One—
Background

The essays in this book were written over a period of thirty years. They might have spanned six years more, my first article having appeared in 1955.^[1] Political science was very different then, and not just because of its operative "paradigm." The journal in which my first article appeared still paid its contributors. One of its coeditors was William Robson, a professor of public administration at the London School of Economics and a luminary in the Labor party and the Fabian Society. The other was Leonard Woolf, who, of course, was not a professional political scientist at all. Evidently, Max Weber's soul-searchings were not yet common. We did not yet worry about the relation of science to political action. Nor did we fuss about value-neutrality. And the dividing line between "scientific" and "literary" writing had not yet fully hardened.

The next three decades were a heady period of transition in the field, not least in my subfield, comparative politics. The changes that occurred in the field after 1960 (a short period, as academic time is measured) surely produced an instance of scientific "revolution." The first cause of that revolution can as usual be found in uncomfortable facts that accustomed modes of thinking in the field left puzzling. My generation in political science lived under the shadows of the Nazis and the holocaust; of Stalin; of the use of nuclear weapons; of the large-scale appearance of new nations; of the disappointment of democratic expectations in these nations; of the appearance of issues of political development; and much more. Old, familiar methods of study in political science left all these events and processes mystifying.

The "revolution" in political science was profound. It even involved questioning so basic a matter as the way political scientists defined their subject of study. David Easton was the leading figure in raising that issue.

(A few people, no longer read in the 1950s, had raised the issue during the 1920s—for instance, George Catlin in The Principles of Politics .) I also raised it in an article not republished here.^[2] The article went far beyond Easton's reformulation of the way political scientists conceived their subjects, politics and political systems; although what I argued remains a basis of much of my work, its impact on others was close to zero.

The overriding purpose of the revolution in political science was to make the field more scientific, in the manner of the "harder" and more successful fields of inquiry. That revolution, it seems to me, took a wrong turn from the start. A reaction against its objective has by now occurred, and political science and comparative politics have as a consequence become fields divided against themselves—fields in which more or less radical extremes are engaged in an unfortunate Methodenstreit that can bear no fruit but, until we outgrow it, can do much harm. In brief, the field, while I have worked in it, has traveled from its 1789 to its Thermidor, but not yet to anything analogous to Empire, Restoration, or what Lyford Edwards considered the last stage in the "natural history" of revolutions: a return to normality. Sad and in many ways ironic; but this course has not been dull; at least we took little, or nothing, for granted.

I discuss these points in some detail in this chapter. I also try to clarify the admittedly almost invisible thread that ties together the disparate essays that follow and explain why they are in fact disparate.

Consider first the general attempts to transform comparative politics (to which chapter 3 provides an introduction, at an early stage).

Our Estates-General, as it were, was an interuniversity seminar, funded by the Social Research Council; it met in the summer of 1952 at Northwestern University. The council, at that time, provided resources to bring together, for substantial periods (six weeks, in our case) and for intensive collaboration, groups of scholars in the same field but from different universities. Such scholars would otherwise have had only superficial contact through publications, private correspondences, or in the turmoil of the brief meetings of professional societies. (It seems unfortunate that the council long since discontinued providing the petty funds needed for such meetings of minds, but that is not to the point here.)

In our case the initiative to bring together a seminar in comparative politics was taken by Roy Macridis, who then taught at Northwestern. Macridis gathered a group of mostly youngish Turks—most of whom have gone on to superlative careers—who agreed that comparative politics needed a thorough overhaul. My own role in the seminar was peripheral in most ways and central in others. Macridis, a former teacher of mine at Harvard, brought me into the group as a graduate student rapporteur . The official function of rapporteurs is, of course, to take and distribute notes

on the discussions among the full-fledged participants. But it is hardly a secret that, by obvious devices, rapporteurs can, and perhaps must, influence and slant the notes. Besides, Macridis had asked me to write a general paper on the state of comparative politics and possible directions for radical change in it, as an initial platform for the group's discussions, and I wrote a final report on what the seminar seemed to agree upon. Thus my role in the field's 1789 hardly was that of a mere note-taker.^[3]

