Creative Marginality

Innovation At The Intersections Of Social Sciences

Mattei Dogan

• Publisher: Taylor & Francis
• Year: 2019
• eBook ISBN: 9780429714320
• Edition: 1
• Topic: Social Sciences
• Subtopic: Sociology
• Index: Social Sciences

Tracing the nine formal social science disciplines - political science, sociology, economics, history, anthropology, philosophy, geography, psychology, and linguistics - through their cycles of growth, specialization, fragmentation and hybridization, Dogan and Pahre reject the notion of catch-all "interdisciplinary" research. They set out to demon

Part One
Scientific Innovation and Obsolescence

Innovation is at the core of this book because we maintain that it is more likely to appear where at least two specialized subfields overlap. Innovation, however, is not easy to define. “Creativity,” a term related to “innovation,” is a very elusive concept notwithstanding a large body of psychological research on the topic. Some scholars have defined creativity as the novel combination of two or more ideas, without having explained precisely how this is done by creative persons. Such an interpretation is surely suggestive for our purposes, although to take this definition as an equivalent of innovation would make our thesis almost tautological.

We define innovation as the addition of something new, whether large or small, to the scientific project. It must be examined in its scientific context. Innovation is not merely unequally distributed among scientists, it is unequally distributed among scientific subfields. It is also unequally distributed within the same field over time. Innovation has a history in each field, and the accumulation of innovations produces a “patrimony” of knowledge.

Subfields have both cores and margins, and innovation is different in each. In a core, innovations are often smaller in scope, hemmed in by a crowd of other researchers sharing similar assumptions and blinders. In contrast, areas which are at the margins of two subfields show the greatest potential for innovation. Not only are the margins less densely populated, providing more room to grow, but successful combinations of material from two subfields typically allows greater scope for creativity. In fact, the greatest accumulation of incremental advances takes place at the intersections of fields.

This should not imply that combining two specialties will make the scholar a giant. A scholar need not be a star to be an innovative hybrid, and innovation is a mass phenomenon.

1
Defining Innovation in the Social Sciences

Every self-respecting scholar wants to innovate. Some have grandiose ambitions; others would be satisfied adding a few bricks to the construction of the scientific edifice. How have earlier innovators arrived at their discoveries? Is it solely a matter of individual genius, or are there strategies which help a scientist make the most of whatever talent he or she has?

To answer this question we must first attempt to identify the innovators. In the United States, there are nearly 150,000 college-level teachers in the social sciences as a whole, on the order of 10,000 to 50.000 in each discipline, (see Clark 1987: 12, 55) There are another 30.000 or more in Japan, about 20,000 in West Germany and an equivalent number in Great Britain. Depending on the discipline and the country, there may be several thousand more Ph.D.’s, employed by government agencies, private research centers, and other institutions, who are active in research. Not all of these researchers publish, and not all published articles are useful for others. For instance, out of all the people who received Ph.D.’s in sociology in the United States in the 1930s and 1950s, more than half published at least one article or book; only a third of the total, or about two-thirds of the published authors, garnered one or more citations. (Chubin 1973: 188) How many of these latter could be considered innovators? It would be impossible to provide a consensual definition.

It is difficult to define innovation, in part because science can advance by small increments, at a snail’s pace. Imagine, as one example among hundreds, a linguist studying the languages of inland New Guinea—unmapped territory, to say nothing of unstudied. Whatever this scholar learns is new, and may or may not be important for colleagues. Yet one cannot deny this work its novelty, and science advances. Some of these studies will produce discoveries of wider theoretical value—but it is difficult, if not impossible, to know beforehand which will prove to be most important. Many languages distinguish nouns on the basis of animacy, for instance, but a proper understanding of the role of this distinction in langugage awaited the analysis of the elaborate hierarchies of animacy in several Australian languages. The first intrepid grammarians of these languages could not have known this in advance. Ethnographers are another example; each culture studied adds to our knowledge, but only a few such works will achieve the wide importance of Bronislaw Malinowski, A. R. Radcliffe-Brown, or Margaret Mead. The differences are in large part attributable to the scholar’s talent, of course, but there is also an element of chance which makes some cultures more interesting than others. Certainly anthropology would be different if the Trobriand Islanders studied by Malinowski lacked the trading institution of the kula, for instance.

