Paradigms and Sand Castles: Theory Building and Research Design in Comparative Politics

by Barbara Geddes

Overview

Paradigms and Sand Castles demonstrates the relationship between thoughtful research design and the collection of persuasive evidence in support of theory. It teaches the craft of research through interesting and carefully selected examples from the field of comparative development studies.
Barbara Geddes is Professor of Political Science at the University of California, Los Angeles.

Product Details

ISBN-13:	9780472023974
Publisher:	University of Michigan Press
Publication date:	03/25/2010
Series:	Analytical Perspectives On Politics
Sold by:	Barnes & Noble
Format:	eBook
Pages:	328
File size:	2 MB

About the Author

Barbara Geddes is Professor of Political Science at the University of California, Los Angeles.

Read an Excerpt

Paradigms and Sand Castles: Theory Building and Research Design in Comparative Politics

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By Barbara Geddes

University of Michigan Press

Copyright © 2003 Barbara Geddes
All right reserved.
ISBN: 0472098357

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CHAPTER 1 - Research Design and the Accumulation of Knowledge

'My name is Ozymandias, king of kings:

Look on my works, ye Mighty, and despair!'

Nothing beside remains. Round the decay

Of that colossal wreck, boundless and bare

The lone and level sands stretch far away.

--Percy Bysshe Shelley, "Ozymandias"

The last thirty years have treated students of the politics of developing countries almost as unkindly as the years did Ozymandias. At precisely the moment when the impulse toward authoritarianism had "been fully explained by a variety of converging approaches and [was] therefore understood in its majestic inevitability and perhaps even permanence" (Hirschman 1979, 98), democratization began its sweep through much of the world. In a second and even more unexpected development, governments in every region began to abandon state interventionist economic policies in favor of greater market orientation. On top of everything else, the Soviet empire collapsed. Though scholars have greeted most of these events with delight, few expected them, because theories dominant at the time these changes began did not predict them (cf. Remmer 1995, 103; and Kalyvas 1999).

Confronted by compelling and exciting events in the world, scholars quickly turned their attention to trying to understand them. One of the first fruits of these investigations was the recognition that few of the theories dear to the hearts of students of comparative development offered much leverage for explaining recent events. The limited usefulness of old theories was noticed early on--sometimes by the authors of earlier studies themselves--in the study of transitions from authoritarianism. Neither the dependency-influenced arguments that had figured so large in explanations for the surge of authoritarianism during the 1960s and 1970s (e.g., O'Donnell 1973; Cardoso 1973a) nor historical accounts of democratization (e.g., Moore 1966) seemed to offer much help in explaining flip-flops between democracy and authoritarianism. Guillermo O'Donnell and Philippe Schmitter eloquently express the inadequacy of standard interest group or class-based approaches.

During these transitions . . . it is almost impossible to specify ex ante which classes, sectors, institutions, and other groups will take what role, opt for which issues, or support what alternative.. . . [These are] choices and processes where assumptions about the relative stability and predictability of social, economic, and institutional parameters-- and, therefore, of their descriptive and explanatory power-- seem patently inadequate. (1986, 4-5)

Christopher Clapham and George Philip also highlight the apparent indeterminacy of regime transitions: "Patterns of military regime succession are rather like paths through the jungle: there are various trails, all pretty rough going ..., and most of them not leading where you want to go anyhow" (1985, 24). Processes appear complicated and unpredictable when we lack theories to explain them.

The literature on marketization has faced similar difficulties. Empirical studies find that the staple causal factor for explaining economic policy--interest group influence--accounts for few of the policy changes associated with economic liberalization (see, e.g., Haggard 1990; Haggard and Kaufman 1992, 1995; and Bates and Krueger 1993). Yet no one has discovered or devised a theoretical approach that works better than interest group theories. As a result, analyses of economic liberalization, like Students of the Soviet empire, in contrast, found it easier to explain its collapse. Their problem was not too few predictions of collapse, but too many. Since at least the 1950s, many analyses of communist regimes have stressed their inherent dysfunctions and contradictions. When the regimes finally broke down, these dysfunctions were invoked as causes. Yet these political systems had lasted forty years in Eastern Europe and seventy in the Soviet Union. An oddity of the transitions literature is that most early analyses of the breakdown of long-lived communist regimes emphasized their contradictions and weaknesses, while few discussions of the collapse of military regimes--which last on average about nine years--focus on inherent sources of regime fragility.

Since the cultural, social structural, and economic theories that had long informed the study of developing countries seemed to offer little help in explaining contemporary events, scholars turned to the study of politics for answers. But the theoretical cupboard was nearly bare. Because of our past failure to theorize the internal workings of political processes in developing countries, most analysts found themselves in uncharted territory when it came to building theories that use political causes to explain political outcomes. The result was the emphasis on contingency and voluntarism found in the early literature on democratization (e.g., O'Donnell, Schmitter, and Whitehead 1986; Diamond, Linz, and Lipsett 1989).

