The Duck of Minerva

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Much Ado About Nothing (Very Intellectually or Politically Important)?

June 18, 2015

The following is a guest post by Jeffrey C. Isaac, the James H. Rudy Professor of Political Science at Indiana University, Bloomington.  


What constitutes important political science research? This question has been much discussed lately in connection with “When Contact Changes Minds: An Experiment on Transmission of Support for Gay Equality,” an article by Michael J. LaCour and Donald P. Green published in Science magazine.

The reason for the attention is straightforward: because the piece was apparently based on fraudulent data, the article has become a veritable scandal. In the face of strong evidence that the article’s lead author had engaged in repeated and willful misrepresentations, co-author Donald Green, a distinguished senior scholar, issued a retraction and dissociated himself from the piece, and Science magazine itself later followed with a retraction of its own.

Fraud is almost always a serious ethical infraction and in some cases it constitutes a crime. In social science, and in the scholarly disciplines more generally, fraud, plagiarism, and other forms of deliberate misrepresentation are particularly egregious.

Commentary on the scandal has centered on three questions: (1) how could LaCour behave in such an unprofessional manner, get away with it, persuade a senior scholar to sign on to tainted research, and have the work published in a top peer-reviewed scientific journal, without being exposed until after publication? (2) what kinds of collaborative research processes are involved in situations like this, involving scholars on opposite sides of a continent who are not well acquainted with one another, how common are such practices, and how common should they be? (3) what does this episode say about political science as a serious science that possesses the resources to critically evaluate and judge scientific contributions, to expose error much less fraud, and to credibly distinguish valid from invalid, and important from unimportant, knowledge claims?

Each of these questions is important. But I would like here to press a fourth: what is political science, such that its practitioners might believe themselves to have something interesting to say about politics?

When LaCour and Green’s piece first came out, it was lauded by many as a “groundbreaking study,” and was regarded by some political scientists as particularly noteworthy because it passed the bar in Science, which is not simply a peer reviewed journal but an exclusive and prestigious general science journal. The piece seemed to demonstrate the real credibility, and value, of political science inquiry among (“real”) scientists and thus for all of those who value science. It is a shame that its reported findings are apparently based on fraudulent data and data analysis, and it is good that these mistakes were disclosed, so that better and more honest studies along these lines can be performed.

But I have a different problem with the piece: even if its data and data analysis were not fraudulent, and its findings “fairly” and “accurately” reported,” the piece is a narrow, limited, and relatively uninteresting contribution to political science.

Indeed, if political science is the scientific study of politics, power, and people broadly construed, than I question whether the piece constitutes a significant work of political science. It clearly constitutes a research report written by credentialed political scientists who believe that their research is in fact a branch of a unified science—which presumably is why they sought to publish the piece in Science magazine, alongside many articles and research notes detailing the scientific findings of various physicists, chemists, and biologists. And it clearly reports research findings about opinion formation in Southern California that are of potential interest to political inquiry. But this does not make it a piece that contributes substantially to important arguments and debates within political science scholarship.

If this comment sounds harsh—and it is intended to get your attention—then let me explain, by doing something that almost none of the commentators on the scandal have done: carefully discussing the article, not in terms of its data analysis, but in terms of the thinness of the “knowledge” it purports to advance. My thesis, as it were, is rather simple: the piece, at its best, is a brief, limited, and simplistic contribution to thinking about social behavior, and to regard it as anything more is to do an injustice to a great deal of really interesting and important work being done in political science on the topics of same-sex marriage and GLBT rights more generally.

I begin with a few simple “empirical” observations.

The piece is a three-page article. To describe it as “parsimonious” would be a gross understatement.

Its Abstract identifies the paper as treating a political topic: “Can a single conversation change minds on divisive social issues, such as same-sex marriage? A randomized placebo-controlled trial assessed whether gay (n = 22) or straight (n = 19) messengers were effective at encouraging voters (n = 972) to support same-sex marriage and whether attitude change persisted and spread to others in voters’ social networks. The results, measured by an unrelated panel survey, show that both gay and straight canvassers produced large effects initially, but only gay canvassers’ effects persisted in 3-week, 6-week, and 9-month follow-ups.”

Yet even here, more is said about a particular experimental study than is said about politics. Indeed, the Abstract does not deliver a thesis about politics at all.

Even a casual read of the paper suggests that the article is not really a contribution to political science analysis of “divisive social issues” much less of the particular divisive social issue that is same-sex marriage, and GLBT rights more generally.