As usual the "revolutionaries," including myself, knew much better what they wanted to tear down than either the nature of their hoped-for academic millennium or how to bring it about. One of our grievances was that comparative politics was not really comparative: the study of governments was divided into American government, on one hand, and all non-American governments, on the other. As for the other countries, comparative politics seemed to us parochially oriented to the major powers of Europe (although, by then, area studies—Europe, rather incongruously, was not considered an "area"^[4] —had been well launched, offsetting the long Eurocentered bias in the field). The field, because of its emphasis on formal-legal (constitutional) rules, also seemed "vertically" truncated, neglecting the consequences for politics of its social setting. It seemed atheoretical as well—essentially descriptive, with some offhand interpretations sometimes thrown in. A particular shortcoming arose from the static nature of almost all comparative political studies: the lack of theories of change. Even though it was common to begin the description of a polity with a brief chapter on its history, that is not at all the same thing.^[5]

All this we wanted to change, as did a later conference on the subject at Princeton (1953), and a Social Science Research Council committee on comparative politics was established after the Princeton conference.

It was only natural for embryonic scientific revolutionaries to flounder during the first years when most scholars in the field continued to work in familiar ways, as should have been expected. It was also expected that the revolutionaries would want quick and great results. The effect, unfortunately, was a growing fixation on what is usually now called "grand theory"—theories that, rightly applied, potentially can either explain everything or provide a "framework" (whatever that is) for doing so. There was a tendency to try to leap directly from start to finish: in Evelyn Waugh's sarcastic characterization of the United States, to proceed "from barbarism to decadence, skipping the intermediate stage of civilization." What seemed most wanted was a sort of equivalent of unified field theory, which left the narrower theories to be worked out later. Robert Merton has described this approach as "all-inclusive speculations comprising a master conceptual scheme from which. . . . to derive a very large number of empirically observed uniformities of social behavior."^[6]

All-inclusive theoretical system building had a distinguished past in mod-

ern times, chiefly in German thought, for example, that of Hegel and Marx. But certain contemporary American influences seem to me much more responsible for the tendency to construct grand theory in comparative politics. A major influence was Thomas Kuhn (probably to his dismay). In 1962 Kuhn published his splendid, provocative book on "scientific revolutions."^[7] The book challenged the common view that progress in the "hard" sciences has been steadily cumulative. Kuhn argued, instead, that progress has occurred fitfully, through convulsive ("revolutionary") changes in virtually all aspects of a field: that is, through the collapse of a consensual "paradigm" of inquiry and of the "normal science" based on it and the rise of a fundamentally different paradigm. Just exactly what the idea of a scientific paradigm, and a shift in paradigms, meant to Kuhn was never entirely clear to me, except through example—the term referred to something like the change in astronomy from the Ptolemaic to the Copernican system (about which Kuhn had written earlier) or, in physics, from the Aristotelian to the Galilean concepts of motion. Beyond that, what mattered was consensus on how scientific work gets done and how progress is achieved.

At any rate one soon heard that comparative politics, being in process of revolution, needed a new paradigm. But this was generally taken to mean all-inclusive theory, in Merton's sense and in the German sense of a Weltauffassung , a full-fledged theoretical system, not a mere Weltanschauung , a perspective for viewing experiences.

This meaning, it seems now, resulted from a confusion of Kuhn with Talcott Parsons. Parsons, who had studied in Germany, devoted his academic life to the related tasks of constructing a "general theory of action," beginning with his mammoth first book and culminating in the multiauthored Toward A General Theory of Action of 1951.^[8] In the process Parsons developed a highly general (and rather idiosyncratic) "systems" theory, elaborated in a set of "pattern-variables" held to be "functional prerequisites" for the existence and persistence of any social system. Parsons generally referred to his "theory" as a "frame of reference," which leaves cloudy whether he meant it to be merely a potentially useful basis for coherent theory building (an unusually large, detailed Anschauung ) or a theory that already contained less grandiose theories, as special cases. I think the second view is correct; consider that in later work, with Neil Smelser, Parsons tried to swallow economics into his framework,^[9] before beginning the process of absorbing political science.^[10] (I was asked to coauthor a book on the subject, but it was never begun.)