Early analyses of economic liberalization suffered from some of the same rudderless quality, though scholars attempting to explain different countries' responses to the international economic crises of the 1980s and 1990s found more uses for traditional ideas than did those studying democratization. International factors, primarily pressure from international financial institutions, continued to receive attention, as did pressures from domestic economic interests. Conjunctural country circumstances and the idiosyncratic beliefs and commitments of decision makers, however, also played a large role in analyses (see Stallings and Kaufman 1989; Haggard and Kaufman 1992, 1995; Bates and Krueger 1993; and Haggard and Webb 1994). Despite some efforts at theory building (e.g., Frieden 1989), this literature, like that on democratization, remained largely descriptive and focused on the details of decision making in different cases. In short, scholars working on two of the topics of highest salience in the developing world during the last quarter century--democratization and economic reform--found old theories wanting.

This did not result from acts of nature or of human contrivance beyond our control. The point of departure for this book is that we have made our own fate through our inattention to basic issues of research design. To be successful, social science must steer a careful course between the Scylla of lovely but untested theory and Charybdis, the maelstrom of information unstructured by theory. Much of the field of comparative politics has failed to keep to this difficult course, veering instead from one catastrophic extreme to the other. The result is a modest accumulation of theoretical knowledge in many parts of the field. Arguments, theories, and even paradigms tend to rise and fall in rapid succession, leaving behind little to show that they ever existed. Like elaborate sand castles, paradigms have been built with great effort and attention to theoretical detail, only to be washed away by the tide of the next generation of graduate students, whose research batters at the weak points of existing paradigms--as it should--until the theoretical edifice crumbles and disappears.

The need to start over with every new current event cannot be attributed to any failure of theoretical imagination among comparativists. Rather, it is the result of our inability to build on, develop, and extend old theories instead of periodically discarding them. This is not to say that we are promiscuous or disloyal to our theories. We cling to them with the same fervor and tenacity as do other scholars to theirs. The problem is that our theories--siren songs composed without systematic checking against facts--eventually disillusion us. Cruel and inconvenient facts, often available at the time of composition but not used, eventually insist on our attention and force the abandonment of our creations.

As a consequence, we face new happenings in the world with few theoretical tools, condemned to begin from scratch with unstructured, inductive searches for patterns. At their best, such inductive explorations lead to generalizations and correlations, which in turn give rise to theoretical speculations. More typically, however, inductive fact-gathering missions result in a disorganized mass of information. "Only very occasionally . . . do facts collected with so little guidance from pre-established theory speak with sufficient clarity to permit the emergence of a first paradigm" (Kuhn 1970, 16). Though they need not be, in practice theoretical speculations arising from inductive studies tend to be marred by vague, unarticulated first principles and behavioral assumptions that have not been carefully thought through. Apparent relationships between cause and effect may be uncovered within the set of cases examined, but few efforts are made to find out if such relationships also occur among other cases. Sometimes historical detail substitutes for causal argument, and the adumbration of events leading up to outcomes takes the place of explanation. Authors may carefully hedge their tentative arguments with caveats about the need for further testing, but most readers ignore the caveats and attribute to such arguments the status of established findings. As a result, sturdy, long-lived theories all too often fail to emerge from inductive work.

The central message of this book is that we could steer a course through that narrow channel between untested theory and atheoretical data more successfully, and thus accumulate theoretical knowledge more rapidly, if certain research norms were changed. Although research norms are changing, basic principles of research design continue to be ignored in many studies. Common problems include inappropriate selection of cases from which to draw evidence for testing theories and a casual attitude toward nonquantitative measurement, both of which undermine the credibility of evidence gathered to support arguments. The failure to organize and store evidence in ways that make it accessible to others raises the costs of replication and thus also slows theoretical progress. Uncritical acceptance by readers of theories that have not undergone systematic empirical tests exacerbates the problem.

Granted, we work in a harsh environment for the development of solid theory because of severe information limitations, but harsh environments sometimes lead to useful innovations. This study will suggest some innovations and some ideas borrowed from other fields. The book deals with several of the widespread methodological practices noted above, showing their unfortunate consequences and making suggestions for their improvement. It begins with a controversial subject: the translation of fascination with "big structures, large processes, huge comparisons" (Tilly 1984) into useful and replicable research. It then moves to relatively well understood issues such as case selection and concept operationalization. Finally, the book concludes with a discussion of the characteristics that a good theory should have and highlights the uses and limitations of the rational choice framework as one possible approach to theory building.

The Rise and Fall of Paradigms: An Example

Although a great deal of excellent research has been done on developing countries, the methodological faults noted above have also been quite common in the study of less industrialized countries. To illustrate how weak research norms can cause the sandcastle effect, I sketch the history of one prominent theoretical tradition in the field of comparative development. The intellectual history reprised here, of the rise and fall of the modernization and dependency paradigms, will be familiar to most comparativists. Hundreds of us reviewed it ourselves on qualifying exams. The basic arguments and concepts will be novel only to the young. I use an important and well-known, though now outdated, debate for this example in order to show the centrality of the problems I address later in the book.

