THE CAUSAL DEVOLUTION Andrew Abbott Department of Sociology University of Chicago Lecture on Causality in the Social Sciences in Honor of Herbert L. Costner Delivered at the University of Washington on April 24, 1997. Copyright 1997 Andrew Abbott When we are all dead and forgotten, some scholar will sit in a quiet office at the end of a weary afternoon and gaze in perplexity at his notes on the sociological journals of the 1960s, 1970s, and 1980s. He will wonder just what it was that sociologists believed, what they really wanted to say about society. They wrote no personal letters, they kept no diaries. Only a handful wrote personal reflections. There remain only the written texts of the journals. He writes the following paragraph: The people who called themselves sociologists believed that society looked the way it did because social forces and properties did things to other social forces and properties. Sometimes the forces and properties were individual characteristics like race and gender, sometimes they were truly social properties like population density or social disorganization. They called these forces and properties "variables." Hypothesizing which of these variables affected which others was called "causal analysis." The relation between variables (what these sociologists called the "model") was taken as forcible, strong. In this view, narratives of human actions might provide "mechanisms" that justified proposing a model, but what made social science science was the discovering these "causal relationships." As one writer - a man named Blalock - put it (1960:275) "These regression equations are the 'laws' of a science." The quote seems to round out the paragraph, and the scholar pushes back from his keyboard. Somehow it is not right. The prose seems wooden and one- dimensional. Can this really have been the essence of what those people really thought? He wonders.... Luckily, of course, this future moment has not arrived. Our reflections this evening about the role of causality in social science are not considerations of a dead and fixed event of the past, but rather of a living idea that can be reshaped, redirected, even redefined. We live inside that idea, not outside it. More important, we understand all the hidden things we mean by the idea of causality, the things that aren't in fact apparent in our articles. We know quite well, for example, that this is not the view the classical social theorists took about how society works. Western social philosophers have generally taken human action as central to social life, and, with some exceptions, the classical thinkers of social science generally followed their lead. We know, rather, that this theory is the vernacular social theory of the methods courses that we all take within a year of arriving at graduate school, a set of things we come to take for granted when we apply standard empirical methods. Initially, of course, we all remember the objections and the caveats. Regression relationships, as our instructors told us and as we tell our students, are the mere entails of real social action. Action is the reality. Causal analysis merely studies whether the numbers come out the way they would if our theories about action were right. But familiarity and practice send the caveats packing, and they become quite invisible to the reader of our work. In economics, it is true, an article begins with a set of formal action theories in the microeconomic tradition. Only once this ritual is performed do we settle into the comfortable technology of regression methods, with a quick glide past the problems raised by the semantic connection between the theoretical formalities and the estimating equations. In other empirical social sciences, an article's theory section characteristically comprises a few illustrative narratives of "possible mechanisms." These provide plausible reasons for trying out the several regressions we have in mind. Either way, the result is the disappearance of action and contingency into the magician's hat of variables and causes, where they hide during the analysis, only to be reproduced with a triumphant flourish from the author's sleeves in the conclusion section. As a result, our empirical work would not be read by an outsider as grounded in the immediate social reality of action, the way it seems to be to us. We live within a view of social reality that we ourselves don't really believe. Our theoretical hearts are one place, our empirical heads another. In this lecture I shall discuss this disjunction. I begin with a classical discussion of causality in sociology, that contained in Emile Durkheim's Suicide. This leads naturally into a discussion of the origins of the concept of causality in sociological methodology. Important perplexities in that history lead me to glance at the broader philosophical literature. But, frightened by what I find there, I return to the safer ground of sociology and seek to recover the real aims behind the movement to causal analysis in the 1950s. These aims send me back to philosophy and point us toward wholly new forms of analysis, with which I close. I Causality in the Classics: Durkheim I begin with Durkheim. Not that his direct influence on images of causality was great. Untranslated until 1951, Le suicide assumed paradigmatic status only as the causal revolution gained momentmum in the decade following its republication. But by now three generations of sociologists have taken Suicide as a sacred text, and the book's great clarity make both its virtues and its vices singularly accessible. It raises, at one point or another, nearly every important problem in the theory of causality. In Le suicide Durkheim insists from the start that causality embodies a kind of "forcing" - a determination - that is like the causality of classical mechanics. Thus, in the Preface, When each people is seen to have its own suicide-rate...; when it appears that...marriage, divorce, the family, religious society, the army, etc., affect it in accordance with definite laws ... these states and insitutions will no longer be regarded as simply characterless, ineffective ideological instruments. Rather they will be felt to be real, living, active forces, which, because of the way they determine the individual, prove their independence of him. (38-9, all page refs are to the Spaulding/Simpson translation) Causality here means "living, active forces." It means determination. It means necessary and sufficient reason. Although Durkheim will later rely on more indirect types of causation, the ideal of social causality that he expresses at the outset is almost mechanical. This mechanical image pervades Durkheim's writing on causality. His argument against cause by imitation rests essentially on a rejection of "action at a distance," the bugbear of classical physics. In the theory of imitation, he says: A cough, a dance-motion, a homicidal impulse may be transferred from one person to another even though there is only chance and temporary contact between them. They need have no intellectual or moral community between them nor exchange services, nor even speak the same language, nor are they more related after the transfer than before. p 123, emphasis added. Imitation is thus rejected as a causal mechanism because it rests on a cognitive connection that is incapable of transmitting real influence between individuals, that is, because it constitutes action at a (social) distance. For Durkheim, it is the sharing of something - in particular of norms - that enables the passage of true causal force from one actor to another. Norms are an aether necessary to explain how social causality moves across seeming voids. But Durkheim's approach at other times reflects less 19th century physics than 19th century medicine. Doctors then separated the causes of diseases into three layers; predisposing causes, precipitating (or "exciting") causes, and anatomical causes. Predisposing causes made people differentially likely to acquire certain diseases; certain climates were thought to affect lung diseases, for example, and excessive work was thought conducive to insanity. By contrast, precipitating causes "tripped the switch" in some of these predisposed people, thereby starting a disease. Alcoholism might trigger epilepsy or "disappointed affection" might trigger mania. Anatomical causes then produced the final common pathways in disease; they were the physical lesions that created the symptoms. Much of Durkheim's analysis of the social origins of suicide fits the predisposing cause model, and indeed the standard translation uses the word "predisposing" repeatedly. Thus: Each society is predisposed to contribute a definite quota of voluntary deaths. This predisposition may therefore be the subject of a special study belonging to sociology. (51) Here we seem to follow the doctors' model precisely; social forces make certain things more likely, but individual, contingent processes take care of the actual outcomes. But Durkheim has something more in mind, as we see in his discussion of heredity, the predisposing cause par excellence of late 19th century medicine. When suicide is said to be hereditary is it meant merely that the children of suicides by inheriting their parents' disposition are inclined in like circumstances to behave like them? In this sense the proposition is incontestable but without bearing, for then it is not suicide that is hereditary; what is transmitted is simply a certain general temperament which, in a given case, may predispose persons to the act but without forcing them, and is therefore not a sufficient explanation of their determination. (93) Durkheim emphatically rejects heredity as a cause of suicide, and precisely for its merely predispositional effects. The social causes that Durkheim will later introduce will be seen not as predisposing but rather as precipitating causes, by which Durkheim clearly means forces of determination, forces of joint sufficiency and necessity. FN (ironic) At times, Durkheim even seems to argue that social causes are alternatives to individual ones. Hence: No description, however good, of particular cases will ever tell us which ones have sociological character. If one wants to know the several tributaries of suicide as a collective phenomenon one must regard it in its collective form, that is, through statistical data, from the start. (148) But in the last analysis, his general approach does make the social causes a general framework within which individual forces exercise specific effects. Thus he says that: [records of presumptive motives of suicides] apparently show us the immediate antecedents of different suicides; and is it not good methodology for understanding the phenomenon we are studying to seek first its nearest causes, and then retrace our steps further in the series of phenomena if it appears needful? (148) The immediate motives - which Durkheim is at pains to dismiss as what we would call intervening variables - thus simply ring changes on tendencies already established by larger forces. Durkheim seems then to take a hybrid approach, a model of causality associated less with the physical or medical sciences than with the social sciences themselves. This is the model we social scientists are all raised on, in which social forces directly determine underlying parameters, and individual cases then vary around them in response to local causality. We might call this the ANOVA model of causality, after the principal method embodying it. It is easy to point to passages in Durkheim embodying this approach. Thus: Certainly many of the individual conditions [i.e., causes] are not general enough to affect the relation between the total number of voluntary deaths and the population. They may perhaps make this or that separate individual kill himelf, but not give society as a whole a greater or lesser tendency to suicide." (51) Durkheim explicitly separates the two "levels" of causality. ...we do not accordingly intend to make as nearly complete an inventory as possible of all the conditions affecting the origin of individual suicides, but merely to examine those on which the definite fact that we have called the social suicide rate depends. The two questions are obviously quite distinct, whatever relation may nevertheless exist between them. .... The [sociologist] studies the causes capable of affecting not separate individuals but the group. (51) The fundamental difference between this position and the predisposing/ precipitating model is that Durkheim, like other social scientists, wants to think of the social causes as determining, necessitous forces, not just as general probabilistic drifts. The general/particular causal distinction is made, but the location of force is changed. Where the 19th century doctors often found the higher level (predisposing causes) unchangeable and hence of merely academic interest, Durkheim's interest lies in precisely those higher level (in his case, social) causes. For him, it is the immediate causes that are uninteresting. He dismisses them. (FN curious) It helps that data on these immediate causes - the so-called "motives" or "immediate stimuli" for suicide - are notoriously poor. Nonetheless, Durkheim rejects them a priori, saying they are mere intervening variables. First, he presents statistics showing that overall suicide rates have risen sharply while these motives have not changed much at all. Then he presents statistics showing motives to be roughly the same for farmers and liberal professionals, when "actually the forces impelling the farm laborer and the cultivated man of the city to suicide are widely different." (151) He puts the matter bluntly: ....The reasons ascribed for suicide, therefore, or those to which the suicide himself ascribes his act, are usually only apparent causes. ....They may be said to indicate the individual's weak points, where the outside current bearing the impulse to self-destruction most easily finds introduction. But they are no part of this current itself and consequently cannot help us to understand it. (148. ) Here Durkheim explicitly turns the predisposing/precipitating model on its head. Individual factors are now the predisposing ones; social level factors are the exciting, effective, forceful causes. The overall design of the great monograph that embodies this conceptualization of causality is familiar. After rejections of non-social arguments, Durkheim briefly considers what we would now call a descriptive or typological analysis - classifying suicides into categories and then analyzing them category by category. But here he finds too many diversities, too much missing data, too many errors on recording motivation. Better to reject this material altogether and pursue a purely social, causal analysis of suicide. In a central passage, he professes his faith: Only in so far as the effective causes differ can there be different types of suicide. For each to have its own nature, it must also have special conditions of existence. The same antecedent or group of antecedents cannot sometimes produce one result and sometimes another, for, if so, the difference of the second from the first would itself be without cause, which would contradict the principle of causality. Every proved specific difference between causes therefore implies a similar difference between effects. Consequently, we shall be able to determine the social types of suicide by classifying them not directly by their preliminary described characteristics, but by the causes which produce them. 146-7 (FN polemic) Later on, Durkheim tries to reclothe egoistic, altruistic, and anomic suicide with the psychological correlates he has been at such pains to strip from them. But for all his complexifications, what appears is a straightforward mapping between psychological states and social types of suicide. Each general suicide type commands two or three basic psychological versions, with no version being common to two different suicide types. (FN concedes) He does allow various hybrids: suppression of one type by another, mutual support or extension, alternation between one and another, and even genuine mixing. But basically, each of the three great types has a principal emotional correlate that is then varied a bit in practice (see p 293 table). Durkheim closes this analysis with a final summary of the ANOVA view of causality: Such are the general characteristics of suicide, that is, those which result directly from social causes. Individualized in particular cases, they are complicated by various nuances depending on the personal temperament of the victim and the special circumstances in which he finds himself. But beneath the variety of combinations thus produced, these fundamental forms are always discoverable. (294) One can easily see why this book became the paradigmatic text of modern causal analysis, despite Durkheim's primitive statistical techniques. It is self-consciously scientific. It invokes the concept of causality. It combines the classical phsyicists' mechanism with the doctors' differentiation of local and global cause. It makes causality both universal and unique. And it lays out a model of causality that prefigures, almost