We obviously cannot dismiss scholars who carry on such research as mere data collectors even if their own work is not of the same degree of importance as Malinowski’s. After all, Copernicus’ discoveries were only possible because of data collected by Georg Peuerbach and Johannes Müller. The next major discovery, Kepler’s laws, would not have been possible without the vast improvement in planetary tables by Tycho Brahe. In the social sciences, Joseph Greenberg’s study of language universals could not have been made without hundreds of grammars written by field linguists. Historically minded theorists in all social sciences are dependent on monographs written by historians who have sifted through a mass of primary sources. In any case, it is not always easy to predict ahead of time which data will be more interesting than the others.

Obviously good data collection is not pursued in a vacuum. The geographer Paul Vidal de la Blache stated the issue for geography succinctly in the preface to his Atlas (1894): “considered in isolation, the features that go to make up the physiognomy of the countryside are significant as facts; only when they are related to the chain of events of which they are a part do they become significant as scientific ideas.” In political science, there are many articles every year which present the results of recent elections and discuss their meaning in depth. While valuable as data collection, such articles are much more useful if they use this new data to confirm or disconfirm existing theories. Then, such work is not only novel data collection but an innovative contribution to science. Both data and interpretation are obviously important, and data collection unrelated to interpretation and theory is usually trivial. Most data collectors are aware of the danger and do interpret or theorize about their data; certainly the more innovative ones do.

Besides the fusion of novel data collection and innovative theories, innovation is also characterized by the fact that large bodies of work spring up around important hypotheses, even within narrow subject areas. We may take as an example two related hypotheses concerning the party systems of Scandinavia—the Rokkan hypothesis, which explains the origins and persistence of the basic five-party systems of Denmark, Finland, Iceland, Norway, and Sweden, and the Bull-Galenson hypothesis, which predicts the degree of radicalization in the social democratic parties of the region. Virtually every work on the politics of these countries makes reference to one or both of these hypotheses, refining their applicability to various subnational regions, to changing cleavages and to the appearance of new political issues, and testing their applicability in light of new knowledge. None have refuted the hypotheses outright, but they have as a group much improved them. It is through this kind of work that science progresses, and we must grant every refinement a degree of innovation. Nonetheless, the most important contributors were obviously Stein Rokkan, Edvard Bull, and Walter Galenson, without whom the further developments would not really have been possible.

These new theoretical and conceptual formulations are mirrored by others who have made methodological improvements in a given theory. Take a researcher who refines the innovative work of twenty years ago, using more sophisticated methods. There have been about a dozen who have improved the data and methodology of Seymour Martin Lipset’s classic “Some Social Requisites of Democracy,” confirming Lipset’s thesis in a more persuasive fashion. This, too, contributes to science.

Other important works are revivals and refinements of forgotten research, rather than innovations in the sense of novelty. Alexander George’s article on the “operational code” very explicitly attempts to revive the work of Nathan Leites. His clarifications and summary are important and useful, and probably more widely read than the original. Can we deny it the label “innovative”? Being able to resuscitate scholarship of the past in such a way that it is relevant to present debates is no mean feat.

All these refinements are at the core of what Thomas Kuhn (1962) calls “normal science.” They take most things as given, and endeavor to improve on the remainder. We must remember, as Derek de Solla Price points out, that “Mountain peaks are not typical. You cannot judge all scientists by the standards of Newton and Einstein. You cannot judge the technological impact of science by the case of transistors.” (de Solla Price 1975: 130) While less spectacular than revolutionary science, gradual improvements are the main engine of the scientific project. No discussion of innovation can avoid them, even if “normal science” is not the only form of science.

It is tempting, but impossible, to determine a single scale of “innovativeness.” There are many varied kinds of innovation, and their relative importance is impossible to judge. Is importance to be defined in terms of a profound essay almost incomprehensible to most other scholars, or should importance be seen in terms of the number of citations? The three volumes of the World Handbook of Political and Social Indicators, edited by Bruce Russett et al., Charles Taylor, Michael Hudson, and David Jodice, were among the most cited books in political science in their day. Yet this is a different kind of innovation than the work which others have built using these data, just as Brahe’s planetary tables were a different kind of innovation than Kepler’s laws. Because they are so different, it is difficult to rank them on a single scale of “innovation.”