If Parsons and Kuhn are put together, grand theory—all-inclusive theory presented as a ready-to-wear scientific paradigm—results. In the 1960s and 1970s political science was in fact inundated with such "theories," which waxed and waned. That is not to say that less grandiose work, on special

problems, was not also going on. But grand theory was the prevalent aspiration and tended to carry off the prizes. In rough order we were offered, as would-be paradigms, group theory, a political version of functionalism (the most conspicuous "framework" at the time I wrote chapter 3 below), a revived version of power-elite theory, two kinds of political systems theory (Almond's and Easton's), political-culture theory, and political rational-choice theory, not to mention a number of more ephemeral schemes. A small industry of books attempting to explain the would-be paradigms also developed during this period.

My attitude toward this activity was mixed. I taught seminars in comparative politics during the period, and in these I expounded and criticized the grand theories. After all, they played the central role in the field. Some of them also certainly were clever, based on erudition, and made for good discussion. But the whole enterprise seemed to me barren because it seemed to have things upside down. One does not, godlike, create a "normal science" out of chaos. Where such a thing exists it grows from the bottom up, through the results of narrower inquiries; broad theories are developed to subsume narrower theories rather than the narrower theories simply being elaborations of a priori broader theories. Still broader theories are developed in the same way. Grand theories I regarded, and still regard, as ultimate and probably unattainable ends. In other words I opted to work on what Merton called theories of the middle range, perhaps by taste (or ability) but also under the influence of philosophers of science like Karl Popper and Gustav Hempel.

Granted that some perspective on one's subject always underlies inquiries into it. It may also be true that it is better to be explicit about one's perspective than to leave it implicit—though I am not at all convinced of this. But if perspectives are regarded as finished theories or frameworks merely to be filled in by such theories, awful things tend to happen. Perspectives become dogmas, and dogmas radically split scholars. They create sectarian conflicts instead of mutual support and sensible divisions of labor. They prevent precisely the cumulation of knowledge that the frames of reference are supposed to facilitate. Intellectual sins result as well. Theories often are little more than translations into the jargon of a would-be paradigm; devious means are used to save (grand) theory; and results that seem clearly to refute such theory tend to be presented as supporting it (with the addition of an epicycle or two or more): Rikerian coalition-theory, a branch of political rational-choice theory, is a good case in point.^[11]

Moreover, when fields are in such a conflict-ridden, utterly unintegrated condition, wholly unwanted reactions to the mainstream are almost bound to occur, making bad worse. In comparative politics, two such reactions to the "revolution" that started in the 1950s now seem to be in full swing. One creates a danger of pedestrianism (not a major problem before the

1950s). This reaction is giving priority to techniques over substance—not least, nowadays, aggregate statistical techniques. Such techniques are useful tools of inquiry, but when they become primary over substance, grotesque results emerge.^[12] The other reaction threatens to produce highflown obscurantism. It involves the renunciation of rigorous, theoretical problem solving in favor of the shadowy worlds of hermeneutics (of purely interpretative social science, in which "meanings" are already regarded as explanations), or one or another "critical" dogma (usually neo-Marxist or quasi-Marxist), often on the assumption that the task of social scientists is not so much to understand the world as to criticize and change it. Both reactions are only too alluring. This is true not only because we seem to have "progressed" only from disrepute to disarray, but also because the reactions free one, in different ways, from the burdens of hard thought. Both permit one, essentially, to be "idea-free": either the techniques, applied to data, churn out results; or ideas are supplied by presumed empathy or by prefabricated systems of ideas.

To return to the earlier point: Inquiry cannot proceed without some perspective on one's subject, wherever that might come from: for example, "normal" science, personal values, class position, gender. Whether or not it might be better to leave such perspectives as silent major premises, one simply cannot do so in a period of open ferment at that level of inquiry. For reasons too complex to go into here, I concluded some years ago that only two of the grand theories of comparative politics were legitimate contenders for the status of points of departure in the field: political-culture theory and rational-choice theory. (I have discussed the reasons in an essay not republished here.)^[13] At one time, I contemplated doing research to determine, via predictive "strong inference" procedure, which of the two was the more promising tack to take, but I regret that the research project was never done. Still, faced by the choice, I opted for the culturalist perspective (for reasons also too complex to discuss here) without being a "true believer." However, chapters 7 and 8 in this volume may be read as a defense of my choice, in that there I try to disarm the most common criticism of culturalist theory in political science.

