premises cease to be silent. In such periods, if the breakdown of scientific consensus is broad enough, intensive philosophical exploration of a general sort occurs. If the breakdown is restricted to a narrow field, its practitioners will engage in metatheoretical and pretheoretical labors that, to others, may seem exotic and unrewarding, if not irrelevant to actual scientific work.
From this we can infer what is perhaps most basic about comparative politics today: that it is a field acutely in dissent because it is in transition from one style of analysis to another. For just this reason, it is a field in which many different styles of analysis are at present to be found. Because this is the case, we cannot give any simple account of comparative politics. Instead, to portray the character of the field today we must do three things: provide an historical account of its development, explain how it reached its present state of dissension, and expound the principal discontents and aspirations of its contemporary practitioners.
The Origins of Comparative Politics
Periodization is always hazardous. Nevertheless, we can locate the beginnings of the modern study of comparative politics with fair precision at that point in time when political systems came to be conceived not as natural bodies ("corporations") but as artifacts, created by people and therefore subject to re-creation (reform) by people. In short, its earliest
source, leaving the classics aside, is Renaissance political thought, most obviously that of Machiavelli; and it comes to its first full fruition in the Enlightenment, above all in the writings of Montesquieu.
Machiavelli and the Renaissance
When Burckhardt says that in the Renaissance the state came to be regarded as "a work of art," he does not mean that it was looked upon as something aesthetically pleasing; nor does he mean that political actions were considered to be self-justifying, like artistic creations, rather than subject, like works of morality, to ethical codes; and he certainly does not mean that politics was not regarded as a proper subject for scientific analysis. He means precisely what he says—that the state had come to be regarded as an artifact, something that was made rather than something that simply was; for just that reason, it came to be looked upon in the Renaissance and Enlightenment as a proper subject in itself for "reflection and calculation."
We can, of course, reflect on the behavior of natural objects that are only imperfectly subject to human control or not subject to it at all; the natural sciences do almost nothing else. But the more unalterably given we regard phenomena to be (that is, the less susceptible to human engineering), the more likely we are to be intellectually passive in regard to them, to dismiss "scientific" inquiry as futile or as an esoteric taste, or to subsume study of the phenomena to the larger contemplation of "being as such"—to metaphysics, ontology, or theology. It is no accident, therefore, that the study of politics through the broad-scale examination of political experience comes to the forefront just when we begin to talk about an "art" of governing and of "statecraft." From this standpoint we can also understand why comparative inquiries, conducted to establish generalizations about political behavior and not merely to illustrate them, came first to be carried on when natural law doctrines were on the wane. If one really believes in a natural law that rigidly governs all human relations, then one is likely either to look for it through abstract speculation upon first principles or, even more likely, through very narrow studies of experience, since any limited range of experience—a single government, for example—will then illuminate as much as very broad ranges of experience—and the analysis of very broad ranges of experience is the hallmark of genuinely comparative studies. The point of view most hospitable to such studies is one that sees social life as governed by necessary relations, knowledge of which can be used in controlling, at least to some extent, human affairs.
In the Renaissance this point of view emerged, although art was emphasized far more than nature, and this emphasis is important. If one studies a subject primarily because one believes in the necessity of human
engineering in the area it comprehends, inquiry into it is bound to be of a particular kind. Inevitably it will focus upon the discovery of techniques through which such engineering can be effectively carried out: upon Staatskunst , not Staatswissenschaft . Machiavelli himself is the primary example. What makes a ruler successful? How can power be won, maintained, expanded? What arrangements and practices make a state powerful, stable, free, prosperous? These are the quintessential problems of the political technician, and they are precisely the problems that preoccupied Machiavelli.
Moreover, if one's purpose is to discover directly techniques of statecraft—if, that is, one proceeds from the very beginning with what we now call "policy-oriented" studies—the methods one uses are also likely to be of a certain kind. In all probability they will be "empirical" in the most literal sense of the term; that is, they will involve the examination of experience as if it were a record of trial and error, of a kind of thoughtless experimentation, in which some procedures are revealed to be conducive and others not conducive to certain ends. If anything further is done with such "rules of prudence," it will be to infer generalizations about psychological propensities underlying the rules and to deduce further rules of prudence, not revealed directly by experience, from the psychological propensities. Crude inductions, crude inferences from the inductions, and crude deductions from the inferences will always characterize such direct inquiries into statecraft. Certainly they characterize Machiavelli's. The Prince and Discourses teem with examples.
Consider only one, by no means the most blatant—the argument against using mercenary soldiers (Chapter XII of The Prince ). No Prince who relies upon an armed force of mercenaries, says Machiavelli, can ever "stand firm or sure"; such troops are "disunited, ambitious, without discipline, faithless, bold amongst friends, cowardly amongst enemies, they have no fear of God, and keep no faith with men." Why so? Because it is not a man's nature to die for another purely for the sake of a wage; because the more competent a mercenary leader, the more, having no deep bond of loyalty to a Prince, he is likely to aspire to the Prince's place or otherwise to overstep his powers. And what is the evidence for these assertions? The helplessness of the Italian cities before King Charles of France, the oppression of the Carthaginians by their mercenaries, the fickleness of Francesco Sforza toward the Milanese, and the successes, in contradistinction, of Rome, Sparta, and the Swiss. But what about the Venetians and Florentines, who seemed to do well enough with mercenary forces? No matter, for they were "favored by chance": the ambitions of their mercenary captains were diverted elsewhere, and these captains would have caused more harm if they had been more competent. And so it goes, in nearly every chapter.
Montesquieu and the Enlightenment
In the Enlightenment, such simple and disingenuous inductions, aiming at the discovery of political rules of prudence, still abound, along with deductive theories of the state influenced by Cartesian philosophy. In some writers of the Enlightenment, however, above all in Montesquieu, we can detect more modern and more sophisticated concerns, if not in method, then certainly in the problems raised and theories proposed. In many ways, The Spirit of the Laws is, in fact, a work astonishingly "modern."
To be sure, Montesquieu is interested, like Machiavelli, in using induction primarily for purposes of statecraft. What, after all, is his famous theory of the institutional conditions of freedom if not a rule of prudence based upon very limited and crude induction? But perhaps it would be more accurate to say that Montesquieu was interested not so much in statecraft, as Machiavelli would have understood the term, as in constitutional engineering—not in how rulers should behave but in how governments should be constituted. Unlike Machiavelli, whose argument proceeds from human nature, Montesquieu thought of right government primarily as a matter of sociology and ecology, of adjusting governmental structure to prevailing conditions. Hence, his interest in some very modern concerns: the relations of political systems to their physical environments, the role in politics of economic factors and of "manners and morals," problems of classifying political systems, and the like.
Any methodical arrangement of The Spirit of the Laws immediately gives it a contemporary ring, granted that such an arrangement must be largely imposed by others upon a study for which chaotic is a term of flattery. Take, as an example, the now widely followed scheme by G. Lanson. Montesquieu, according to this scheme, first considers the various types of government: their nature, their structural principles, and the conditions under which they arise and under which they tend to persist or decline (have "viability" or not, as we would say). He goes on to consider the functions of government, including provisions for the safety of the state (civil-military relations), the liberty of the subject, and the raising and expenditure of public monies ("resource allocation," in modern jargon). Then there follows a long series of chapters dealing with those aspects of their "setting" that condition political systems: ecological conditioning factors, such as climate, soil, and population; social institutions, such as the "relations between the sexes"; matters of culture (the "general spirit, the morals and customs of a nation," and religion); and economic conditioning factors (the "interrelation between commerce, morals, poverty, and the types of government"). Finally, there are some very scattered, but suggestive, hints at "developmental theory," at social dynamics no less than social statics.
Anyone au courant with modern comparative politics will recognize
these topics as a large proportion of its stock in trade. And it is not only the topics that ring familiar, but also the way they are handled. Montesquieu's types of government, for example, are ideal types and quite consciously so in that they are logical structures based upon certain fundamental principles underlying the type, to which actual political systems only more or less correspond. Like modern sociologists, he thought of societies as being interconnected, as patterned structures, as "systems" the parts of which are interdependent in such a way that change in any one part leads to compensating changes in the others or to disintegration of the whole. Therefore, he produced an essentially mechanistic interpretation of social change, in distinction both to the voluntaristic theories prevalent in his time and the eschatological theories of history soon to be propounded. He has been called (by Meinecke, for example) one of the founders of "historicism," but this view is tenable only if we equate historicism with any theory of social change that assigns a role to involuntary social processes or if we use the term to denote any use of the "genetic" approach in social studies and not if we use it to describe grandiose theories of the meaning and goal of history. Montesquieu's modernity lay precisely in the fact that he worked at a nonvoluntaristic theory of social change without going over to the historicist extreme.
Was Montesquieu an aberration, a stranger to his own age? So it is often argued, but surely not correctly, for it is as plausible to regard him as the culmination of past trends of thought as to regard him as the precursor of writers still to come—not to mention other writers of his own time (such as Adam Smith, Hume, and Ferguson). Methodologically, a clear line runs to him from Descartes and through Malebranche. Montesquieu was certainly not the very crude empiricist that Machiavelli was, but he understood what it means to assert the existence of "social laws" (as Machiavelli, with his constant harping on chance and fortune, never did). He understood that these laws are to be found by a combination of logic and observation, that proper induction requires the wide-ranging observation of many contexts, and that logic has at least an equal, if not prior, role to play in scientific analysis.
While Montesquieu's method originated in Descartes, his problems, in contrast, were posed largely by Machiavelli and Bodin. His approach to developmental theory may be quite original, but he wrote at a time when social mechanism was very much in the air and sophisticated historiography at least beginning, however little the latter was influenced by the former. His concern with the relations between governments and their settings, especially his concern with physical environment, was anticipated in a large number of "modern" thinkers, including Bodin and Chardin. And his farranging empirical work was certainly connected with the very broad outlook of his age: its belief in the uniformity of men beneath their cultural
differences and its relative freedom from the nationalistic and provincial biases that predisposed subsequent thinkers to regard political systems as unique and incomparable.
In Montesquieu, then, and in the writings of lesser men of the Enlightenment, we can see emerging a comparative science of politics not so very different from that which present political scientists seem to want: a "science" aiming at the construction of a structural-functional analysis of political systems, a sophisticated typology of such systems, a set of broad generalizations about the links between polity, society, economy, and environment, and a set of mechanistic theories of political dynamics—all in embryo, of course, but, in many cases, in surprisingly sophisticated form. Between the late eighteenth century and the present, however, a number of forces intervened that sidetracked political studies from these paths, so that we can regard the intervening development of comparative political studies as an elaborate veering away from and return to the lines of analysis sketched, however embryonically, by Montesquieu.
Although Montesquieu's ideas had many antecedents, they undoubtedly were aberrations in the sense that very different ideas set the tone in social thought immediately after his time. Not sociological historiography but rampant historicism—universal history, speculations on the first causes and final end of history—became the dominant style of social thought. This style (the style of Bossuet, Vico, and Condorcet rather than Montesquieu) affected the study of all social phenomena. In the study of political institutions interest now came to be centered primarily upon historical first principles, upon the "cunning of history," upon the construction of audacious developmental theories, unilinear in form, based on single determining principles and more often than not predicting the imminent universality of democracy—theories of change more organic than mechanistic in form. The best examples are obvious and familiar: Condorcet, with his belief in the simultaneous unfolding of reason and democracy; Hegel, with his belief in the unfolding of Reason and Freedom; Comte, with his belief in the unfolding of the scientific spirit (and, in contrast to the prophets of democracy, his prediction of the coming benevolent dictatorship of well-informed bankers); Marx, with his belief in the unfolding of utopia through class conflict.
Although historicism has long since become discredited, the field of comparative politics owes a great deal to this phase in Western social thought. In the first place, many of its concepts are still used and used fruitfully ("class," for example). Many of its problems are still raised, above all problems about the relations between politics and economic develop-
ment, politics and education, politics and the "cultures" of societies. Historicist theories also directed attention, to some extent at least, to a broad panorama of political experience. Hegel, for example (among many possible examples), was anything but a parochial thinker; his ideas ranged widely, if not very accurately, over China, India, Persia, Judaea, Byzantium, and the Mohammedan world, as well as over ancient and medieval Western history. The historicists were also responsible for much of the subsequent interest in social dynamics—especially in evolutionary theory, which helped, much more than did the less fanciful Montesquieu, to counterbalance the voluntaristic biases of political historians. Most of all, interest in broad-scale theory as such derives, in large part at least, from historicism.
But if the historicists bequeathed to subsequent students of comparative politics much to aim at and much to imitate, they also gave them much to overcome. Their broad-scale theorizing was mainly a matter of abstract and formal speculation upon the broadest conceivable questions; for the canons of accurate observation—for "content," in Hegel's terminology—they had a monumental disregard. Their data, in almost every case, were invoked merely to illustrate, not to test, their theories, so that one searches in vain in their works for a methodologically valid bridge between theory and data. In effect, their work engendered two interests that never really meshed: an interest in the construction of the most ambitious and contentless kinds of theories, on the one hand, and an interest in detailed and formless political history, a sort of political ethnography, on the other. They did not, however, engender (if anything, they discouraged) the sort of concerns that every young discipline ought to concentrate upon: the formulation and meticulous empirical testing of "middle-range" hypotheses and the tentative conceptual exploration of a field. The basic charge against the historicists is, consequently, that while they induced an interest in theorizing about wide ranges of data (the essence of any comparative study), both their theories and uses of data, and above all the way they related theory and data, ultimately proved sterile. They tried too early to do too much and so, in the end, contributed very little—except some interesting problems and theoretical approaches, and some very far-ranging misinformation.
Perhaps this explains why the historicists, in the final analysis, had a far greater influence upon politics (through the ideological impact of their theories) than upon political science. Concepts they used continued to be used; questions they raised continued to be raised; but the whole style of the historicists, their basic approach to social analysis, constituted only a swiftly passing phase in the development of social thought—granted the occasional appearance of throwbacks to the historicist era. A large number of forces converged in the later nineteenth century to discredit historicism: in the realm of philosophy, the rise of positivism and philosophical plu-
ralism; in politics, the rise of nationalism; in social thought, the impact of cultural relativism; in the general climate of opinion, the reaction against the softer idealisms, the tough-mindedness and perhaps petty-mindedness that followed the great disillusion of 1848. All these conspired against theories inadequately grounded upon observation, blandly optimistic, and assuming a uniformity of development for every society and nation, so that in the end historicism came to be important not so much for the positive influence it exercised as for the reactions to which it led. Certainly this is the case if we confine ourselves to the history of the comparative study of politics.
Reactions against Historicism
In the study of politics, the reaction against historicism took many different forms, each undoubtedly for good reasons, but each involving also a serious retrogression from the promising lines reached in the eighteenth century. Not Condorcet and his kind only, but Montesquieu and his kind as well, were rejected in the process.
One of the reactions against historicism was emphasis upon purely abstract political analysis, especially criticisms and defenses of democracy on the basis of deductions from metaphysical, ontological, psychological, and legal premises. This reaction has only a remote, though nonetheless significant, bearing on the study of comparative politics. Its relevance is, in gist, that in the post-historicist period, institutional and philosophical political studies, studies with "content" and studies with "form," became more rigidly separated than at any previous time in the history of political thought, a fact with the most momentous significance for the development of comparative political studies. Historicist thought, whatever its shortcomings, had at least one virtue: it joined, however unsatisfactorily, thought and data. The historicists did think about something, not just about thought. Even Hegel, who believed in the autonomy of formal thought from its content, at least undertook to fill the form with concrete matter in order to portray, if not to test, his formal theories. Those who reacted against historicism, however, did not initially attempt to improve upon what had been at best an uneasy marriage of fact and speculation. They resorted instead to outright divorce, so that in the wake of historicism (in the late nineteenth and early twentieth centuries, roughly) political thought tended to become, so to speak, increasingly subjective and the study of political objects increasingly thoughtless.
The contemporary study of politics as a separate field, and of comparative politics as a separate subdivision of the field, begins, unhappily, per-
haps disastrously, at this very point in time. That fact tells us a great deal about one of the more remarkable, if not absurd, characteristics of the political science curriculum: the division of the field into the study of political thought and the study of political institutions and behavior. More to the point here, however, is that it tells us a great deal also about the development of comparative political studies in the post-historicist period.
The separation of thought and data is at least partly responsible for a second reaction to historicism that does have a direct bearing upon comparative politics: the increasingly exclusive stress in the study of political actualities on formal political institutions—that is to say, on constitutional and legal structure (then called "public law"). Not all data lend themselves equally well to thoughtless treatment. Those that do so well are unequivocal data, easy to come by and subject to a minimum of interpretation; those that do so best are data that come to us, not in the usual way, inchoate and unordered, but in some already ordered form. And what data in political science present themselves in such a fashion—preprocessed, so to speak? Obviously two sorts: one, political thought itself; the other, formal institutional arrangements, prescribed in documents that are, in fact, mental constructs (and often bad hypotheses), but that can be treated as if they were raw data of political experience, for the political scientist does not invent them, but comes upon them, as he comes upon behavioral data of quite different sorts.
The emphasis in the study of politics upon formal-legal arrangements is thus a natural outgrowth of the positivistic reaction to historicism, simply because primitive positivism, in attempting to restrict the role of thought, naturally leads the analyst to steer clear of the more inchoate data. Primitive, unadulterated positivism insists upon hard facts, indubitable and incontrovertible facts, as well as facts that speak for themselves—and what facts of politics are harder, as well as more self-explanatory, than the facts found in formal legal codes? And what other facts are equally conducive to Wertfreiheit in analysis, to what purports to be hardheaded, ethically neutral empiricism? Perhaps this argument may seem strange today. Most of the self-labeled positivists in contemporary political science are concerned with precisely the sort of inchoate materials that their predecessors ignored: voting behavior materials, power and influence relations, elite structures, informal political processes, and so on. But this does not controvert the fact that the initial impact of positivism upon the field was to direct attention toward superficial facts, even pseudofacts; nor does it deny that the positivistic outlook as such creates, even today, a preference for the superficial over the profound.
The emphasis upon formal-legal structure that came to be the dominant
empirical style of political studies in the late nineteenth century was not, however, due to the post-historicist dissociation of thought and data alone, although that dissociation alone may sufficiently explain it. One other factor that certainly made for emphasis upon formal-legal structure, especially upon constitutional documents, is simply that the nineteenth century was a great age of constitution making. In fact, one would be hardpressed to find "constitutions," in the sense of elaborate formal-legal codes rationally devised to create political organizations and govern political processes, in a previous period.
If we go to earlier periods, we find constitutions in the Burkean and typically British sense of the term (constitutions as historical accretions of institutions and processes that can be stated in, but are not defined by, formal rules); we find one or two prophetic documents, like the Instrument of Government , as quaint in their own time as they are common later; and we find charters—bills and documents called "constitutions"—that are not constitutions in the modern sense at all, but either contractual agreements between princes and subjects (such as municipalities and social groups) or solemn and explicit declarations of historically evolved political relations. This discovery is hardly surprising, for the very idea of a constitution in the modern sense could not have occurred to anyone who regarded the political order as a "natural" thing and is, therefore, properly a product of a time when mechanistic social beliefs, coupled with faith in the powers of human engineering, displaced earlier organicist and historicist ideas. Of course, these beliefs alone were not enough to make political studies focus upon constitutional documents; the documents themselves had to be there to study—as indeed they were, in constantly growing numbers, in the late nineteenth century. But the prevalent mechanistic outlook and faith in social engineering of the period explain at least why constitutional codes were taken so seriously, by politicians and students of politics alike.
Inevitably, these beliefs and interests also left a deep mark on the virgin field of "political science." Indeed, the very fact that political science emerged in this period as a separate, autonomous field of study divorced from philosophy, political economy, and even sociology, may have created a tendency to emphasize the study of formal-legal arrangements, quite apart from any other factors moving the field in this direction. If a study becomes departmentally sui generis , it will try also to assume a subject matter and techniques of study that are sui generis . And what subject matter can be regarded as purely political? Political behavior, in the larger sense in which we now regard it, is touched upon by the subject matters of all sorts of other disciplines: those of sociology, social and individual psychology, cultural anthropology, and economics. If there is any subject matter at all that political scientists can claim exclusively for their own, a subject matter that does not require acquisition of the analytical tools of
sister-fields and that sustains their claim to autonomous existence, it is, of course, formal-legal political structure. Its study, therefore, quite naturally became the focal point of the new discipline of political science in search of a raison d'être .
Perhaps we ought to add to this list of factors making for emphasis on formal-legal studies (it is an emphasis that requires a lot of explaining) still one other: the emphasis in the teaching of politics at this time upon "training"—training for citizenship and for public administration and preliminary training for the law. This emphasis was particularly great in the "new" states of Europe, above all in the newly unified Germany. Sigmund Neumann has pointed out that in the Bismarckian era, the German universities, once the centers of the fight for freedom, were "gradually transformed into guardians of training for leadership in important public offices, the judiciary, the bureaucracy, and the teaching profession." The "value-free" sociology of Weber and others is regarded by Neumann as one illustration of these tendencies; the emphasis on studies in formal public law may be considered another. To what were they due? Neumann attributes them to the regime's authoritarianism and German admiration for the Iron Chancellor's successes; but we can just as plausibly regard them as responses to the new state's need to socialize men into new political patterns: to inculcate in them civic loyalty and educate them to play roles in new administrative and legal arrangements. Perhaps this is an even more plausible interpretation than Neumann's, particularly when we take into account the emphatic interest in formal-legal codes in the United States. No authoritarianism, no admiration for successful Realpolitik , existed here to dampen the impulse to moral criticism in politics or the drive to uncover the deeper forces determining political actualities.
It is true, of course, that the German universities were extremely influential in America around the turn of the century, but the United States had also in common with Germany a tremendous problem in political socialization, due in one case to the creation of a new political system and in the other to mass immigration. In both cases, the agencies most readily available for dealing with these functional needs were educational institutions, especially institutions of secondary and higher education. Hence, there was a mushroom growth of civics courses providing indoctrination into citizenship and of courses preparing for participation, in one role or another, in the political structure—above all, courses in public administration, constitutional development, and public law. Courses in political "behavior," as we now use that term, could hardly have performed the same necessary function in either system—might indeed have been dysfunctional in both settings. And it is a fact that formal-legal studies were mainly German and American in origin, epitomized in the German case by the truly gargantuan collection of monographs appearing from 1883
on, the Handbuch des Oeffentlichen Rechts der Gegenwart (Handbook of Contemporary Public Law), and in the American case by a study of Woodrow Wilson's, based largely upon the Handbuch , which will be discussed presently.
A third reaction against historicism in political studies involved a drift away from comparative studies of all sorts and toward "configurative" analysis—the analysis of particular political systems, treated either explicitly or implicitly as unique entities. Many political studies of the immediate post-historicist period exhibit a considerable narrowing of the analytical attention, a tendency to cover very little ground, and to cover it in great, often indiscriminate detail. This tendency not only restricted attention to one set of political data—formal-legal structure—but also was restricting in a geographic and historical sense. To some extent this narrowing of analysis in time and space may have been the result of the very emphasis on formal-legal structure, for such an emphasis necessarily makes one work within the compass of particular constitutional systems and is, for reasons already mentioned, appropriate only to a limited period in European history. We can see this narrowing influence of the formal-legal approach reflected even in some of the wider-ranging political studies of the post-historicist period, particularly in the large number of compilations of constitutional provisions then published and taken very seriously. But configurative analysis was also an outcome of some of the factors that produced the emphasis on formal-legal studies itself: the reaction against broad speculative theories of any sort; the influence of nationalism and its roots in the idea of national character, which logically implies that each nation is an analytically unique entity; the emphasis on citizenship training and vocational training in an age of rapidly expanding national bureaucracies.
This is not to say that only narrow political studies, confined to particular nation-states, were produced in this period. There was no dearth of studies ranging over very wide territory indeed, but it is characteristic of these studies that their theoretical import should be almost inversely proportional to the range of material included. Generally speaking, they presented a wide panorama of political materials with a theoretical equipment restricted to little more than Aristotle's classifications of governments and to abstract speculations on abstract questions and with the materials arranged either in terms of the three basic forms of government, in chronological order, or in a combination of chronology and forms of government.
An example of this sort of political study—probably the most famous—is Wilhelm Roscher's Politik , written intermittently between 1847 and 1892, but chiefly in the last few years of this time span. The revealing
subtitle, Geschichtliche Naturlehre der Monarchie, Aristokratie und Demokratie (Natural History of Monarchy, Aristocracy and Democracy), gives the whole work away. Its principal theoretical concern is with the proper classification of states, a question Roscher settled by adding a fourth category, Caesarism, to the three classical categories and by distinguishing among plutocratic, proletarian, and middle-class states (still well within the Aristotelian framework). The study is based upon an explicit rejection of the "idealistic" studies of the times—that is, purely abstract treatments like that of Fichte, who, in Roscher's own words, "conceived political science to have only the business of depicting a best state, so that reality appeared to him as real only in so far as it corresponded to the image of this best state." Roscher, on the contrary, sets out to do precisely what the idealists most disdained, namely, to present a Naturlehre , a set of "naturalistic descriptions" of the Notstaaten so despised by the theorists of the Idealstaaten . And this he does very largely, though not exclusively, in the manner of historical narrative within each of the classificatory categories he adopts.
The result is a work displaying, even by Germanic standards, a truly massive learning. Switzerland, Athens, Rome, Gaul—Egypt, Normandy, Sparta, Venice—Spanish America, Tudor England, the Hebrew State—Brahmanism, Buddhism, Jesuitism, Protestantism—Demosthenes, Henry VIII, Hannibal, Napoleon—the book is almost a political encyclopedia. In this it is reminiscent of nothing so much as the more extravagant historicist theories; but the history it presents is history without the "ism," a matter of content with very little form, a pointless display of interminable exactitudes. It is in such works that we see the real impact of the divorce of thought and data on the field of comparative politics, just at the time when its practitioners became conscious of having a separate disciplinary identity.
Political ethnography, purely abstract speculations, formal-legal studies, and configuration studies—these are all different, even antithetical, reactions against historicism. But because they come from a single source, one should not be surprised to see them combined, however uneasily and in however ill-fitting a manner, in the large syntheses of political thought of the period. These "large syntheses" are not necessarily works of great merit. More often than not, in fact, such works are written by secondary figures, by those who ape the styles of the times rather than those who create them; but they do provide a very broad picture of the dominant fashions in analysis. Any number of such studies could be used to exemplify the immediate post-historicist period in comparative politics, but two may suffice here: one, published in 1878 by Theodore D. Woolsey, a former
president of Yale, entitled rather grandiosely Political Science, or the State Theoretically and Practically Considered; the other, by his later Princeton counterpart, Woodrow Wilson, a work with the even more prolix title, The State: Elements of Historical and Practical Politics: A Sketch of Institutional History and Administration (1895).
Both Woolsey's and Wilson's subtitles, like Roscher's, tell us, in the typically ingenuous fashion of the late nineteenth century, the most basic things we need to know about their studies. Each portrays mainly two of the anti-historicist styles we have discussed, though in each may be found examples also of the others.
Woolsey's work, an ambitious and pretentious undertaking indeed, is in effect a combination of purely abstract speculations and purely concrete political ethnography. When Woolsey talks about the state "theoretically considered," he refers primarily to two of the three categories into which German writers on politics had by then come to divide political studies: Naturrecht (natural rights—sometimes Staatsrecht , public rights) and Staatslehre (theory of the state). The first of these, Naturrecht (Woolsey calls it the "Doctrine of Rights as the Formulation of a Just State") is, of course, concerned with normative theories of political freedom and obligation. This part of the study bears no relation to anything subsequently said in it, but it is justified in Woolsey's own mind on the ground that no state worthy of the name is unjust, that justice in the state mainly consists of the safeguarding of natural rights, and that, therefore, there is no point in discussing the state without discussing the theory of natural rights—a curious syllogism, to say the least, but one that does encompass in a flimsy way the bifurcation of theory and data that confronted Woolsey.