word for word, the analysis of variance as set forth more than three decades later by Fisher and his colleagues. But we must hesitate before accepting this facile judgment, for it reads the present into the past. If we ask what Durkheim thought he was doing with all this talk of causality, which for us seems the very blazon of ctonemporary quantitative sociology, the answer is that Durkheim saw himself in a battle with immanent evolutionists like Spencer and Comte, scholars who saw in the course of events the mere working out of even grander and more universal forces than Durkheim's social powers. The Rules of the Sociological Method makes it very clear that Durkheim took up the cudgel of causality in the name of contingency and variation, in the name of the particular against the universal. Odd as it may seem today, he thought he was urging the importance of real history. Thus, what seems to us now like the ur-text of the causalism produced by the great sociological generation of the last forty years was in fact seen by its author as a manifesto in favor of the contingent analysis of social action as over against the chronicling of transsocial forces. II Causality and Empiricism in Sociology As I noted before, Durkheim's present symbolic importance belies what was in fact a negligible historical effect on social science's images of causality. The synthesis of causal analysis with quantitative methods so evident in Suicide in fact became widespread only in the 1950s, around the time Suicide was translated into English and republished by the Free Press. It was only then that the accidetal affinity between Durkheim's theories and Fisher's mathematics made Suicide into the bible of causal analysis, repeatedly cited by Lazarsfeld, Stinchcombe, and other makers of modern methodology. In fact, the new synthesis of causalism and quantitative analysis arrived in a quite different way, via a redefinition of terms within the tradition of empirical quantitative analysis. Quantitative analysis was old in sociology, indeed in the social sciences more broadly, by the 1950s. But early quantitative analysis was not inferential in the modern sense. The revolution of Fisherian inductive statistics swept through the field of statistics itself only in the late 1920s. Contemporary quantitative analysis in sociology took various forms - social trends under Ogburn, ecological analysis under the Chicago school, social distance scales under Bogardus - but none of these involved the use of the new Fisherian orthodoxy, although they did make us of correlational methods. The new social statistics of the 1930s had three broad origins: biometrics, psychometrics, and econometrics. The biometric avenue is both the simplest and the most important. It was the biometricians who created modern inferential statistics between 1890 and 1930. Galton, Pearson, Fisher, Wright, and their colleagues invented correlation coefficients, regression methods, and path analysis. They also devised sampling theory and hypothesis-testing, with its presumption of probabilistic reference models. (FN sources) In the early days, the biometric revolution was quite anti-causal. It emphasized association alone. To be sure, within the experimental designs characteristic of early biological research the distinction between causality and association tended to blur. Experimentation aimed to isolate treatments from the influences of extraneous (we would say spurious) factors and to permit thereby a simple causal inference between treatment change and observed results. But much of the early work - from that on intelligence to that on inheritance - was in fact conducted in non-experimental situations and without any real theories of mechanism. It therefore tended to deemphasize causality. In particular, the main goal of the agricultural work was operational - how best to improve crop yield. Knowledge of mechanism was tangential to such work, which was effectively evaluation research without theoretical pretensions. The study of intelligence led to another set of statistical developments, this time within psychology. There, Thorndike, Spearman, and Thurstone developed scale and factor analysis. The psychometricians were even less causally oriented than the biometricians. Factor analysis reduces complex data to simple forms in order to reconcile quantitative data with intuitive categories. Causality is not considered. This anti-causalism is hardly surprising. The major theoretical problem to which factor analytic studies were addressed was the debate over the faculties of the mind - the longstanding concern about whether there were separate "organs" of memory, desire, intellection, and so on. This was not a causal but rather a descriptive problem. Econometrics provided a third entrance for statistics into social science. Here the central numerical issue was the behavior of time series. Again the central practical matters were as much descriptive as causal: filtering out white noise, unraveling the tangle of serial correlation, forecasting future patterns. Economists tended to use the language of cause more often than did the other new statisticians, but meant by it simply relationship or association. Thus the three main strands by which the new statistics emerged and entered the social sciences were all skeptical, cautious, or outright negative in their approach to causality. Indeed, this mute role for causality was characteristic throughout the quantitative social science of the 1920s and 1930s. William Fielding Ogburn said that his PhD thesis was "not a study to determine causes, but it is hoped that it may be used as a basis for a study of causes." (Bernert 237). Ogburn's peers in statistical social science were mcuh more comfortable with talk of association than with talk about cause. It was, by contrast, the old-style qualitative theorists who wanted to talk of causality. Thus, Robert MacIver's Social Causation (1942) attacked mathematicization precisely for losing sight of causality in a haze of associations. Much of MacIver's anger was directed against what he called the "mathematical limbo" of the more extreme versions of logical positivism, for example Morris Cohen's claim that "mathematical and logical relations form the intelligible substance of things." (MacIver 49,53) The positivists in sociology - George Lundberg being the most vociferous - had argued that the concept of causality was anthropomorphic and "theological"; only association could be observed, never force or compulsion. Indeed the program of the early socio-logical-postivists included not only this extreme anti-causalism but an equally extreme operationalism (MacIver 157) that they had taken from the physicist Percy Bridgman. The concept of causality with which MacIver attacked these positivists was in fact closer to our concept of explanation than of causality. Causal assessment, he says, is seeking answers to the question "why does something or some regularity happen." Like Aristotle, he gives a number of different kinds of why questions, suggesting a number of generic types of causes. It is plain that the word causality means something fudamentally different for him than for Cohen, Lundberg and their like. Thus the Second World War found qualitative, non-statistical sociologists talking about causality and action, while on the other hand quantitative, statistical sociologists focused merely on association and were quite skeptical of causation. Yet after the war, the language of causality quietly drifted into quantitative social science generally and into quantitative sociology in particular. Causality reappeared as part of Lazarsfeld's gentling of the harshly scientistic paradigm associated with the social physics of Lundberg, Stuart Dodd, George Zipf, and others. The Lazarsfeld and Rosenberg reader of 1955 on The Language of Social Research established the modern concept of methodology (quite consciously, by choosing that word [1955:4]) and made the investigation of causes central to that methodological process, citing MacIver alongside Lundberg, Dodd, and Durkheim, and indeed using MacIver's term "causal assessment." But the old skepticism remained. In the main section on multivariate analysis, the analyst is said to be pursuing "explanation" not causal assessment. Explanation, for Lazarsfeld, seems to have meant discovering general regularities, whereas causal assessment meant "applying available knowledge to the understanding of a specific case, be it a person or a collective." (387) He gave examples of causal assessment in a section on "empirical analysis of action," focusing