Welcome to the International Studies Compendium Project blog!

The following exchange was generated by a discussion that emerged at a New Orleans ISA panel of IPE editors, and was published as a symposium in International Studies Quarterly 54:3 (pp. 887-907). We are grateful to William Thompson for facilitating the interaction and publishing it in ISQ, as well as to Renee Marlin-Bennett for inviting us to post it as a comment on her gateway essay to IPE in the ISA Compendium Project.

Are IPE Journals Becoming Boring?

Benjamin J. Cohen

University of California at Santa Barbara

Are IPE journals becoming boring? The question is a serious one. Over the four decades or so since the

modern field of International Political Economy was born, the character of what gets published in leadingjournals in the United States – IPE standard setters like International Organization, International Studies Quarterly, and World Politics – has changed dramatically. Arguably, the change has not been for the better.

To illustrate, consider a simple thought experiment. Think first of some of the memorable work published in the early years of the field – work like Keohane and Nye’s special International Organization issue on “Transnational Relations and World Politics,” published as a book in 1972; Peter Katzenstein’s 1976 IO essay on “International Relations and Domestic Structures, which in turn led to his special issue on “Between Power and Plenty,” also published as a book in 1978; or Stephen Krasner special issue on “International Regimes,” published in book form in 1983. Or think of Krasner’s 1976 World Politics study of “State Power and the Structure of International Trade”; Peter Gourevitch’s 1978 IO article on the second image reversed; John Ruggie’s 1982 IO essay on embedded liberalism; or Jeff Frieden’s 1991 IO paper on invested interests. All were seminal, foundational works – influential scholarship that is still widely read and cited.

Now compare these with anything that has appeared in mainstream journals over the last five to ten years. A great deal of quality research has been published, much of it making use of the most rigorous and up-to-date statistical methodologies. The intellectual candlepower is impressive. But how well does this work stack up against the output of earlier years? How much can be regarded as truly path breaking? How much is likely to be read or cited five to ten years from now? The answers, I think, are obvious. Our major journals are full of articles that are thoroughly peer-reviewed and edited with care. With rare exceptions, research meets the highest standards of scholarship. It’s just not very interesting.

The Problem

In my judgment, this is a grave problem. As I wrote in my recent book, International Political Economy: An Intellectual History (2008), somewhere along the way the field of IPE in the United States – what I call the American school – took an unfortunate turn. Increasingly priority has come to be given to formal scientific method, a hard science model resembling nothing so much as the epistemology of neoclassical economics with its well-known penchant for formal modeling and higher mathematics. Analysis is based on the twin principles of positivism and empiricism, which hold that knowledge is best accumulated through an appeal to objective observation and systematic testing. Pride of place is given to work that embodies the latest and most sophisticated quantitative or qualitative techniques. The trend is clearly confirmed in the latest TRIP survey of the international relations field (Jordan, Maliniak, Oakes, Peterson, and Tierney 2009; Maliniak and Tierney 2009), which carefully surveyed the contents of twelve leading journals since 1980.

Many reasons have been suggested for American IPE’s love affair with scientific method:editorial control of journals, the standards applied in tenure or promotion cases, the way we teach our graduate students. But these are more symptom than cause. Underlying them all is a deeper issue, involving us and our peers in the economics profession. To be blunt: political scientists in the United States appear to have an inferiority complex when it comes to economics – what I have elsewhere described as a case of peer-us envy (Cohen 2009). The parsimonious reductionism of mainstream economics has come to set the standard for what passes for professionalism in our field. If today the most highly rated work in the American school tends to mimic the economist’s demanding hard-science model, it seems in large part to demonstrate that the field, for all the ambiguities of the political process, is no less capable of theoretical elegance and formal rigor. IPE scholars want respect, too. A kind of “creeping economism” has come to define what constitutes the legitimate study of our subject.

Not everyone agrees that this is a problem. For many, the trend represents progress – all part of the “maturing” of the field, as David Lake (2006) puts it. The more IPE scholars agree on a common epistemology, the more their work approaches the respectability of “normal” science. In Lake’s words (2009:49), “cacophony” yields to “Kuhnian normalcy.” But at what cost? To my mind, such a happy assessment is altogether too kind, since it ignores all that is lost as a result. The price of this kind of “progress” is measured by how much now gets left out of what we have available to read.