To this concern with natural rights is added a series of concerns that Woolsey himself identifies as Staatslehre , a veritable rag bag of ethical and nonethical questions: "Opinions on the Nature of the State and on Its Origins," "Theories of Sovereignty," "The Proper Ends and Sphere of the State," "The Organization of States" (whether the desire for it is instinctive or habitual, the need for a "constitution," the various departments of government, distinctions between representative and nonrepresentative systems), "Theories of Communism and Socialism," "Limits and Extent of the Punitive Power of the State," and sundry normative questions ("Can the Citizen's or Subject's Connection with the State Terminate?" "What Are the Limits of Loyalty and Obedience?" "What of Conflicts between Law and Conscience?").
All these problems, normative or not, are mainly discussed abstractly in the light of the abstract speculations of other political theorists. Politics "practically considered," however, turns out to be what the late nineteenth-century Germans understood by Politik: the large-scale historical examination of political institutions from earliest to modern times,
mainly in terms of the classical categories; the formal examination of the "departments" and "institutions" of central and local government; and, at the very end, a few afterthoughts (one or two quite reminiscent of Montesquieu, whom Woolsey had obviously read but not really understood) on the influences of "Physical Causes on Politics," on "National Character," and on the "Causes of Political Change and Revolutions." In short, the whole book, save only for the very end, is either unmitigatedly abstract or pointlessly concrete, and the quotation cited from it on the relations of the study of rights and the state, which introduces the work, is a good indication of the way Woolsey relates theory to data throughout.
Woodrow Wilson's The State is admittedly his minor piece—though anything but a modest one, going on as it does through 1,287 sections, large and small. From our standpoint, however, it is much more worth examining than his more distinguished work, for two reasons: one, that it purports to be a text on politics of unprecedented scope, a summation of the empirical knowledge of the state in his time; the other, that it begins with large claims for comparative politics as the only proper approach to understanding political experience.
What is "comparative" politics to Wilson? Essentially, it signifies to him, as to Woolsey, a very detailed and far-ranging political ethnography primarily as historical narrative and secondarily through the depiction of contemporary formal-legal structure. About five-sixths of the work is devoted to such bald descriptions. Wilson begins the study with some questions about the probable origins of government—a fact whose significance we shall see later, but this subject, after a cursory consideration of evolutionary and early anthropological theories, soon takes him to the more congenial ground of classical history, where his political ethnography proper begins. The political institutions, first of Greece and Rome, then of "Teutonic Polity" in the Middle Ages, and then of German and French feudalism and monarchy are painstakingly examined; the chapters on them constitute the "institutional history" section of the work. The "practical politics" side of the study involves mainly an indiscriminate detailing of the formal-legal structures of French, German, Swiss, Austro-Hungarian, Swedish-Norwegian, British, and American governments. And all this, counting some historical discussions scattered throughout, takes up nearly a thousand sections.
Not until section 1,121 is any attempt made to draw any "comparative" conclusions. And what are these conclusions? Their modesty is perhaps as remarkable as the ostentatiousness of the data on which they are based. Essentially, Wilson distills from his materials three inferences: political change has taken the form of a very slow process of development from more primitive to more highly developed political organizations; modern political experience confirms the Aristotelian classifications, although mod-
ern monarchies, aristocracies, and democracies have some features not found in the ancient world; governments are all pretty much alike—denying the view of those (Wilson claims the great majority) who believe in the uniqueness of political systems—but there are differences between governments, due partly to unique historical backgrounds and partly to "nation-marks," an argument that immediately reinstates the belief in uniqueness, albeit in a milder form. Finally, in a sort of epilogue, Wilson considers some purely abstract questions in primarily an abstract way: sovereignty, the nature of law, the classification of the functions of government, political rights, whether society is greater than government, and so on. That is the total extent of Wilson's summa —for a summa in a way it is, a summation of all the dominant modes of political thought of his time.
Undoubtedly this is an incomplete account of post-historicist studies in comparative politics. It has dealt only with dominant themes in American and German political studies. As a result, it necessarily is less than just to those writers who were, as some writers always are, out of tune with the dominant trends, who lagged behind the times or marched ahead of them. For example, Bluntschli, in his monumental (and much neglected) Theory of the State , begins with an explicit rejection of two "false methods," "abstract ideology" and "mere empiricism," and a special plea for methods of "concrete thinking," and lives up to this position at least to some extent (though Bentley denies it). We can no doubt find other important writers equally at odds with the tenor of the times. This is especially the case in regard to a school of writers who, more than any others, kept comparative politics alive throughout this largely anticomparative period, writers whose works have very wide scope, who combine theory and data almost on the scale of the historicists, and who are alluded to in almost every work on politics of the period, even the narrowest, most abstract, and most formal-legal—the political evolutionists.
Evolutionary studies might of course be considered a particular kind of historicism, and in some forms they do come close to what is nowadays (after Popper) generally meant by that term. Those evolutionary studies that posit some inevitable goal (such as democracy or perfect freedom) for the evolutionary process and a basic evolutionary principle (such as survival of the fittest, economic growth, progressive economic differentiation) as, so to speak, the "spirit" of the process are almost indistinguishable from historicist theories. Most evolutionists rejected, however, the too audacious, often ill-informed, theories of the historicists no less than did the pure philosophers, the formal-legalists, and the political ethnogra-
phers, although they rejected them in different ways and for different reasons.
Evolutionary theories about politics involved, in the first place, an empirical reaction against historicism in that the evolutionists paid meticulous attention to data that the historicists had on the whole treated only in the vaguest generalities—particularly primitive, early Western, and non-Western political systems. Evolutionism involved also a theoretical reaction against historicism. Instead of attempting to write universal history, including the future no less than the past, they concentrated upon much more limited problems—particularly the problem of the origin of the modern territorial state. As a general rule, they tried merely to find the processes and laws underlying the development of complex political systems. This is in every sense a more limited concern than that which motivated Condorcet or Hegel. At their best, evolutionary studies combined the respect for data of the ethnographers with the modesty in speculation of contemporary middle-range theorists. Granted that some of the theories the evolutionists produced look very peculiar nowadays—that is less the result of any dubious procedures on their part than of the fact that they proceeded from theoretical presuppositions and asked theoretical questions that have simply gone out of fashion.
What sort of theories did the evolutionists produce? Essentially two kinds: theories of sequence—the stages of political development—and theories of the moving forces behind the evolutionary sequences. The most common theory of sequence traced the origin of the modern state to a continuous process of social enlargement and complication beginning with the primordial family. Among many works arguing this point of view probably the most illustrious are Sir Henry Maine's Ancient Law (1861) and Early History of Institutions (1874), in which political life is depicted as beginning with the patriarchal family and proceeding through two intermediate units, the house and the tribe, before the territorially contiguous form of the state is reached. This argument is based on a meticulous examination of Hebrew, Greek, Roman, and Hindu history.
The principal alternative to this interpretation is one that traces the origin of the state not to the family but rather to the disintegration of primitive social forms—not to the growing size and complexity of social units but to the opposite, the gradual individuation of human beings, their extrication from collectivities in which individuality itself is absorbed into the larger unit. So, for example, Edward Jenks argued, in A Short History of Politics and The State and the Nation , both published toward the end of the period under consideration (1900 and 1919), that the proper sequence
for the emergence of the territorial state is not Maine's, but rather from hunting pack to tribe, from tribe to clan, from clan to family, and from there to nonkinship units, individuals, and the state. In a sense, he reverses Maine's arguments.
As to the moving forces behind these sequences, a much greater variety of theories confronts us. Some evolutionists attributed the rise of the state, particularly the transition from the patriarchal family to the more extended political groups, to religious forces. The usual theory is that of Fraser's Golden Bough (for a political scientist's version, see Sir John Seeley's Introduction to Political Science , 1896), which traces the evolution of simple patriarchal authority through gerontocrats claiming a special skill in dealing with the world of spirits and through the rule of specialized magicians to that of the priest-king. Fraser's work was based largely on studies of societies with which Maine had not dealt in detail, such as ancient Egypt and primitive societies portrayed in early anthropological studies.
Another group of theorists, especially Oppenheimer in The State (1914), find the propelling force leading to the state not in religion but in force, in the building-up of gradually larger units through systematic conquest. Still another theory claims that the state comes into being through the impact of social differentiation on primitive social forms, especially through the appearance of vertical stratification. This view is argued, for example, by W. C. MacLeod in two works, The Origins of the State (1924) and The Origin and History of Politics (1921), studies in which Darwin, Marx, and early anthropology are all combined in a curious mixture.
A fourth theory linked the evolution of political institutions with economic changes, not so much in the style of Marx as in that of Rousseau's Essay on the Origins of Inequality . An example is Oppenheimer's The State , which, in effect, combines the conquest theory of the state with an economic theory of its origins. Oppenheimer argues that complex forms of government are made necessary by class distinctions based on wealth and that the institution of slavery to build up a labor force is the basic foundation of the state. ("The moment when the first conqueror spared his victim in order to exploit him is of incomparable historical importance. It gave birth to nation and state.") Some writers linked the development of the state with the development of pastoral pursuits, others with the accumulation of surplus wealth, still others with the development of the idea of property or population pressures upon resources and resulting wars of conquest or, as we have seen, social differentiation of any sort.
Finally, certain writers produced "diffusion" rather than "convergence" theories of the state. These theories argue, in effect, that the factors leading to the state did not produce it in different places through force of similar circumstances, but that the state came into being only once and in only
one place through "natural causes" and then gradually spread, presumably because of its organizational superiority and through a process combining conquest and borrowing, to other societies, like ripples in a pool. For example, G. E. Smith and W. J. Perry, in The Origin and History of Politics (1931), place the origin of the state in Egypt around the year 5000 B. C. Here the state emerged, in their view, through a convergence of religious and economic forces never duplicated elsewhere. From Egypt it spread, by quite another sort of inevitability, to the rest of the world.
The Legacy of Evolutionism
Developmental theories of this sort have gone out of style in our age of models, "system" theories, and equilibrium analyses; and so they have about them a musty and archaic flavor, an ambience of crumbling volumes in the dark recesses of libraries and of vain debates long since resolved in irreconcilable disagreements. Yet the pursuit of such theories spans a period from mid-nineteenth century to a mere generation ago, a period that overlaps on one end with historicism itself and on the other with the comparative politics of our own time. In fact, the larger syntheses of political evolutionary studies still smell of fresh ink; the best-known perhaps is Book I of MacIver's The Modern State , first published in 1926 and reissued last in 1955, and Part II of E. M. Sait's Political Institutions , published first in 1938. Sait calls his study A Preface , a rather melancholy fact when viewed from the perspective of our time, for it is, in fact, an epilogue and a summing-up. This useful summing-up synthesizes all the divergent tendencies of nearly a century of evolutionary thought about politics, however, as witness the following extract:
The State is composed of three elements: people, government and territory. From the beginning, groups of people are bound together by the cohesive force of kinship and religion. The family is the primordial unit, which expands into sibs (gentes , clans) and the tribe. Among pastoral people, patriarchal discipline prepares the way for tribal government; tribesmen who are accustomed to give unquestioning obedience to their respective family heads naturally accept the authority of the council of elders or patriarchs and of the chieftain who rises out of the council. But the emergence of government—that is, an intensified regulative system—within the kinship group must be associated with economic causes, with the adoption of pastoral pursuits and the accumulation of surplus wealth. Property introduces all sorts of complications. There are disputes within the tribe to be settled; there are raids by avaricious neighbors to be repelled. The situation calls for individual leadership. Some member of the council, more energetic and enterprising than his fellows (and for that reason more wealthy), pushes his way to the front with or without the assistance of religious superstition. He, or some one who later essays the same role, is recognized as chieftain. Since the
qualities of leadership are likely to be inherited, the office becomes attached to a particular family and is transmitted like other forms of property. Government exists. But although the pastoralists may confine their wanderings within roughly determined geographical limits, they are still nomads.
The territorial State does not appear until population begins to press upon subsistence. Then one of two courses may be followed: new land may be acquired by migration or the old land put to more productive use. Fertile pasturage, when brought under cultivation, will support a much larger population; and the tribesmen have long been familiar with the possibility of raising grain and vegetables from wild seed. Rather than leave the region to which they have become attached, they supplement the prevailing pastoral economy with the rudiments of agriculture. Gradually the herdsmen become husbandmen. The transition takes place slowly, as, by trial and error or by the imitation of some neighboring agriculturists, the methods of tillage are improved and their potentialities realized. Along with the new system of production come great social changes: above all, the sharpening of class distinctions, the systematic resort to slavery, the emphasis placed upon military life (first for defense, then for conquest), and the establishment of monarchy. With settlement upon the land and the acquisition of fixed abodes, the original kinship tie gives way, naturally but stubbornly, to the new territorial tie.
In some such way the state arose.
Because evolutionary political studies have passed out of fashion, their importance is all too easily underrated, but they constituted a tremendously important phase in the development of comparative politics. Above all, they kept comparative study itself alive in a period when it was threatened from every direction. Along with political ethnography they helped to focus attention on political systems other than those of the West just when the academic emphasis on training exerted great pressure toward restricting the political scientist's span of attention. They posed genuine theoretical problems when political scientists were concerned mainly with depicting formal-legal structures. They kept alive a systematic interest in links between political institutions and other aspects of society and kept political science in touch with other social sciences, especially sociology and cultural anthropology, when the newly won departmental autonomy of the field produced attitudes threatening to cut it off from a vast range of relevant data and many useful theories. To be sure, they led in political studies to the consideration of a very limited range of problems, especially concern with the origin of certain widespread political forms and the attempt to discover common sources for similar political institutions in different societies—the chief purpose of E. A. Freeman's celebrated Comparative Politics . But that was better at least than no concern at all with problems requiring large-scale comparisons.
Early Political Sociology
Anyone acquainted with political thought in the late nineteenth and early twentieth centuries will realize immediately that some formidable names that might have been mentioned in connection with the state of comparative political studies in this period are still missing from the picture, even after writers like Bluntschli and the evolutionists have been discussed. I refer to a number of men who loom very large in political science (not least in comparative politics) today, but who do not readily fit into any of the categories used here to characterize the political thought of their own time—men like Mosca and Max Weber, Pareto and Michels, the most illustrious of the early modern political sociologists. All constructed large-scale theories of politics, but theories certainly not purely formal in character. With the possible exception of Michels, they all ranged over wide sweeps of data, but not in the pointlessly empirical manner of the political ethnographers. They were more interested in actual power relations than in constitutional documents, more concerned with recurrent actual patterns of authority than with the inherited formal distinctions between types of government.
They did not restrict the subject matter of their studies to the state but branched out into all sorts of other political phenomena, from the government of political parties to that of private groups, and they explored systematically the impact on politics of its setting. In doing these things, they developed novel analytical perspectives for political studies, devised new concepts, proposed empirically relevant hypotheses, and developed unconventional techniques for applying comparative methods. They engaged, in short, in just the sort of conceptual, methodological, and theoretical explorations that would seem to be the major present concerns in comparative politics.
Why then have they been omitted from the story? Simply because only the creation of their works belongs to the period we have been discussing. Their impact on the field of comparative politics belongs to a later time, when the concerns of its practitioners had changed in such a manner as to make them more receptive to the sociologists' ideas. But this is not to say that political scientists in general simply ignored the political sociologists. They did read them and they did teach them, but only to some extent, and only in a way: they taught them as if they had been political "philosophers" in the then familiar sense, concerned primarily with abstract and normative political theory. Without exception, the early political sociologists were represented as "critics of democracy," "irrationalists," latter-day Hobbesians, who attacked the comfortable premises of the defenders of democracy, equality, and human reason—in short, as foils to men like Locke, Mill, and T. H. Green. Anyone who becomes familiar with
the work of the early political sociologists today will realize that it was a travesty of their intentions, and indeed of what they actually said, thus to represent them, even though some of them—Mosca, for example—certainly invited such treatment by drawing large normative conclusions from their sociological studies. But basically the political sociologists were treated as they were, not because of anything they did themselves, but because the categories with which they dealt seemed naturally to place them, if not outside political science altogether, then in the area of political theory rather than in the political institutions division of the field. And this is something doubly regrettable, for it means that some of the most promising modern works on comparative political institutions and behavior were long misrepresented in the "political theory" courses, to which they were only indirectly relevant, while they were ignored in the comparative politics courses, on which they had a direct and important bearing.
No wonder that students of comparative politics had to rediscover, and even to relearn, the early political sociologists for purposes of their own work. No wonder either that this rediscovery is something quite recent. In my own undergraduate days Mosca, Michels, and Pareto were still represented mainly as abstract critics of the abstract bases of democratic ideology. I remember, with some horror and some relish, the comment of a venerable teacher (not a "theorist" by any means) on an undergraduate essay about Weber's political sociology: "An interesting analysis of a brilliant but obscure"—yes, obscure—"German thinker."
Today, of course, the names of Weber, Pareto, Mosca, and Michels are among the more luminous in the study of comparative politics. But before they could become this there had to be a reaction against the older conception of comparative politics and the actual lines of analysis pursued in the field. This reaction in fact occurred in the 1920s and 1930s.
One of its first manifestations—not confined to comparative politics, but, in fact, appearing at first mainly in studies of American politics—was a growing interest in political parties and pressure groups. This interest is important because parties and pressure groups are not, strictly speaking, parts of legal-institutional structure and because they link politics to other social phenomena more closely than does the formal-legal framework of a political system. The reasons for the growing interest in "informal" political processes throughout the 1920s and 1930s are fairly obvious. Most obvious of all is the fact that parties and pressure groups by this time played a greater role in the politics of most states than they had before. Parties, in the sense we now think of them, developed rather late in the history of representative systems, however much the term itself might
have been in use in earlier times. Large-scale, bureaucratized, intensely active pressure groups, especially great economic and other "interest" groups, also belong to a relatively recent period. This fact, however, while important, is not alone enough to explain the increased interest in parties and pressure groups, for the mere fact that something exists and plays an important role in politics does not mean that it will necessarily be studied by political scientists. The analyst's attention must first be prepared by operative preconceptions to seek out the data and to recognize them as significant. What theoretical influences, then, disposed political scientists to look intensively at party and pressure group activities?
One of these influences undoubtedly was political pluralism. By rejecting the idea of sovereignty and by intruding into the Lockean dualism of individuals and the state the concept of groups either mediating between them or coequal with the state, pluralism made all sorts of phenomena appear "political." Under the influence of the monistic theory of the state these phenomena had appeared extraneous to politics. To be sure, the pluralists argued mainly a normative case: that the state was only one social organization among many and that it had no special right to impose obligations upon individuals or their collectivities, that is, no special status above the other associations of society. But this normative position inevitably influenced the way politics was conceived for all theoretical purposes. In breaking down the distinction between the political and the social, the pluralists did not remove the consideration of politics from the study of society, but, quite the contrary, they invested all things social with political significance. Under their influence, one saw politics and government, power and authority, everywhere and in all social collectivities, but first of all, of course, in those collectivities most closely bound up with the state: pressure groups and parties.
There can be little doubt that the pluralistic point of view underlies, consciously or otherwise, the work of such men as Lasswell and Catlin, the undoubted pioneers in enlarging the subject matter of political science from the state to social relations as such. "The writer," says Catlin in the Preface to his Principles of Politics (1930), "sees no objection to calling the science of social inter-relations by the good Aristotelian name of Politics." Shortly thereafter, Catlin acknowledges his "profound debt" to Harold Laski, who was, at one time, perhaps the most celebrated of the normative pluralists. Politics he then defines as a particular kind of activity, "not as a thing," specifically as any act of human or social control. A broad definition indeed, but no broader than that with which Lasswell begins his famous Politics: Who Gets What, When, How (1936): "The study of politics is the study of influence and the influential," the influential being "those who get the most of what there is to get."
The growing emphasis on parties and pressure groups can also be at-
tributed to a second major influence on political preconceptions: certain experiences made students of politics more aware than in the past of the great difference between constitutional forms and political reality. In America, the muckrakers had led the way toward the discovery of the "anonymous empire" of lobbyists and influence-wielders, conducting a kind of private government under the public facade of the Constitution and in interplay with formal authorities. This process seemed to the leading "group theorist" of them all, Bentley, to be the total sum and substance of politics.
Perhaps the most crucial experience leading to a disenchantment with constitutional forms was the fate of the Weimar Constitution, that professionally engineered document so widely acclaimed in its time, such a dismal failure in operation, which eventuated in the most extreme of totalitarian regimes. Some political scientists managed to cling to their preconceptions in the face of the Weimar experience (and the equally sorry operation of the French Third Republic) by claiming that it was all the result of faulty constitutional engineering. Many more, however, drifted toward the view that political processes are only imperfectly subject to control by formal rules and mainly the products of social and economic forces, of the interests and attitudes of the public and politicians, military officers and public officials, capitalists and trade unionists, and the like. Certainly these experiences helped to make political scientists aware that men like Marx and Pareto, Michels and Mosca, Wallas and Lippmann, did not belong merely among the abstract, primarily normative, political theorists, but that they could help one to reach a better understanding of actual political processes than could the constitutional lawyers and writers on formal political structure.
From this growing concern with informal political processes, political competition, semipolitical groups, and actual distributions of power, there naturally followed a growing interest in the links between politics and other aspects of society. From this in turn there followed a growing interest in systematic problem solving on the middle-range level rather than in the construction of mere morphology. "Political sociology" came by degrees to be reconciled with what had passed for political science. It is clear from the literature of the period that the crisis of democracy in Europe provided the main impetus toward this reconciliation—even more than the widespread influence of Marxism, which certainly had a greater impact on political activists than political scientists in these years.
The Synthesis of Data
The reaction that took place in the 1920s and 1930s against the older conception of comparative politics had also another important manifestation. There appeared in this period a number of studies that attempted
to synthesize the findings of configurative studies in large-scale comparative works and, in the course of this synthesis, attempted also to reunite political theory and political data. These syntheses—the most weighty are James Bryce's Modern Democracies (1921) and C. J. Friedrich's Constitutional Government and Democracy (1937)—are fundamentally different from those of Woolsey, Wilson, and their kind, particularly in two ways. They do not present theory and data simply as cohabitants under a single set of covers but chastely separated. On the contrary, they bring the data directly to bear on the theories, making the resolution of theoretical issues turn at least to some extent upon the evidence of experience rather than exclusively upon the promptings of reflection. And they do not synthesize configurative studies by presenting broad historical narratives in the manner of Wilson (narratives in which each link in the chain still appears as something quite unique in whole or in large part). Rather—and this is especially true of Friedrich—they present data in terms of general functional and structural categories, which, by implication, are elements of all political systems, or of all political systems of a particular sort. Because of this presentation, they are much more obviously "comparative" in nature than Woolsey's and Wilson's syntheses. Perhaps these two tendencies—the reconciliation of theory and data and the use of generalized categories for the analysis of political systems—are still rather primitively developed in the work of Bryce and Friedrich. Perhaps also, the theories are still too much taken from purely abstract political speculations and the generalized categories from the existing corpus of formal-legal studies. This is saying no more than that their work was affected by studies already in the field, as any scientific work must be. There is much that is old-fashioned in both Bryce and Friedrich (and, of course, much more in Bryce than in Friedrich); but there is also much that is original and portentous for the future and much that is derived from the original studies of informal political processes of their own time. Bryce and Friedrich are in effect transitional figures in comparative politics; and just for that reason it is worth looking in some detail at both what is essentially old and what is essentially new in their studies.
Bryce's Modern Democracies
Bryce's Modern Democracies is in many ways a synthesis in the grand old manner, certainly in scope and to some extent also in content. Much of it consists of old-fashioned configurative studies of a large number of "democratic" countries: ancient Athens, the republics of Latin America, France, Switzerland, Canada, the United States, Australia, and New Zealand. In these configurative studies much space is devoted, in the established manner, to formal-legal structure. But quite apart from the fact that Bryce also gives considerable space to political parties and "the action
of public opinion"—subjects not at all discussed by Wilson, whose index of seventeen pages does not even list parties, and discussed only cursorily, in the main abstractly, by Woolsey, who gives them twenty-five pages out of twelve hundred—the whole conception of the work makes it into something unprecedented, in idea, if not in every aspect of the way the idea is carried out.
The configurative studies that Bryce presents are in fact intended only to provide data necessary to achieve a broader analytical purpose. And what is this purpose? Basically, it is to solve a single substantive problem that ties together the whole prolix and often incoherent work and to solve it by applying a particular procedure that to Bryce is the only proper procedure for comparative analysis. Both of these aspects of his purpose, his problem and his method, furnish evidence of the transitional character of his work.
The basic substantive objective of Modern Democracies is to examine the plausibility of the justifications and criticisms of democracy on empirical grounds, to see what light actual experience sheds upon the abstract arguments used either for democracy or against it (in his time, chiefly for it). His object, Bryce explains in the Preface, is not to develop "theories" but to state facts and "explain" them. Explaining facts is of course precisely what most of us today understand by developing "theory," but to Bryce theory means something quite different, and significantly different. It denotes what he later refers to as the "systematic" approach: purely speculative thought, unencumbered by data. Such thought, he argues, leads only to "bloodless abstractions," based, more often than not, on supposedly self-evident propositions about man and society, which inevitably give rise to empirically false or dubious conclusions.
The usual procedure in arguments about democracy is, according to Bryce, to establish first certain natural human rights; to argue from these to the logical desirability of democracy (that democracy is "government upright and wise, beneficent and stable"); to posit certain propensities in the nature of man that make it possible to argue that "democratic institutions . . . carry with them, as a sort of gift of Nature, the capacity to use them well"; and then to deduce further a great many not at all self-evident propositions about the desirability of liberty and equality, the educatability of all men, the relations of literacy and political wisdom, the rightness of public opinion, and so on. Bryce himself wants nothing to do with such abstractions, nor with any discussions of schemes of political reform "on general principles." His aim is to subject all such assertions to a single question: are they borne out by political experience and, if not, what propositions fit such experience better? The whole work, then, is intended to be an antidote to abstract theory about questions that the abstract theorists had wrongly preempted from the empiricists.
Of course, this very definition of his problem means that the abstract theorists exercised a great influence upon Bryce's study, if only in that his own theoretical problems are derived from them. This fact alone gives the work a curiously old-fashioned tone. Like the abstract political theorists, Bryce is concerned with what is right or wrong with democracy and a host of subsidiary normative problems. (Does power corrupt? Does wealth? Can the arts and sciences flourish under democracy?) Since his data are in most cases not adequate to solve such problems, there is in his work, as in the older syntheses, still a considerable gulf between speculations and data, even though the basic aim is to bring the two together.
Furthermore, just as Bryce's problems are rooted in tradition, so also, in some respects, are his methods of dealing with them. Not only does he present his data in the first instance through a large series of configurative studies, but his whole conception of the relations between facts and theory is primitive and old-fashioned. Nowadays we certainly do not believe that facts speak for themselves, that we need only know them in order to know what follows from them. We believe that facts are dumb and slippery, that they reveal their significance only when we have set all sorts of cunning traps for them—when we have gathered them in various ingenious ways and subjected them to various complicated processing devices: experiments, carefully chosen samples, multivariate analysis, and the like. But Bryce's attitude to facts is essentially that of a methodological innocent, even though, like Machiavelli, he has more than the ordinary amount of shrewd common sense.