To avoid possible misunderstanding, it should probably be added that what I have written about comparative politics (politics at the macrolevel) does not apply to the study of political "behavior" (politics at the microlevel, in which I include political psychology, participation, most studies of interest groups and parties, and, especially, studies of voting behavior and public "opinions"). That part of political science, in which ferment started much earlier—as far back as the 1920s—was never encumbered by grand theory. It was rooted in, and remained in, the middle range—a fact that might well have been taken as a lesson by inquirers concerned with the political macrolevel. If microlevel study in political science has had a

demon, it has been mindlessly technical work—relying too much on statistical techniques to convert data automatically into theory. More recently, one grand theory of macropolitics, rational-choice theory, has also invaded micropolitics, for dubious reasons and with dubious results (see chapter 11). But that is not apropos here.

My own ineffectual attempt to set political science on a new course did not involve grand theory. It grew out of a theory of the middle range. In 1961 I wrote a monograph on the conditions of political stability and instability, especially in democracies, published five years later as an appendix to a book (see part III of this volume). The core argument of the monograph was that political stability results from "congruence" (similarity, defined in special ways) between the authority patterns of governments and those of specified nongovernmental institutions and organizations. The theory was only tenuously based on empirical observation, and because rigorous testing was bound to be a costly matter, I conducted, to help determine whether testing was worthwhile, a probe into the plausibility of the theory in a country that it absolutely had to fit and about which I had only minimal prior knowledge.^[14] Convinced by that inquiry that testing was in fact worthwhile, I undertook additional testing through a group project (with Ted R. Gurr as codirector) that produced much print but no definitive test.^[15]

Such undertakings often have quite unexpected results. In this case the most important unanticipated consequence was that the subject matter of political study came to seem ill conceived to me: there was no reason why it should not, and every reason why it should, encompass any and all authority patterns of social units, both large and small. The focus solely on the state, and matters that are state oriented (political parties, interest groups, and so on), struck me as both logically specious and stultifyingly limited in scope, space, and time.^[16]

So I set out on a lonely journey intended to transform political science at its most basic level: the way it conceives its subject. The initial result was an article published in 1973.^[17] In a book (coauthored with Ted R. Gurr) I pursued the matter on a much larger scale, discussing in great detail the dimensions and subdimensions of the complex phenomena that are authority patterns and the problems of operationalizing them and suggestions for doing so—for the accurate description of particular cases and for potential, systematic comparisons. Gurr and I also added rather lengthy speculations on the causes and consequences of variety in authority patterns.^[18]

All these ideas fell on deaf ears. Although nothing in what was argued precluded concerns with governmental phenomena, the field was too state oriented to pay attention to so radical a proposal. I have in fact been told

that the book written with Gurr was the major mistake of my academic life. I agree that the book was the greatest failure of my career, judging by its impact (nonimpact?), but I do not think of it as a mistake. It strikes me now as rather overdone, but still fundamentally right in its central argument and useful in its elaborations. Perhaps others will also come to regard it as such, though I doubt it.

In my own work, nongovernmental patterns of authority crept back in, as an independent variable, through work since 1985 on "civic inclusion"—the tendency over time to include in politics, in workplace decision making, in education, and in other institutional realms, people previously excluded from them. I came to this interest via Tocqueville's argument (to which I assent) that social "development" involves irresistibly increasing equality in "the condition of men," and via the large literature on the disappointing results of growing political equality: the literature on nonparticipation, new oligarchies, "crowd" and "mass" behavior, and political machines. That interest led to inquiries into authority relations in lower-class families, in supposedly participatory workplaces, and in lower-class schools (these matters are discussed in part V of this book). And so the old interest in nongovernmental authority remains alive, after some odd twists and turns and in the context of a very different concern.

I would not be distressed if the essays in this book were simply regarded as disparate, the products of an incorrigible fox. I do not dislike hedgehogs, although I do not particularly admire them either. Still, we are told that all products of the mind contain some elements of autobiography, even if deeply buried. And I have long been conscious of a unifying thread in what I have done. To be sure, the work involved led to some efforts in which autobiography played no discernible part: usually conceptual or methodological efforts; but even these grew out of personal concerns. When I review the whole, it looks to me like pieces of a jigsaw puzzle, where most fragments are missing, as is the whole picture.