on a favorite example, the process of purchasing a good. "Any bit of action," he tells us, "is determined on the one hand by the total make-up of the person at the moment, and on the other hand, by the total situation in which he finds himself." (393) In this formulation - which could easily have come from Herbert Blumer's symbolic interactionism - Lazarsfeld views causality as a way of understanding and explaining action in particular settings and particular cases. By the 1970 edition, however, the whole picture has changed. The leadoff article of the section on multivariate analysis is a Hirschi and Selvin chapter on "the logic of causal analysis." The whole section on "empirical analysis of action" has disappeared (along with the coverage of qualitative research). For the 1960s had brought Blalock's Causal Inferences in Non- Experimental Research, which treated causality as intrinsically linked with quantitative analysis, and indeed with the analysis of general, not particular, phenomena. The opening pages of Blalock's book tell us just how dominant the causal model had become and how it had been redefined, losing the connotations of action that had been associated with it in Durkheim, MacIver, and even the early Lazarsfeld. There is no mention whatever of action, actors, or intentions. Causation is literally called a "forcing," and is something more than mere constant conjunction or sequence. Like Durkheim, Blalock regards "causal laws" as deterministic in classical physical terms (p17), but clouded by error, by which he means unspecified causes, individual variability, and so on. By the word "theory," he means representations of reality in linear transformations. It is clear, in fact, that the philosophical prologue derives logically from the regression argument that follows it in the actual book. This new emphasis on and restructuring of the concept of causality hinged on a redefinition; the term "causality" could become important again because it had a new meaning. Causality was now seen as a property of mathematical and statistical propositions rather than a property of reality, a fact clear in Blalock's phrasing of discussions of causality specifically in terms of equations and conditional probability. This shift in part paralleled earlier trends in the philosophy of science. The logical positivists had sought to escape from the traditional epistemological problems of empiricism by redefining virtually all the central concepts of science, making them descriptions of scientific language rather than of empirical reality; causality was one of several terms so treated. Thus, in Cohen and Nagel's immensely influential Introduction to Logic and the Scientific Method (1934), causality was defined simply as a kind of statement; a statement labeling an invariant relationship. Which specific aspect of this invariance was of interest would vary with the theoretical interests of the investigator, a point Blalock was to emphasize as well (18). The move towards the Durkheimian model of causality was thus not justified on the ontological grounds Durkheim himself had used, but rather on general philosophical grounds. The new model reinstated the idea of causality, but only by making it to a predicate of discourse, not reality. At the same time, however, Blalock also quietly reinstated the Durkheimian concept of cause as forceful and determining. I should reiterate the history to make this development clear. For Durkheim himself, "causality" meant envisioning social reality as governed by real actions rather than by grand immanent forces. "Causes" were the local (although to our thinking still emergently social) forces determining these actions. For the early statisticians, "causality" had seemed of relatively little concern; they were interested in description or outcome analysis rather than in mechanisms. For the logical positivists, causality in the usual sense was an anthropomorphic bugbear, to be purged from real science. They were militant supporters of mere associationism, and would accept the concept of "causality" only if it meant nothing more than association. For MacIver and other non-statisticians, by contrast, causality seemed the essential heart of explanation in human affairs. Indeed, what they meant by causality was what the others meant by "explanation." Even for the early Lazarsfeld, "causality" meant something about understanding particular human actions. What the new causalism of Blalock and others did was first to accept the causality concept of the logical positivists - causality as a predicate of statements rather than reality and as a concept not referring to action - then to reinvest it with both the quality of emergentism and the character of forcing or determination, both of which are present in Durkheim, although qualified by his sense of causality as tied up with action. As a result there emerged the fullblown ANOVA concept of causlity, the one that underlies such seminar taunts as "this work is purely descriptive" or "what have we learned from this theoretically." I need not tell this audience that this view of cause is hegemonic in American sociology, although not, interestingly enough, in American psychology or market research. As I have just told it, the history of causality in sociology is more or less a history of redefinitions and slides. The discipline has toyed with varying notions of causality at varying times. But we have ended up with a view that in practice holds that social reality is determined in the main by certain general forces, and that these generalities are then specified by combinations of forces, and further limited by various aspects of "individuality," which in this sense is best understood as idiosyncratic higher order interaction. Although we are, as I noted at the outset, very careful to tell ourselves and our students that this is really only the mathematical framework, in practice a surprising number of sociologists believe, for all intents and purposes, that this is the way the social world itself operates. We might ask ourselves whether this view of causality has figured in the debates of philosophers about that subject. III The Modern Philosophy of Causality The welding together of Durkheim's almost medieval theory of causality and quantitative empirical work into the ANOVA view of causality in fact bears little relation to developments in the analysis of causality by philosophers. The classical analyses are those of Aristotle and Hume. With characteristic measure, Aristotle noted that people meant a variety of things by "cause." Today, each of his four causes supports a major theoretical strand in social science. Material causes are studied by demographers, who believe that the explanations of social phenomena lie in the different qualities of the human materials going into them. Formal causes are studied by structuralists, who see in networks and patterns the determining shapes of human affairs. Final causes are studied by functionalists, with their interest in the purposes and ends of action. And efficient causes are the focus for choice modelers, who seek the final pathways by which action is determined. In most empirical social science, the first three (at least) are mixed together, although recently the last is entering the mix almost as often. Aristotle's notion of cause is thus a broad one, covering much of our activity as social scientists, and, like MacIver's notion in the current century, it comes closer to our idea of "explanation" than to our idea of cause. The Humean analysis is more specific. As is well-known, Hume directly attacked the notion of causality as a "forcing" of things to happen and as a necessary relationship in the real world. For him causality was a simple matter of invariable sequence or constant conjunction. Cause and effect had to be both adjacent and temporally successive, and in addition that relation between them had to be constant. But the necessity of it was purely in the mind of the beholder. It could not be directly perceived. As the logical positivists were later to argue, causation denoted a kind of statement, rather than a kind of relationship between things. Even Kant could rescue causality from Hume's attack only by making it one of the categories of the pure reason, an a priori aspect of knowing. On this point, Durkheim - and with him most social, indeed most natural, scientists - completely ignored the Western philosophical tradition, for he took "forcing" and determination as central to his concept of cause. Since Hume, the modern philosophy of causality has however divided over a number