Basically, Bryce is the crudest sort of empiricist in that he believes, implicitly at any rate, that facts are really self-explanatory, and in that he decidedly belongs to the past rather than the present. So also he echoes the past, though in a different way, in his basic conception of "comparative method." Modern Democracies is indeed represented as a "comparative work"; in fact, its very first chapter, after the introduction, is devoted to an explicit discussion of comparative method, something surprisingly rare in the field. But comparative method to Bryce has only a very special and limited utility; it can yield no direct knowledge of anything he wants to know but only give a more solid grounding to those first principles from which all political positions must be deduced. Comparative method is not really intended by him to be an alternative to the "systematic approach." In the last analysis, he uses comparison only as a way of arriving at basic premises for systematic analysis, a way supposedly superior to the formulation of "self-evident" propositions. While, therefore, the basis of Bryce's arguments is certainly empirical, or meant to be empirical, the arguments themselves, once we leave his country studies behind, sound curiously abstract.
Methodologically speaking, Bryce is in effect both a crude empiricist
and a reductionist of the most extreme sort. This combination explains all the essential characteristics of his work: why he is a theorist who uses almost no theoretical equipment and, even more important, why he carries out an explicitly comparative analysis in a basically configurative way. Bryce believes, in effect, that every concrete social pattern is something unique, something ephemeral and nonreplicable, and therefore that it can be adequately represented only by means of configurative analysis. But just because every concrete social pattern is a world unto itself, a precise social science must be based, he argues, upon psychology, upon the constants of human nature that underlie the varieties of social experience.
What then is the comparative method to do? Is it not, upon this view, irrelevant to social science? Not quite; comparative method, to Bryce, does have a role to play in social science, a psychological role: one uses it to discover the fixed characteristics of human nature by examining the differences in actual social phenomena. What we do in comparing is simply that we subtract from actual experience that which is seen not to be "fundamental" to it: anything due to "disturbing influences," such as the influence of race, "external" conditions, historical antecedents, and so on. We are then left, as a residue, with the human constants we need for a precise social science. For the sort of issues Bryce raised, this social science is necessarily deductive once the psychological premises have been established, but for the explanation of concrete social facts it yields a simple ad hoc empiricism. To explain any concrete behavior we simply combine the psychological constants with the unique disturbing influences bearing upon the behavior pattern—and there we are.
This sort of procedure is nothing original in Bryce's time—though there is no evidence that he knew anything of Pareto, with whose Mind and Society his Modern Democracies has much in common, not only in method but also, as a consequence perhaps, in manner: particularly in the disorganized presentation of great heaps of information in volume after interminable volume; the whole is sifted here and there for a very few dubious propositions of cosmic import. Psychological reductionism happened to be very much in the air in Bryce's time, not least in political studies. What is important in Bryce's version of it is his insistence on the actual analysis of political systems in order to discover relevant psychological constants, rather than proceeding from common-sense notions about human nature or "self-evident" propositions.
Whatever one may think of reductionism in principle, it is certainly a procedure difficult to carry out in practice. It is no small matter to try to find in the enormous varieties of concrete social life anything constant at all, except variety itself. And so it is not surprising that Bryce is, in the final analysis, not quite true to his method. He actually distills from his configurative materials not only psychological constants but also, with more
emphasis and at much greater length, certain broad ad hoc generalizations about the essential bases of successful democratic government and the contingent circumstances that help or hinder its existence.
His argument comes down to this: Successful democracy, he thinks, requires a legislature rather like the British House of Commons up to the late nineteenth century. It should consist of illustrious men who command great respect and have a high sense of political responsibility, who are not divided into many antagonistic groups and yet not subject to great party discipline either, who are not mere speakers for constituents or parties and yet can easily be integrated into majorities for the expeditious discharge of business—a legislature devoid of caucuses, groups, opportunists, and the second-rate. The possibility of the existence of such a legislature depends on the general national character of a people. This character, in turn, Bryce treats not as a simple given fact but as the product of numerous conditioning factors that he never makes explicit but that keep appearing in his analysis: demographic and geographic factors (smallness is absolutely essential: only its great size keeps China from being a successful parliamentary democracy!); the ethnic, religious, and class diversity of a society; occupational structure and economic development (agriculture is conducive to democracy, while industry, because it generates occupational diversity and class conflict, and because wealth corrupts, is a threat to democracy); history (especially the gradual development of a desire for democracy and a tradition of self-government); and a mysterious factor he refers to as "racial qualities."
While most of the work thus deals with the "disturbing influences" that condition societies, some of it is devoted, as it must be, to the constants on which these influences work. Bryce's constants resemble those of Michels as much as his method resembles that of Pareto, again without any evidence of acquaintance with Michels's work. What Bryce really discovers is not any psychological constants at all but a sociological principle and certain principles subsidiary to it. This principle is the universal fact of oligarchy in politics. He finds it to be a universal fact because "organization is essential for the accomplishment of any purpose," because the majority takes little interest in politics and lacks sufficient knowledge to play a positive political role, and because the natural capacities of people are unequal. Democracy in its classic form, therefore, is a human impossibility; at most it can mean only the prescription of broad ends and the selection of leaders from among competing elites by the electorate. Bryce thus develops a very early version of Schumpeter's elitist argument in Capitalism, Socialism and Democracy , and couples it with some very pessimistic findings about the educability of people, the usefulness of mass media of communication, and the appetites for self-government and authority.
But this is not the place to go fully into Bryce's substantive findings.
The important thing is to note the ways in which he presents them and arrives at them. To sum these up: Bryce is, in the first place, still an abstract theorist, but one who insists on the empirical derivation of his first principles. He is also, by conviction, an exponent of configurative analysis, but he insists on using the data of configurative studies for broader theoretical purposes. Finally, he is also something of a middle-range theorist (insofar as he looks for the probable effects of particular conditioning factors like ecology, social structure, and economic structure on particular aspects of political behavior), but he assigns to such middle-range theories a relatively low importance compared with residual first principles and arrives at them through the crudest sort of empiricism. What we should note above all perhaps is that he insists that theories be fully grounded upon data and that data be presented always for theoretical purposes. Politics appears to him an activity embedded in all social relations yet not governed by any single transcendental principle. In these respects, his work represents a long step away from the world of historicism and its aftermath and toward the approach of Montesquieu, who was by Bryce's own admission, along with Tocqueville, the model he sought to emulate.
Friedrich's Constitutional Government and Democracy
In one sense, perhaps, Friedrich's Constitutional Government and Democracy is more like the late nineteenth-century syntheses than Bryce's Modern Democracies . It is packed with discussions of the abstract political theorists that are in many cases not clearly integrated with the empirical parts of the study. Bryce at least derived from the abstract theorists his analytical problems; in Friedrich, references to the political "theorists" sometimes are little more than displays of erudition, albeit impressive erudition. In many important respects, however, Constitutional Government and Democracy takes great strides beyond Modern Democracies .
For one thing, there really is no purely configurative analysis in the book. Instead of presenting his empirical materials on a country-by-country basis, Friedrich organizes them in terms of a large number of structural and functional categories, under each of which theoretical speculations and data from a number of political systems (all Western) are given; the data are then sifted for theoretical significance. It is true that information under most of Friedrich's categories is itself presented in a country-by-country fashion, but the intent is clearly to go beyond configurative analysis; the country-by-country approach is used merely as a way of organizing the materials and not as the result of a belief in the uniqueness of each configuration. It should also be noted that many of the categories in terms of which the work is organized refer to formal-legal structure. That may, however, be the result simply of the nature of the materials available to
Friedrich rather than of a narrow conception of politics on his part. In any case, the study includes much comparative material on parties, interest groups, and media of political communication; and throughout Friedrich gives considerable attention to the interplay between political forms and social conditions. In Constitutional Government and Democracy we thus come upon a full-fledged modern comparative synthesis, although one which still leaves many theoretical strands dangling in empty abstraction and which is still deeply rooted in the formal-legal style of early political science—two facts perhaps inevitable, given the period in which it was written.
Just as the contents of the study and the way they are organized are a mixture of the new and old, so also is the methodology underlying it, although it is a methodology very different from that of Bryce. As we have seen, Bryce's methodology had as its object mainly the establishment of first principles on empirical grounds. The ultimate purpose of Friedrich's, on the other hand, is to defend crude empiricism in the direct (not the deductive) construction of middle-range theories, although in the course of establishing this position he passes over some of Bryce's methodological ground.
Friedrich is not nearly so optimistic as Bryce about the possibility of scientific precision in political science on any basis. In a methodological appendix that portrays exactly what he does in his substantive chapters (but that is omitted from the later editions of the work, since Friedrich himself no longer holds these views), he rejects the possibility of formulating "laws" about politics and argues that one can at most formulate only "reasonably accurate hypotheses concerning recurrent regularities" in political experience. A reasonably accurate hypothesis about politics seems to him doomed to be always a greatly inaccurate hypothesis. Why so? Because all social phenomena involve the operation of a great many variables, and the greater the number of variables bearing upon a subject, the more inexact generalizations and forecasts about it must be.
The proper method for such a subject matter, among all the methods available to us, is what Mill called the inverse deductive method, and this is simply the method of reductionism: the establishment of psychological constants by reasoning back from cultural variations to invariant underlying conditions. Here we seem to be back with Bryce. But—and this is the rub—to find the constant human nature underlying social experience, argues Friedrich, no complicated procedures are needed; psychology is fully available to common sense, for in talking about human nature we are only talking about ourselves, and therefore about data available to simple introspection! Friedrich is almost touchingly certain, in fact, that we already know almost everything worth knowing about politics and that any "partially inaccurate" notions we may have about the subject are easily corrected by deeper introspection and a wider inspection of data, for if psy-
chology is the basis of political knowledge, we need "only" look inward to know politics, and if, despite this fact, inaccurate notions about politics become established, the "facts" will soon disabuse us of these notions. In this way, Friedrich, having ruled out scientific precision at the outset, then makes things still easier on political scientists by holding that all "reasonably accurate" hypotheses in political science are immediately accessible to common sense—anybody's common sense, though best of all the common sense of the well-informed political scientist. This "methodology" is nothing more than an argument for ordinary shrewdness and nothing less than an argument against "social science."
In the substantive chapters of the work Friedrich is faithful to these views. Unlike many social scientists, he knows exactly what he is doing. His actual method in Constitutional Government and Democracy (though not in later works) is first to inspect a certain range of behavior (now broad, now narrow) pertaining to one of his subdivisions of constitutional government, then to generalize about it on the basis of common sense (that is, without using any special technical apparatus), and finally to see whether the generalizations so arrived at, when reduced to psychological terms, are congruent with his own common-sense notions about human nature. He collects a set of facts, reflects upon them, and checks the common-sense plausibility of the reflections; this, in his view, is really all that social scientists can do fruitfully.
We get the quintessence of this procedure in the conclusion to his chapter on electoral systems. "Proportional representation," Friedrich says there, "has been found wanting and incompatible with parliamentary government"—as indeed it had to be, for the "natural" effect of P.R. is to splinter political forces and thus prevent the formation of majorities on which stable parliamentarianism depends. The Weimar Republic illustrates the case. But if we look at all the other cases of P.R. that Friedrich cites—Belgium, the Netherlands, Sweden, Norway, Denmark, Ireland—this conclusion seems by no means to follow. What then? Well, "there are special factors to be considered in these several lands." Apparently, P.R. is not incompatible with parliamentary government in constitutional monarchies, or in small countries, or in countries with strong administrative traditions, or in countries where a single emotional issue divides the electorate. And "all this goes to show that the prevalent English and American opinion against proportional representation is practically sound." What we get here is in effect a generalization based on a single case, supported by common sense, and then an almost model exercise in what to methodologists is one of the cardinal sins: "saving the hypothesis" by enlarging it to cover all the cases that seem to falsify it—in this instance, the great majority.
But it is too easy, and quite unjust, to be harsh on Friedrich from a contemporary perspective. Despite the deliberate antiscientism to which
Friedrich adhered when he wrote the book, Constitutional Government and Democracy deals with a host of middle-range problems that simply cry out for more methodical treatment and includes a large number of theoretical propositions that have furnished issues to comparative politics for a long time now.
The objective that unifies the work is to determine the conditions of success of constitutional government (and, by the way, to develop, through the examination of existing systems, a set of maxims of constitutional prudence). In regard to this basic problem Friedrich chooses an essentially "cultural" solution—that is, the primary significance of what Bentley called "soul-stuff," political ideas and attitudes. Constitutional government and democracy, he argues, are threatened primarily by "intensity" in politics, especially intense disagreements over fundamental procedures and ultimate political objectives; intensity itself is measured by the extent of political enthusiasm ("consent") and animosity ("restraint") in a society. This broad hypothesis—which seems commonplace now but was not at all conventional twenty years ago—is the apex of a great many more limited generalizations: for example, that successful constitutional government requires a "balance of social classes" (whatever that might be), that "objective" heterogeneity in a society does not undermine constitutional government so long as there is a minimal unity of political outlook, that the number of parties in a representative system depends upon conditions prevailing in the system prior to the establishment of parliamentary government, that an inflexible constitution is to be preferred over a flexible one in societies that have no firm constitutional tradition but not in societies that have such a tradition—and many more, all based, of course, on artless inferences from very few cases.
At the end, we are left with three sets of theoretical ideas, two substantive and one procedural. First, the study presents what is in effect a set of requisites for successful democracy, many of them truistic, as they must be in view of Friedrich's method, but some not at all obvious. These requisites fall into two categories. One comprises organizational requisites, such as a responsible bureaucracy, an efficient diplomatic service, an effective judiciary with wide powers (including controls upon administration), a legislature organized for fruitful deliberation and not merely accurate representation and unlimited debate, some sort of separation of powers, functional or territorial, a neutral arbiter of constitutional disputes, and broad but rigidly defined executive emergency powers. The other comprises social and cultural characteristics: a viable economy, low intensity in politics, an effective constitutional symbolism, informative media of communication, and a high degree of political integration of economic and other material interests in society. Second, Friedrich presents a number of conditions that, while not requisites of effective democracy,
do help to create a favorable climate for it: for example, a firmly rooted political tradition (its absence is not fatal because it can be overcome by proper constitutional devices), judicial review, the plurality systems of elections, and the existence of only two political parties in the system. And third, he provides throughout, chiefly by implication, a number of variables to use in the analysis of the functioning of all political systems, the most important of which are, in his view, political attitudes and constitutional structure, although he also resorts in places to factors such as social structure (note the requirement of a balance of social classes), history, and personality (that is, "leadership" as something that is not the product of any social forces).
All in all, then, Constitutional Government and Democracy is an early example of the functional approach to political analysis. It is a thoroughly comparative work, partly because a functional conception of a subject is in its very nature more conducive to comparative study than any structural definition. It is a study entirely devoted (leaving aside the generous references to traditional political theory) to the construction of middlerange theory about political institutions and behavior. In other words, its analyses are neither as all-encompassing as those of the historicists nor as narrowly restricted to configurative and formal-legal descriptions as those of the post-historicists. The middle-range theories presented deal mainly with the interplay of formal political processes with political parties and groups, and, in a still larger sense, with cultural, historical, and social forces. These are the "new" elements of the work. But Constitutional Government and Democracy has no real method (at most, an antimethodical methodology) and uses, geographically speaking, a rather limited range of data.
With Friedrich, however, we are at least to a large extent back in the world of Montesquieu's political sociology. We are not yet very far beyond it or in some respects even abreast of it. But it is no accident that it is Friedrich who really begins to synthesize political science with the political sociologies of Mosca and Pareto, Weber and Michels, to all of whom there are liberal references—though mostly critical references—throughout his study. What is still missing in his work is even that beginning of a systematic and rigorous approach that we can detect in The Spirit of the Laws .
Postwar Developments in Comparative Politics
By World War II, then, comparative politics was characterized by a reawakened interest in large-scale comparisons, a relatively broad conception of the nature of politics and what is relevant to politics, and a growing emphasis upon solving middle-range theoretical problems concerning the
determinants of certain kinds of political behavior and the requisites for certain kinds of political institutions. Comparisons, however, were still made largely without the use of any special technical procedures; speculation and data were only beginning to be deliberately integrated. The subject-matter treated was still predominantly the sovereign state, indeed still mainly the formal aspects of Western nation-states. The concepts used for analysis were largely conventional rather than technical, no explicit conceptual schemes designed for theorizing were used, and some of the most important aspects of analysis were left implicit. The interwar period was one preeminently of ad hoc and common-sense theorizing. This brings us to our own time.
What have been the trends in comparative politics in the postwar period? The most basic have been four. First, the empirical range of the field has been greatly enlarged, primarily through the intensive study of non-Western systems, but also through research into aspects of politics previously little studied. Second, concerted attempts have been made to overcome the lack of rigor and system that characterized the field in the prewar period—to make it more "scientific," if the use of unconventional technical concepts, systematic analytic approaches, and rigorous testing procedures may be called scientific. Third, there has been much greater emphasis upon the political role of social groups (whether explicitly organized for politics or not) and upon social institutions that play a special role in molding political values and cognitions, loyalties and identifications—agencies of political "socialization." Finally, political systems have been analytically dissected and questions raised about them in terms of conceptual schemes largely imported from other social sciences, above all in terms of structural-functional analysis. These trends take us back fullscale at last to the political sociology of Montesquieu, and indeed greatly improve upon it.
I have not listed the trends here in any logical sequence, but neither have I listed them in a merely random way. Granted some unavoidable overlapping, they appear in the order in which emphasis upon them actually developed in the postwar period (save only for the fact that structural-functional analysis has played an important role throughout, but a constantly greater role as the trends unfold), and they appear in this order because each stage in the postwar development of the field helps us to understand why the next was embarked upon.
The Study of Non-Western Systems
The influences leading to the gradual extension of subject matter to non-Western systems are fairly plain. The most obvious of them is the fact that societies and areas that political scientists interested in current events could once safely ignore became important and obtrusive in the postwar period
for a great many reasons: the emergence of many new states in non-Western areas, the impact of the Pacific and North African wars (which certainly made many Westerners intimately acquainted with areas previously regarded as merely exotic), and the fact that only the non-Western areas were uncommitted, or open to a revision of commitment, in the power conflicts of the cold war. There was, consequently, and still is, a considerable demand in the nonacademic world for specialized knowledge of these areas, and such a demand for expertise necessarily acts as an impetus toward its acquisition, most of all in a policy-oriented and training-oriented discipline like political science.
Yet it would be much too one-sided to regard the intense postwar interest in the developing areas merely as a response to postwar politics, even conceding that the most obvious academic influence that might have made for this interest, political evolutionism, had played itself out by this time. Why had not this great interest arisen much sooner? Perhaps because financial support for studies of premodern systems was harder to come by in the prewar period—and such systems are expensive to study—but financial support was scant at the time for almost all projects in the social sciences. Perhaps because international power relations centered heavily upon the European countries; but there was Japan to contend with in the East no less than Germany and Italy in the West, there were riots, demonstrations, and mass arrests in India, there were important upheavals in China and Turkey. There was much to study outside of the West.
Why then did so very few students of comparative politics turn to study other areas? The answer is, at least partly, that their aims and preconceptions as political scientists simply did not direct their attention toward them. Perhaps the most important factor responsible for this was the almost universal emphasis in political science upon the study of democratic institutions, then, and still, to be found mainly in the West. We must remember that even Alfred Cobban's pioneering study Dictatorship: Its History and Theory , which now may strike us as very antique, dates only to 1939. And why this emphasis on democracy? The answer was already noted by Bryce: because of an almost universal belief not only in the desirability and possibility but also the inevitability of representative democracy in the development of nations. After all, was not all of Western history itself indicative of this trend? Even the early Soviet Union did not raise any particular problem in this regard, for one could always take its doctrines at face value and persuade oneself to believe that it was itself tending in a democratic direction. So, in their larger-scale political works, political scientists wrote, if not about the modern democracies themselves, then about the Ur-democracies of the ancient world and the historical processes leading from them to the more fully developed democracies of modern times; but it seemed pointless and superfluous to write about contemporary
predemocratic, obviously transitional, systems—certainly as long as the end of the transitional process did not seem problematic.
From this standpoint, the interest in non-Western systems in political science is closely bound up with the crisis of democracy in Western Europe, the emergence of Italian and German totalitarianism, and the brutalization of Soviet Communism under Stalin. The declining faith in the inevitability of democracy led not only to a general interest in authoritarian governments, as exemplified by Cobban's own work, but also to two other, and relatively new, interests: in the processes of political change and the forces governing it and in the social forces rather than the legal rules governing politics. All of these interests obviously helped to open the door to the study of nondemocratic, rapidly changing societies either lacking highly differentiated political systems and highly articulated formal-legal structures or possessing them only on the level of colonial authority.
Also as a result of the crisis of democracy, political scientists now undertook a more intensive searching of the early political sociologists in order to gain insights into the cause of the unexpected political experiences of the modern world, and through the works of the political sociologist—certainly through Pareto, Mosca, and Weber—they acquired at least a cursory acquaintance with a wider range of political systems than political scientists had normally possessed.
The great postwar interest in non-Western areas is therefore a reaction to prewar no less than postwar political conditions. At any rate, it is a consequence of certain modes of thought engendered by prewar political experiences. And it may also be regarded as a consequence of a trend more purely internal to the field—namely, the growing interest in middlerange theories as such. The connection here is really quite simple: configurative study is bound, by its very nature, to narrow the empirical scope of studies, and comparative study, for the purpose of formulating, and even more for testing, middle-range theories, is bound to broaden it. This is a truism, but for the present purpose an important one.
Without slighting the role of external influences, therefore, one might reasonably have expected a broadening of the scope of comparative politics in the postwar period in any event. So also with the postwar interest in scientific method. Already in the 1920s and 1930s one can detect a certain unease about the looseness of analysis characteristic of the field. Bryce's chapter on comparative method is about a dubious version of it, but it is a chapter on the conditions of rigorous social analysis. Friedrich's epilogue on method is an apologia for his unscientific empiricism, but he does appear impelled to apologize for these aspects of his work. Certainly it is not difficult to see how formulations of middle-range theories about be-
havior within numerous contexts might lead the analyst, quite without other stimuli, toward increasing rigor of procedure and unconventional concepts and approaches; the moment one begins to question propositions like those which abound in Constitutional Government and Democracy , one can hardly avoid such matters, for it is precisely the lack of rigor and unconventionality that gave rise to the propositions.
But the postwar quest for a more rigorously "scientific" comparative politics is also due to certain "external" causes. It is certainly a reflection of the growing postwar cult of "behavioral" science throughout all the social sciences (taking "behavioral science" to denote (1) middle-range theorizing on the basis of (2) explicit theoretical frames of reference with the use of (3) rigorous, particularly quantitative, procedures for testing the theories). The "behavioral" approach has affected comparative politics primarily through the growing influence upon the fields of sociology and cultural anthropology, and this influence in turn may be attributed in large part (though not entirely) to the very fact of increasing interest in non-Western political systems. For one thing, when political scientists turned to the study of non-Western systems, they found other social scientists already occupying the ground, mostly cultural anthropologists but also a growing number of sociologists (or sociologically trained anthropologists); and so they naturally went to school with them and absorbed their techniques and style. For another, the theoretical equipment of political scientists, such as it was, generally failed them when they confronted political systems unlike the highly differentiated, formally organized, predominantly democratic or totalitarian systems of the West. For this reason also they went to school with social scientists who offered more appropriate theoretical tools and learned to use these tools.
The Emphasis on Setting
Just as the growing interest in non-Western political systems helped to engender a desire for going much further beyond common-sense propositions and common-sense testing procedures, so also it helped to produce—and much less obliquely—the present emphasis on the social setting of politics and on agencies mediating between the social and the political, such as political groups and agencies of political "socialization." Because political scientists found in such systems much less differentiation between the social and political—that is, few specialized organizations for political decision making or competition—they simply could not help seeing the extent to which the political is embedded in social relations in such systems, or suspecting that it might be so also in the more highly differentiated political system.
If they were indeed confronted by specialized political institutions and agencies, these, like the whole political system, were generally very much
in flux—in process of coming into being or being altered. And when political processes are unsettled—when patterns of politics are in the making rather than functionally autonomous of the conditions creating them—the nonpolitical is always particularly obtrusive and apparent, as it was to political observers in Europe in the great age of revolutions from 1789 to 1848 and as it was in the era of the rise of totalitarianism. It is worth noting in this connection that the halcyon days of formal-legalism in the study of politics fell precisely in that relatively calm and settled period between the great revolutions and the totalitarian era.
Here again, however, we must add other factors leading in a similar direction. We must remember, for example, that interest in the broader setting of politics, and in its more informal aspects, was already well advanced in the prewar period, above all in studies of American politics. In fact, many of the concepts, methods, and interests now being applied in comparative politics came out of the intensive study of American politics in the interwar and postwar periods—not least because of a gradual awareness on the part of specialists in comparative politics that the study of American politics was far outstripping their own specialty. The great role of the Social Science Research Council's Committee on Political Behavior in stimulating interest in applying comparatively some of the insights and techniques developed in American political studies—not least, its important role in helping to bring into being the SSRC Committee on Comparative Politics, which has done so much to help advance the field in recent years—should certainly be mentioned here.
In a way, also, interest in the setting of politics flowed almost naturally from the desire for scientific rigor in the field. It did so in two ways. First, in so far as the pursuit of rigor led to the more intensive study and emulation of sociology and cultural anthropology, it also led to the introduction into comparative politics of broad frameworks of analysis that, on the whole, regard all social phenomena as interrelated and certainly do not concentrate on any functionally distinctive aspect of society as if it were divorced from all other aspects of it.
Second, it is on the whole much easier to develop theories subject to rigorous testing by taking certain social and economic categories and relating them to politics (for example, such easily measurable categories as wealth and economic development, demographic data, occupational distributions—even value-orientation data) than by taking the often unmeasurable "pure" phenomena of politics as such—especially in societies where electoral data, the most easily measurable of all purely political data, are nonexistent, unreliable, or beside the point. As the opponents of rigorous quantitative methods in political science never weary of pointing out, the phenomena of politics, as traditionally conceived, simply do not lend themselves well to rigorous (that is, statistical, logical, mathematical) treatment—
but this may (and did) as easily induce political scientists to conceive such phenomena differently as persuade them to give up rigorous methods altogether.
The influence of sociology upon comparative politics can be seen most clearly of all in the postwar emphasis upon a particular constellation of facts in the setting of politics, the facts that Montesquieu referred to as "the general spirit, the morals of a nation" and that have now come to be called "political culture." This term, as now used, refers in general to politically relevant values (purposive desires), cognitions (conceptions of the nature of reality), and expressive symbols, from language to visual ceremony. It refers in particular to the "internalized" expectations in terms of which the political roles of individuals are defined and through which political institutions (in the sense of regularized behavior patterns) come into being.
The emphasis upon such "cultural" data is clearly a reflection of the influence upon political studies of the currently dominant sociological frame of reference, the action frame of reference, evolved chiefly by Parsons and Shils, upon the basis of Parsons's interpretation of Weber, Durkheim, and Pareto. At any rate, the "political culture" approach has been pioneered in comparative politics chiefly by two writers who freely admit their debt to Parsons and Shils, Gabriel A. Almond (who may rightly claim to have originated the concept in political science) and S. H. Beer. It is mainly through this emphasis on "cultural" data that the study of political "socialization" processes has come to be of great significance in the contemporary field, for if the values, cognitions, and symbols defining people's political conduct are regarded as the primary substratum of their political behavior, then explanations of political behavior must stress ipso facto the processes through which values, cognitions, and symbols are learned and "internalized," through which operative social norms regarding politics are implanted, political roles institutionalized, and political consensus created, either effectively or ineffectively. This, essentially, is what we mean by political socialization.