In effect, the creep of economism has tended to shrink the horizons of scholarship. To a significant extent, this is because of the practical requirements of empiricism. By definition, a hard science model depends on the availability of reliable data. Research, accordingly, tends to become data-driven, diverted away from issues that lack the requisite numbers. In effect, the approach plays a key role in defining what can be studied, automatically marginalizing broader questions that cannot be reduced to a manageable set of regressions or structured case-study analysis.

The consequence, as I wrote in my Intellectual History, has been a distinct loss of ambition in American IPE. Out are the kind of big ideas and intellectual challenges that characterized the field in its earlier years. Instead, scholars are incentivized to focus on mid-level theory. In contrast to macrotheory (or metatheory), mid-level theory eschews interpretive theory or grand visions of history and society. Rather, work tends to concentrate on narrow individual relationships isolated within a broader structure whose characteristics are assumed, normally, to be given and unchanging. (Economists would call this partial-equilibrium analysis, in contrast to general-equilibrium analysis.) Such work is by no mean unimportant; much of it yields useful new insights. But like a steady diet of gruel, it leaves us hungry for more – more variety, more exotic ingredients, more spice.

Solutions

Can the menu be spiced up? Journal editors often take the view that they are prisoners of the submission process. They too may hunger for more variety, but what can they do? They can only select from among the manuscripts that are submitted. If all that comes in is economistic mid-level theory, then that is what they will publish.

To me that attitude is, to say the least, defeatist. We know that the editor’s job is an unenviable one, demanding long hours and many difficult, even painful, decisions. Reviewers must be found, verdicts rendered, manuscripts edited, schedules managed. We all owe the editors of this and other journals a debt of gratitude for the profound service they render on our behalf. But that does not mean that they must therefore remain passive in the face of the field’s disappointing loss of ambition. A more pro-active posture ought to be possible.

The goal is simple. Journals should aim to encourage more work that goes beyond the narrow straitjacket of a hard science model – work that dares to take on broader questions, even if that means some loss of parsimony or mathematical elegance; work that boldly poses new theory or paradigms, even if the necessary evidence may not yet be available; work, in short, that does not fear to be interesting.

To illustrate, consider some recent reflections from Robert Keohane (2009), who shares the discontent of many with the shrinking horizons of American IPE. A pioneer of the field, Keohane professes himself to be “disheartened” by the “new IPE” that has taken over in our journals. Much is missing, he avers – in particular, “the synthetic interpretation of change” (2009:40). More attention needs to be paid to major transformations that are going on in the world political economy, such as the emergence of China, volatility in financial and energy markets, the increasing role of global civil society, and the explosive growth of electronic technologies. In Keohane’s words, we need to “let the wings of imagination spread” (2009:43).

What can journal editors do to let the wings of imagination spread? Many innovations are possible. I would stress three strategies that I think could have an impact in the relatively short term.

Review essays

First, I would hope that editors could be more pro-active in soliciting review essays or surveys of selected issue areas like those identified by Keohane. Today only a few journals express a willingness even to consider review essays. Fewer still actually go out and look for them. This is regrettable, since one of the consequences of American IPE’s preference for mid-level theory is an increasing fragmentation of journal contents. We get isolated bits and pieces – a statistically significant regression here, a throughly documented case study there – but little sense of how all the pieces fit together. We would all benefit from more overarching analyses that try to tell us something about the forest, not just individual trees. Review essays provide an opportunity to survey important developments in a particular area of study, synthesize new ideas, and raise key issues for future scholarship. They give us a sense of where we are and – more importantly – where we might or should be going.

The counter-argument is familiar. Persuading scholars to undertake a review essay or survey is difficult, editors tell us. Academics are busy with teaching and their own research agendas; they just don’t have the time. Worse, few see much professional payoff from such an undertaking, as compared with a solid exercise in scientific method. Review essays don’t help much in gaining tenure or promotion. In the hierarchy of status among publications, they barely rank above book reviews or an op ed in the local newspaper.