of issues. First, Hume's view makes large and empirically impossible ceteris paribus assumptions; most of the time, other things are varying and so what is immediately succeeding what is unclear. Put another way, we think of most events as having many causes. Such plural causality has been a major problem for philosophers. This problem has fed into another, that of whether causality involves necessity or sufficiency. One way of resolving the plural cause problem has been to talk about independently necessary and jointly sufficient conditions. Ayer, Mackie, and others have developed this argument extensively. But the enduring temptations of the necessitous view of causality lead directly to a third philosophical problem, that of direction. The strict necessary cause position makes the effect sufficient for the cause, tempting some to see the latter direction as the true "causal" one; effects, in this view, "cause" their causes. As Singer and Marini have argued, the social sciences have more or less settled for Mackie's INUS view of causation, which defines a cause as "an insufficient but nonredundant part of an unnecessary but sufficient condition." This more or less justifies the common practice of apportioning out causality in proportions, telling the public - or at least as they hear it - that criminality is 65% due to heredity or intelligence 35% due to nurture or whatever. The fact that the causes are insufficient in themselves covers us if they don't work separately. The fact that they are non-redundant parts of something covers our obvious assumption of plural causality. That they add up to something that is sufficient rather than necessary gets us out of directional difficulties. The use of the INUS theory of causality, however, seems to me to have followed practice rather than preceded it. Our current views of causality came from doing the kind of work we have been doing, not the other way around. Three other debates in the philosophical literature bear on the social scientific concept of causality. There is, first, an extensive discussion of the exact nature of causal regularity, particularly important since the Humean analysis of cause as invariant sequence leaves one open to "causal" regularities that we don't usually take as causal (night following day being the famous example). This problem led Collingwood and others to think of causality in terms of "levers;" for them, that is causal which is within the control of agents. This argument makes voluntary action the paradigm of causality, a position argued against Hume by Thomas Reid and followed in the current century by Whitehead, Collingwood, and others. Still others have handled voluntary action by exempting it from causal determination, arguing that causality, although deterministic, is not universal; some events have no causes. In social science, the Collingwoodian view of causality has become important, for it lies - implicitly, to be sure - behind rational choice theory and also behind the essentially operational use of Fisherian statistics in the original agricultural context and in the modern equivalent of that operational use in evaluation research. Second, although it may seem strange to social scientists, who have always made temporal priority necessary to causality, there is a substantial minority in philosophy - including people like Collingwood and Russell - who have held that causality is always a simultaneous relationship. Russell, for example, founded this position on an Eleatic argument about the infinite subdivision of time. Others have insisted per contra on the Humean criterion of temporal succession. A related debate concerns whether things that don't change (e.g., race and gender) can be said to be causes. Large portions of social science assume that this is possible, in particular the social demographers and other followers of Aristotle's "material cause" approach. A substantial number of philosphers disagree, and they have recently (1986) been joined by the statistician Paul Holland. Finally, there has been a substantial debate throughout the twentieth century about the status of probabilistic statements of causality. The problem first arose in the context of quantum mechanics, contemporary with the logical positivists' rethinking of scientific language. Confronted with these difficulties, philosophers jettisoned determinism, thus guaranteeing the Humean position. At first, causality went along with determinism. Neurath (IEUS ii:21), for example, urged social scientists to avoid thinking about "the cause-effect muddle" altogether. But those philosophers who retained causality worked towards the necessity/sufficiency analysis that is dominant today, which was easily relaxed into a probabilistic position on determination (Reichenbach, Suppes). In summary, 20th-century philosophers have treated causality with considerable skepticism. There seems a general tendency to treat causality as more a property of propositions than of reality, a strategy implicit in Hume and reemphasized by the logical positivists. Correlatively, causality has been reconceptualized in complex logical terms relating sufficiency and necessity, although the contents of these reconceptualizations vary widely. But beyond that, disorder reigns. Some hold for plural causes, others don't. Some make rational action the epitome of causality, others exclude it. Some see causality as necessarily involving temporal succession but not necessarily change, while others see it as necessarily involving change but not necessarily temporal succession. The philosophical literature thus seems to engage many of the same issues that have concerned social scientists in their views of causality, but to see those issues through different lenses. Because of its abstraction and its internal disarray, then, it offers us little help towards understanding the issues involved in sociology's allegiance an everday model of causality that we ourselves all regard as a polite fiction. We assign to social forces and properties a "determinative" character that neither we nor our theorists nor even our philosophers believe in. To a large extent we ignore social action itself, applying ourselves not to modeling that action, but rather to studying its consequences for the reified variables that have become the center of our corporate intellectual life. Indeed, as I have noted, it is now standard to despise studies of action itself as "mere descriptions" or "atheoretical" or "just simulation." IV Perhaps it will help us understand this curious paradox if we return to the history of causal analysis in sociology and ask ourselves why the Blalock/Duncan generation took up causal analysis in the form they did with the vigor they did. There seem to have been a number of reasons for this adoption. One of these was a bona fide belief in "science" as a stance for sociology. Thus, although Duncan regarded himself as a student of Blumer as much as of Ogburn, it was Blumer's insistence on rigor and science that appealed most strongly to him (see the documents in ....). Blalock's similar faith in science speaks in page after page of his published writings. To be sure, scientism was in the air. Logical positivism was triumphant in philosophy, and science had, in many people's eyes, won the war. But in social science, scientific stances seemed particularly strong. Polls were becoming universal. Market research was booming, both the Lazarsfeldian scientific variant and the softer, psychologistic style of Lloyd Warner and Burleigh Gardner. And scientism as an ideology went beyond a simple methodological stance. It was a general commitment, as evidenced by the arrival of double- blind reviewing in sociology journals in the mid 1950s. In the area of new methodologies, this belief in science was very much a young man's game. In 1955, Duncan was 34, Blalock and Coleman 29, Goodman 27. Lazarsfeld was the grand old man at 54, dedicating the 1955 reader to "Charles Glock and his 'young turks' at the Bureau of Applied Social Research." Of course, sociology as a whole was young at the time because of its rapid expansion after the war. But there was a very generational flavor to the causal revolution. Duncan's famous public attack on Lloyd Warner's "unscientific" categories, written when he was 29 and coauthored with his graduate student colleague Harold Pfautz, was as much a young person's attack the establishment as it was a blow in a quantitative/qualitative fight. Blalock first published his text Social Statistics at 34. Coleman's capacious and quixotic book on mathematical sociology came at 38. The