At the same time, the concern with political culture helps to explain the emphasis upon the study of political groups, although this emphasis is also a continuation of prewar tendencies and a result of basing middle-range theories about politics upon hard, preferably measurable, facts. The vogue of the group approach to politics reflects the preoccupation with political culture simply in that there are very few societies, even among the most politically centralized, that have homogeneous political cultures, rather than being composed of a variety of political subcultures; certainly there are very few such societies among the emerging or rapidly changing states of the non-Western areas.
Throughout the postwar period, but particularly, as I have pointed out, in very recent years, students of comparative politics have also made increasing use of the perspectives and categories of structural-functional analysis. What precisely does structural-functional analysis denote in this case? The term certainly cannot be left without explication, even when used in discussions of the fields in which it originated, for structural-functional analysis seems to include a very large, perhaps all-comprehending, variety of analytical questions and procedures. One of its principal exponents, M. J. Levy, has even claimed that, as used nowadays by most sociologists, it is merely another term for "talking prose"—that the structural-functional theorists do nothing more than state in a particular language what everybody already states in other languages. That may be so, although it makes one wonder why a structural-functional language should then be used at all; but in the postwar study of comparative politics the term does refer to certain specific, though still somewhat heterogeneous, procedures and problems.
It refers, first, to the very definitions of politics: to what we conceive to be a political system. One can define a political system in two ways: either as a particular set of concrete organizations, such as "governments" or "sovereign states," or as any social structures that perform whatever we conceive to be the function of politics—that is, any social structures that engage in political activities.
The latter may be considered a structural-functional definition, and this kind of definition of the political system has become increasingly common in the field. We tend no longer to think of political systems solely as sovereign states and their formal subdivisions but as any "collective decision-making structure," or as any set of structures for "authoritatively allocating social values," or as structures that perform the function of "maintaining the integration of society," or as structures that perform the functions of "the integration and adaptation of societies by means of the employment, or threat of employment, of more or less physical compulsion"—and in many other ways in similar vein. Some of these structural-functional definitions, like the first two examples cited, simply define a special activity, whatever its effect upon the larger social unit in which it occurs. Others, like the last two examples, define an activity that is presumed to be a requisite of the viability of a larger social unit. The latter definitions are more strictly characteristic of the style of structuralfunctional analysis than the former, for the problem of the requisites of the viability of social systems, of their stability and efficient operation, is perhaps the most basic substantive concern of those using the structural-functional approach.
Just as we can define a political system in structural-functional terms, so also we can devise analytical breakdowns of political systems—construct schemes of the elements that constitute them—in such terms, and this again in two ways. One way is simply to define the subsidiary activities that go into the larger activity of politics. In effect, this is what Almond does in breaking down political function into four input and three output categories. The other way is to break down the political function into those subactivities and structures performing the subactivities that are required for the effective performance of the political function, as a viable political system is required for the effective operation of the larger social system. This is what Apter does in breaking down political systems into five "structural requisites," and this latter procedure also is more strictly characteristic of structural-functional analysis than the former.
The purpose of structural-functional definitions and breakdowns of systems is, of course, to allow one to state and solve certain problems in which structural-functional theorists are particularly interested and that are based upon their preconceptions of the nature of social life. For all intents and purposes, the problems typical of structural-funcdonal analysis can all be subsumed under a single concern: the impact of any social structure or function upon the larger social unit of which it is a part (or, less frequently, upon any other structure or function to which it is related).
Social structures of functions can impinge upon social systems in a variety of ways. The structure or function under consideration may be a "prerequisite" for the larger (or related) pattern, in that it must exist before the larger pattern can exist. It may be a "requisite" for it, in that it is required if the larger pattern is to be maintained. It may be "eufunctional" if it helps the pattern to persist or "dysfunctional" if it helps to undermine it. Its operation may be "manifest" if it is intended and understood by the actors involved or "latent" if its operation is not intended and understood. Quesdons about such relations between structures or functions and larger social units are obviously not profoundly different from questions often raised in other terms. There is, for example, little difference between saying that something is a requisite or prerequisite for something else and saying that something is a necessary but not sufficient condition for (or cause of) another.
A distinctive preconception of societies does, however, underlie structural-functional analysis that gives to such questions an import, certain overtones, that they do not possess when raised in the language of causality or other theoretical languages. This preconception is that societies are mutually interconnected wholes, every aspect of which impinges upon every other and contributes something to the viability (or lack of viability) of the whole. Societies, upon this view, are equilibrated units that have a tendency toward inertia and change through the persistent or serious dis-
turbance of any part of their equilibrium. They are "systems" in the technical sense of the term: hence the concern with their functional interrelations.
It is this preconception of the nature of political systems, and of the way they fit into the larger social setting, that has gradually come to the forefront in postwar comparative politics. With it has come an emphatic interest in structural-functional problems, particularly problems regarding the requisites of any viable (stable, effective) political system or of the viability of certain kinds of political systems (for example, representative democracies) and problems regarding the functional consequences upon politics of other social patterns and upon nonpolitical patterns of political structures and activities.
What explains the present vogue in comparative politics of these pre-conceptions and problems? To some extent, of course, the very fact that social sciences in which structural-functional analysis is widely used have exerted an important influence upon comparative politics in the postwar period. But there are more deep-seated reasons.
Curiously enough, one of these deeper reasons is connected with the rapidly changing character of many contemporary non-Western systems—curiously enough, because structural-functional analysis is often accused of being a purely static approach to social science. It is so represented, however, for two bad reasons: one, the very concept of equilibrium is taken (erroneously) to imply immobility; the other, the major social scientists who have developed structural-functional analysis have in fact emphasized static over dynamic studies—most of them have worked in the anti-Marxist tradition, which assumes integration rather than conflict, and consequently inertia rather than constant motion, as the "normal" state of society. But this fact represents a coincidence rather than a logical relation. Indeed, structural-functional analysis, as depicted here, seems perhaps to lead logically (if it leads logically to anything at all) to theories about the coming into being, transformation, and breakdown of societies rather than to static analyses of fixed social states.
Rather than arguing that structural-functional analysis has a logical affinity to static analysis, one should argue that it is likely to produce a particular approach to social dynamics, different from that produced by theories like Marxism or evolutionary theory—an approach that always sees social change as a transition from one static, equilibrated state to another. Marxist and evolutionary theory are perhaps more inherently dynamic than structural-functional analysis in one sense: one cannot imagine, in terms of them, any fixed states, any equilibria other than dynamic equilibria, at all. For the structural-functional analyst, a fixed state is entirely possible and even necessary, although it does not rule out the analysis of changes of state.
At the same time, however, theories like Marxism and evolutionary theory make it difficult, if not impossible, to think of rapid, cataclysmic changes in society; note, for example, the great difficulties created for Marxist theorists by the doctrine of "permanent revolution." Such theories lend themselves chiefly to a conception of orderly, constant flow in social phenomena: one thing leads, never very rapidly or abruptly, to the next, and the whole flow is conceived, but only for heuristic purposes, as a series of "stages" through which societies must always pass in their life-histories. But structural-functional analysis makes it perfectly possible to think in terms of very broad and rapid changes, of one society skipping the stages of growth passed through by another or embarking very rapidly upon a new course of growth, through some large-scale change, however brought about, in one of the functional elements of society. It makes it possible to think of rapid transformations, revolutionary breaks, innovations, and metamorphoses, while other, supposedly more dynamic, approaches make it possible only to think of flows and phases.
Precisely these two characteristics of structural-functional analysis—that it leads to a conception of social change as a process from static states to other static states and offers the possibility of explaining very broad and rapid changes—make it attractive for those concerned with contemporary non-Western political systems. With what kinds of social dynamics do these systems confront us? Certainly not with orderly and constant flow. In such systems one always seems to begin with very static traditional societies, hardly changed in essential respects for centuries—societies exhibiting "fixed states" in any reasonable meaning of the term. And from such beginnings one always seems to proceed to the swiftest and most large-scale changes: from tribalism to the nation-state, from agrarian subsistence economics to modern industrialization, from feudalism to socialism; hurricanes of change strike the societies and swiftly transform them in ways that elsewhere took generations, even centuries.
Perhaps we shall find that this is not really an accurate depiction of what is happening in the "developing" areas. Perhaps the large-scale changes that appear to be occurring in them are merely surface phenomena under which more gradual processes of social flow proceed. But rapid metamorphosis from relatively unchanging states does seem , to naked observation, to be the essence of their contemporary history. For that sort of dynamism a theoretical approach at once static and dynamic is obviously the most appropriate.
Thus, the very study of rapidly changing political and social systems creates a predisposition toward structural-functional analysis, not despite but precisely because of its affinity for static theory. And thus also the present emphasis on social setting and on theoretical rigor in comparative politics has induced an increasing use of structural-functional analysis and
directs the analytical attention, more perhaps than any other approach, to the whole web of relationships of which politics is a part: the social phenomena on which politics impinges and those phenomena that impinge upon politics. Structural-functional analysis is the preeminent approach to the study of social interconnections. The emphasis on rigor has induced structural-functional analysis because it at least offers the possibility of something more than crude, unsystematic description and induction, without committing the theorist to a premature, perhaps vain, search for social "laws" or for "grand theories" in the historicist manner.
Nor does it commit him to a quest for sufficient "causes" in a realm where multicausality and multivariation operate to such an extent that necessary—or favorable—but insufficient conditions of phenomena are perhaps all we can ever hope to find. Structural-functional analysis, from this standpoint, is the preeminent approach to what I have called middle-range theories—theories that go beyond mere description and commonsense generalizations, that are based upon some explicit theoretical frame of reference, that permit some rigor in formulating and testing hypotheses, and that yet do not present ironclad laws or total interpretations of the meaning of social life. Talcott Parsons, whose name is perhaps the most famous of those associated with structural-functional analysis in the contemporary social sciences, defends the approach precisely on this basis:
It may be taken for granted that all scientific theory is concerned with the analysis of elements of uniformity in empirical processes. The essential question is how far the state of theory is developed to the point of permitting deductive transitions from one aspect or state of a system to another, so that it is possible to say that if the facts in A sector are W and X, those in B sector must be Y and Z. In some parts of physics and chemistry it is possible to extend the empirical coverage of such a deductive system quite widely. But in the sciences of action dynamic knowledge of this character is highly fragmentary, though by no means absent.
In this situation there is danger of losing all the advantages of systematic theory. But it is possible to retain some of them and at the same time provide a framework for the orderly growth of dynamic knowledge. It is as such a second best type of theory that the structural-functional level of theoretical systematization is conceived and employed.
In the first place completely raw empiricism is overcome by describing phenomena as parts of or processes within systematically conceived empirical systems. The set of descriptive categories employed is neither ad hoc nor sheer common sense but is a carefully and critically worked out system of concepts which are capable of application to all relevant parts or aspects of a concrete system in a coherent way. This makes comparability and transition from one part and/or state of the system to another, and from system to system, possible.
Comparative Politics Today:
Because the postwar tendencies in comparative politics are illustrated and analyzed fully in many other essays and books, I conclude this essay without further describing and evaluating these tendencies. And yet, in a sense, we cannot really "conclude" it, for in the contemporary development of the field nothing has really been concluded. It would be nice if we could say that the study of comparative politics, after its many vagaries and tergiversations, had reached at last a new consensus upon concepts, methods, and analytical approaches capable of yielding a broad and precise science of political institutions. It would be nicer still if we could point to the actual existence of such a science. But there is a great distance still to go before this point is reached, and we are unlikely to reach it without further serious modifications of the field. Given its present state, it is quite inevitable that we should end on a note of ambiguity and suspended judgment, primarily for three reasons:
1. The field is today characterized by nothing so much as variety, eclecticism, and disagreement.
2. Disagreement and divergences are particularly great in regard to absolutely basic preconceptions and orientations (in terms of which one recognizes "scientifically" valid findings).
3. The tasks contemporary practitioners of comparative politics (especially the more radical ones) have set for themselves are so many and so difficult that they are unlikely to achieve satisfying results without further important changes in their approaches.
It should not be supposed that in describing the four main tendencies in present-day comparative politics—structural-functional analysis, the quest for scientific rigor, concern with non-Western systems, and concern with the broader setting of politics—we have in fact described the whole field of comparative politics in the postwar period. Not at all; we have only described what is new and progressive in a field that is in fact to a large extent old-fashioned and conservative. It is important to realize that the stages in the development of comparative politics described here did not unfold in an orderly and episodic manner. In the manner of all things historical, these stages overlapped one another, each leaving within the contemporary discipline a certain residue, a particular style of analysis incongruent with other styles in the field.
In the contemporary field of comparative politics, we can in fact find, not two, but three quite distinctive styles; indeed we can sometimes find them in the writings of a single individual. One is the predominantly formal-legal, morphological, essentially descriptive, and configurative style
of the immediate post-historicist period. In any of the established texts in the field (Ranney, Hertz and Carter, Cole, Zink, Neumann) that is essentially what will be found. If any approach is today dominant in the field, it is still this one. The second is middle-range theory based upon commonsense concepts and methods—crude empiricism, unguided by any rigorous procedures or explicit analytical frames of reference. That is what one finds in most of the deliberately comparative and problem-solving works of the present day, like Duverger's Political Parties , Rossiter's Constitutional Dictatorship , or Friedrich and Brzezinski's Totalitarian Dictatorship and Autocracy . The third is the broad and self-consciously systematic style distinctive to the postwar period.
The Concern with Fundamentals
This coexistence in the field of three quite different styles accounts, as pointed out at the beginning, for the present concern in comparative politics with a multitude of pretheoretical and metatheoretical problems. These problems were not raised in earlier times—or not raised with such intensity and by so many people—simply because no one saw anything problematic in them. Political scientists knew the proper subject matter of their science: the state. They knew what it was most essential to deal with in studying this subject matter: public law. They knew how to classify political systems, how to divide them into parts, the nature of the basic units to be used in analysis, and what sort of a finding was a satisfactory and trustworthy finding. Today, precisely because of the variety of approaches in the field, we are not at all sure about these and other basic matters, and so we spend almost as much time and effort in thinking about the field of comparative politics as we spend in the comparative study of politics.
Nowhere are this self-concern and self-criticism more apparent, and nowhere are the depth and intensity of intradisciplinary disagreement more clearly revealed, than in the two general works about the study of comparative politics so far produced in the postwar era, Gunnar Heckscher's The Study of Comparative Government and Politics and Roy C. Macridis's The Study of Comparative Government . Macridis and Heckscher—the first speaking for what is essentially "modern" in the field, the second for what is essentially "traditional"—disagree not so much about whether comparative politics is to be a "science," as may appear to be the case in the readings, but—and this is much more serious—about what a political science, properly speaking, ought to be; and that is the deepest and most frustrating disagreement that can arise in any discipline.
Macridis and Heckscher can speak for themselves; there is no need here to reproduce their arguments. In any case, all the essential issues their arguments raise, explicitly or implicitly, are sketched at the beginning of
the essay. But it is essential to note one fact about their disagreements: not only do such arguments impede the development of the field by distracting its practitioners from substantive tasks, they also impede the development of the field because, while such issues are unsettled, one cannot even determine when a field has been developed. All science involves building upon tacit assumptions and silent premises; and this means that the moment such assumptions and premises are made explicit by being argued no science can be said to exist. In such cases one can only have methodology and metaphysics, only prolegomena to study, research designs, conceptual proposals, and the like—preliminaries that now in fact afflict comparative politics in astounding volume. But one cannot have that heaping up of tested theoretical findings ("cumulative research," in the wishful jargon of modern social science) that we generally think of as science.
Would it then be better not to raise questions regarding basic preconceptions? In the final analysis, it is unnecessary to answer this question one way or the other because we simply have no choice in the matter. Pretheoretical and metatheoretical concerns become significant in fields of inquiry under certain conditions; they arise because it is necessary that they should arise, and once they have arisen they cannot be wished away. One can operate with agreed preconceptions or one can disagree about preconceptions, but one cannot operate without any preconceptions. Therefore, when preconceptions are being questioned, one can only let the questioning take its course until some general understanding is reached, or, better, one can try, by procedural argument or substantive research, to influence others to accept one's own preferred preconceptions and thus contribute to the outcome of the questioning. In one way or the other—by argument or example—some dominant opinion will sooner or later become established, but in the meantime one can only leave the analysis of the field open-ended or indulge in prophecy.
The Need for Simplification
What kind of a comparative politics, then, is likely to emerge out of the present disorder in the field? Whatever the final product, one thing seems certain. Even if we confine ourselves to the postwar developments in comparative politics, it seems improbable that a coherent discipline could be built upon concerns so various and complicated as are the present concerns of comparative politics. The most obvious need in the field at present is simplification—and simplification on a rather grand scale—for human intelligence and scientific method can scarcely cope with the large numbers of variables, the heaps of concepts, and the mountains of data that seem at present to be required, and indeed to exist, in the field.
Consider what the contemporary practitioner of comparative politics is supposed to know in order to be au courant with all the mainstreams of
his field. He is supposed to be at once a political scientist, a logician, and a methodologist. He is supposed to know a good deal of sociological, anthropological, social-psychological, and general systems theory. His knowledge must (ideally) extend not merely to a specific country, nor even a particular region or type of government, but over the whole universe of political phenomena. He must not only know contemporary politics, but be something of a universal historian as well. And there is even a suggestion that his familiarity with political behavior should extend not only to nation-states but to every social relationship in which authority is exercised, or influence wielded, or the allocation of social values carried out. Certainly, the study of public law, in which scholars of the past made rich and busy careers, has become a mere fraction of all the things he is supposed to study. He must also learn all about informal politics, relate politics to its setting (ecological, social, economic), and be able to deal adequately with attitudes and motivations, with culture and socialization processes. These, obviously, are absurd demands to make even of the highest intelligence, the most retentive memory, the busiest industry, the most versatile manipulator of the skills of social science. They are demands that could conceivably be met by a sensible division of labor in the field, but such a division of labor presupposes some agreement on what is being divided, an accord (which we do not possess) on the desirable nature and direction of inquiry. The fact that at present it is very difficult, perhaps impossible, for any specialist in the field to know just how his work fits into any broader picture makes it necessary for everyone to work essentially according to his own lights, in terms of what he conceives to be the ultimate destiny of the field.
Dissent on fundamentals is thus reflected in lack of focus and definition in regard to "circumstantials" in the field, and in a way this is to the good. In the past, comparative politics had clearly defined boundaries only at the cost of too narrow and perhaps too inconsequential a concentration on subject matter, formal-legal structure. Any workable approach to the field, particularly at a time when we are concerned largely with relatively undifferentiated political systems, was bound to depart from such a rigidly constricting focus. But what have we to put into its place? If the answer is that we must deal with everything instead, that nothing can be omitted, then we are lost just as surely—indeed, more surely.
The basic need of the field at present, therefore, is focus and simplification. While we can detect searches for simplified approaches in the contemporary literature about the field, these are so far only searches. What is more, the usual tack taken in analytical writings on comparative politics is to throw into proposed schemes everything considered in any sense relevant to political study. Thus, students of comparative politics today confront a profoundly serious problem, even a dilemma. They must
not focus on formal-legal studies only; we know that from long and dis-appointing experience. Yet they must not deal with everything else—and formal-legal data to boot. They must somehow limit inquiry. Yet the most obvious way to limit political inquiry is to focus on the most obviously political thing there is, as political scientists did in the formative years of their field—namely, formal-legal structure. What, then, are we to concentrate upon? We do not know as yet; that is to say, we are not agreed upon a solution.
This essay, as stated, was written at a still early stage of the "revolution" in comparative politics, but a good deal before the Terror of the Grand Theories discussed in chapter 1. Readers who wish to be brought more fully up to date on that subject might look at Oran R. Young, Systems of Political Science (Englewood Cliffs, N.J.: Prentice-Hall, 1968), and James A. Bill and Robert L. Hargrave, Jr., Comparative Politics: The Quest for Theory (Columbus, Ohio: Merrill, 1973).
As I wrote in chapter 1, it seems to me that we have now settled down to a fundamental choice between perspectives to follow in macropolitical inquiry: between culturalist and rationalist points of departure. It would take far too much space here to explain the reasons for this and the exact nature of the perspectives. My greatest regret in the academic work I have done remains, however, the fact that the envisaged "test" of the more fruitful path to follow, also discussed in chapter 1, was never done. Had it been, we might not now be afflicted, as we are, by attempts to join what, at the basic theoretical level, should be dissociated—attempts that have had results something very like the mess Tycho Brahe, a fine astronomical data-gatherer but a timid and messy theorist, made of his attempt to join Ptolemaic to Copernican astronomy.
In general, I have taken the culturalist tack (for reasons), but I should mention that I do not regard culture as independent of objective structure, though I also do not regard it as merely superstructural. Culture has to come from something, and that, no doubt, is something objectively structural. And it must adapt to structural objective changes (see chapter 7, below). It is, in Paretian terms, a derivative from "residues." But that view does not provide an easy answer to the question of what to emphasize in our theorizing. In chapter 7, I try to make the point that the culturalist tack can be made more fruitful than theory based on "deeper" structural factors because of cultural "inertia." Still, no conclusive test of the position exists.
Simplification has also occurred in another, more encouraging, way: a gradual shift toward macropolitical theories of the middle range (e.g., in
Lipset; in the literature on contemporary peasant wars and, more generally, collective political violence; in Inglehart, et al.). From the weight of such work, if not more directly, a result about the value of culturalist or rationalist perspectives might gradually emerge.
Case Study and Theory in Political Science
Author's Note : One aim of the attempt to overhaul comparative politics was to make it more theoretical. Before the 1950s comparative politics consisted almost entirely of studies of particular cases (polities or aspects of them); many of these were highly learned, but not theoretical. Even the major texts in the field were collections of case studies: usually Britain first; then France and Germany; in some cases, also, a smattering of Italy and Sweden; and, for contrast, the Soviet Union. This was the genre in which I was formed, and thus I have always found intensive case study congenial.
One can readily understand why, to achieve "theory," highly extensive large-n studies using aggregate statistics (that is, studies in the manner of Gurr, Hibbs, or the Cross-Polity Survey ) would be used, despite sacrificing intensive knowledge of the cases covered. I have not been much impressed by their results. Usually they have been complex, weak, and much-qualified by ill-fitting variables. And, although alienated from the configurative case studies prevalent in the field before, I was impressed by the import of single or limited observations, critical for theory, in the "hard" sciences or, in sociology, by the theoretical case-method as used by Michels, Malinowski, or Whyte.
This led to reflections on "extensive" versus "intensive" studies for purposes of building theory; to reflections on what the process of theory building is about: and about the roles that case studies, which come in a number of varieties, might play in the process.
The essay that resulted has been widely used and cited, and I have received much positive feedback about it. That would be gratifying, if it were not for an irony. The essay has widely been taken to vindicate case studies of the old, accustomed mode, when even a minimally careful reading should make clear that I attack that mode and make the case only for certain, rather rare, kinds of case study, especially for a kind that hardly exists at all as yet: "crucial case-study."
I have by now come around to a somewhat modified view of that argued here: that "matched comparisons" of cases carefully selected for theory—a kind of "strong inference" procedure—are even more telling for theory. Alexander George has argued for that method cogently in the abstract; Ronald Dore's inspired comparison of virtually identical electrical industries in Britain and Japan is a good case in point. (Dore keeps the fact that his superb, apparently idiographic, descriptions have a theoretical purpose well-concealed by stating it only in his preface, but the purpose both exists and is well-served by the case studies.) Matched comparisons of properly selected cases serve especially well the experimental methods of both agreement and difference. But single case study also, as I argue here, can have powerful, even conclusive, theoretical results.
The extent to which certain kinds of study are carried out in the field of political science seems to be a poor indicator of their perceived utility for building theories.
The type of study most frequently made in the field is the intensive study of individual cases. Case studies run the gamut from the most microscosmic to the most macrocosmic levels of political phenomena. On the microlevel, we have many studies of conspicuous political personalities (political leaders such as Lincoln, Stalin, Gandhi), and of particular leadership positions and small leadership groups (the American presidency, the British cabinet, the prime minister in British government, the operational code of the Soviet leadership, and so on). At the level of political groupings, the literature of the field teems with studies of particular pressure groups, political parties, party systems, revolutionary and protest movements, and political "elites," on both the national and local levels. More abundant still are studies of individual polities in all corners of the world and at many stages of history and development. Many of these treat polities as overall macrocosms; many deal with their subsidiary organizations (administrative apparatuses, legislatures, judiciaries, systems of local government), or with their programs and policies, or their particular electoral, legislative, executive, or judicial decision processes. Beyond that
level, one finds a similar profusion of case studies of transnational phenomena: specific processes of and organizations for transnational integration, particular "systems" of international politics, particular crises in international relations, and the like.
The abundance of examples is such that it seems pointless to provide bibliography. Precisely because the genre is so common, political scientists can easily construct a representative list of examples for themselves. If not, a brief visit to the political science section of the library will serve. It is not much of an exaggeration to say that the case study literature in the field comes close to being coterminous with its literature as such.
This plenitude of case studies is not associated with any perception that they are a particularly useful means for arriving at a theoretical understanding of the subject matter of political study. Most political scientists who do case studies appear to have no views at all, or only ambiguous views, on the role that case studies can play in theory building. For them, the case study is literally a genre, not a method. If they do express views on the subject, they usually disparage the genre as a method—for instance, by holding that case studies can at most stir up becalmed theoretical imaginations. One might explain this apparent paradox by holding that political scientists do not place a high value on theory building. No doubt this is true for many of them. But it is much less true nowadays than it used to be, and the volume, or proportion, of case studies in the field has not notably decreased.
It is in order, therefore, to raise three questions: What general role can the case study play in the development of theories concerning political phenomena? How useful is the case method at various stages of the theory-building process? And how is case study best conducted for purposes of devising theories?
I intend here to propose answers to these questions that run sharply counter to the now conventional wisdom in political science, especially in the division of the field we call "comparative politics." The quotation marks no doubt give the dénouement away. Readers are supposed to conclude that "comparative" studies are by no means necessary (and often not even wise strategy to follow) in pursuing the objective for which they are usually conducted: the discovery of valid generalizations about political phenomena. Indeed, I hold that the conventional wisdom has things virtually upside down. Case studies, I will argue, are valuable at all stages of the theory-building process, but most valuable at that stage of theory building where least value is generally attached to them: the stage at which candidate theories are "tested." Moreover, the argument for case studies as a means for building theories seems strongest in regard to precisely those phenomena with which the subfield of "comparative" politics is most associated: macropolitical phenomena, that is, units of political study of con-
siderable magnitude or complexity, such as nation-states and subjects virtually coterminous with them (party systems or political cultures). More precisely, the abstract brief in favor of the case study as a means of building theories seems to me to hold regardless of level of inquiry, but at the macrocosmic level practical research considerations greatly reinforce that brief.
Extensive argument is necessary to make these points. But while the fun is in arguing against conventional views (especially if, as in this case, they seem truistic), arguments do not make sense, and counterarguments are unlikely to be apropos, unless major terms are first defined. In political science the safe bet usually is that even widely used concepts are not widely understood in a uniform, unambiguous manner. Readers must therefore bear with me for a while as I clarify some basic terminology.
Case Study and Comparative Study
1. The conception of case study commonly held in the social sciences is derived from, and closely similar to, that of clinical studies in medicine and psychology. Such studies are usually contrasted dichotomously (as if they were antitheses) to experimental ones, which furnish the prevalent conception of comparative study. Contrasts generally drawn between the two types of study cover virtually all aspects of inquiry: range of research, methods and techniques, manner of reporting findings, and research objectives.