But it doesn’t have to be that way. Much depends on the standards by which such work is reviewed and edited, as well as on how prominently it is positioned in a journal’s table of contents. In my own time, I’ve written my share of surveys and have never regretted doing so. One of my pieces has been reprinted repeatedly in edited anthologies and is still cited in the literature. I don’t really think that my career was set back by the time I invested in such endeavors. The challenge is to use the marquee power of our journals to give review essays the same cachet as standard research papers. If they put their mind to it, editors really could do much to make surveys seem a smart career move for ambitious scholars.

Symposia

Second, I believe that we would all benefit from more organized symposia on selected themes. Many journals already do try occasionally to provide something along this line, say by clustering together two or three articles that appear to be related in some way. But here too it seems that editors could be more pro-active. Why wait until a few papers come along that can be conveniently grouped under a single heading in the table of contents? Why not go out and do what the editor of International Studies Quarterly did in the case of this symposium: actively recruit contributions from an array of interested parties? Here is an opportunity for editors to really make a difference. Because of all the research they are exposed to in the submission process, editors are in a unique position to identify cutting-edge questions that we ought to be thinking about – in effect, to steer the development of the field. In my opinion, this sort of initiative should be made an integral part of their job description: a responsibility to spotlight critical problems, seek out potential authors, and encourage direct, stimulating engagement. This should be done on a regular, indeed routine, basis. The aim should be to promote constructive argument and debate – the more controversial, the better.

Again, I acknowledge that not all would agree. Why stir up controversy needlessly?, some might ask. Why risk fights that could just end up polarizing the field? Why not just let sleeping dogs lie? But as scholars, can we really afford the luxury of avoiding debate just because it might ruffle a few feathers? Contrary to those who yearn for the peacefulness of “Kuhnian normalcy,” I believe we regularly need to rouse the sleeping dogs, to acknowledge and energetically explore underlying cleavages in our field. As Peter Katzenstein (2009:130-131) has reminded us, “basic division is what constitutes the social sciences.... We cannot help but live our disagreements in cacophonous debates.” In his words, debates “remind us of the foundations of the normal work we do in our research and teaching” (2009:123). Argument is essential if we are to avoid intellectual complacency.

Submission policy

Finally, I think it is time for editors to fundamentally rethink existing submission policies. Typically, the instructions posted for contributors are straightforward. What the journals want are research papers, pure and simple. Appealing qualifiers may be added – words like “theoretical,” “analytical,” “empirical,” “original,” “innovative,” even “integrative” or “interdisciplinary.” But the basic message is clear. Preference will be given to submissions that meet the test of systematic and rigorous inquiry, backed to the extent possible by the standard methodologies of social science. Work of a more venturesome nature need not apply.

How might this change? Certainly no one wants to discourage the serious research tradition. That would mean abandoning the core mission of our journals. But must pages be reserved exclusively to standard research papers, at the expense of everything else? Why not reserve a portion of each issue to work of a different character, under some heading like Opinion or Commentary or New Thoughts? Journals in other disciplines do it. There seems no reason why we in IPE could not do so as well. Instructions to contributors could be easily amended to make clear that space will be regularly reserved for more unorthodox submissions – Big Think pieces that really do let the wings of imagination spread.

Of course, there would be a price. Journals have page limits. The more space is set aside for the unconventional, the less room is left for the traditional. Fewer straight research papers would find a home. Many would regard that as an unacceptable cost. But surely it is an empirical question – in the language of my original discipline of economics, a matter of marginal cost and benefit. In my judgment, the value added would far exceed the value lost, but I concede that this is an issue on which sincere people can sincerely disagree.

In the end, the question is simple: If indeed the menu needs spicing up, what is the best way to do it? Nothing less than the future of IPE in the United States is at stake.

References

Cohen, Benjamin J. (2008) International Political Economy: An Intellectual History. Princeton, NJ: Princeton University Press.

Cohen, Benjamin J. (2009) A Grave Case of Myopia. International Interactions 35:4: 436-444.

Jordan, Richard, Daniel Maliniak, Amy Oakes, Susan Peterson, and Michael J. Tierney (2009). One Discipline or Many? TRIP Survey of International Relations Faculty in Ten Countries. Williamsburg, VA: College of William and Mary.

Katzenstein, Peter J. (2009) Mid-Atlantic: Sitting on the Knife’s Sharp Edge. Review of International Political Economy 16(1): 122-135.