youthfulness of the new causalism suggests another reason for its adoption, one for which I have a strong theoretical hunch, but only scant evidence. Nicholas Mullins saw the new causalists as cromwellian puritans. But I think, by contrast, that the leaders of the new causalism were a little like Hilary climbing Everest. They did it because it was there. The methods had been worked out by others. They could be quickly borrowed and applied. Trying them out would be fun. Who knew what might result? The did it, I think, for fun. We get this "let's try it out" feeling again and again in Coleman's Mathematical Sociology, as we do even at times in The American Occupational Structure. Duncan was explicit in that book about the extreme assumptions necessary for the analysis, but repeatedly urged the reader to "try something out and see what we learn." The memoirs one reads of Columbia in the early days of the BASR all suggest a similar mood of experimentation, often contemptuous of outsiders, but lightheaded and giddy and energetic as only young people with a new truth can be. To be sure, this try-it-out attitude was combined with the scientific puritanism Mullins so disliked. More consequentially, it was also combined with extraordinary exclusivity, for few senior sociologists could follow the mathematics necessary to undertake causal analysis on their own, and the computerized commodity versions of the necessary statistics were not yet available. As a result, the young causalists were rulers of a roost no one else could attack at an age when in more typical careers they would have been chafing for a decade or more under their elders' tutelage. It is little wonder, on this argument, that as the years passed they began to take their own creation with such remorseless seriousness. This seriousness was passed on to their students, who had not had the experience of inventing causalism and therefore could not know at first hand its contingent, historical character. Rather they rather learned causalism in methods courses as the way science was done. Thus Duncan passed on to his students neither his desire for what he once called "a properly relativistic sociology" nor the comprehensive vision of social life that he had gotten from Blumer. He finished his career decrying nearly everything that people had done in following him. "We have won all the battles," he once said, "only to lose the war." What was the war about? Very simple. It was, I think, about providing a compelling and interesting account of social life. Causalism was a tactical avenue to that larger strategic aim. The great mistake of the causalists, in Duncan's eyes, was to have mistaken the tactical victories of "doing the science right" for the strategic victory of getting a better representation of social life. To put it into the familiar terms of causalism itself, the mistake was to have taken the indicator for the concept. It is this process of losing sight of the main objective that I denote by my title phrase "the causal devolution." But if the mistake was to have thought that a fairly narrow causality concept was the only way to undertake the explanation of social life, what are the alternatives? Here it turns out to be helpful indeed to return to the philosophical literature. V The modern philosophy of explanation rests on Carl Hempel's celebrated argument - set forth at the high-water mark of logical positivism in 1942 - that explanation of particular events always takes the form of a syllogism whose major premise is a "covering law" and whose minor premise is an assertion that a particular situation meets the hypothesis conditions of that law. Thus, in Durkheim's case, sociology provided the theoretical major premise whereby certain social conditions entailed certain necessary consequences: lack of social integration causes high suicide rates. The minor premise was the demonstration that a particular case fit the hypothesis of the major premise: Saxony lacked strict religion and hence lacked social integration. The syllogism then produced the inescapable conclusion that Saxony had a high suicide rate. Thus sociology "explained" that suicide rate. Over the years, Hempel's argument has drawn considerable opposition. From the outset, Karl Popper argued that all social covering laws are trivial, the classic example being that people do what they are interested in doing and hence that behavior is explained by interests. For Popper, to invoke such alaw was simply to restate the problem, not to explain anything. He ultimately came to believe that the covering law model was worthless because all the real explanatory action was in the side conditions specifying which covering laws hold, that is, which of a set of plural causes were doing the explaining and which were simply assumed in the conditions. But the larger response to Hempel came from philosophers of history, who proposed a completely alternative view of explanation based on narrative. There were three general versions. The first was the "understanding" model of Collingwood (1946), Dray (1957), and many others, which deals to some extent with Popper's issue of side conditions. According to Collingwood, the historian aims to get inside a historical figure's own justification of action, to understand what was "reasonable" given that figure's tastes and conditions. The Collingwood position is thus a broadened version of a rational choice theory; the historian figures out "what it made sense for the actor to do," given the actor's beliefs, knowledge, and psychology. Clearly, this approach correlated perfectly with Collingwood's position that causality was paradigmatically intentional. The understanding view has, however, been seen by recent philosophers of history as overly "idealist," given to dangerous subjectivism. A second view of narrative explanation, responding to this challenge, is the "followability" thesis of W. B. Gallie (1968). Like Collingwood's constructionism, this view attempts to describe how narrative history actually works. On this argument narrative is itself explanatory by virtue of truth, consistent chronology, and a coherent central subject. Narrative is held to combine things that are determined by general laws with things that are contingent, producing a plausible, because followable, story. This notion of "combination" is much looser than the formalities of the covering law model, but still leaves a place for general determinism that is missing in the Collingwoodian position. A third position on historical explanation recognizes a central problem in Gallie's followability view - the fact that we know, in fact, how the story turns out, a fact that is central to "follwing the story." Louis Mink, for example, argued that history was one of three basic modes of thinking about the world: theoretical (the view of the natural sciences), categoreal (the view of philosophers), and configurational (the view of historians). What made configurational thinking unique was its insistence on putting particular pieces together into larger wholes. This was the process that Whewell and others had called colligation: the assertion that a group of conflicts should be collectively defined as a social movement, for example, or that a certain group of composers made up a school or a style. Conceived across time, colligation became the process of creating "configurations" - that is, histories or plots - of events. The argument was taken a step further by Hayden White (1973), who treated historical writing as directly similar to fiction and hence applied a purely literary analysis. He argued that there are really only four kinds of historical plots: Tragedy, Comedy, Romance, and Irony. V Causal and Contingent Views of Social Reality With Haden White, we seem to ahve come very far inded from the now traditional world of sociological causalism. In what sense do views of explanation that derive from the philosophy of history provide viable alternatives to explanation of social life via our current concept of causality? To be sure, they stand much closer to both the tradition of western social philosophy and to that of our own modern social theorists - Marx, Weber et al - than does the ANOVA view of causality that has become our main vector of explanation. They make room for action, indeed allow action to be central. They mix determined and free acts. They embrace contingency. But to espouse them wholly would be to surrender an enormous amount of very real knowledge about social determinants produced under the causality paradigm. We must then use them to recast our strategies of explanation