As to range of research : Experimental studies are held to be conducted with large numbers of cases, constituting samples of populations, while clinical studies deal with single individuals, or at most small numbers of them not statistically representative of a populous set. Experimental studies thus are sometimes said to be "extensive" and clinical ones "intensive." These adjectives do not refer to numbers of individuals alone, but also involve the number of variables taken into account. In experimental studies that number is deliberately and severely limited, and preselected, for the purpose of discovering relationships between traits abstracted from individual wholes. Clinical study, to the contrary, tries to capture the whole individual—"tries to" because it is, of course, conceded that doing so is only an approachable, not an attainable, end.
As for methods and techniques : The typical experimental study, first of all, starts with, and adheres to, a tightly constructed research design, whereas the typical clinical study is much more open-ended and flexible at all stages. The clinical researcher may have (probably must have) in mind some notions of where to begin inquiry, a sort of checklist of points to look into during its course, or perhaps even a preliminary model of the
individual being studied; but actual study proceeds more by feel and improvisation than by plan. Second, the techniques most commonly associated with such inquiry in the case of "collective individuals" (i.e., social units) are the loose ones of participant observation (simply observing the unit from within, as if a member of it) and Verstehen (i.e., empathy: understanding the meaning of actions and interactions from the members' own points of view). The typical techniques of experimental inquiry, per contra, are those rigorous and routinized procedures of data processing and data analysis concocted to ensure high degrees of "nonsubjective" reliability and validity—the techniques of the statistics texts and research methods primers.
Reports of the findings of clinical study are generally characterized as narrative and descriptive: they provide case histories and detailed portraiture. Such reporting might therefore also be termed synthetic, while that of experimental studies is analytic, since it does not present depictions of "whole" individuals but rather of relations among components, or elements, of them. Beyond description, clinical studies present "interpretation"; beyond raw data, experimental ones present rigorously evaluated "findings."
It follows that the objectives of the two types of study also differ. That of experimental study is generalized knowledge: theoretical propositions. These may certainly apply to individuals but never exhaust the knowledge it is possible to have of them. Being general they necessarily miss what is particular and unique, which may or may not be a lot. The objective of clinical study, however, is precisely to capture the particular and unique, for if anything about an individual whole is such, so must be the whole per se. It is conceded that in describing an individual configuration we may get hunches about the generalizability of relations not yet experimentally studied, but only hunches, and even these only by serendipity. Clinical study is therefore associated more with action objectives than those of pure knowledge. In the case of single individuals, it aims at diagnosis, treatment, and adjustment; in that of collective individuals, at policy. This association of clinical study with adjustive action is based on the assumption that therapy and policy can hardly proceed without something approximating full knowledge of its subjects, however much general propositions may help in proceeding from clinical knowledge of a case to the appropriate manipulation of a subject. Clinical and experimental objectives draw near, asymptotically, as "pure" knowledge becomes "applied" (i.e., in engineering models), but application is merely a possible extension of experimental knowledge while generally being an intrinsic objective of clinical research.
2. Anyone familiar with the modern history of comparative politics (see chapter 3) will realize that its development since the early 1950s involves
a transition, or shift, from the clinical to the experimental mode of study. Macridis and Brown criticized the old "comparative" politics for being, among other things, noncomparative (concerned mainly with single cases) and essentially descriptive and monographic (not substantially concerned with theory and, at least in aim, wholistic); and they imply that it had a dominant therapeutic objective: to find ways of diagnosing the ills of unstable democracies and making them more stable. Such studies, conforming to the model of clinical research, still abound, but the proportion of those conducted in accordance with that of experimental study has steadily grown, as has the proportion of monographic studies seeking, somehow, to tie into the other variety.
However, while the distinction between clinical and experimental studies is useful for contrasting the old and new comparative politics, it does not serve nearly so well in distinguishing the case study from other modes of research. At best, it can provide an initial inkling (but only an inkling) of the differences among them. Certainly this chapter, which argues in favor of case studies, is not by any stretch of the imagination to be taken as a defense of the kind of work Macridis assails and the field has downgraded. The distinction offers a useful denotative definition of case studies in the social sciences (that is, what people usually mean by the term) but a far from useful connotative and generic one (how the term ought to be used if it is not to raise serious difficulties of meaning and classification and not to define merely one of numerous types of case study).
3. The essential objections to equating case study with clinical and comparative study with experimental inquiry all revolve on one basic point: nothing compels the clustering (hence, dichotomization) of the various characteristics used to distinguish clinical and experimental studies. Although that clustering in fact occurs very frequently in the social sciences, it does so chiefly because of dubious beliefs and assumptions. At most, the characteristics have a certain practical affinity; for example, the fewer the cases studied, the more intensive study may be, other things being equal. But no logical compulsion is at work, and the practical considerations often are not weighty.
We may certainly begin with the notion that case studies, like clinical studies, concern "individuals," personal or collective (and, for tidiness of conceptualization, assume that only one individual is involved). From this, however, it does not follow that case studies must be intensive in the clinician's sense: nothing like "wholistic" study may be attempted, and the researcher may certainly aim at finding relationships between preselected variables—unless he assumes, a priori, that this is foolish. The research may be tightly designed and may put to use all sorts of sophisticated research techniques. (An excellent example is Osgood and Luria's "blind
analysis," using the semantic differential, of a case of multiple personality.) Its results need not be cast in narrative form, and its objective can certainly be the development of general propositions rather than portraiture of the particular and unique; nor need case studies be concerned with problems of therapeutic action when they go beyond narration, depiction, and subjective interpretation.
The same applies, mutatis mutandis , to studies of numerous cases, even leaving aside the fact that the cases need not be, and often are not, very numerous and certainly not a "sample." This leaves a large residual no-man's-land, even from the standpoint of numbers, between the clinical and experimental. Studies of numerous cases can also take into account numerous variables. Modern data-processing capabilities have, in fact, encouraged a kind of omnibus approach even to cross-national research, à la Banks and Textor, in which anything one can think of is cross-tabulated and correlated with just about everything else. Even before these capabilities existed some comparative works treated the various aspects of complex whole, like polities, as comprehensively as any clinical investigation. Studies of numerous cases also leave room for improvisation in research. They are not always tightly designed, do not always use rigorous research techniques, are sometimes reported in the descriptive vein, often have few or no theoretical pretensions, and also often seek direct answers to policy and other action questions, not answers that amount to the deduction of applied from pure theory.
These points of overlap and ambivalence in the distinction between the clinical and experimental have led to a concerted attack on the dichotomy in psychology itself. One typical attack argues that the dichotomy originates in an archaic and absurd Methodenstreit between "mechanistic" and "romantic" views of human nature. Another argues that experimental modes of study can also be used profitably in research into single cases; this is the theme of a notable book of essays, N = 1 This work implies the most important definitional point of all: if case study is defined as clinical study in the traditional sense, then we not only construct a messy generic (not necessarily classificatory) concept, but also foreclose the possibility of useful argument about case study as a tool in theory building. The definition answers the question: case study and theory are at polar opposites, linked only by the fortuitous operation of serendipity.
4. This attack on the conventional idea of case study serves a constructive as well as destructive purpose. It provides ammunition for later arguments against highly restrictive views concerning the role of case study in theory building and also points the way toward a better, and simpler, definition of what case studies are.
An unambiguous definition of case study should proceed from the one
sure point that has been established: case study is the study of individuals. That is about as simple as one can get—but, because of one major problem, it is too simple. The problem is that one person's single individual may be another's numerous cases. Take an example: In order to help break down the dichotomy between the clinical and experimental, Davidson and Costello reprint a study by Chassan on the evaluation of drug effects during psychotherapy. Chassan argues for the greater power of single-case study over the usual "treatment group" versus "control group" design—in this case, for determining the relative effects of tranquilizers and placebos. Readers can catch the flavor of his argument through two of his many italicized passages:
The intensive statistical study of a single case can provide more meaningful and statistically significant information than, say, only end-point observations extended over a relatively large number of patients.
The argument cited against generalization to other patients, from the result of a single case intensively studied, can actually be applied in a more realistic and devastating manner against the value of inferences . . . drawn from studies in which extensive rather than intensive degrees of freedom are used.
And so on, in the same vein. The whole paper is an object lesson to those who seek theoretical safety only in numbers. But there is a catch. Chassan studied only one patient, but used a large number of treatments by drug and placebo: "frequent observations over periods of sufficiently long duration." The individuals here are surely not the patients, although they may be for other purposes; it is each treatment, the effects of which are being compared. It is easy enough to see the advantages of administering different treatments to the same person over a long period (hence, safety in small numbers of a sort), as against using one patient per observation (although it is to Chassan's credit that he pointed them out in contrast to the more usual procedure). But n , despite the title of the book, in this case is not one.
If this problem arises with persons, it arises still more emphatically with "collective individuals." A study of six general elections in Britain may be, but need not be, an n = 1 study. It might also be an n = 6 study. It can also be an n = 120,000,000 study. It depends on whether the subject of study is electoral systems, elections, or voters.
What follows from this is that ambiguity about what constitutes an "individual" (hence "case") can only be dispelled by not looking at concrete entities but at the measures made of them. On this basis, a "case" can be defined technically as a phenomenon for which we report and interpret only a single measure on any pertinent variable . This gets us out of answering insoluble metaphysical questions that arise because any concrete entity can
be decomposed, at least potentially, into numerous entities (not excluding "persons": they differ almost from moment to moment, from treatment to treatment, and consist of highly numerous cells, which consist of highly numerous particles, and so on). It also raises starkly the critical problem of this essay: what useful role can single descriptive measures (not measures of central tendency, association, correlation, variance or covariance, all of which presuppose numerous measures of each variable) play in the construction of theory?
If case study can be thus defined, comparative study is simply the study of numerous cases along the same lines, with a view to reporting and interpreting numerous measures on the same variables of different "individuals ." The individuals, needless now to say, can be persons or collectivities, or the same person or collectivity at different points in time, in different contexts, or under different treatments. And the term "measure" should of course here be treated with latitude: it might be a highly precise quantity (34.67 percent of all Britons always vote Labour) or a rather imprecise observation (the British Labour party is now a chronic minority party).
Theory and Theory Building
We will be concerned with the utility of case studies in the development of theories in macropolitics—their utility both in themselves and, to an extent, relative to comparative (n = many) studies. While nearly everyone in the field at the present time agrees that the development of good theories is the quintessential end of political inquiry, conceptions of theory, and of the processes by which it may be developed, vary extremely in our field. This makes unavoidable a definitional exercise on theory and a review of the normal steps in theory building.
1. Two polar positions on what constitutes theory in our field can be identified. While positions range between them, they have recently been rather polarized, more often on, or very near, the extremes than between them.
On one extreme (the "hard" line on theory) is the view that theory consists solely of statements like those characteristic of contemporary theoretical physics (or, better, considered to be so by influential philosophers of science). A good summary of this view, tailored to the field of political science, is presented in Holt and Richardson's discussion of the nature of "paradigms," but even better sources are the writings of scientist-philosophers such as Kemeny, Popper, and Hempel.
Theories in this sense have four crucial traits: (1) The concepts used in them are defined very precisely, usually by stating definitions in terms of empirical referents, and are less intended to describe phenomena fully than to abstract from them characteristics useful for formulating general
propositions about them. (2) The concepts are used in deductively connected sets of propositions that are either axioms (assumptions) or theorems deducted from them. (3) The object of the propositions is both logical consistency and "empirical import," that is, correspondence to observations of phenomena. And (4) empirical import is determined by tests themselves deduced from the propositions, and these are designed to make it highly probable that the propositions will flunk the tests because confidence in propositions is proportionate to the stiffness of the tests they manage to survive. In our own field, theories of this type are sometimes called "formal theories," mainly because of the large role of formal deduction in their elaboration; and economics is generally taken as the nearest social science model for them, not only in general form but also in regard to substantive "rationality" axioms.
On the other pole (the "soft" line), theory is simply regarded as any mental construct that orders phenomena or inquiry into them. This qualifies as theory many quite diverse constructs, including classificatory schemes that assign individual cases to more or less general classes; "analytic" schemes that decompose complex phenomena into their component elements; frameworks and checklists for conducting inquiry (e.g., the "systems" approach to macropolitics, or "decision-making" checklists for the study of foreign policy formation); any empirical patterns found in properly processed data, or anything considered to underlie such patterns (e.g., learning processes or class position).
2. If the term theory were always prefaced by an appropriate adjective, wrangling about these, and less extreme, positions could be avoided. But this would not take us off the hook of having to specify how "good theory" as an objective of inquiry in our field should be conceived. The best position on this issue, it seems to me, is neither hard nor soft but does come closer to the hard than the soft extreme. It rests on two major premises.
The first is that it makes no sense whatever to call any mental construct a theory. Such constructs differ vastly in nature and purpose, so that they can hardly be considered to be of the same species. With some of them, not much more can be done than to assign names to phenomena or to order one's filing cabinets. And it can be demonstrated that, strictly speaking, the soft position compels one to regard as theory any statement whatever in conventional or technical discourse.
Second, it makes little more sense to restrict the term to constructs like those of theoretical physics, or those abstracted from that field by philosophers of science. While such constructs have proved extremely powerful in certain senses, one may doubt that they alone possess power (even in these senses). If constructs like them are not attainable in a field such as our own at its present stage of development (which is at least an open
question, since constructs like them have in fact not been attained), commitment to theory in such a narrow sense may induce one to forego theoretical inquiry altogether. Most important, theories in the "hard" sense are a particular form developed, over considerable time, to realize the purposes—the motivating goals, animus, telos—of an activity; and while they do this very well, it does not follow that they are absolutely required for realizing these purposes.
Consequently, even if the constructs of theoretical physics are taken as a model, it seems unwise to restrict the notion of theory entirely to such constructs. It seems better to label as theory any constructs designed to realize the same ends and formulated with the same animus as those that characterize the fields in which hard theory has been developed—leaving open, anyway provisionally, the forms such constructs may take consistent with reasonable achievement of the ends. On this basis, theory is characterized by a telos, or animus, of inquiry rather than by the particular form of statements. The only requirement (which, however, is far from soft) is that the forms of theoretical statements must be conducive to the goals of theoretical activity.
Such a teleological conception of theory requires that the goals be made explicit. They can be characterized under the following headings: regularity , reliability , validity , foreknowledge , and parsimony .
a) The quintessential end of theorizing is to arrive at statements of regularity about the structure, behavior, and interaction of phenomena. "Regularity" here means, literally, "rulefulness": the discovery of rules that phenomena observe in the concrete world, as players do in games or logicians in logic. Such regularity can exist in many senses. The rules may describe simple relations among variables without specification of their exact nature; or they may describe sequences like causal paths or historical and genetic patterns; or they may be statements of the conditions of persistence or efficacy of structures. The rules may also be more or less "ruleful." They may be "probability statements" that permit no inferences about individual cases but only more or less confident ones about sets of them, or they may be "laws" in which probability is at unity. Both of these can further vary in "rulefulness" according, for example, to the number and significance of variables held constant or ignored, or whether they state necessary, sufficient, or both necessary and sufficient conditions if causal sequences or conditions of viability or performance are specified.
b) The animus of theoretical inquiry requires not merely empirical rules, but also that the rules be as reliable and valid as possible. Reliability exists to the extent that inquirers, proceeding in the same manner, arrive at the same results; validity to the extent that a presumed regularity has been subjected, unsuccessfully, to tough appropriate attempts at falsification. Not all presumed or discovered regularities are subject to tests of reliability
and validity, and certainly not to equally tough ones: for example, a statistical inference about a set of cases observed by a researcher that cannot be restudied at all or in much the same way can never be reliable and is unlikely to be valid (i.e., successfully tested). Hence, just as concepts become theoretical by being used in regularity statements, so such statements become theoretical if they are subject to tough reliability and validity tests.
c) Foreknowledge is the correct anticipation, by sound reasoning, of unknowns (whether the unknown has or has not yet occurred). Theory not only does, but needs to, aim at that objective, because the toughest, hence most conclusive, test of any rule is the correct deduction from it of unobserved experience. In most cases, theories are shaped to fit observations already made, and this is fine, so long as observations are not deliberately selected to fit theories. The manner in which theories are shaped to fit observations does tell us something about their probable validity. But generally there are numerous rules that fit well any body of observations and numerous techniques that yield different results when the question of degree of rulefulness arises. Even if this were not so, all we can really learn from rules shaped to fit knowns is that they hold (in some degree) for the cases observed under the whole complex of conditions prevailing when they were observed, not that they hold for all such cases, under all conditions or under other precisely specifiable conditions. Only foreknowledge, in the sense above, can provide confidence that the regularities are less tenuous.
The objective of foreknowledge has been neglected in recent political science studies because of a fixation on the power of sophisticated data processing to yield valid rules (rather than just rules likely to be validated). Even more, it has been neglected because of a belief that foreknowledge always involves literal prescience of events in the future of the natural world, which, in view of the complexity of macropolitics, seems as near to impossible as anything can be. In fact, theoretical foreknowledge rarely takes the form of prescience. More often it involves experimental prediction (anticipating, by correct reasoning from presumed regularities, the results of activities in which variables are fully controlled), or concrete prediction (anticipating, by such reasoning, what will occur in the natural world if and only if specified initial conditions obtain), or forecasting (anticipating, by such reasoning, the probabilities of specified events occurring, given the initial conditions that do obtain). These types of foreknowledge all fall short of prescience and are not all equally conclusive for theory. The failure of a single forecast, for example, is generally (not always) less conclusive than that of an experimental prediction, although repeated forecasting failures are pretty definitive. All, however, give an essential insight into validity that the mere fitting of regularity statements to known data can never provide.
It should be evident that constructs exactly like those of theoretical physics are not needed for foreknowledge: certainly not for every type of it. All that is required of theory in the generic sense is that some unknown be strictly deducible from the posited regularities, whether the unknown is the outcome of an experiment, or the probabilities of natural events under obtaining conditions, or the occurrence of natural events under conditions specified by the theorist.
d) The notion of parsimony is hard to define precisely. The philosophers of science seem themselves to have had inordinate trouble with the concept. I take it to mean that regularity statements are parsimonious in proportion to (i) the variety and number of observations they order; (ii) the number of discrete theoretical constructs (i.e., constructs not strictly deducible from one another) used to order a constant volume and variety of observations; (iii) the number of other theoretical constructs subsumed to or derivable from them; and (iv) the number and complexity of variables used in the statements. On this basis, regularity statements are never parsimonious or unparsimonious (although the concept is often used dichotomously) but always more or less so, especially since trade-offs among the criteria of parsimony are possible.
The ideal of parsimony is to an extent aesthetic, but a high degree of it is required by the objective of foreknowledge and thus hangs together with the general animus of theoretical inquiry. The reason is simply that regularity statements can be made so cumbersome and complex that nothing (or, much the same, too many different things) can be strictly deduced from them, even when the cardinal sin of hypothesis saving is not committed. A case in point is Easton's "systems analysis" of macropolitics. By my reading, Easton identifies at least twelve crucial stresses that can arise in the political system's input-conversion-output-feedback cycle, each potentially fatal and each capable of being more or less reduced ("managed") by different adaptations to stress. Since the stresses can occur in various combinations and sequences, deducing what may ensue from any given initial condition in a polity becomes a matter of permutation, and 12! = 479 million (approximately); hence, any state of political affairs can lead to something like half a billion subsequent states of affairs without violating Easton's theory. Given that fact, the probability of correct forecasting of any sort seems low. So does that of finding a unique solution for why any given state of affairs exists, or that of failing to account for anything within the terms of Easton's theory. This is precisely why parsimony is essential: only a high degree of it can ensure that regularity statements may fail, and therefore also succeed.
Theories can, of course, be more or less powerful, or "good," depending on the rulefulness of regularity statements, the amount of reli-
ability and validity they possess, the amount and kinds of foreknowledge they provide, and how parsimonious they are. The animus of theoretical inquiry is constantly to increase their power to some unattainable absolute in all these senses. And while that absolute might have a unique ideal form to which the forms of theoretical physics might provide a discerning clue, it should be evident that it can be approached through many kinds of formulations, and always only approached. This is why "theory" is better conceived of as a set of goals than as statements having a specified form.
At the same time, no mental construct qualifies as theory unless it satisfies the goals in some minimal sense. This minimal sense is that it must state a presumed regularity in observations that is susceptible to reliability and validity tests, permits the deduction of some unknowns, and is parsimonious enough to prevent the deduction of so many that virtually any occurrence can be held to bear it out. If these conditions are not satisfied, statements can still be interesting and useful; but they are not "theory."
These are the sort of constructs we want about macropolitics. It should be evident that the pivotal point in the whole conception is that regarding foreknowledge: validity is held to depend on it, parsimony is mainly required for the sake of establishing validity, and regularity statements are not an end unless valid. Any general appraisal of the utility of a method of inquiry must therefore also pivot on that point, as will my brief for the case study method.
3. It should also be evident that foreknowledge is most closely bound up with the testing of theories and that the process of theory building involves much that precedes testing and some activities subsequent to it as well. It follows that modes of inquiry might be highly serviceable at one state of the process but not at others, and this also must be considered in arguments about them.
a) The process of theory building, needless to say, always begins with questions about experience for which answers are wanted—and raising questions, especially penetrating ones, is anything but a simple matter; indeed it is perhaps what most distinguishes the genius from the dullard (for whom common sense, the sense of ordinary people, leaves few mysteries). It is also an ability that, conceivably, could be sharpened or dulled by various modes of inquiry.
b) Questions, to be answered by theories, must usually be restated as problems or puzzles . This is a complex process that I have discussed elsewhere, and it consists essentially of stating questions so that testable rules can answer them (which is not the case for any and all questions) and determining what core-puzzles must be solved if questions are to be answered. A familiar example is the subtle process by which Weber arrived at the conclusion that the question of his Protestant Ethic ("Why did modern
capitalism as an economic system develop spontaneously only in the modern West?") boils down to the problem "what engenders the (unlikely) attitude of continuous, rational acquisition as against other economic orientations?"
c) The next step is hypothesis ,: formulating, by some means, a candidate-solution of the puzzle that is testable in principle and sufficiently plausible, prima facie, to warrant the bother and costs of testing. Like the formulation of theoretical problems, this initial step toward solving them generally first involves a "vision," then the attempt to state that vision in a rigorous and unambiguous form, so that conclusive testing becomes at least potentially possible. The candidate-solution need not be a single hypothesis or integrated set of hypotheses. In fact, a particularly powerful alternative is what Platt calls "strong inference" (and considers characteristic of the more rapidly developing "hard" sciences, such as molecular biology and high-energy physics): developing a set of competing hypotheses, some or most of which may be refuted by a single test.
d) After that, of course, one searches for and carries out an appropriate, and if possible definitive, test . Such tests are rarely evident in hypotheses themselves, especially if questions of practicability are added to those of logic.
Testing is, in a sense, the end of the theory-building process. In another sense, it is not: if a test is survived the process of theorizing does not end. Apart from attempting to make pure knowledge applied, one continues to keep an eye out for contradictory or confirmatory observations, continues to look for more definitive tests, and continues to look for more powerful rules that order larger ranges of observations, or the same range more simply, or subsume the tested rule under one of a higher order, capable of subsuming also other tested rules.
We now have the basic conceptual equipment needed to discuss sensibly the usefulness of case studies in the building of theories in our field, both in general and at different stages of the theory-building process. The scene-setting has been long, and perhaps tedious, but nothing in political case studies (which are many) or writings about them (which are very few) suggests that the stage is overstocked with props. Others may, of course, argue for different constructions of the props—in which case, they will also reject much that follows.
Options On The Utility Of Case Studies:
an Overview of the Argument
In taking positions on the value of case studies for theory building, both in themselves and relative to comparative studies, one can choose between
six, not all mutually exclusive, options. These have been derived from a review of actual political case studies, the scant methodological literature about them (and counterparts in other social and behavioral sciences), and my own reflections on unconsidered possibilities. They are listed in order of the value seen in case studies, especially as one progresses along the path of theory building—a progression in which, arguably, intuitive vision plays a constantly decreasing role relative to systematic procedure.
Option 1 holds case studies and comparative studies to be wholly separate and unequal. They are separate in that the two modes of inquiry are considered to have so little in common that case studies are unlikely to provide more than a severely limited and crude basis for systematic comparisons (e.g, variables of major importance in "n = many" studies might be wholly ignored in studies of pertinent cases or might not be treated in readily comparable ways, and so on). The two modes of study are unequal in that only comparative studies are associated with the discovery of valid theories; case studies are confined to descriptions and intuitive interpretations.
Option 2 desegregates case studies and comparative studies, but hardly lessens their inequality. It holds that the two modes of inquiry draw near (asymptotically) in the interpretation of cases, because such interpretations can be made only by applying explicit or implicit theoretical generalizations to various cases. Case study, however, remains highly unequal because it is certainly not required, nor even especially useful, for the development of theories. There is an exception to this principle, but it is very limited. One never, or, at least very rarely, has all the theories needed to interpret and treat a case; hence, something in the process of case interpretation must nearly always be left incomplete or to intuitive insight (which is why the two modes may approach closely but not intersect). Any aspects of case interpretation in regard to which theory is silent may be regarded as questions on the future agenda of theory building, as any intuitive aspects of interpretation may be regarded as implicit answers to the questions.
Option 3 grows out of the exception to Option 2. It holds that case studies may be conducted precisely for the purpose of discovering questions and puzzles for theory and discovering candidate-rules that might solve theoretical puzzles. The idea is simply that, if subjects and insights for comparative study are wanted, case study can provide them, and that case study might be conducted precisely for that purpose and perhaps satisfy it by something less chancy than serendipity or at least by affording larger scope to serendipitous discovery than studies that sacrifice intensive for extensive research. This still confines the utility of case study to the earlier stages of theorizing and makes it a handmaiden to comparative study. But it does tie case study into the theory-building process by some-
thing less contingent than possible feedback flowing from the "clinician" to the "experimentalist."
Option 4 focuses on the stage in theory building at which one confronts the question whether candidate-rules are worth the costs (time, effort, ingenuity, manpower, funds, etc.) of testing. It holds that, although in the final analysis only comparative studies can really test theories, well-chosen case studies can shed much light on their plausibility, hence whether proceeding to the final, generally most costly, stage of theory building is worthwhile. This cLearly involves something more than initial theoretical ideas. It begins to associate case study with questions of validity, if only in the grudging sense of prima facie credibility.
Option 5 goes still another step further, to the testing (validation) stage itself. It might be held (no revelation forbids it) that in attempting to validate theories, case studies and comparative studies generally are equal, even if separate, alternative means to the same end. The choice between them may then be arbitrary or may be tailored to such nonarbitrary considerations as the particular nature of theories, accessibility of evidence, skills of the researcher, or availability of research resources. A corollary of this position is, of course, that case studies may be no less systematic in procedure and rigorous in findings than comparative studies.
Option 6 is the most radical from the comparativist's point of view. It holds that case studies are not merely equal alternatives at the testing stage, but, properly carried out, a better bet than comparative studies. It might even be extended to hold that comparative studies are most useful as preliminary, inconclusive aids to conclusive case studies: that is, the former may suggest probabilities and the latter clinch them. (Beyond this, of course, lies the still more radical possibility that comparative studies are good for nothing, case studies good for everything. But all inquiry suggests that this is wrong, and while the history of ideas also suggests that the unthinkable should be thought, there is no point in doing so unless a good case can be made for Option 6.)