Keohane, Robert O. (2009) The Old IPE and the New. Review of International Political Economy 16:1: 34-46.

Lake, David A. (2006) International Political Economy: A Maturing Interdiscipline. In The Oxford Handbook of Political Economy, edited by Barry R. Weingast and Donald A. Wittman. New York: Oxford University Press.

Lake, David A. (2009) TRIPS Across the Atlantic: Theory and Epistemology in IPE. Review of International Political Economy 16(1): 47-57.

Maliniak, Daniel, and Michael J. Tierney. (2009) The American School of IPE. Review of International Political Economy 16(1): 6-33.

I Don’t Get No Respect:[i] The Travails of IPE[ii]

Vinod K. Aggarwal

University of California at Berkeley

The question of whether IPE journal are boring, in Benjamin Cohen’s provocative words, provides us with a useful opportunity to introspect on the state of the field. Briefly, to set the stage, Cohen argues that IPE has begun to mimic the methodological approach of most of the economic field—leading to a focus on mid-level theory—rather than on the big picture that characterized IPE in the early 1970s and 1980s. Cohen argues that journal editors have an important role to play to rectify this lack of imaginative thinking and writing. Specifically, he develops three well-articulated solutions. First, he suggests that the field would benefit from more review essays and that editors should actively solicit such articles. Second, he argues that symposia on various themes could help spice up the debate in the field. And third, he notes that changing submission policies to encourage commentaries and provocative arguments would enhance the prospects for greater creativity.

One might simply dismiss these concerns about the obsession with quantitative techniques and large data sets as just another fad. After all, much of political science (particularly the study of international conflict) was dominated by the “scientific” approach to studying conflict in the 1970s. UN voting studies are another example of obsession with quantification. The Correlates of War (COW) data set and analysis are the most prominent exemplars of this phenomenon in conflict studies. Since that time, COW data has been extensively used, but at the same time, there has been backlash against the original statistical approaches. Many alternatives, including formal modeling, qualitative techniques, and critical security studies, among others, have been developed to overcome what was often seen as “mindless number crunching.” So maybe it’s just a matter of time before the pendulum swings back. This symposium might then be seen as an effort to give the IPE pendulum a nudge.

Another competing hypothesis that warrants consideration is that the concerns raised by Cohen and other scholars he cites may just be a concern with preserving their own ontological and methodological preferences in view of their skill sets. This might then simply be a matter of the “old guard” that overthrew the previous regime in the 1960s (particularly in the case of the journal International Organization with its dramatic board transformation in the 1970s), and thus the dominance of new methods is just a matter of “out with the old, in with the new.”

Yet although these hypotheses may have some merit, I believe the problem that Cohen identifies is deeper than this. On the whole, I have few differences with the big picture of Cohen’s arguments: namely that journal editors can contribute to enhancing the contributions of IPE by being more creative in how they manage their journals. Yet although I cannot speak for other journals, the multidisciplinary journal I edit, Business and Politics, has attempted to do what Cohen calls for: publish review essays, symposia, and commentaries/cases over the last twelve years of its existence. From the very beginning, we have sought out all three types of contributions. At the same time, it would be difficult to claim that we have had great success in securing such articles. We have been able to secure high-quality review essays that have an impact, but getting them through the review process despite a note from the editor that these are review articles always generates a “what is the new theoretical or empirical contribution of this work?” from our referees. Symposia on selected themes are more popular, but generally in the form of special issues on topics rather than debates—as with this current ISQ effort. Finally, securing commentaries or cases has also been difficult, as the same issue of

“what is the new contribution?” comes up.

Our newest effort is to publish policy issues; but here, both writers and referees tend to be resistant. Policy submissions tend to be rare in our case—most likely because of the criteria that are used for promotion. And referees often try to judge policy articles we send them on traditional research contribution criteria – despite a note to them indicating the nature of the article. Given that Cohen himself has served and continues to serve on several eminent journal boards, successful pursuit of his recommendations may be more difficult than one might imagine.