Length is certainly not a measure of innovation. It does not indicate profundity, in contrast to what some scholars seem to believe. Three seminal essays by Frederick Jackson Turner, “The Significance of History” (1891), “Problems in American History” (1892), and “The Significance of the Frontier in American History” (1893), are only sixteen, twelve, and twenty-five pages long, respectively. On the other hand, the great historian Leopold von Ranke wrote fifty-four volumes, including a twelve-volume history of Prussia. Both were great historians, and it would be futile to rank one’s life work against the other’s, but Turner is far more innovative on a per page basis. His succinctness also helps make him widely read even today. The virtue of succinctness can be seen in its clearest form when a single article, in all its brevity, proves to be seminal. Paul Samuelson’s original theory of public goods is only three pages long, but served as the basis for the study of an important topic in both economics and political science. W. S. Robinson’s article, “Ecological Correlation and the Behavior of Individuals” (1950), is only six pages long but succeeded in driving scholars out of ecological analysis and into survey research in sociology, urban studies, geography, political science, and demography. Mark Jefferson’s “The Law of the Primate City” (1939) in the Geographical Review is only seven pages long; he uses statistical methods to propose a theory at the interstices of geography and demography. There are also books in which only a single chapter is innovative. For instance, a single chapter in Daniel Lemer’s Passing of Traditional Societies established for the first time a meaningful relationship between the processes of urbanization, literacy, mass media, and political participation. To do so, he used statistical techniques and material from several specialties. This chapter is widely cited, usually by authors who do not cite the remainder of the book. The reader could easily think of other examples of innovative but brief works.

The most important aspect of innovation is that modern innovators do not span whole disciplines or even major parts of them, but at most only a few subfields each. As the examples of succinctness show, the catch-all interdisciplinary approach is by no means necessary, and is in fact undesirable. Specialization is essential. If we were to compile a list of the innovators in ten or so subjects or subfields, even related ones, we would find that the overlap of names is relatively limited. Take, for instance, the related literatures on neocorporatism and consociational democracy. Among the most prominent contributors to the study of neocorporatism we would include such scholars as Philippe Schmitter, Suzanne Berger, Gerhard Lehmbruch, and many Scandinavian scholars; for consociational democracies, Arend Lijphart, David Apter, Val Lorwin, Jtirg Steiner, Gerhard Lehmbruch, Kenneth McRae, G. Bingham Powell, and many others. While the topics are related, the overlap of names is small.

Because of such specialization, it is easy to overlook innovations in subfields other than our own, out of detachment from the problems others are trying to solve. To avoid oversights, we should define innovation in terms of importance for those in the relevant fields. Only a specialist in a given subfield can define what is innovative in that area; this is, after all, the principle of peer review. We are not competent to decide this question for most specialties, and rely on the evaluations of others of what is important. In cases of ambiguity as to whether a given method, concept, or work is innovative, it is better to err on the side of inclusiveness. This is not to say that we should include everything which could possibly be considered innovative, but if we are in doubt about the innovativeness of a work, we are willing to suspend judgment. With thousands of publishing scholars in each discipline, we will leave definitive evaluation to each author’s peers.

It is clear that innovation is a mass phenomenon, as can be seen by browsing through books and journals. The index of the Handbook of Sociology (Smelser, ed. 1988) lists approximately 3,000 names, and it is doubtful that each and every innovator in sociology made the list. The American Political Science Review has reviewed about 100 books in each issue over the last ten years, or 400 per year; the rate was about 200 per year in the 1960s. That is 8,000 in a quarter century, and it does not include all the books published in the discipline. Even if only one out of four was innovative, a conservative estimate, that nevertheless leaves us with 2,000 innovative books. The number of innovative journal articles must be enormous.

Of course, some attribute the explosion of publications not to innovation, but to the imperatives of “publish or perish.” Certainly scholars are driven to publish. They are not, however, driven to cite the uninteresting work of others. We may use citations, in some respects, as an indication of innovation (see Chapter 4). The size of the Social Sciences Citation Index clearly shows the massive extent of citation, suggesting that there is indeed a lot of citation-worthy work being done throughout the social sciences. Naturally the extent of the innovation varies widely: the modal number of citations per article per year is one, while the mean is over four, reflecting relatively few articles each with very many citations. If no one in the specialty cites a given article in the ten years following its publication, we may safely conclude that it was not innovative (if we allow for a few exceptions). And the rest? We are inclined to be generous. Some, with a few citations, are minor innovations; others are earth-shattering; hundreds and hundreds fall somewhere in between. This is true in all of the formal disciplines.