Arguments on the Options:
The options discussed above tell us how we might answer the first two questions posed in the introduction to this chapter, while the answer to the third depends on the others. Since the answers to be proposed are complex and the manner of the presentation is far from simple (being intended to present others' views as well as my own), I will outline them before arguing them, as a sort of map to the discussion.
1. First of all, a taxonomic point should be emphasized. This is that "case study" is in fact a very broad generic concept, whether defined
technically as "single-measure" study or by the simpler "single-individual" criterion. The genus can and, for our purposes, must be divided into numerous species, some of which closely resemble, some of which differ vastly from, the model of clinical study. The species that need distinction are: configurative-idiographic studies, disciplined-configurative studies, heuristic-case studies, case studies as plausibility probes , and crucial-case studies . There may be still other types, but these five occur most frequently or are of most consequence to us.
Two things are notable about these species. They are intimately associated with the options on the utility of case studies in theory building: each option is linked to a special type of case study (except that options 5 and 6 make no difference to the type of case study used). And as the utility attributed to case study increases, especially in progression through the phases of theory building, the associated type of case study increasingly departs from the traditional mode of clinical research and, except for numbers of individuals studied, increasingly resembles that of experimental inquiry.
2. As for choice among the options, and associated types of case study, it seems that the modal preference of contemporary political scientists is the third and/or second (not so different, except in nuance, that they preclude being chosen in conjunction); that few choose the fourth (more for reasons of unfamiliarity than methodological conviction); that options 5 and 6 are not chosen by anyone, or at least by very few. The evidence for this is mostly what political scientists actually write, reinforced by reactions to a preliminary version of this paper by a pretty fair cross-section of fellow professionals and a desultory poll among colleagues and students (only one of whom chose any option beyond the third, and that only because he reckoned that no one would list other possibilities unless up to tricks).
The prevailing preferences seem worth challenging on behalf of the options more favorable to case study. The latter appear to be rejected (better, not considered) for reasons other than full methodological deliberation, more as a result of overreaction against one weak type of case study than because of full consideration of the whole range of alternatives. In consequence, potentially powerful types of case study are neglected, and case studies are carried out less rigorously than they might be. Arguably, as well, this incurs liabilities in the conclusiveness of theories and the definitiveness of findings.
I propose to conduct the argument to this effect by evaluating each option, and associated type of case study, seriatim. In gist, my argument runs as follows:
a) Option 1 is hardly worth arguing against. Its basic premise—that
comparative and case studies are, for all intents and purposes, antithetical—has been exploded for good and all by Verba in our field, and has been widely attacked in other social sciences as well. Nevertheless, it is worth discussing because the type of case study associated with it was once dominant (and is still fairly common), and still provides the most widely prevalent notion of what case study is all about and of its potential for theory building.
b) All the other options are tenable, but only because there are different types of case study that have different power in regard to theory building, and because the utility of case studies is not fully determined by logic (abstract methodology) but depends also on practical considerations (e.g, characteristics of one's subject matter).
c) Options 2 and 3 identify perfectly legitimate uses of case study and methods of carrying them out. They are implicit in a host of meritorious political studies, but these studies do not come near exhausting the utility of case study for theory building. Case studies may be used not merely for the interpretative application of general ideas to particular cases (i.e., after theory has been established) or, heuristically, for helping the inquirer to arrive at notions of problems to solve or solutions worth pursuing, but may also be used as powerful means of determining whether solutions are valid.
d) Option 4 deserves special consideration for two reasons. It identifies an objective for which case study of a particular type is eminently serviceable and which can be of vast importance in theory building, but which is rarely pursued, by case study or other means. In addition, the utility of case study for that objective prepares the ground for arguing the case for the more radical options remaining.
e) Option 5 will be held to state the logically most defensible position: to attain theory in political inquiry, comparative studies and case studies should be considered, by and large, as alternative strategies at all stages, with little or nothing to choose (logically) between them. Since that argument will be most difficult to sustain—at least against the conventional wisdom—for the testing stage, the argument will concentrate on the type of case study suitable to it.
f) When practical considerations are added to logic, option 6 seems still more sensible, at least for studies of politics on the macrolevel. Case study is generally a better choice than comparative study for testing theories in macropolitics, but the type of case study useful for this purpose requires a kind of prior knowledge for which preliminary comparative study (of a limited kind) may often be useful or even necessary. This amounts to saying that comparative study can, in some circumstances, be treated as a handmaiden to case study, not vice versa, and thus, in a sense, stands the popular option 3 on its head.
Before working through all this in detail, I want particularly to emphasize two points. First, nothing that follows should be regarded as an attack on the utility of comparative study in theory building, simply because case studies are defended. (Some readers of an early draft of this essay concluded from this that comparative and case studies were not distinguishable after all. This is wrong: they have been distinguished. The point is that, logically at any rate, the distinction is not necessarily consequential for theory building.) Comparative studies have proved their utility. To the extent that they are invidiously evaluated vis-à-vis case studies, this is done on two grounds only: on practical grounds of limited applicability and because "n = many" studies invite avoidable errors of method (psychological, not logical hazards) in theory building that case studies are more likely to preclude.
Second, it is not to be inferred that just any case study will do for the purposes of theory building. Some readers of a draft of this essay concluded that it constituted a defense of "traditional" political studies against the "behavioralists." This is ludicrous, but it occurred. The discussion presents an argument for both case studies and for carrying them out in a particular way . Since the type of case study for which it argues is very demanding, implying great rigor of thought and exactitude of observation, it is hardly "anti-behavioralist"; and since that type of case study, to my knowledge, is as yet virtually nonexistent in our field, the argument can hardly be "traditionalist."
Types and uses of Case Study
1. In philosophy and psychology a distinction has long been drawn between nomotheric (generalizing, rule-seeking) and idiographic (individualizing, interpretative) types of, or emphases in, science. The philosophic progenitor of this terminology (and, in part, the ideas that underlie it) is Windelband, the most notable contemporary defender of the distinction is Gordon Allport. Idiographic study is, in essence, what was earlier described as clinical study and configurative-idiographic study is its counterpart in fields, like macropolitics, that deal with complex collective individuals. (Verba calls them configurative-idiosyncratic studies, but the difference in terminology is of no consequence.)
The configurative element in such studies is their aim to present depictions of the overall Gestalt (i.e., configuration) of individuals: polities, parties, party systems, and so on. The idiographic element in them is that they either allow facts to speak for themselves or bring out their significance by largely intuitive interpretation, claiming validity on the ground
that intensive study and empathetic feel for cases provide authoritative insights into them.
If configurative-idiographic studies are made from philosophic conviction, then the following assumptions usually are at work: (a) In the study of personalities and the collectivities they form, one cannot attain prediction and control in the natural-science sense, but only "understanding" (verstehen )—and thus, from understanding, limited, nondeductive conceptions of probable futures and prudent policy. (b) In attaining understanding, subjective values and modes of cognition are crucial, and these resist quantification. (c) Each subject, personal or collective, is unique, so generalizations can at most be only about their actions (persons) or interactions (collectivities). And (d) the whole is lost or at least distorted in abstraction and analysis—the decomposition of the individual into constituent traits and statements of relations among limited numbers of these; it is "something more" than an aggregate of general relations, rather than "nothing but" such an aggregate.
As already stated, configurative-idiographic studies were long the dominant mode of case study in political science. They still are common, although harder nowadays to distinguish from other types of case study in the field because, as Verba points out, homage is now often paid to the behavioral "revolution" in the field by using "some systematic framework to preface or organize the chapters of such studies and by including new variables and aspects of political systems" in them—frameworks and variables, that is to say, developed for nomothetic purposes.
2. Configurative-idiographic studies are certainly useful, and, at their best, have undeniably considerable virtues. They may be beautifully written and make their subjects vivid. They may pull together and elegantly organize wide and deep researches. The intuitive interpretations they provide may be subtle and persuasive and suggest an impressive feel for the cases they treat.
Their most conspicuous weakness is that, as Verba puts it, "they do not easily add up"—presumably to reliable and valid statements of regularity about sets of cases, or even about a case in point. This is plain in regard to sets of cases; the summation regarding them is at most factual (information about similar subjects, e.g., legislatures, parties, etc., in different contexts) and, because of idiosyncrasies in fact collecting and presentation, rarely involving even the systematic accumulation of facts. Anyone who has used secondary sources for compiling comparable data on numerous cases knows this to his pain, and, even more painfully, that inventories of interpretative propositions culled from case studies usually contain about as many distinguishable items as studies. The point is less plain, but just as true, for regularity statements concerning individual cases. The interpretations, being idiosyncratic, rarely come to an agreed position, or even
to a point of much overlap. For example, in the configurative-idiographic literature on France there seems to be overlap on the position that there are "two Frances," but nearly everyone has his own conception of what they are and where they are found. This situation is hardly surprising: in configurative-idiographic study the interpreter simply considers a body of observations that are not self-explanatory, and, without hard rules of interpretation, may discern in them any number of patterns that are more or less equally plausible.
The criticism that configurative-idiographic study does not add up to theory, in our sense, is mitigated by the fact that its capability to do so was never claimed by its exponents; in fact it is often explicitly repudiated. What is really troublesome about configurative-idiographic study is the repudiation itself (i.e., the claim that case study in the behavioral and social sciences can only be idiographic) and its consequences for the way in which the nomothetic utility of case studies in these fields is regarded.
For a thorough refutation of the idiographer's position, and a broad attack on the distinction between the nomothetic and idiographic itself, readers should consult Holt. His argument, in gist, is (a) that both the position and distinction have "peculiar origins"—misunderstandings of Kant by lesser German philosophers and "romantic" assumptions prevalent during the early nineteenth century ("Teutonic ghosts" raised against classical ideas and styles) that led to unreasonably sharp lines between nature and mechanisms on one hand and behavior and organisms on the other; and, more important, (b) that none of the postulates of idiographic study, as outlined above, withstands examination. As for the consequences of the claims of idiographers, the most stultifying has been the association of nomothetic study in macropolitics with study different from that favored by idiographers in all respects: not only study based on more systematic methods of collecting and processing data and on explicit frameworks of inquiry intended to make for cumulation, but "comparative" (i.e., multicase, cross-national, cross-cultural) studies.
If case study could only be configurative-idiographic in character, then the conclusions that case studies and comparative studies are wholly antithetical and that theories about politics require comparative study, or are unattainable, could not be avoided. But case study need not have that character, and the comparativists themselves have pointed the way to other varieties—without, however, overcoming a fundamental bias against case study of any kind in theory construction, largely anchored to the archetype of such studies in our field.
1. The comparativist's typical reaction to the theoretical poverty of configurative-idiographic studies is to hold that, while theories cannot be
derived from case interpretations, such interpretations can, and should, be derived from theories. "The unique explanation of a particular case," says Verba, "can rest on general hypotheses." Indeed, it must rest on them, since theoretical arguments about a single case, in the last analysis, always proceed from at least implicit general laws about a class or set to which it belongs or about universal attributes of all classes to which the case can be subsumed. The logic involved has been succinctly stated in Hempel's discussion of "scientific" explanation, the essence of which is the explanation of particular phenomena (in my terms "case interpretation") "by showing that [their] existence could have been inferred—either deductively or with a high probability—by applying certain laws of universal or of statistical form to specified antecedent circumstances." Those who consider this the only way of interpreting cases scientifically hold that the theoretical bases of case interpretations should always be made explicit, and that ad hoc additions to a framework of case interpretation should always be made as if they were general laws, not unique factors operating only in the case in point. The bases of case interpretation, in other words, should be established theories or, lacking them, provisional ones, and such interpretations can be sound only to the extent that their bases are in fact valid as general laws.
Case studies so constructed are "disciplined-configurative studies." The terminology is Verba's, who recommends such studies to us. Studies of this type are in fact very common in contemporary political studies—although, because of our disciplinary embarras de pauvreté in regard to validated, or even provisional, "general laws," they more frequently involve the application to cases of frameworks of inquiry, hopefully intended to help knowledge become nomothetic, not deductions from theory in any strict sense of the term.
Disciplined-configurative studies need not just passively apply general laws or statements of probability to particular cases. A case can impugn established theories if the theories ought to fit it but do not. It may also point up a need for new theory in neglected areas. Thus, the application of theories to cases can have feedback effects on theorizing, as Hempel recognizes. In addition, it is unlikely that all aspects of a case can be nomologically explained. As in the field of engineering, where general theories are applied to achieve conscious ends in particular circumstances, there are nearly always elements of prudence, common sense, or "feel" in case interpretations. Theory building, however, aims at the constant reduction of those elements, by stating notions that fit particular cases as general theoretical rules and subjecting them to proper theoretical tests.
In essence, the chain of inquiry in disciplined-configurative studies runs from comparatively tested theory to case interpretation, and thence, perhaps, via ad hoc additions, newly discovered puzzles, and systematized
prudence, to new candidate-theories. Case study thus is tied into theoretical inquiry—but only partially, where theories apply or can be envisioned; passively, in the main, as a receptacle for putting theories to work; and fortuitously, as a catalytic element in the unfolding of theoretical knowledge. This is, of course, still close to the clinician's conception of his role, and configurative studies that are disciplined in intent are not always easy to distinguish from unadulterated idiography. The two types are often intermixed and easily blend together.
2. The essential basis of Verba's argument about the relations between general theory and particular case interpretation is surely correct. If the interpretations of a case are general laws correctly applied to the case, the interpretations may be valid or invalid, depending on whether the laws are valid; otherwise, their validity simply cannot be known at all. Moreover, if cases are complex, the number of possible alternative interpretations, equally plausible because not at variance with the facts of the case, is usually vast, so that undisciplined case interpretation in much-studied cases usually yields large inventories of quite different propositions, none of which is clearly superior to any other. Preferences among them depend on personal tastes or general intellectual fads.
This point can be illustrated by a long quote from an essay of mine on the causes of revolutions. Studying the etiology of internal wars, I argued,
poses a difficulty . . . how to choose among a rare abundance of hypotheses which cannot all be equally valid nor all be readily combined. This problem exists because most propositions about the causes of internal wars have been developed in historical studies of particular cases (or very limited numbers of cases) rather than in broadly comparative, let alone genuinely social-scientific, studies. In historical case studies one is likely to attach significance to any aspect of prerevolutionary society that one intuits to be significant, and so long as one does not conjure up data out of nothing one's hypotheses cannot be invalidated on the basis of the case in question.
That most studied of all internal wars, the French Revolution, provides a case in point—as well as examples in abundance of the many social, personal, and environmental forces to which the occurrence of internal wars might be attributed. Scarcely anything in the French ancien régime has not been blamed, by one writer or another, for the revolution, and all of their interpretations, however contradictory, are based on solid facts.
Some interpreters have blamed the outbreak of the French Revolution on intellectual causes, that is to say, on the ideas, techniques, and great public influence of the philosophes (who were indeed very influential). This is the standard theory of post-revolutionary conservative theorists, from Chateaubriand to Taine, men who felt, in essence, that in prerevolutionary France a sound society was corrupted by a seductive and corrosive philosophy.
Other writers have blamed the revolution mainly on economic conditions, although it is difficult to find very many who single out as crucial the same
conditions. The revolution has been attributed to sheer grinding poverty among the lower classes (who were certainly poor); to financial profligacy and mismanagement on the part of the government (of which it was in fact guilty); to the extortionate taxation inflicted on the peasants (and peasant taxation verged upon brutality); to short-term setbacks (which actually occurred and caused great hardship) like the bad harvest of 1788, the hard winter of 1788–89, and the still winds of 1789 which prevented flour from being milled and made worse an already acute shortage of bread; to the overabundant wine harvests of the 1780s (one of the first historic instances of the harmful effects of overproduction); to the increased wealth and power of the bourgeoisie in a society still dominated to a significant extent by aristocrats, the growth of the Parisian proletariat and its supposedly increasing political consciousness, and the threatened abrogation of the financial privileges of the aristocracy, particularly their exemption from taxation—all unquestionable facts producing manifest problems.
Still another set of writers locates the crucial cause of the revolution in aspects of social structure. Much has been made, and with sufficient reason, of the fact that in the last years of the ancien régime there occurred a hardening in the lines of upward mobility in French society—for example, a decline in grants of patents of nobility to commoners and the imposition of stringent social requirements for certain judicial and administrative positions and the purchase of officerships in the army. This, many have argued (following Mosca's and Pareto's famous theory of the circulation of elites), engendered that fatal yearning for an aristocracy of wealth and talent to which the philosophes gave expression. Much has also been made, with equal reason, of popular dissatisfaction with the parasitic life of the higher nobility, with its large pensions and puny duties, its life of hunting, love-making, watchmaking, and interminable conversation.
And much has been attributed to the vulnerability of the privileged classes to the very propagandists who wanted to alter the system that supported them ("How," asked Taine, "could people who talked so much resist people who talked so well?"), reflected in the Anglomania which swept through the higher aristocracy toward the end of the ancien régime and in the rush of many aristocrats to the cause of the Americans in their war of independence.
There are also certain well-founded "political" explanations of the French Revolution: that the revolution was really caused by the violation of the tacit "contract" on which the powers of the monarchy rested (a contract by which the aristocracy surrendered its powers to the monarchy in return for receiving certain inviolable privileges), or that the revolution was simply a successful political conspiracy by the Jacobins, based on efficient political organization. Personalities, needless to say, get their due as well: the revolution has been blamed, for example, on the character, or lack of character, of Louis XVI (who was in fact weak, vacillating and inconsistent), the supposed immorality of the Queen (who indeed was the subject, justly or not, of many scandals), the effect on the public of the dismissal of Necker, and, of course, on the "genius," good or evil, of unquestionable geniuses like Mirabeau, Danton, Marat, and Robespierre.
We could take other internal wars and arrive at the same result—similarly
large lists of explanations, most of them factual, yet inconclusive. The more remote in time and the more intensively analyzed the internal war, the longer the list of hypotheses. . . .
How can this embarrassment of interpretative riches (one hesitates to say theoretical riches) be reduced? If the examination of any single case allows one to determine only whether an interpretation of it is based on facts, then broad comparative studies in space and/or time are needed to establish the significance of the facts on which the interpretations are based. Was a blockage in the channels of social mobility a significant precondition of the French Revolution? We can be reasonably confident that it was only if it can be shown that elite circulation and political stability are generally related. Was the Chinese population explosion really an important cause of the Chinese revolution? Surely this is unlikely if demographic pressures do not generally affect the viability of regimes.
The argument of this passage still strikes me as correct. However, the operative sentence in the last paragraph should have read that "valid theory is needed to establish the significance of the facts on which the interpretations are based," leaving open the extent to which the formulation of valid theories requires "broad comparative studies." For the problem here is one of case interpretation, not theory building, and the possibility that sound bases for case interpretation might be furnished by case studies themselves cannot be dismissed, unless one assumes (as Verba does, and as I did) that no types of case study other than the configurative-idiographic or disciplined-configurative varieties exist. But this, as will soon be evident, is far from the case—and concedes far too much to idiographers or those who, opposing idiography, nevertheless accept the dichotomy between the clinical and experimental that ultimately gives rise to idiographic studies.
It remains to add a point insufficiently stressed in writings on disciplined-configurative studies. The application of theories in case interpretation, although rarely discussed, is not at all a simple process, even leaving aside the question of how valid theory is to be developed. Such applications only yield valid interpretations if the theories permit strict deductions to be made and the interpretations of the case are shown to be logically compelled by the theories. In the case of revolutions, for instance, it is not enough to know that a regularity exists and that a case somehow "fits" it (i.e., does not manifestly contradict it). One should also be able to demonstrate, by correct reasoning, that, given the regularity and the characteristics of the case, revolution must have occurred, or at least had a high probability of occurring. Not all theories permit this to be done, or at least equally well. For example, a theory attributing revolution to aggressions engendered by social frustrations will hardly fail to fit any case of revolution, nor tell us exactly why any case of it occurred. Unless it specifies precisely how much and what sort of frustration en-
genders revolution, on whose part, and under what complex of other conditions, the frustration-aggression theory of revolution, applied, say, to the French Revolution, can yield about as many plausible case interpretations as can configurative-idiographic study (there having existed many sources of frustration in the ancien régime , as in all regimes).
This point brings out a major utility of attempting disciplined case interpretation. Aiming at the disciplined application of theories to cases forces one to state theories more rigorously than might otherwise be done—provided that the application is truly "disciplined," that is, designed to show that valid theory compels a particular case interpretation and rules out others. As already stated, this, unfortunately, is rare (if it occurs at all) in political study. One reason is the lack of compelling theories. But there is another, which is of the utmost importance: political scientists reject, or do not even consider, the possibility that valid theories might indeed compel particular case interpretations. The import of that possibility, assuming it to exist, lies in the corollary that a case might invalidate a theory, if an interpretation of the case compelled by the theory does not fit it.
But this goes too far ahead, toward a crucial argument that will require much discussion below. The point for the present is merely that exponents of disciplined-configurative study have insufficiently considered both the difficulties and promises of the relations between general theories and particular case interpretations.
Heuristic Case Studies
1. Disciplined-configurative study assumes that "general laws" are available. It is not thought of as a part of the process of theory building as such, except in that the interpretation of cases may lead to ad hoc, serendipitous additions to existing theories in order to cover puzzling aspects of a case. However, the feedback effect in Verba's recommended sequence of inquiry can be isolated from the rest of the sequence and case study deliberately used to stimulate the imagination toward discerning important general problems and possible theoretical solutions. That is the essence of heuristic case studies (heuristic means "serving to find out"). Such studies, unlike configurative-idiographic ones, tie directly into theory building and therefore are less concerned with overall concrete configurations than with potentially generalizable relations between aspects of them; they also tie into theory building less passively and fortuitously than does disciplined-configurative study, because the potentially generalizable relations do not just turn up but are deliberately sought out.
Heuristic case studies do not necessarily stop with one case, but can be conducted seriatim, by the so-called building-block technique, in order to construct increasingly plausible and less fortuitous regularity statements.
This technique is quite simple in principle. One studies a case in order to arrive at a preliminary theoretical construct. That construct, based on a single case, is unlikely to constitute more than a slim clue to a valid general model. One therefore confronts it with another case that may suggest ways of amending and improving the construct to achieve better case interpretation; and this process is continued until the construct seems sufficiently refined to require no further major amendment or at least to warrant testing by large-scale comparative study. Each step beyond the first can be considered a kind of disciplined-configurative study, but is better regarded as heuristic case study proceeding with increasingly refined questions and toward increasingly more specific ends. It is important not to confuse the whole process with comparative study. The latter seeks regularities through the simultaneous inspection of numerous cases, not the gradual unfolding of increasingly better theoretical constructs through the study of individuals. Of course, comparative studies can also employ the building-block technique by successively refined theories through a series of multicase studies.
Heuristic case studies should also not be confused with pedagogic ones, which abound in politics and closely related fields. Pedagogic cases in politics generally have the aim of teaching policy and administrative skills by putting students into the positions of policymakers and administrators through detailed narrative accounts of real action problems. They are derived from case-method teaching in the law and business schools and are most akin to configurative-idiographic studies, except that the idiography is supplied by students, under the guidance of pedagogues assumed to possess special practical wisdom or experience. Theory is not supposed to emerge, and to my knowledge never has emerged, from them.
2. The claim that theoretical puzzles and insights can be usefully (perhaps most usefully) sought in case study is the standard defense of case study by theory-oriented social scientists. Equally commonplace is the belief that this is all that case study can usefully accomplish in the process of theory building. Consequently, studies of this type abound in political science and have recently crowded or displaced configurative-idiographic studies as the predominant species (no actual frequency count has been made); and there has been little exploration of case studies that might take one beyond the stage of hypothesizing. In many cases, such studies are carried out in light of preconstructed checklists of variables or frameworks of analysis, such as the "functional" framework associated with Almond and his associates. As one might expect in case study oriented toward theory, these frameworks focus attention on special variables, but not so narrowly as is common in extensive experimental work.
The justification for heuristic case studies runs as follows: (a) Theories
do not come from a vacuum, or fully and directly from data. In the final analysis they come from the theorist's imagination, logical ability, and ability to discern general problems and patterns in particular observations. (b) There are ineffable differences in such imaginative and other abilities, but various aids can be used to stimulate them: among them, the printouts from data banks or other comparative studies (which, however, never obviate the use of theoretical imagination, e.g., for interpreting the printouts into proper regularity statements and for determining what data banks should contain or how comparative studies should be designed in the first place), (c) The track record of case studies as stimulants of the theoretical imagination is good. (d) One reason it is good is precisely that, unlike wideranging comparative studies, case studies permit intensive analysis that does not commit the researcher to a highly limited set of variables, and thus increases the probability that critical variables and relations will be found. The possibility of less superficiality in research, of course, also plays a role here.
3. Arguments in favor of heuristic case studies surely have merit. Whatever logic might dictate, the indubitable fact is that some case study writers in macropolitics have come up with interpretations notably incisive for their cases and notably plausible when taken as generalizations for sets of them, with or without the benefit of special frameworks or approaches. See, for example, the works of such men as Tocqueville, Bagehot, Halévy, Bryce, and Bodley, or, in another field, anthropologists too numerous to mention.
Nevertheless, one may argue that too much is made of heuristic case studies, for two related reasons. One is that those who defend them sometimes seem to do so simply because they can see no more ambitious function to be served by case study. The other is that, not wishing to make other claims but to defend case studies, they claim too much for such studies as heuristic tools, especially in comparison to "n = many" studies. Scenting a valid claim, they exaggerate it—and miss the possibility that a more persuasive brief might be based on a greater sense of limitation at the heuristic stage of theory building and a lesser one at others.
The point that case studies are good for more than getting clues will concern us later. But the anticipation of that point in the previous section can be supplemented here by a further suggestive argument. Case studies intended to serve a heuristic function can proceed much in the manner of "clinical" study, that is, with a minimum of design or rigor, and tackle any case that comes to hand. In that event, however, nothing distinguishes the study from configurative-idiographic study, except the researcher's hopes and intentions, and results can only turn up by good fortune—which the bright will seize and the dull miss, but which the researcher can do
nothing to induce. The alternatives are to use at least a modicum of design and rigor in research and not to choose just any case on any grounds but a special sort of case: one considered likely to be revealing, on some basis or other. The suggestive point in this for later argument is not that case study may often depart markedly from the archetype of clinical study (although that is noteworthy), but that certain kinds of cases may be regarded as more instructive for theory building than others . Actual heuristic case studies seem in fact generally, even if often just implicitly, to make that claim for the cases selected. The grounds are often obscure, and the claim often seems post hoc and intended to disarm charges of idiography. The point nevertheless remains that the brief for heuristic case study is strong only to the extent that cases especially instructive for theory, and subject to rigorous inquiry, can be identified. And if that possibility exists, then the further possibility arises that some cases might be especially instructive also at other stages of the theory-building process.
If the prevalent emphasis on heuristic functions is too modest, in what senses does it also exaggerate? First of all, the fact that case study writers have often spawned ideas notable as generalizations proves nothing. The Tocquevilles or Bagehots might have been successful in spawning plausible theories without writing case studies, since their imagination and incisiveness clearly matter more than the vehicles chosen for putting them to work. If they had used comparative studies they might have been even more successful, and more successful still if they had had available modern technology for accumulating, coding, storing, and processing data—not to mention the fact that they do always make implicit, sometimes explicit, use of comparisons in their case studies (e.g., Bagehot's contrasts between Britain and America, Tocqueville's between America and France), even if only to demonstrate that factors used to interpret their cases do in fact differ in different cases. Moreover, for every case study that has notably succeeded in spawning theory, there are scores that have notably failed—and this does not refer to idiography alone. Case study certainly furnishes no guarantee that theoretical abilities will be awakened or sharpened. And comparativists have been at least as successful in spawning theories as configurativists; for every Tocqueville or Bagehot we can produce an offsetting Aristotle, Machiavelli, Mosca, Pareto, or Weber.