without losing what we have gained. To do that, we must begin by asking what we want from explanation. The main desiderata of explanation, it seems to me, have to do with consistency and interest. First, even though disciplines grow in fits and starts - pushing out here, surrendering there - our knowledge will become great only when it acquires a certain internal consistency. Our theories, our explanations, our methods, and our research programs should resonate with and support one another. I believe moreover, that in addition to this consistency we should set for our knowledge of society the second standard that it produce - as Duncan and others wanted - a comprehensive, interesting, and compelling account of social life. That account should be interesting and compelling not only to us in our specialty, but also to the larger culture around us. Our knowledge of social life must then be intellectually consistent and compelling. It is no secret that sociology at present meets neither of these tests, although it has done so in the past and, with luck, will do so in the future. I have just discussed at length the profound inconsistency between our general theoriesm and the theories implicit in our methods, sketching at the same time its historical origins. And surely none of us thinks that sociology has, at present, a publicly compelling account of social life. If any discipline has that account in American today, it is economics. I would like to begin with a preliminary point about compelling public interest before returning to my main topic of consistency. One of the central reasons for sociology's disappearance from the public mind has been the steady deprecation of description in sociology. The public - and here I mean not only the reading public but also the commercial sector - really wants to know how to describe society. It wants to know, to put it most simply, what is going on. But such descriptive knowledge has been steadily despised in mainstream sociology for at least twenty years. Our narrow focus on causality has long meant that an article of pure description, even if quantitatively sophisticated and substantively important, effectively cannot be published in our journals. Commercial firms pay millions for such descriptions, and in fact our society is "described" in surpassing detail by the mass of proprietary market research information. But we who like to imagine ourselves responsible for the public's knowledge of society despise description and indeed despise the methods - scaling and clustering - that are the main methods for accomplishing quantitative description. We talk about social indicators, of course, but these are completely disaggregated variables, ready for input to causal analysis. The notion of complex combinatoric description, of typologies based on multiple variables: this fills the average sociologist with disgust. This disgust is disingenuous, for ease of computing has made of regression itself a descriptive method. When dozens of regressions can be run in an afternoon and when the average regression-based journal article reports perhaps five to ten percent of the runs actually done, it is time to stop kidding ourselves about science and hypothesis testing. One doesn't need the profound critique of causalism by David Freedman to recognize that we use regression in a way fundamentally different way from Dudley Duncan, who had to decide once for all every single table he would ask the CPS to run for him, because there would be only one run on the data. And taken as a descriptive technique, regression is pretty poor. The aim of description is to reduce a massive welter of data to something one can reasonably think about. But regression reduces the dimensionality of the data space only by one. If it weren't for the myth of causalism, there would be no reason to retain such a technique. Worse still, that lost dimension usually retains most of its variation, so in fact we haven't even really gotten rid of one dimension or, put the other way, we haven't really understood why that one thing happens. We have, to be sure, understood the effects of the independent variables on that one dependent dimension, and in an evaluation context - when we are trying to make decisions about whether to use fertilizer on the field or dopamine on the brain - regression is without question the method of choice. But as a general method for understanding why society happens the way it does, much less as a strategy for simple description of what is going on in social life, it is really very poor. Scaling and clustering by contrast throw away the vast majority of dimensionality. But by doing so they often produce results that are intuitively compelling and that provide powerful descriptions of enormous arrays of information. People with millions to spend on descriptions of society pay far more attention to them than they do to regression, which is used in market research to clean up the details. But the simple fact is that we don't like scaling and clustering, we don't teach them, and other than Ed Laumann no major figure in American sociology has made a career doing them. Serious quantitative description is invisible in sociology. I realize that causalism has been so successful as a methodological ideology that many of you probably identify causal analysis with science. Well, reflect a bit about biology. Where has the understanding of dozens of evolutionary trees come from? From accurate description and numerical taxonomy. What is numerical taxonomy? Cluster analysis. What has vastly increased our ability to find drugs with specific powers? Sequence analysis, a descriptive technique often applied in conjunction with scaling or clustering. Many major causal discoveries about protein mechanisms have been enabled by the vast descriptive geography of proteins that has emerged from the sequence analytic community. So we shouldn't assume that science can only be about causality. Much of real science is about description. I want then to start by simply underlining this point. (FN Profession regression) Sociology will not be taken seriously again as a general science of social life until it gets serious about description. But my more important, and my final, concerns are with the problem of consistency. I have argued throughout this paper that our methods imply theories of society that none of us actually believes. And I have argued that it is essential to free ourselves from the narrow concept of explanation that we have adopted, again implicitly, from our methodologies. I have mentioned some alternative conceptions of explanation from the philosophy of history. I would like now to trace a path from those alternative conceptions towards what I believe should be our canons of explanation. When I first began to be concerned with historical explanation, I took it as a simple alternative. So my aim became to create explanations of social life that accepted the idea that reality happened in stories, but that instead of breaking those stories down into variables, left them together and compared and categorized them as wholes. I would treat social life as the historians did - in stories - but then I would generalize. Thus, I embarked on a ten-year quest for "characteristic plots," looking at sequences of professionalization across professions, at careers of individuals across occupations, at patterns in the evolution of themajor welfare states. Incidentally, I found out that my methods worked even better on what we might call culturally established sequences, looking at changing patterns of figures in folk dances and changing rhetorical structures in sociological articles. But the basic idea was to argue that maybe the historians were right about the story-like character of social life. We should analyze it by sorting it into characteristic plots or stories. Then we could try to explain why those stories existed. Needless to say, this endeavor attracted a lot of hostile press, largely from people who - following the Durkheim argument I quoted earlier - said this endeavor was "just descriptive." I've already told you the twofold response to that judgment: first there's nothing bad about description - indeed it ought to be one of our central endeavors - and second so-called causal methods as practiced today are effectively themselves simple descriptions, so where's the difference? But my approach was wrong, although for reasons my critics and I both failed to see. It wasn't, as we sometimes say, "sociological." That is, I didn'treally believe the world happened in independent stories. I knew full well that