So is this just a matter of the need for greater persistence by editors, including myself, and others? Or is there a fundamental problem with how IPE is viewed by other academics and by the policy community? To elaborate on what Cohen has aptly called “peer-us envy” and our relationship to economics, I find that the origins of the field are worth a brief exploration. In the 1970s, IPE became attractive to graduate students (such as myself) because of the clear problems in assuming, as international economists did, that global economic institutions were functioning smoothly and only in need of “fine-tuning.” As the Bretton Woods regime fell apart, the oil crisis of 1973-74 challenged power relationships, and as trade liberalization faced political problems, nothing seemed more relevant than IPE. Standard economic theory (and then dominant approaches to international relations and international organization) seemed incapable of answering the questions that were raised by these dramatic changes.

Although Cohen approvingly cites the creativity of this “foundational” work, what has nearly forty years of IPE research and writing brought to the field of international economics, whether in terms of new ontologies, methodologies, or new empirical research? Whether financial changes, trends in investment, commodity politics, and trade, or regional analysis of economic groupings, it is still rare for economists to actually cite any of this work. Maybe their own field has become so inbred that they are reluctant to look outside their own writing – or worse, not cite anyone outside their discipline. To them, IPE barely exists, despite IPE having secured a few strong draft picks from “the other side,” such as Benjamin Cohen and Richard Feinberg.

In my view, the respect that IPE seeks continues to elude us. Moreover, in the policy world and in the journalistic world, it is economists and historians who are sought out. Despite often recycling old ideas that have been a mainstay of IPE (the need for institutions, the role of power in the international economics system, the role of state intervention), when mentioned by economists in particular, these ideas are seen to be startling and original! Just to name a few, the views of Simon Johnson, Paul Krugman, Jeffrey Sachs, and Joseph Stiglitz, particularly in the current crisis, get wide play. The “peer-us” envy, then, is both with respect to academic respectability and policy-impact. On both scores, IPE continues to be wanting. Of course, a more cynical view would suggest that being cited by international economists, given their significant failures to anticipate the global financial meltdown of 2008-2009, is hardly something for which we should strive.

Cohen argues that many academics believe that the road to respectability is to use the high-tech quantitative techniques, large-data set approach, and formal modeling that characterizes much of economics. Yet as he clearly notes, it remains an open question whether such techniques, particularly in view of their relatively narrow focus on mid-level theory, will actually lead to greater academic respectability or policy influence. By contrast, economists may publish highly esoteric academic articles, but they have also been much better at addressing the key policy issues of the day.

A second theme that Cohen raises concerns the issue of standards of tenure and promotion. Here, the rise of globalization may have had a detrimental effect on IPE and political science more broadly. For many years in most countries, publication in “international” (often American) journals had only limited cache. Whether in South Korea, Australia, Singapore, or even the UK, connections and the “old boys network” often counted for more than citations. Yet while some continue with their old ways (Japan and France come to mind), we have now seen a dramatic transformation in publication standards for tenure and promotion as universities around the world have sought to move up the global rankings. Often based on a hard science and an economics model, citation counts and publication in SSCI journals have become the sine qua non for advancement. Many countries such as Korea have a point system: each type of publication is given a numerical value (with top rated SSCI journal publications, for example, counting for 200 points, but books only 70!). By my rough estimate, some of the leading lights in IPE would have secured insufficient points by tenure time to be promoted—despite their manifestly important contributions. Although this is a welcome change from the old boys in-house approach to promotion, this particular pendulum has clearly swung to the other extreme.

What does such a concern for journal publications at the expense of other types of contributions generate? Simply put, quantitative research using data sets that address narrow issues provide a risk-averse (clearly not rare in untenured faculty) path to tenure. MPUs (minimum publishable units) rule the day. Why risk conceptual or ontological innovation that might not be well received, when plodding along with marginal contributions will raise one’s point count? With such assessment standards, who would risk working on a book for 5 years? Moreover, with university presses increasingly becoming concerned with the bottom line, only commercially viable publications are generally the order of the day in any case (and with some university presses giving a disturbing emphasis to publishing only potential textbooks). The result is worship at the SSCI altar (a private company to boot) that does little to foster innovation and creativity.

This analysis may be unduly pessimistic. Although markets have shown evidence that they are not always self-correcting, it would appear that the type of debate that is being fostered by ISQ may well be the intervention that may be necessary to bring our field of IPE back to a more balanced footing.

Notes