Second, the benefit of being able to take into consideration more variables in case study incurs the cost of highly circumscribed breadth of inference. And it is probable that the number of hypotheses suggested, hence also the number of invalid ones to be pursued, will be proportional to the number of variables considered. Heuristic case studies have a demonstrable tendency, as in the case of studies of the French Revolution, to spawn a crushing and chaotic number and variety of candidate-generalizations, or hypercomplex multivariate theories, especially when
these studies are made by imaginative people. And, unlike comparative studies, they cannot even yield initial clues about the generalizability of relations selected from all those that constitute the case—unless, to repeat, the case is considered, on some good basis, especially revealing for sets of phenomena, that is, one for which breadth-of-inference problems may be claimed to be slight.
These problems have led some to identify "grounded theory" (theory that is initially derived from observations, not spawned wholly out of logic and imagination) with comparative inquiry rather than case study. The reasons for doing so are rather convincing. But the more sensible position surely is that, if we are really only concerned with the initial formulation of candidate-theories as a phase of theoretical inquiry (and not theory leaping full-blown out of data), case study is useful but by no means indispensable, as also is comparative study or any other exercise of the theoretical imagination. It is manifestly more useful for some people than others. It also would be generally more useful than it has been if more case studies were deliberately undertaken as exploratory means for arriving at candidate-theories, rather than simply allowing these to occur fortuitously, and if special characteristics of heuristically instructive cases could be specified and something like a heuristic "method" could be developed.
If nothing more were to be said for case studies than that they may be helpful in initially formulating candidate regularity statements, we could only conclude that there is no special reason for either making or not making such studies. It follows that if there is a strong justification for case studies as tools in developing theories, it must be found in the special utility of such studies at some later stage of the sequence of inquiry by which theories are established, or, at a minimum, their availability as reasonable alternatives to comparative studies during the later, no less than earlier, stages of the theory-building process.
1. After hypotheses are formulated, one does not necessarily proceed immediately to test them. A stage of inquiry preliminary to testing sometimes intervenes and ought to do so far more often than it actually does in political study (or in other social sciences). It involves probing the "plausibility" of candidate-theories. Plausibility here means something more than a belief in potential validity plain and simple, for hypotheses are unlikely ever to be formulated unless considered potentially valid; it also means something less than actual validity, for which rigorous testing is required. In essence, plausibility probes involve attempts to determine whether potential validity may reasonably be considered great enough to warrant the pains and costs of testing, which are almost always consider-
able, but especially so if broad, painstaking comparative studies are undertaken.
Such probes are common in cases where costly risks have to be run. These probes are roughly analogous to the trials to which one subjects a racehorse before incurring the costs of entering and preparing it for a major race: success cannot be guaranteed, but some kind of odds (ratios between certain costs and probable benefits) can be established. The simple principle at work is that large investments in less likely outcomes are worse propositions than large investments in more likely outcomes. Here the analogy between theorizing and horse racing becomes a little specious, for in probing the plausibility of a theory we can hardly expect to know much, or anything, about previous performance or to have exact estimates of probability like those given by a stopwatch. But we do not lack means for at least getting a reasoned, not merely intuitive, "feel" for the odds against a theory.
At a minimum, a plausibility probe into theory may simply attempt to establish that a theoretical construct is worth considering at all, that is, that an apparent empirical instance of it can be found. I take that (together with heuristic objectives) to be the purpose of Dahl's influential study of power in New Haven. Dahl, as I read him (contrary to some other interpreters of his work), wants to establish that power in democracy may be "pluralistic," or may not be "monolithic," not that it must be the former and cannot be the latter. The study certainly succeeds in that regard, although it would succeed even more if New Haven had been selected for study because it is typical of a specified class of cases.
Some ways of surmising the plausibility of a theory beyond that minimal point are nonempirical, and since they entail only the cost of thought, these should generally be used before, or instead of, empirical probes. We may have confidence in a theory because it is derived logically from premises that have previously yielded valid theory in a field or because it is derived from premises contrary to those that have led to major failures. We may also have confidence in a theory if it is able to account for both strengths and weaknesses in existing relevant hypotheses or otherwise seems to organize considerable volumes and varieties of unexplained data. An example of both these methods of estimating plausibility is furnished by those passages of my monograph on stable democracy that show the grounding of its main proposed regularity statement in (as I then thought) validated psychological theories and those that try to show how the strengths and weaknesses of three alternative hypotheses, all rather powerful yet flawed in certain ways, can be explained by the main proposed regularity statement (see chapter 5). Demonstrating logically that proposed regularity statements can potentially explain data not yet explained, and/ or provide a common foundation for previously validated but quite discrete
and unconnected hypotheses, and/or extend assumptions found powerful in some areas to other areas, all create presumptions in favor of testing the statements independently, even by costly means.
Plausibility probes can also be directly empirical, that is, in the nature of preliminary, rather loose and inconclusive, but suggestive tests before more rigorous tests are conducted. Such probes confront theories with lesser challenges that they must certainly withstand if they are not to be toppled by greater ones. If, for example, it were posited that democratic power structures are normally monolithic (which is in fact often done in political theories) and one had strong reason to believe that New Haven was unlikely to be a deviant case (which is also arguable), then Dahl's study of its power structure would establish much more than that the counteridea of pluralism in democratic power is not completely vacuous. It would cast serious doubt on the posited regularity. Such empirical probes are especially important where nonempirical probes yield very uncertain results, and there is also reason to use them, as additions to others, as cheap means of hedging against expensive wild-goose chases, when the costs of testing are likely to be very great.
2. There is no reason why empirical plausibility probes should not take the form of modest or rather diffusely designed comparative studies, as preludes to more ambitious and tighter ones. Indeed, most systematic comparative studies in macropolitics make more sense as plausibility probes (or as "heuristic comparative studies") than as what they are generally claimed or regarded to be: that is, works presenting definitive results. Almond and Verba's The Civic Culture is surely a case in point. The sample of cases covered by the study is hardly large and dubiously representative; the regularity statements about "democratic stability" emerging in its final chapter could certainly be made more exact, are mainly afterthoughts imputed to the evidence, and are hardly conclusively compelled by that evidence. But they seem sufficiently rooted in data and reasoning to warrant their statement in more precise form and their thorough testing, preferably by logically deduced predictions about findings in a project specifically designed not to get interesting data but to get those crucial to establishing the validity of the work's central propositions. (One may consider it reprehensible that so many comparativists are willing to stop where only that much, or little more, has been accomplished, and then go on to other, still merely plausible, ideas on different subject matter. We have no right to bewail the fact that others do not take up our ideas if we ourselves drop them far short of the point to which they could be taken.)
The essential point for us is that, as empirical plausibility probes, case studies are often as serviceable as, or more so than, comparative ones—and nearly always a great deal cheaper—a prime consideration in probing
plausibility. The economic case for them is strongest where required information is not readily available in aggregate data or good secondary sources and is intrinsically hard to get. Case studies can certainly serve the purpose well if well selected, that is, if they are such that a result, for or against a theory, cannot readily be shrugged off. It is true that case studies have been little used in political studies as plausibility probes, but this is largely due to the fact that the idea of any sort of plausibility probe is foreign to the field, plus the fact that comparative studies to amass data from which finished theories supposedly emerge have been its dominant contemporary genre. (Comparative studies as plausibility probes are equally uncommon, except only in the sense that some of them appear better tailored for that purpose than the purposes they pretend to serve.)
Because of the rareness of plausibility probes in the field, an example may be more instructive than abstract discussion. The example I shall use involves my work on governmental performance, following up my monograph on stable democracy (chapter 5). Self-advertisement is not intended, and no claims about the quality of the work are made. But cases in point are, as stated, rare; and the work in question illustrates well the circumstances under which probing plausibility becomes important and case study is useful to that end.
As to circumstances that indicate the advisability of plausibility probes: After first formulating the hypotheses on stable democracy (see chapter 5), I thought it imprudent to plunge immediately into concerted testing, even assuming that an argument for more than minimal potential validity had already been made. Although the propositions were simple and parsimonious, there is unfortunately no close relationship between the simplicity of propositions and the ease or economy of testing them; in this case, in fact, the effort required was bound to be immense. Concepts used in the propositions had to be more precisely and rigorously formulated. Virtually all the data required to test them had to be produced by extensive fieldwork: one could certainly not base cross-national research into "congruence" among authority patterns (the main independent variable used in the hypotheses) on conveniently available statistical annuals and the like. This called for resources—time, language skills, historical and cultural knowledge—that a single scholar never commands. Consequently, it would be necessary to involve others in the work, an effort likely to fail, or to be wasteful, while ideas are still little more than mildly plausible. Furthermore, testing the propositions would not be possible without developing an elaborate scheme of concepts for getting at the multifarious facets of authority relations: concepts unambiguously defined, standardized to apply to interactions in virtually all kinds of social units, and operationalized to make field observations reliable and some sort of measurement of resemblances
among authority patterns possible. To relate the independent variable to levels of governmental performance (the main dependent variable), it was necessary also to develop a set of categories and techniques for reliably determining different levels of such performance. And all this done, a large number of taxing field studies had (as it then seemed to me) to be carefully designed, thoroughly carried out, rigorously processed, and their results collated. Under such circumstances it surely is reasonable, even imperative, to seek some decent, however inconclusive, estimate of probable success before any concerted attempt at testing, better than that provided in the initial work.
As to the utility of case studies as plausibility probes: Several things were done to arrive at that estimate, but the most important was a study of Norway. That country was selected in part for extraneous reasons (language, personal connections, the high development of social research in the country). The main reason for selecting it, however, was that Norway seemed somehow critical for the theory to be tested, in the sense that the theory could hardly be expected to hold widely if it did not fit closely there. The theory purported to account for high, but not necessarily low, levels of governmental performance—and such performance had been outstandingly high in Norway for a long time on all the criteria initially used to gauge it. Moreover, the theory related social (i.e., nongovernmental) structure to governmental performance, but selected from all facets of such structure one special aspect that intrinsically could remain unchanged while all or most others changed, or, conversely, could change while others remained constant. As it happens, there had been virtually no significant change in governmental structure, but much in social structure, in Norway since late in the nineteenth century. Two things consequently had to be found if the theory were to be considered plausible. The proposed correlates of high governmental performance had to be unmistakably present in high degree and the aspect of social structure selected for emphasis had to be constant over time despite considerable other changes in Norwegian society. Neither was known in advance and both were in fact the case, or so it seemed; hence confidence that the theory might withstand concerted comparative study was greatly increased, to a level more in line with expected costs. The essential point is that Norway seemed to have special characteristics particularly illuminating for the theory: in short, it appeared to be a specially instructive case, of the sort that might be particularly useful for heuristic inquiry but that is more readily identified if candidate-theory already has been formulated.
3. The study was not conclusive for the theory; it merely strengthened its prospects. One reason for its inconclusiveness was that the methods
used in it were less rigorous, and the research less thorough, than they might have been, precisely because economies are a major consideration in probing plausibility. Another reason was the prevalent belief that the study of a case could, at most, yield a subjective estimate of the theory's plausibility, simply because it was case study, hence that no massive research assault on it, which would long postpone comparative inquiry, was needed or even justifiable.
And here again we come to a critical possibility. If studies of well-selected cases, no less than comparative studies, can serve the purposes of plausibility probes (the idea of which is, after all, to form estimates of probable validity), could they not also serve, painstakingly selected and rigorously carried out, as tests of validity itself, with similar economies in the work required? The possibility should at least be entertained and the case for it argued, since the potential practical gains could be enormous. It arises, at bottom, from the obvious fact that cases are not all equal in their import, even for the modest purposes of heuristic exploration. The question is whether their inequality extends to the point where certain types of cases, and modes of case study, can serve to test theories for validity—the step most demanding on rigor and in which breadth-of-inference problems seem most damaging to case studies.
To explore this question further, we shall have to look more closely at a suggestion made in the discussion on disciplined-configurative study: that if theory can compel particular case interpretations, then particular cases could invalidate or confirm theories.
1. The position that case studies are weak or useless for testing theories rests, at bottom, on the mistaken application of a correct principle—a principle that applies more, but still imperfectly, to the discovery of theories in data than to their testing.
We can think of theory formulation as a process that leads one to postulate a curve or line to which observations of reality are expected to correspond; and we can think of theories as valid if the curves or lines that best fit relevant observations in fact match the theoretical expectation, or, put in a different manner, if the points yielded by measurements of relevant observations fall on or very near the postulated curve at logically specified locations. The principle that seems to rule out case study for the purpose of finding valid theory is the elementary one holding that any single instance of a relationship yields only one observed point, and that through any single point an infinite number of curves or lines can be drawn. (A less abstract variant of this principle is the argument above that any number of different explanations, not contrary to fact and thus at least minimally plausible, can be offered for any political event.)
The principle is, as stated, incontestable. But we are not constrained to conclude from it that comparative studies are indispensable to the development of valid theories and case studies useless for the purpose, unless we inject between the premise and conclusion a major fallacy that apparently dies hard: the inductive fallacy. The essence of that fallacy is the belief that theories, being contained in phenomena, can be fully derived from observations by simple inspection or, at any rate, sophisticated data processing. This is fallacious in several senses that should be disentangled, although the fallacies are all of a piece and usually all committed at once.
a) One aspect of the fallacy involves confusion between the discovery of candidate-theories and their testing: in deriving theory from observations ("grounded theory") one may be tempted to think that curves suggested by comparative data are themselves valid theories. This hazard is not logically inherent in comparative study, but contemporary political science, among other fields, suggests that it is extreme in practice, most of all where the behavioral sciences' model of experimental study is closely followed. Such study, regardless of how punctiliously carried out, cannot, in and of itself, reveal general laws guaranteed to be valid. It only provides more or less powerful clues as to what they are, that is, helps to discover them. In some cases these clues may be so powerful that testing may seem superfluous or not worth the cost, but this is highly exceptional.
Strictly speaking, generalizations directly inferred from data only hold (probabilistically) for the phenomena observed under the conditions prevailing during observation. If the observations are voluminous and accurate, and if the conditions of observation are highly various or controlled, then one may have very high confidence that the curve that best fits the observations in fact manifests, in graphic form, a valid theory. Nevertheless, the element of surmise in going from data to theory always is considerable, and the "epistemic gap" between them, as Northrop calls it, ineluctable. And such great limitations usually exist, in practice, on the volume, accuracy, and variety or control of observations (including, of course, the obvious limitation that we cannot observe the future) that the risk in identifying an empirical generalization with a theoretical rule usually cannot be defended unless special testing of the presumed rule is carried out.
b) A second aspect of the fallacy concerns the discovery of candidate-theories in the first place. It is the principles that give rise to empirically discovered curves that constitute theories, not the curves as such: these only represent the principles, that is, show them at work. When an empirically grounded curve has been drawn, therefore, the principles it expresses must still be elucidated. Often this is not much of a problem, and statistical techniques (like causal path analysis) can help solve it. Nevertheless, curves can deceive as well as instruct, regardless of such techniques; and they most resist the discerning of simple regularities governing phe-
nomena because the data from which they are constructed usually express all the complex interactions of factors in the concrete world, or sometimes even the laboratory. Nature, as Bacon knew, is a tough adversary capable of innumerable disguises. More than routine method is often required to strip off these disguises.
It seems, in fact, unlikely that the more powerful laws of physical science could have been discovered (their testing aside) by the mechanical processing of observations, however "sophisticated." Certainly one is struck by the small role played by systematic comparative observation in both their formulation and critical testing—in effect, by the thorough lack of correspondence between the psychologist's and physicist's conception of "experimentation." As illustration, take that touchstone of ancient, modern, and contemporary physics: conceptions of gravity and the closely associated law of the velocity of freely falling objects.
The Galilean challenge to the Aristotelian conception of free fall (the heavier the object, the faster it falls), accepted as gospel for nearly two millennia, did not grow out of observation at all but out of a simple "thought-experiment" (simple in retrospect, but apparently not at all obvious until performed). In gist (and with apologies for a layman's bowdlerization): if Aristotle is correct, then two bricks of the same weight, dropped at the same instant from the same height, must strike the ground at the same instant. If the two bricks are dropped side by side, as if cemented, the rate of fall of each must be the same as if dropped separately; but if cemented, they would be twice as heavy as a single brick and must therefore drop much faster; hence, since both conclusions cannot be right, the theory must be wrong. And the only way to square the two conditions logically is to make the weight of the falling objects irrelevant to acceleration in free fall, with the relevant variables being only the gravitational forces that account for falling and, possibly, the duration of the fall.
There is no observation here at all (and much doubt even about whether Galileo ever climbed the Tower of Pisa to check out, by a single "probe," the plausibility of his conclusion). Had systematic comparative measurements been used, anomalies in the Aristotelian conception would certainly have turned up, at least in the fall of objects "heavy" above a certain threshold. But if a well-chosen sample of objects had been dropped from a well-selected sample of heights under a well-selected sample of wind and other conditions, the likely conclusions would surely have been something like this: that the whole process of falling, like macropolitical phenomena, is "immensely complicated and cannot be accounted for by one or two simple causes"; that weight is a factor (as it is at certain heights and other conditions); and that weight, size, shape, and density of object, and wind conditions account for such and such a (no doubt high) percentage of the variance in rates of fall, singly or in various combinations. A radical,
deductively fertile simplification of the whole complex process might, but almost certainly would not, have emerged.
The Galilean notion was widely disputed until a crucial experiment could be conducted to check it out. Objects of different weights did demonstrably fall at different, sometimes vastly different, rates. So the Galileans' extraneous factors, having no place in the law, remained other people's favored explanatory variables. Only with the invention of the air pump, about 1650, was a definitive experiment possible: dropping a heavy object (coin) and a light one (feather) in an evacuated tube. Again, no systematic comparative measurement was used, only a single experimental observation that foreclosed weaseling out by ad hocery to Galileans and Aristotelians alike.
Newton's theory (F ¥mm'/r2 ) was certainly suggested by observations of the movement of astronomical bodies (although Singer argues that all Newton's laws are quite abstract and not concerned directly with phenomenal observations), but the value of the universal gravitational constant G , needed to convert the expression of Newton's theory into an equation, was worked out initially by Lord Cavendish (in 1798) through a single experiment and the measurement derived from it. And Einstein's theory could certainly not have been derived from quantitative analysis of observations, while its conclusive test involved a single critical phenomenon: the deflection of light as it passed close to the rim of the sun.
Comparative observations may be significant in fleshing out basic conceptions of regularities (e.g., determining that the velocity of freely falling objects is described by s =gt2 , or measuring any specific value g ). But they are far from necessary, and quite likely to deceive, when these basic conceptions—critical variables and their basic relationship—are to be formulated.
c) The inductive fallacy has a third facet, pertaining exclusively to testing. It might be conceded that discovering and testing theories are different processes, but not that testing requires data different from those that help in discovery. The analysis of data may be so convincing that one might not consider it worthwhile to test rules derived from them but, despite this, the experiences in light of which theories are constructed cannot be used again as tests of them. Testing involves efforts to falsify, and anything giving rise to a theory will certainly not falsify it; nor will any body of replicated observations do so, if replication indeed is faithful. (Replication pertains to reliability, not validity.) The object of testing is to find observations that must fit a theory but have a good chance of not doing so. Nothing that suggests a theory, therefore, can also test it.
2. Having established a need for the independent testing of theoretical
curves (on the grounds that the discovery and testing of theories are intrinsically different activities, that no method of discovery can guarantee validity, that even painstakingly gathered and analyzed data can deceive, and that data which suggest regularities cannot also validate them), we come to the crux: the argument of the fifth option that, in principle, comparative and case studies are alternative means to the end of testing theories, choices between which must be largely governed by arbitrary or practical, rather than logical, considerations .
Comparative studies can certainly be used to test theories. If we use them for this purpose, our object, as stated, is to demonstrate that a curve that fits their results well in fact closely coincides with a curve postulated by theory, however that may have been worked out. In the case of a law like that of the velocity of falling objects, for example, one might try to demonstrate that the curve yielded by a set of observations sustains the expectation that the postulated law is an increasingly better predictor as one increasingly approximates the conditions under which the law is considered to hold absolutely.
However, there is available (not necessarily in all cases, but in many) an alternative to that rather cumbersome procedure, and it involves a kind of case study. One can use a well-constructed experiment, conducted to simulate as closely as possible the specified conditions under which a law must hold, and compare its result with that predicted by the law. In the history of science the decisive experiments have been mostly of that kind, a fact that makes one wonder how the comparative observation of unmanipulated cases could ever have come to be regarded as any sort of equivalent of experimental method in the physical sciences. (The main reasons are, by my reading, the influence of J. S. Mill's Logic , the intuitive decision reached by some influential contemporary social scientists that their regularity statements must unavoidably be "probabilistic" in form, origin, and testing, and the fact that much experimentation in the physical sciences is simply hopeful fishing for regularities in masses of data.) And if a well-constructed experiment can serve the purpose, then so may a well-chosen case—one that is somehow as crucial for a theory as are certain experiments, or indeed natural observations, in the physical sciences.
This argument is not at all impugned by the incontestable principle regarding the relations between points and curves with which we started. For there is another principle about those relations that is equally incontestable. This is that any given point can fall only on an infinitesimal fraction of all conceivable curves: it will not fall on any of the curves, the number of which is also infinity, that do not in fact pass through the point. (A less abstract variant of this principle is that for every plausible explanation of a political event, there is an infinite number that are not even minimally plausible.) The fact that a point falls, or does not fall, on a curve,
therefore, is not at all insignificant. If the curve is not constructed to pass through the point but preconstructed to represent a theory, and if, given the nature of a case subsequently examined, we can predict, according to the theory, that it must fall on, or very near, the curve at a specified location, the fact that it does so is of the utmost significance, and its location far from the predicted point will impeach the theory no less than the tendency of several points to describe a divergent curve. At any rate, this is the case if the bases for predicting the location of an unknown point are really compelling—which is the object of crucial case study. In such case study, the compelling instance "represents" a regularity as, in comparative study, a sample of individuals "represents" a population.
3. Crucial case study presupposes that crucial cases exist. Whether they do or not in macropolitics can hardly be settled abstractly. All one can say on the subject is the following: (i) If they do not, no reasonable alternative to testing theory by comparative study exists. (ii) The inability to identify cases crucial for theories may not be the result of their nonexistence but of the loose way theories are stated, their relative lack of what we earlier termed "rulefulness." (iii) Any a priori assumption as to their nonexistence manifestly is a self-fulfilling prophecy, and it is difficult to see with what compelling reasoning such an assumption might be justified, (iv) If that reasoning rests on the inability to use controlled laboratory experiments in macropolitics, it suffices to point out that crucial measures in the physical sciences can be of natural observations (as, for example, the confirmation of Einsteinian relativity). And, obviously most important, (v) both hypothetical and actual examples of (apparently) crucial observations in the social sciences, including observations of complex collective individuals can be found—and would almost certainly be found more often if deliberately sought more often.
A more important question, therefore, is how a crucial case can be recognized. What guidelines can be used?
The essential abstract characteristic of a crucial case can be deduced from its function as a test of theory. It is a case that must closely fit a theory if one is to have confidence in the theory's validity, or, conversely, must not fit equally well any rule contrary to that proposed. The same point can be put thus: in a crucial case it must be extremely difficult, or clearly petulant, to dismiss any finding contrary to theory as simply "deviant" (due to change, or the operation of unconsidered factors, or whatever "deviance" might refer to other than the fact of deviation from theory per se) and equally difficult to hold that any finding confirming theory might just as well express quite different regularities. One says difficult and petulant because claims of deviance and the operation of other regularities can always be made. The question is therefore not whether they
are made but how farfetched or perverse the reasons for them (if any) are.
Generally speaking, "must-fit" cases are those that naturally have the characteristics of a well-designed experiment, so that mere forecasts must be as accurate as concrete, or even experimental, predictions. The case of Norway, as discussed above, is a case in point, if what is claimed about it is indeed true: that is, that governmental performance has been continuously high while social structure has thoroughly changed. The case would also be in point if social structure had remained nearly constant while a substantial change in level of governmental performance had occurred. But it may be admitted that such cases, naturally paralleling the artificial controls of the laboratory, will not commonly occur and that one will need unusual luck to find them out economically even if they exist.
An alternative is to focus inquiry on "most-likely" or "least-likely" cases—cases that ought, or ought not, to invalidate or confirm theories, if any cases can be expected to do so. The best-known example in political study probably is Michels's inquiry into the ubiquitousness of oligarchy in organizations, based on the argument that certain organizations (those consciously dedicated to grass-roots democracy and associated ideologies, representing classes whose interest lies in such democracy, having highly elaborate and pure formal democratic procedures, and leaders from the same social strata as the membership) are least likely, or very unlikely, to be oligarchic if oligarchy were not universal. (One may argue with Michels's choice of social units, his methods, or his findings, but the principle of the idea is surely sound.) Another example is Malinowski's study of a highly primitive, communistic (in the anthropological sense) society, to determine whether automatic, spontaneous obedience to norms in fact prevailed in it, as was postulated by other anthropologists. The society selected was a "most-likely" case—the very model of primitive, communistic society—and the finding was contrary to the postulate: obedience was found to result from "psychological and social inducements." A similar example is Whyte's study of Boston slum gangs, collective individuals that should, according to prevailing theory, have exhibited a high level of "social disorganization," but in fact exhibited the very opposite.
The "least-likely" case (as in Michels) seems especially tailored to confirmation, the "most-likely" case (as in Whyte and Malinowski) to invalidation. Methodological purists will find this a curious sentence. They will find it odd because philosophers of science deny the distinction between confirmation and invalidation. The philosophers are right to the extent that they argue that nothing can categorically prove theories in the manner of logical proofs, but that some findings may categorically invalidate them. But to the working scientist the distinction between confirmation and disconfirmation does have meaning, even if logic compels one ultimately to equate "validates" with "fails to falsify." There is a difference in nuance
between saying "this can't be so if a theory is weak" and saying "this must be so if a theory is powerful." Per contra, of course, any most-likely case for one theory becomes a least-likely case for its antithesis, and vice versa (e.g., the Boston slum was a least-likely case for the ubiquity of social "organization"), so that the distinction is one of research design and objectives rather than the inherent characteristics of a case. For the same reason, crucial case study obviously proceeds best when a case is treated in both senses and confronted with both theory and countertheory.
Cases that are extreme on pertinent measures can usually be regarded as crucial in the sense of being least-likely and most-likely cases. If, for example, one holds that democratic stability is directly proportional to level of economic development and inversely proportional to rate of economic growth (Sd ¥Ed /Er ), a very high value of Sd (as in Norway) should predict a high value of Ed and a low value of Er . If either is not the case, then grave doubt is de rigueur; and if both are not, then the theory simply cannot be right. The same holds, of course, if the starting point is the economic variables, or if one starts with extremely low stability (as in Republican Spain). And this logic follows, in particular, if the extreme measure is of change on the stability measure: a marked change, for example, from instability to stability. This appears to have occurred in Germany, which was highly unstable during the Weimar Republic but, by one calculus, ranks third out of twenty only to New Zealand and Sweden (with a score of 112.56 on a range from 118.42 to 67.19) in the post-World War II period. (This measure is not greatly at odds with a different and more complex one of change in German "political performance" made by Gurr and McClelland. If, in that case, a relatively low level of Ed and high level of Er , turned up, and the regularity statement were not rejected, any theory at all could be saved, presumably by casually adding explanatory factors or casually dismissing cases as "deviant."