What, then, is a minimal innovation? We may give several examples. Someone who works to improve a correlation coefficient from someone else’s work does advance science, but in a minor way; the same is true of many works which explain residuals. Unimaginative experiments in psychology are also new, and may be useful for others, but are minor innovations. In economic theory, scholars often improve the mathematical proofs of other scholars by correcting errors or by making the proof shorter or more elegant; these, too, are innovations, but of a decidedly minor kind. At the other end of the spectrum we find Darwin.

It is impossible to determine accurately the distribution of works along any imaginary continuum of innovation, although estimates are possible. Some have suggested a rough “law” of scholarly productivity which suggests both that innovation is a mass phenomenon and that it is very unevenly distributed among scientists. According to the “Lotka-Price law of productivity,” the number of scientists producing n papers is k/n², where k is a constant. In relative terms, this implies that for every one hundred scholars producing one article apiece, twenty-five other scholars will produce two each, eleven will produce three, eight will produce four, and four scholars will each produce five articles. As a result, approximately ten percent of all scientists produce about half of all scientific papers. Even so, the mass of scholars who publish only rarely do, as a group, produce a signficant volume of research. Citations seem to follow a similar pattern: in a study of the articles which three leading sociological journals published in 1960, twelve percent of the sample received fifty-five percent of the citations; about two-thirds of the papers were cited at least once, excluding self-citations (Oromaner 1977: 127). This is approximately what the Lotka-Price law would predict. As another example, by our estimate only three or four percent of the 10,000 citations in the Handbook of Sociology (Smelser, ed. 1988) belong to the five “stars,” Karl Marx, Max Weber, Emile Durkheim, Talcott Parsons, and Robert Merton; the other 97 percent are spread among 3,000 people. Again, this is roughly in accordance with Lotka-Price. Of course, we should not read too much precision into this “law,” and we must remember that it says nothing of “innovativeness,” an unquantifiable concept. Even so, as a rough rule of thumb which has empirical support in both publication and citation data, it is a reasonable working hypothesis on the distribution of innovation among scientists.

Some have explored the innovations at the highest levels of the continuum. Karl Deutsch, John Platt, and Dieter Senghaas (in Deutsch, Markovits, Platt, ed. 1986) have compiled an important list of twentieth-century innovations in the social sciences using much more exclusive criteria than we, defining an innovation as an “advance which makes a substantial contribution.” The Deutsch-Platt-Senghaas list does identify some of the most important innovations in the social sciences, but few scholars can hope that their work will be of this magnitude. Furthermore, in some ways their list is rather curious, for they have a substantial bias in the direction of general approaches (“elite studies”) as opposed to specific findings (“iron law of oligarchy”), and they do not in fact identify individual works at all. This means that a lot of innovative work, especially findings in specialized subfields which are not necessarily of relevance for the social sciences as a whole, are excluded. Their list also ignores cumulative advances, such as those by researchers filling in the substantive gaps between subfields by using already-discovered innovations. Furthermore, many important findings are inexplicably left out; Alex Inkeles (1986) has suggested a large number of innovations in sociology which are strangely absent, and the same could be done for each formal discipline. Another peculiarity of their list is the inclusion of “innovations” which are actually a matter of praxis: the Fabian Society’s strategy of gradual social transformation, Lenin’s revolutionary strategy, Mao’s revolutionary strategy, the Soviet one-party state, and Gandhi’s strategy of non-violence were all political innovations, but not scientific...

Table of contents

• Cover
• Half Title
• Title
• Copyright
• CONTENTS
• Preface
• Introduction
• PART ONE SCIENTIFIC INNOVATION AND OBSOLESCENCE
• PART TWO FROM SPECIALIZATION AND FRAGMENTATION TO HYBRIDIZATION
• PART THREE THE CRUMBLING WALLS OF THE FORMAL DISCIPLINES
• PART FOUR THE INTERPENETRATION OF DISCIPLINES: THE PROCESSES OF HYBRIDIZATION
• PART FIVE GALLERY OF HYBRIDS: CREATIVE MARGINALS
• PART SIX CROSSROADS: FOUR ILLUSTRATIONS
• Final Remarks: The New Kaleidoscope of Social Sciences
• Bibliography
• Author Index
• Subject Index