Growing up in Germany just before and after the Nazis came to power hardly is a forgettable experience, and it hardly leaves one with a sense of intact understanding. The experience certainly left me in a state of mystification, a sense of the world as an enigma. (I recall reading the beginning of Kafka's Amerika as an uncannily naturalistic rendering of my own experiences as a child immigrant to the United States.)

The collapse of the Weimar Republic and the rise of the Nazis coincided exactly with the waking of my political awareness. I remember it now only in the disconnected pieces expected of early memories.

At the beginning, strange men appeared in brown uniforms, wearing an odd symbol on armbands; they were given to singing and marching in torchlight parades. No one seemed to take them seriously in the discussions

I was allowed to listen to in my talkative family, and childhood and school on the whole took benign and cheerful courses. The men in brown seemed like figures in a prolonged masquerade. I do recall an early false note, when talk dwelled on depression and unemployment; but this supposedly dramatic event seemed to affect my family only through a sudden shortage of salad oil. Soon, though, much greater dissonances occurred. I remember vividly the fateful January 30, 1933. A man of no great note, whose rantings I had sometimes heard on the radio, had become chancellor, succeeding a number of other inconsequential, and transient, men; the town in which we lived (near Frankfurt) was decked out in flags bearing swastikas; and when I came home from school an air of calamity seemed not only to possess our house but also to take possession of me. Then things appeared to settle down for a while—but only for a while. The later experiences that I recall in bits and pieces have no firm chronological order.

One of the first memories of later events was being forbidden to visit or play with my best friend, the son of a government official. It soon became apparent that the reason was an ineradicable blemish, the fact that I was a Jew; and I became convinced myself that being a Jew was, somehow, shameful. (Perhaps that helps explain the later assumption, which takes the shape of "positive theory" in my academic work, that our realms of self-determination are severely constricted by forces somehow thrust upon us.) I remember also the boycotts and the boarding up of Jewish shops. There were three especially icy peaks in that range of experiences. One night some men came knocking on our front door and asked for my father. I heard the knocking and demand and then went back to sleep. The next day I was told that the men had ordered my father to dress and my mother to bid him farewell because she would not see him again. But the next morning he was back; he had worn his Iron Cross, earned in the First World War, to the ordeal, and the local fat man and bully had made plain that harm would be done to a decorated German soldier only over his considerable body. That added dread to earlier feelings of shame and the vague sense of disaster. During that time, too, going to school usually involved passing through a gauntlet of insults, threats, and frequent barrages of stones. So I took to avoiding the streets, and instead walked in lonely alleys and fields, in the safety of an unpeopled world. In 1934, my parents released me from that ordeal by sending me to a Jewish secondary school in Frankfurt. That was of course a much more anonymous place, though also lonely and, in its own way, enigmatic to a ten-year-old boarder in a house of strangers. In December 1936 that interlude also came to an end when my parents managed to send me to America: a rescue that felt like an expulsion into exile.

All this occurred before the much more atrocious events to come, from the Kristallnacht to the final solution. And I have omitted the more mun-

dane experiences of that period: incessant paramilitary marches by brownshirts and blackshirts; waves of anti-Semitic propaganda; emigrations; friends becoming strangers; random mayhem; growing despair. For each Jew (and others), Nazism had its special abysses of experience, but Nazism was not simply a set of disjointed personal memories. It was a whole world out of joint, which touched and polluted every aspect of social life. Of course, viewed a half century later, the peaks of personal and collective experience overshadow all else. When I recollect them, I still feel deep revulsion (coupled, no doubt, with sublimation).

What I have written should suffice to make the point that my academic work is rooted in autobiography that, despite appearances, gives it coherence. I have no doubt that the very choice of political science as a "major," as soon as I discovered its existence at the university, grew from a deep wish to understand the forces mysteriously governing politics that also seemed to govern my life. But I soon became a disenchanted, though not yet openly rebellious, student of politics; I already had experience of the consequences of being "different." Although the time was postwar and postholocaust, my professors seemed still to live in a well-ordered world of textual elucidations, of constitutional descriptions and interpretations—in short, of polite and genteel scholarship. In that world the Weimar Republic, for example, still incongruously loomed larger than the Nazi period. Nazism, of course, was mentioned, but without noticeable grasp beyond the perception of villainy (inspired, one professor told us, by Hobbes). In general, it seemed to be regarded as a deviant episode, a singular upheaval, its horrors traceable either to a misguided electoral system or to too-easy legal dismissals of chancellors or else to demonic flaws in the German "character." Certain "political theorists"—for example, the theorists of mass society and power-elite from Robert Michels to Joseph Schumpeter—were dismissed as antidemocratic "irrationalists" who were therefore wrong, as were Graham Wallas and Walter Lippmann writing about instincts and stereotypes in early political psychology. I could not see that being congenial to democratic myths might be a criterion of validity. And the irrationalists spoke to my inner world much more comprehensibly than the others. I kept my own counsel about this, for fear of being myself consigned to the world of misanthropic, thus mistaken, political scientists. But by 1952 I was certainly ripe and eager for "revolution" in comparative politics; in the condition in which I began study in the field it seemed incapable of explaining anything significant.