Measures need not always be extreme to be considered crucial for theory, nor will any extreme measure do as well as any other. It depends on the theory and the circumstances of the case that provides the measure. For example, I have proposed elsewhere that (1) high governmental performance requires congruence between the government's authority pattern and the authority patterns of other social units in the society; that (2) other specified factors also affect performance levels; and that (3) the effects of congruence on performance are considerably greater than those of the principal other factors, which, by and large, work only to depress fractionally the level of performance predictable from congruence. If all these propositions are valid, any case of very high performance becomes crucial: it must permit accurate predictions about the independent variable, congruence. But a less extreme case may still be crucial, if a marked change in performance has occurred and noncongruence factors remain constant or change little (no doubt hard to know in advance of intensive
study), or (not so hard to know) if a positive change in performance is considerable enough to make it very unlikely that it has anything to do with increased congruence but only expresses the amelioration of other factors that previously depressed performance. For this purpose, a change from near the bottom to somewhere near the middle of a scale may suffice, although the more considerable the change the better.
These arguments about most-likely and least-likely cases, cases in which some pertinent variables change and others remain constant, extreme cases of most kinds and some that are not extreme, have a bearing on the question whether crucial cases may be found in macropolitics. It seems rather unlikely that all cases should be equally unlikely or likely, equally changeable or constant in all respects, equally short of extreme values on pertinent variables, and equally modest in change on the variables. More and less crucial cases should therefore be available en masse, and some of the more crucial ones identifiable without taxing preliminary studies—on their face value or because the special work required has already been done, even if for other purposes. The possibility, of course, remains that a particular theory, even if suitably stated, cannot be confronted by a clearly crucial case, or that such a case can only be found by wide-ranging preliminary observations and measures of many cases. But these prospects should now appear less daunting than might have been the case, and not at all inevitable.
4. To this point, the discussion has presented the case only for option 5: that case and comparative studies are best conceived as equally useful, alternative means for testing theories. The utility of case study and the weaknesses of comparative studies have been stressed only because the reverse is far more common in our field.
If logic does not intrinsically favor one method or another, the method to be used must be selected for other reasons, that is, out of practical, prudential considerations. One such reason may be the unavailability of clearly crucial cases. But assuming that not to be the case, probable costs and benefits become the pertinent calculus. On that calculus rests the case for the sixth option on case study, which pertains only to macropolitics. Inquiry into macropolitical units involves problems of scale and of sound comparison that point strongly toward crucial case study as the preferable method; the same considerations might also apply to stages of inquiry other than testing but are less telling there since rigor is at a lesser premium.
The most manifest practical advantage of case study is, of course, that it is economical for all resources: money, manpower, time, effort. The economies are not strictly equal to 1/n , where n is the number of cases studied comparatively, since some resources usually have to be devoted to
the identification of crucial cases, and some work needed to prepare rigorous case study is similar to that required by rigorous comparative studies. But even so they are likely to be considerable. This economic advantage is especially important, of course, if studies are inherently costly, as they are if units are complex collective individuals. Sociologists of knowledge might note, in this connection, that the growth of comparative studies coincided with the influx of unprecedented research monies and other facilities (research institutions, crowds of postgraduate students) into political study, and that my revisionism coincides with a sudden shrinkage in these factors. If that shrinkage compels us to develop less costly means to the same ends, it will be a blessing in disguise.
A second practical advantage involves access to the subjects of study. Samples of macropolitical units are always likely to be poor and highly uncertain in result: small in number (the population being small) despite the likelihood of a sizable range of variation. If, as is usually the case, they consist of contemporary cases, they are also bound to be a badly biased sample for all cases relevant to general laws. These problems in principle are compounded by practical problems of access resulting from the political exclusion of researchers (as in Burma), the inaccessibility of subjects in other cases, the lack of local research facilities (e.g., survey research organizations), and language problems for foreign researchers, among many other factors. As a result, contemporary comparative studies in macropolitics predominantly have one or more of three characteristics: (1) small numbers of cases chosen by intuition or for convenience; (2) the use, in wide-ranging studies, of readily available, aggregate data that are often quite untrustworthy and dubious indicators of traits they supposedly represent; or (3) think-pieces based on discussions of cases by "country-experts" in light of a common framework that are usually not at all well coordinated. Crucial case study may, of course, also suffer from problems of access. However, since crucial cases rarely appear singly, the likelihood of being unable to study properly even one of them seems considerably smaller than the likelihood of working with poor samples in comparative studies or that of having to tailor theoretical research to practical possibilities rather than the far more desirable vice versa.
A huge practical problem in comparative research involves special knowledge of the cultures being studied. The arguments made by the German exponents of the view that the Naturwissenschaften and Kulturwissenschaften are ineluctably different, and the arguments of the clinicians inspired by them are surely right insofar as they hold that "social facts," personal or collective, are embedded in widely varying, even in each case unique, cultural systems of meaning and value, and that one can neglect these only at great peril. Their position may not imply that "social laws" are therefore unattainable, but they do imply that the cultural sciences
impose a requirement of special cultural "understanding" that does not exist in natural science. Crucial cases can often be selected to satisfy this requirement for individual researchers, and it is always possible to acquire a great deal of cultural Verstehen in the course of in-depth study of a case if one does not already possess it. Even if we reject the notion of a special inherent requirement for cultural science, this point can still be made to rest convincingly on the question of special language skills and special historical and sociological knowledge of cases, for lack of which comparativists are often justly criticized.
At the very least, one can obviously, if other things are equal, go more deeply into a single case than a number of them and thus compensate for loss of range by gains in depth: to that extent, at least, the clinicians have a foolproof case. In crucial case study, the advantages of traditional scholarship, as displayed in configurative-idiographic studies, can thus be combined with those of modern technique and rigor. And it is also more possible to apply in crucial case study certain techniques developed in social science for overcoming the imperfections of single measures, especially the "triangulation of imperfect measures" technique developed in social psychology and applied, impressively, by Greenstein and Tarrow in political socialization research. (As an aside: the problems of Verstehen , depth, and imperfect measures are especially great in research into "political culture"; hence, it is rather astonishing to find that exponents of the political culture approach should also be devoted comparativists.)
Specialists in macropolitics have tried to overcome these problems by spawning general frameworks to be applied by different individuals in different cases or by deliberately organizing group research, hoping that the results will add up to coherent comparative study. The results have been uniformly disappointing. The frameworks have not been widely taken up, except as terminology, or have been widely butchered, and a whole volume could be written on the difficulties and meager results of different organizational frameworks for group research. At least until macropolitics develops a consensual paradigm, there seems to be no adequate collective substitute for the work of isolated researchers or, much the same, small and intimate teams of close collaborators.
At this point it should be clear that the practical advantage of crucial case study does not lie merely in resources. Case studies yield methodological payoffs as well. This is in large part due to the fact that they help avoid difficulties that are hard to reduce or abolish in cross-cultural research. Not the least of these are two related difficulties not yet mentioned: the problem of the proper cross-cultural translation of research instruments, a subject rapidly becoming a methodological field in itself and one that absorbs ingenuity and thought better devoted to theory construction and testing themselves. In addition, if we conduct crucial case studies, we
are far more likely to develop theories logically and imaginatively, rather than relying on mechanical processing to reveal them. More important still, we are more constrained to state them tightly and in proper form, suitable to testing: that is, in a manner that permits their deductive and predictive application to cases. Sloppiness in the forms of theory compatible with the criteria developed in the section on "definitions" above is not inherent in comparative studies (certainly not in the "disciplined" variety), but crucial case study involves far more compelling practical demands for the proper statement of theories, or else exposes far more manifestly when theories are not properly stated: that is, when nothingor a great number of different things—can be deduced for any case from regularity statements about it.
More thought, more imagination, more logic, less busy work, less reliance on mechanical printouts, no questions about sampling, possibly firmer conclusions (including that extreme rarity in political study, the conclusively falsified hypothesis), fewer questions about empathy: these surely establish a heavy credit. It remains to see whether any debits may cancel it out.
Objections to the Argument and Replies to the Objections
A number of arguments that might be, or have been, raised against my brief for crucial case studies should now be considered. None seem unanswerable, except in ways not very damaging to the argument. But others may see more merit in the objections than in the ways they are answered—and it is also possible that the really telling objections have been missed, or subconsciously avoided to restrict discussion to those that can be answered. The most telling objection of all, of course, would be that crucial cases simply are not available in macropolitics, but that has already been ruled out as unlikely for most, or many, theories. It is true that the literature of political science is not rich in crucial cases, but neither does it abound in efforts to find them; the most likely reason is that the very idea of crucial case study is alien to the field.
Comparative studies have the advantage over case studies of allowing one to test for the null hypothesis that one's findings are due to chance. Case studies may turn up validating or invalidating results fortuitously, not because theories are actually valid or invalid, but because one cannot determine by single measures whether or not this is so.
Answers . (a) The possibility that a result is due to chance can never be ruled out in any sort of study; even in wide comparative study it is only
more or less likely. Now, it is surely very unlikely that, out of all possible states of affairs (which normally are vastly more than the two faces of a coin and sometimes approach infinity), just that predicted by theory should fortuitously turn up in a case carefully chosen as crucial for the theory, and also improbable that in such a case the predicted result should, just by chance, be greatly out of line with actual observation. The real difference between crucial case study and comparative study, therefore, is that in the latter case, but not the former, we can assign by various conventions a specific number to the likelihood of chance results (e.g., "significant at the. 05 level"). Thus, if a theorist posits that democratic stability varies directly with level of economic development and inversely with rate of economic growth, and finds a case of extreme instability with high Ed and low Er , he cannot rule out plain bad luck, but the presumption that he has an invalid theory surely is vastly greater.
(b) Any appreciable likelihood of unlucky chance findings in a crucial case study arises from the fact that very short-run fluctuations generally occur in any measure of a variable. (Think of air temperature, or rainfall, or the climate of a marriage.) For example, a polity generally high in performance will probably experience some peaks and troughs in its level, and peaks and troughs will also occur in variables used to explain levels of performance. If we then measure a dependent variable at a peak and an independent variable at a trough, a deceptive result will certainly be obtained. But the remedy is obvious: observe over a reasonable period of time.
(c) There is, of course, also a possibility of observer bias in the observation of a case (seeing only what one wishes to see), hence of misleading, if not literally fortuitous, measures. That problem exists also in comparative studies, but not so acutely because of the prophylaxis provided by statistical measures of significance. But again, simple remedies are available. The most obvious is to recognize that falsifying a theory is to be reckoned as success rather than failure, and thus to redefine what one generally wants; knowing what is valid tells one more than knowing what is not, but knowing something to be invalid does signify progress and often provides very powerful clues as to what is valid. It is true that the reward structure of the social sciences overvalues positive findings, especially in publication—which may be why methods that maximize the probability of some sort of positive result (e.g., multiple regression) are so widely used. But such prizing of positive results, however tenuous, indicates scientific immaturity or insecurity and ought not to be perpetuated. It works like Gresham's law: bad theory crowds out good. (In fact, the question most frequently, and fearfully, asked about the preliminary version of this paper was: "What do you do if a prediction about a crucial case fails?" Answer: You publish the result—if editors permit and the
failure is informative, as it is almost bound to be—and you go on, trying to do better.) Apart from that fundamental point, the problem of observer bias arises more in configurative-idiographic studies than in the more rigorous varieties of case study—hence the stress on it in existing critiques of case study —and can certainly be reduced in the study of collective individuals by the same methods used to reduce it in comparative studies, such as the correct sampling of the microunits that constitute the case.
(d) In crucial case studies a powerful substitute for the null hypothesis can be put to work: testing for a theory's "countertheories," that is, likely alternative solutions if a theory is invalid, or a theory's "antithesis," if one is available. (This can also be done in comparative research, but practical considerations make it more feasible in case study, especially if theory and countertheories cannot be tested by exactly the same data.) The process of testing simultaneously for alternative hypotheses ("strong inference") has been held persuasively by John Platt as the correct way to put Baconian empiricism to work and, also persuasively, as the hallmark of the most rapidly developing hard sciences (high-energy physics and molecular biology). An example (not yet acted upon) from my own work on the relations between governmental performance and resemblances among governmental and other authority patterns may again provide a useful illustration of the procedure. "Congruence" theory rests, at bottom, on psychological learning theory in general and some of its specific variants. Since learning theory emphasizes the operation in behavior of gradually internalized orientations (something like habit, although not in the crude sense of the term), its obvious countertheory is one that postulates rational calculations in the light of one's current life-situation, untrammeled by the accretive influences of past learning: in short, an "economic" model of behavior. A theory of political performance could be rigorously developed on that basis. A crucial case study can readily be designed not only to determine whether a case lies off a predicted point on one curve but also whether it lies on, or nearer, a predicted point on a crucial countercurve. Since only one case is involved, the cost of doing both will not be much greater than that of performing one operation alone. Several advantages accrue. We may not merely establish that a theory is false but also why, at bottom, it is false, and what sort of theory would serve better. Furthermore, a finding near a predicted point on one curve but far off such a point on the countercurve, adds to one's case enormously. One may thus not only shed special light on one's theory, but also more general light on the more fundamental bases for further theory construction. And if both theories are confirmed, a false contradiction is exposed; if neither is, the same result is obtained, or sloppy deduction is unmasked. All this takes one far beyond the mere void of statistical nullness.
If preliminary comparative studies are required to identify crucial cases (e.g., cases extreme on pertinent measures, or highly changeable on a measure, or having the characteristics of natural experiments), the practical advantages of case study are severely reduced. And if they are severely reduced, certain practical advantages of comparative studies, such as their ability to provide data for reanalysis or simply data from numerous contexts, tend to tip the scales in their favor.
Answers . (a) Independent comparative study is not always required to identify crucial cases, simply because in an ongoing discipline the evidence needed to identify a crucial case often is already available. One may want to recheck that evidence or try to improve on it, but that is not tantamount to starting from scratch.
(b) Even if one starts from scratch, comparative studies specifically designed to uncover crucial cases can be very limited in scope, even confined to a single variable, and so much reduced in costs of all kinds. (For example, in the case of congruence theory, one might not initially do research on both performance and congruence, but on performance alone—a fact which, if realized earlier by the author, would have saved funding agencies much money and him much effort and time in designing research projects and carrying them out.) Common knowledge, no less than disciplinary knowledge, can also reduce problems of sampling in the search for such cases. For example, if the object were to discover a long stable polity, it would take more than ordinary ignorance to include, say, Germany in the search. Comparative studies to uncover crucial cases thus have little in common, in regard to required breadth of study or data requirements, with comparative studies as currently conducted.
(c) The fact that comparative studies provide "extensive" data from many contexts can be offset by the usual claim for "intensive" study: that it can provide more varieties of data (and is likely to do so not only if study is clinical but also if strong inference procedures are used). Such data, moreover, are as much subject to reanalysis as any others. They may not suit well the purposes of others, but then neither might those produced by comparative study; and virtually any body of data has import for a variety of purposes.
Several crucial case studies are always better than one. Some degree of additional safety is always provided by additional numbers. If therefore the intent is to be conclusive, crucial case study ends as comparative study anyway.
Answers . (a) The basic problem here again is the equation of success with confirmation. A single crucial case may certainly score a clean knockout over a theory (as Galileo's thought-experiment would have, had it been a real experiment, and as the falling feather and coin in the evacuated tube later did). The problem arises only if confirmation occurs. Because distrust is a required element of the scientific culture, confirmation only eggs us on to allay our own always remaining doubts and disarm those of carping adversaries: and thus we may want to know whether a theory that fits crucial case X also fits cases Y and Z, assuming these are also crucial, and whether, despite precautions and great unlikelihood, chance has tricked us after all. But the further examination of other cases can be restricted much more than in comparative studies that rest their case on sampling, and in such studies "added confirmation" may also be deemed advisable—in fact, is necessary if the studies merely establish curves rather than matching them.
(b) Conceivably, the most powerful study of all for theory building is neither the presently common form of comparative study (of cases studied randomly, or intuitively selected, or simply studied because they seem readily available or accessible) nor the study of single crucial cases, but, so to speak, "comparative crucial case studies." The case for such studies, however, is strong only to the extent that the most crucial cases available are not very crucial, so that high confidence in the results they yield needs the increment of other crucial case findings. Thus, the feather and coin falling in a vacuum leave virtually no doubt to the skeptic or the inquirer devoted to the tested theory, while a case of change in governmental performance highly unlikely to be due merely to the disappearance of performance-depressing factors, as against the factor posited to be required for high performance, probably leaves enough doubt to both to make desirable a further study or two of equal import. The study of such a more tenuous case might also, in some instances, be considered an especially powerful "plausibility probe," warranting the (costly) comparative testing of a probabilistic hypothesis like that logically implied in the congruence theory of governmental performance: that "in all cases, the correlation between performance and congruence will be high." The comparativist may treat any and all crucial case studies as plausibility probes, warranting the costs of using his favored method. The notion of the crucial case study was, after all, devised largely from that of the plausibility probe. The point is that he need not do so, unless the crucial case falls far short of the ideal.
Crucial case studies turn out to be comparative studies in disguise. For instance, when dropping a coin and feather through an evacuated tube
we take two simultaneous measures and compare them; or, when studying the correlates of a change from low to high governmental performance we again take two measures at different points in time and compare them. The distinction between comparative studies and case studies thus vanishes, along with that between the clinical and experimental modes of inquiry.
Answers . (a) Not all crucial measures are like that. Observing the deflection of light near the rim of the sun compares nothing with anything (unless it is claimed that it compares deflection with nondeflection). The same holds true if only high governmental performance, not change toward it, is the critical observation.
(b) It is by no means sophistic to maintain that the supposedly dual measures above are single measures, that is, measures of the amount of change in performance between an earlier and a later period or the amount of difference in the rate of fall of two objects. Such changes and differences can be used as points on a curve no less than measurements of static conditions at a particular point in time, and thus satisfy the exacting technical definition of case study.
(c) Measures of "more than," "less than," and "equal to" do presuppose two anchoring measures (see also Objection 5, Answer (d) below), but are not to be confused with comparative measures of samples, and n = 2 always suffices to establish them. Thus the distinction between case studies and comparative studies is watered down little, even if points (a) and (b) are disregarded.
Social science, especially on the macrolevel, does not have available measures precise and discriminating enough to make the sort of predictions needed for crucial case study.
Answers . (a) If this is true, the fact must bedevil comparative studies as much as any others, unless there is some magic by which many poor measures are equal to one that is good. Numerous poor measures can, of course, cancel one another out, or increase confidence in any one of them. But they can also make for increased distortion, that is, reinforce one another, and will certainly do so if a measuring instrument contains a consistent bias.
(b) What gospel ordains that social measures must be highly inexact and undiscriminating? That of experience? Perhaps; but perhaps only because of the prevalent assumption that nothing precise can be done in social study—surely a self-fulfilling prophecy if ever there was one. And while there is research there is hope: most of the natural sciences had to live
long, and managed quite well, with rather imprecise measures too, and ours have been improving.
(c) Highly discriminating measures are not required to put crucial case study to work. If the measure to be predicted is, let us say, the level of democratic stability in postwar Germany, it is not necessary to be able to say that the level is at 112.56 (àla Hurwitz), with reasonable assurance that it is not then at 112.57. It may quite suffice to say that the measure must come out somewhere between 8 and 10 on a ten-point scale, either because theory permits or because of recognized possible error in a measuring technique. The possibility of disconfirmation then still exists, and is, after all, about four times as likely as confirmation. There must, of course, be a limit on imprecision. The minimum requirement is that measures must not be so inexact that any measure considered to validate (or invalidate) a theory could also, because of inherently possible measurement error, be taken to imply the opposite. If we cannot do much better than that in the social sciences, we might as well not measure at all, in any kind of study. Therefore, arguments about imprecision impugn quantitative social science, not crucial case study only.
(d) If no more than a single point is measured, however, crucial case study does presuppose interval measures (even if measurement techniques do not allow discrimination between minute intervals). If only ordinal measures are available, then (and only then) one must have two measurements to confirm, or invalidate, the prediction that a variable will have a higher, or lower, value at one time than another, or under one condition than under another. Ordinal measures only state "more than," "less than," or "equal to," and that always requires two points of reference, as stated above. And, as also already stated, this still concedes next to nothing to comparative study, and perhaps nothing at all if the predicted measure is interpreted as the measure of a difference of some discernible magnitude.
Crucial case studies cannot confirm multivariate theories, in which one deals with one dependent and several independent variables. The social sciences (especially on the macrolevel, where crucial case study is most advantageous) deal with multivariate phenomena: phenomena in which a variety of determinants converge upon observed experience.
Answers . (a) Again one wants to know: What gospel ordains that social phenomena must be multivariate, or decisively more so than any others? One might answer, the phenomena themselves: look, for instance, at all the factors associated with revolution, or authoritarian political behavior, or political instability, or nonvoting. True—but not decisive, and quite probably pernicious. In the natural sciences, too, "causes" converge in
phenomenal experience, but notable successes have been achieved in cutting through the phenomenal complexities to simple theoretical constructs that are powerful tools in explaining particular occurrences or, by engineering, for bringing them about. (For example, the law of velocity of freely falling objects consists of one dependent variable, velocity, and one independent variable, time, gravitational force being a constant; but actual "falling" depends on many more factors, although some operate only with infinitesimal effects.) The problem of multivariate complexity largely dissolves if theory is thought of as a tool of explanation of the behavior of concrete individuals rather than as total explanation. And the probable perniciousness of the assumption that theories must be multivariate if phenomena are resides precisely in the fact that then they will be, thus missing beautiful and powerful simplicities, even if they might be found.
(b) Multivariate theories do not necessarily rule out crucial case study in testing, provided that one does not simply list independent variables that affect a dependent variable (x has some relationship to a, b, c, . . . n ) but specifies precisely the relationship of each to the dependent variable and their effects on one another. Newton's theory of gravity, for example, is multivariate: the dependent variable, gravitational force, is determined by two independent variables, mass and distance. But it specifies a direct relationship to one and an inverse relationship to the square of the other. Given the constant necessary to turn these ideas into an equation, predictions can be made for any case that may conclusively confirm or invalidate. The problem then lies more in the way multivariate theories are stated than in multivariation as such. The job of avoiding that problem is immensely difficult (most of us probably need not apply) but it ought to be tackled, even though here again the prevalent reward structure of the social sciences discourages the attempt to do the better work that is more likely to fail, or to be perceived as failure.
(c) A real problem is that a case finding may be the result of complex "interaction effects." The careful choice of a case may allow one to discount that as a probability, but never altogether, and the fact that the problem might also queer comparative findings (more factors are nearly always interacting than a research design takes into account or allows one to separate) does not abolish the difficulty. The only sensible response is to treat the possibility as reason for continued doubt of some magnitude or other, and thus for further research. If the findings confirm a theory, that simply implies that one might want additional assurance in another pertinent instance. The point here is exactly the same as that regarding the possibility of "chance" results. If the findings disconfirm, and one has strong prior reasons to consider a hypothesis valid (e.g., because of various sorts of estimates of plausibility), the sensible course is simply not to give in all at once but to try another crucial test. In neither case is comparative
study the required solution. The responses simply involve added confirmation, or added disconfirmation, by further crucial case study. And studies of additional cases for added assurance are not, strictly speaking, "comparative" studies.
Crucial case studies cannot test probabilistically stated theories.
Answers . (a) Agreed.
(b) Theories need not be probabilistic, and the more powerful are not, even if the occurrence of phenomena is. Here, once again, the difficulty lies in confusion between theory as a tool of explanation and theory as the full explanation of concrete events. (That confusion is especially reprehensible in this case because probability statements, inherently, are not total explanations either.) The position rests also on two further fallacies: that if something is true probabilistically of a numerous set of cases, then the probability of its being true is equal for each individual in the set (which is true only in rare cases, like tossing fair coins); and that no mere probability can be deduced from a "law" (it can, to the extent that the conditions under which a law is supposed to hold absolutely do not in fact exist, or to the extent that a law treats variables as constants).
(c) Probability statements are used more often than they need be in political study because of the uncompelled belief that they must be, which works, like other methodological assumptions, as self-fulfilling prophecy.
Even if all these objections are answerable, it is highly suspicious that so many should arise. Case study seems more susceptible to challenge than comparative study, in regard to which most of these problems are not even raised.
Answer . The essential difference here is not the volume of issues, but that the issues differ because the methods differ. Moreover, comparativists have only recently begun to raise important difficulties inherent in their method, especially on the macrolevel. But, in a relatively short time, an impressive number of difficulties in the method have turned up. After all that has recently been written about difficulties in comparative crossnational study, or even in microlevel studies—problems concerning the selection and proper number of cases, the feasibility and trustworthiness of research instruments (like survey research schedules), the comparability of data, or the utility of various data processing techniques and modes of inferring regularities from numerous data (e.g., various types of significance tests, attributions of causal paths to correlations, attributing lon-
gitudinal characteristics to synchronous data)—it is impossible to take seriously the position that case study is suspect because problem-prone and comparative study deserving of benefit of doubt because problem-free.
Case study in macropolitics begins in idiography and is rooted in the traditional conception of clinical study. In recent years the position that case study cannot be "nomothetic" has been increasingly attacked in psychology, the very field that made the distinction between idiographic and nomothetic study sharpest and most insuperable. But the notion of nomothetic case study has not been taken far. If not conceived as the application of established theory to case interpretation, it has merely been represented as case study in which rigorous methods, similar to those of "experimental" study, are used and/or in which individual experience is used to help find clues to general theories. If more has been claimed, as by Chassan, it has turned out that the term case study ("n = 1" study) is indefensibly applied, by confusing a case with a concrete person rather than a measure.
My object has been to take the argument for nomothetic case study far beyond this point, following up clues provided by examination of more modest arguments in favor of it. The point has been to relate "n = 1" studies to all phases of theory building and particularly to stress the utility of case study where rigor is most required and case studies have been considered least useful. Comparative studies have not been attacked, except on practical grounds in limited fields of inquiry; nor is it claimed that appropriate case studies are always available for all theoretical purposes, and absolutely not that any kind of case study will serve all purposes. The types of case study are numerous, and that recommended for going beyond formulating candidate-theories is extremely rare in our field or related disciplines.
The argument thus is mainly abstract. There is no track record worth mentioning. But if the horse is run, the results just might be astounding—or, possibly, abysmal. The point is that trials seem in order, not in place of but alongside comparative researches.
It should be evident that case study can be nomothetic only if cases are not selected for the theoretically trivial reasons that nowadays predominate in their selection: because one knows the language, finds a culture congenial to live and work in, can get money for study in it through an affluent area program, considers the case important for foreign policy or otherwise publicly marketable, finds it exotic, and the like. Considerations of congeniality or publicity are well and good if other things are equal, not otherwise. And not the least advantage of crucial case studies is that they
may permit one to study intensively attractive or convenient cases without sacrifice of disciplinary conscience.
Chapter 8 deals with a methodological subject, the observation of "subjective" culture and thus might well have been included in this part of the book. It is not because it is best read as a companion piece to chapter 7, for reasons explained in the introduction to that chapter. It should be noted, however, that chapter 8, like the essay on case study, emphasizes the critical significance of testing in proper procedure. We do not subject theories to tests—especially our own theories; and there has been distinctly less emphasis on that aspect of method than others, especially data gathering and processing, and, to a lesser extent, conceptualization and operationalization. These are all important, but they fall far short of genuine "results" if not severely tested. Chapter 8 not only reiterates that argument but also tries to make a more novel point: testing is significant also for obtaining reliable and valid data of certain kinds, not just as the final stage of rigorous theoretical inquiry.