the foundational insight of sociology is that the social world is made up of situated actions, of social relations. Social life is a process that continuously recreates itself and embodies itself in constraining structures. My methods assumed away those structures just as fast as did the causal methods I was attacking. I was locating social facts to be sure, but only within the individual stories of career or occupational cycle, only within time. I was not putting those careers and occupational cycles in motion in relation to one another. I wa snot locating them in social structure. To be sure, as with standard methods, there are times when the broad assumption of casewise independence is reasonable and useful. So it was all right to compare the order of medical professionalization in Detroit with that in Boston and that in Altoona. But it had probably not been legitimate to see the careers of the German musicians I analyzed as independent, because the system was a vacacy system, in which successes in certain careers led to failures in others. And it also should have been no surprise that I found among the great welfare states not only no clear internal reasons for the sequencing patterns, but no obvious diffusion explanation for them either. For they were bound up in the single cultural unit of Western Europe. With any given social phenomenon, we can probably identify its independence of context in social space and social time. Phenomena that are completely free of context are the province of standard causal methods. Phenomena that are strongly conditioned by their temporal context but relatively free of environing social structure are best thought about with time series or event history or sequence methods. (I have my problems with the first two, but they all have their uses.) Phenomena that are strongly conditioned by structural context but not by temporal ones are the province of network analysis and spatial autocorrelative methods, a relatively underexplored area of methods. But, finally, the heart of sociology is those phenomena that are fully enmeshed both in social time and social space, what I have elsewhere called interactional fields. It is because we study interactional fields that we are a discipline of social relations, concerned with the social process. What are the great empirical literatures of such analysis? the literature on small group interaction from Goffman onwards, the literature on urbanism and city patterns, the literature on occupations and professions, a substantial portion of the literature on crime, much of historical sociology. What we should require of explanation is that it give us an account of how such interactional fields work. First, this account will not be purely causal. For nearly all of these literatures give a large place to free action, often to strategic choice in particular. Second, it will include temporal effects of many sizes, for in each of these areas a past of many depths shapes the present. Third, it will also include a complex understanding of social structure, for that too pervades interactional fields at many scales. Middle range theories and empirical methodologies must, it seems to me, meet these tests if they are to be consistent with our foundational visions of the social world. At the level of middle range theory, I think such work has in fact been done. Wallerstein's The Modern World System is essentially a theory of such an interactional field, with history and structure of varying sizes and powers. So also was my own book on professions. Such books don't predict what will happen, indeed they suggest that interactional fields are probably too complex for us to predict. But they do show various internal patterns; they do sketch the "rules of the game;" they do portray the limits and possibilities of action in such systems. We require quantitative methods that do the same thing. If I may use another forbidden word in sociological methodology, it is probable that simulation will play an important role here. Game theory as currently practiced won't get us very far, because it is ignorant, except in the most general terms, of a serious concern with structure and with complex temporal effects. But simulation itself may help us understand the limits and possibilities of certain kinds of interactional fields, and that would be profoundly sociological knowledge. So, for example, in the world of professions, there are local contexts - local historically and local in terms of the competitors facing a profession - in which it is very useful for a profession to be rigidly organized. There are other contexts in which it is not. When work is expanding rapidly, professions are better off being able to expand rapidly to meet it, for example. But the definition of which kind of moment it is resides in the evolution of the system; it is produced by the ensemble of strategic and non-strategic actions by all the professions competing in a given area. There is no parameter we can put on the variable of rigidity of organization, for that parameter is situationally determined, emerging from the evolution of the system. It is not systematically time varying or space varying. There is no way to "window" it or see it as a property of anything other than the moment and the situation. Lazarsfeld was right that understanding "the actor in the situation" was the heart of analysis, but wrong to think that it was a simple matter of assembling enough general covering laws and applying them. A better strategy of explanation is understanding how such a system evolves internally. Simulation may be the only way to do that. More important, the "meaning of parameters" can change for strategic reasons, that is through deliberate action of actors in a system. Virtually all forms of current positivism assume that the meaning - causal or otherwise - of an event is fixed for the duration of analysis. But we all believe that one of the central, basic human actions is to redefine something, so that the very shape of the present, perhaps even the identities of the actors in the present is new. Any serious methodology has to be able to encompass this kind of meaning change. So, to shift to a different example, one of the problems with analyzing urban politics over time is that the actual contents of coalitions shift. The very groups whose interaction one would like to analyze are regrouped and reattached dozens of times. A coalition that sponsors a new sewer system may shatter over problems in school location but reemerge, its split halves merged into other groups, in a debate over zoning. And these changes are in fact being defined and contested from within the system by actors, who themselves may well be changing like figures in a kaleidoscope. The problem begins to sound like one of programming a chess game, and it may well be that that is a direction our methodologies need to take. We seem then to be at a turning point in sociology. Our explanations seem of little interest to the general public, and have little to do, in any case, with our general views of society. I have urged us to broaden our concept of explanation and redirect it towards the foundational problems of our field. I do not mean thereby to denigrate the achievements of causalism. In fact, methodological revolutions always need post hoc theoretical restructuring. The impromptu borrowing and iconoclastic rigor of early causalism are often repeated and should not be felt surprising. Thus, for example, it might not seem theoretically grounded to base one's understanding of human action on a theory of waiting times, as if one were studying how long it radios and other complex machines to break down. But the mathematics born in that area has found a very comfortable home in sociology in the guise of event history analysis. Similarly, my own application of DNA-sequencing algorithms to career information was hardly appropriate theoretically; careers are built directionally through time and DNA strands are modified as whole units. So we should not be upset at having to pick up the mess created when young iconoclasts take up a new cudgel that happens to be lying around and beat social reality up with it. But we do have to do it. And with respect to causalism, cleanup is more than ever necessary. Causalism has been an immensely successful paradigm for sociological methodology, but the blunt fact is that it is now getting in the way of developments essential to the field. We have to refurbish and rethink our ideal of what it means to explain social life and we must reintegrate our theories and methods around that ideal.