The problems on which I have always concentrated—political stability and instability, political violence, and the politics of "inclusive" (mass) societies—are sufficiently accounted for by these personal experiences. But some other points, personal and otherwise, should be added.

First, my interests came to encompass a much wider scope than the German experience. This occurred in two ways. Simply through the normal processes of education, it became evident that Nazi Germany was hardly unique, even in its most egregious aspects—as in fact I had always surmised; the holocaust, for instance, was only one case of the "killing fields," from the slaughter of the Anabaptists to Stalin's purges and beyond. Probably more important than this realization was that, while studying and living in England, I became aware of both a fundamentally decent and fair society and undisrupted history as a counterpoint to earlier experiences. Thus, added to my American experience, political "stability" became a real phenomenon, not just an abstract opposite of instability (and of the dark side of mass behavior). This is the personal background to the essay that is chapter 5 of this book, an essay that played a pivotal role in my academic life.^[19] Still, even in that essay the earlier experience is central, not only in the problem tackled in the essay but, much more, in its argument that stable democracy is the less frequent case, perhaps even a rare exception, contrary to all I had been taught.

Second, I was never so much intrigued by the egregious in Nazism (and in politics generally)—either the demons or saints it mobilized—as by the general tenor of life in the Nazi world: the minutiae of life in that frenzied society. Hannah Arendt found evil "banal" even in Eichmann; to me the banality of evil and essence of Nazism existed much more in day-to-day relations, which after all are by far the greater part of social life.

No doubt that is why what gripped me most in Crane Brinton's Decade of Revolution was not the guillotine but his discussion of "the little things" of the Terror: its "revolutionary" clothes, its bric-a-brac, its toys (miniature guillotines, etc.), its penchant for renaming, even its revolutionary beds.^[20] Brinton writes:

The guillotine, prison, Jacobin dubs, political elections, even political riots—these might all be avoided, especially by the obscure; but no one could altogether avoid clothes, theaters, furniture, cafes, games, newspapers, streets, public ceremonies, birth, death, and marriage. On all this, the Revolution . . . left its mark. It broke in rudely on the accepted ways of millions of humble people, turned their lives inside out, made them take part in a public life keyed to an amazing pitch of collective activity.^[21]

So it was in Nazi Germany, and in my childhood.

The fact that I have avoided writing about the Nazis' worst excesses may well have psychological roots, but it is surely also true that some version of "normal" day-to-day life went on within the system. Moreover, I suspect that if one could make sense of some of the petty inanities of that life—like the edict issued to Walter Nolde to stop painting, the subject of Siegfried Lenz's brilliant novel Deutschstunde —much else might also fall

into place. Lenz's novel in fact is the only work on Nazi Germany that managed to induce in me a feeling of illumination, but of course not of the social-scientific kind.

This brings me to a final point. I am not at all sure that the understanding I have wanted is attainable through social science. At bottom it involves passions that may simply defy dispassionate understanding. They may well be material fit only, or more, for artistic empathy and visions. But social science is the way I have chosen to grasp what I can of the world. And having chosen that way, I have tried to live up to its vocational demands. In regard to these I have long tried to follow Max Weber's strictures, which I find wholly convincing (as described in chapter 2): to keep passions out of the classroom and academic publications, and to cultivate a certain coldness and distance from the phenomena—especially where personal emotions are most involved and the phenomena closest to personal experience. It is child's play to be engagé when one's deeper emotions are safely uninvolved; it is much more difficult to cultivate detachment from one's own wounded sensibilities.