The history of the study of the relationship between economic development and democracy can be periodized by the rise and fall of paradigms in much the same way that the history of many developing countries themselves can be periodized by the rise and fall of regimes. My use of the word paradigm differs slightly from Thomas Kuhn's (1970), in that he defines a paradigm as the dominant understanding of a particular class of phenomena at a particular time. As Mattei Dogan (2001) notes, political science is in Kuhn's terms prescientific. Consequently, no Kuhnian hegemonic paradigm has existed. The collections of theories, hypotheses, applications, and favored methodologies I refer to as paradigms do, however, have most of the other features Kuhn attributes to paradigms. They encompass a set of factual and explanatory knowledge claims, in other words, theories, that are widely accepted by adherents. And they structure further research: determining which facts are theoretically salient; defining what constitutes a paradox and what questions urgently require answers; identifying which cases need to be examined and what kinds of evidence are considered meaningful.

Like regimes, paradigms are sometimes overthrown by well-organized, coherent, mobilized opposition--as, for example, modernization "theory" was toppled by dependency "theory." At other times, paradigms fall because of their own internal contradictions and their inability to deal with the inconvenient facts thrown up by the world--the fate of dependency theory in the early 1980s. When this happens, paradigms, like regimes, are succeeded by periods of chaos and contention. Such a phase followed the fall of dependency theory.

To achieve success, paradigms need to have the same characteristics as successful ideologies. Ideologies simplify the world, explain what we see around us in a compelling way, and identify what needs to be done. The basic ideas need to be simple, yet applicable to a broad range of puzzling questions. They need to have the "aha!" factor--that is, to lead the newly exposed individual to exclaim, "That has to be right! Why didn't I think of it?" And finally, paradigms need to be fruitful; the theories they contain need to explain previously unexplained regularities and to create new paradoxes and puzzles. As ideologies imply needed political action or policies, a successful paradigm implies a research frontier of puzzles and paradoxes on which scholars need to work. Among the theory-induced paradoxes of note, the vast outpouring of work on voter turnout spawned by the theory of collective action plays the same role within its intellectual framework as did the vast outpouring of work on false consciousness within the Marxist framework. In both instances, real-world phenomena that might otherwise have been considered thoroughly unremarkable--that is, citizens vote and workers fail to rebel-- have been subjected to intense scrutiny and debate because basic theoretical premises render them puzzling within their respective theoretical worldviews.

The brief history below demonstrates the relationship between evidence and paradigm shifts. Each paradigm lost its power to structure research when evidence of gross inconsistency between expectations arising from theories within the paradigm and real-world events became impossible to ignore. This is the usual mode of progress in science: earlier theoretical understandings are first undermined by inconsistent facts and then replaced by newer theories that can accommodate both old and new evidence. The claim here is thus not that theories or paradigms are overturned in some unusual way in the subfield, but rather that evidence was available that should have called them into question at the time of their creation. It should not have taken decades to notice the plethora of inconvenient facts.

When developing countries first began to receive concentrated attention from political scientists after World War II, central questions for the emerging subfield were (and remain today): what causes democracy? and what impedes economic development? Scholars not only scrutinized events and processes in developing countries themselves, but also returned to the study of the historical development of the more industrialized countries and compared different political and economic routes to development. The paradigm that emerged was the loose collection of assumptions, generalizations, and hypotheses referred to, generously, as modernization "theory." I label modernization theory a paradigm because the generalizations, hypotheses, and theories of which it was composed formed a more or less consistent and logically coherent body.

The modernization paradigm reflected the times in which it developed, as do all paradigms. Some of its central ideas drew on observations of the world during the 1950s, a time when technology and democracy seemed to be spreading rapidly from the North Atlantic countries to the rest of the world. Observers assumed they could extrapolate their own time into the future. Other ideas in this paradigm derived from contemporary academic theories, especially pluralist understandings of politics and neoclassical economics.

The pluralist image of political life contributed to expectations that change would come about incrementally and peacefully through the interplay of societal interests (cf. Binder 1986). Neoclassical economics supplied theoretical support for a view of the international economy as simply the medium through which trade could occur, enabling resources to flow to their most efficient use and all parties to capture the gains of specialization based on comparative advantage.



Continues...

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Table of Contents

Contents Acknowledgments 1. Research Design and the Accumulation of Knowledge 2. Big Questions, Little Answers: How the Questions You Choose Affect the Answers You Get 3. How the Cases You Choose Affect the Answers You Get: Selection Bias and Related Issues 4. How the Evidence You Use Affects the Answers You Get: Rigorous Use of the Evidence Contained in Case Studies 5. How the Approach You Choose Affects the Answers You Get: Rational Choice and Its Uses in Comparative Politics 6. Conclusion Appendix A Appendix B Appendix C Bibliography Index