The article has 12 endnote citations. Only the last one references a political science publication about politics (it is a Codebook). Most of the citations reference work in social psychology. None reference important work on same-sex marriage or GLBT rights.

Here is the paper’s first sentence: “Foremost among theories of prejudice reduction (1) is the contact hypothesis (2), which contends that outgroup hostility diminishes when people from different groups interact with one another.” This sentence states a problem—“prejudice”—and cites the study’s key theoretical source—Gordon Allport’s The Nature of Prejudicea book of social psychology which was published in 1954—over sixty years ago. Now, the dynamics of “prejudice” are surely an interesting problem of social psychology with political implications. But political science has come a long way since the 1950’s, both in understanding “prejudice” and in understanding the deep and reinforcing ways that political identities—especially sexual and gender identities—are shaped and maintained. In recent years there has indeed been an extraordinary outpouring of research and writing—in social movement theory, gender studies, cultural studies, political theory, “queer theory,” and even behavioral research—on these topics. The LaCour and Green piece cites none of this work. And its self-described research question is posed at a level of generality at which such work would seem irrelevant: “The question is whether brief or indirect contact is sufficient to produce meaningful and enduring attitude change.” As posed, the question would seem to lend itself to research on attitudes toward rival football teams or the music of Beyonce or any consumer good, or any electoral candidate, as much as to research on attitudes toward same-sex marriage (and, implicitly, attitudes towards sex and sexuality).

Indeed, this very short article offers no political analysis. None. Instead, it briefly discusses one small-group experiment involving the canvassing of 972 Southern California registered voters, each of whom was approached by a randomly assigned canvasser for a 22-minute conversation. LaCour and Green report that: “Conversations with canvassers who identified themselves as gay had a very large effect in changing pre and post-conversation opinions about same-sex marriage, and these opinion changes seem to have endured among most of the respondents as long as 280 days after initial canvassing took place.”

At its best, the piece offers a fairly anodyne knowledge claim: that conversations with activists might under certain circumstances change people’s minds, and indeed under certain circumstances an activist’s disclosure of their GLBT identity might positively impact views of respondents about same-sex marriage. To be clear, this result is not uninteresting, and it could well feed broader arguments about descriptive representation and the ways that sexual minority activists can best “represent” themselves in their efforts to build solidarity and garner political support. But the piece does not discuss these things at all. It does not engage a range of political science perspectives on the topic of GLBT rights or same-sex marriage even in the U.S.. It does not offer any political analysis of the causes or consequences of the results it reports. And indeed, it blithely reports the results of a single survey of a single locale as if its findings have some broader traction, in a manner that would not pass muster for any scholar of comparative politics writing a case study of anything. It is common practice for so-called “area specialists” writing on a region or a country—say the Middle East, or Tunisia—to be pressed by data analytic political scientists to answer this question: but how can you justify your case selection, and are your results generalizable? With this simple question, incredibly rich, interesting, and important work can sometimes be prematurely sidelined. And yet LaCour and Green studied one district in one part of Southern California and on the basis of this study they purported to shed light on opinion formation regarding the divisive issue of same-sex marriage in the U.S. And until the fraud was discovered, this was regarded by some as a credible (and indeed “groundbreaking”) contribution to knowledge rather than as a perhaps interesting finding that begs for more extensive but also for deeper and more substantial theoretical analysis.

If LaCour and Green seemed indifferent to methodological questions standardly pressed on more ethnographic researchers, they were also blithely indifferent to huge swaths of research on their purported topic.

Within political science there is a burgeoning literature in social movement theory about the evolution of gay rights, repertoires of contention, and shifts in public discourse in the U.S (see Deborah Gould’s Moving Politics: Emotion and ACT UP’s Fight Against AIDS ) and in comparative perspective (for most social scientists understand that there are broad global trends in play here, related to a transnational politics of GLBT rights ). There is also a growing effort of scholars of American politics to situate current controversies in a longer term historical perspective (Richard Valelly’s “LGBT Politics and American Political Development,” in the June 2012 Annual Review of Political Science , is one good overview of this literature; Stephen Engel’s “Developmental Perspectives on Lesbian and Gay Politics: Fragmented Citizenship in a Fragmented State,” in Perspectives in Politics , is another).

Indeed, there is a very large literature in political science more broadly—in comparative politics, public law, and even US politics– on the topics of gay rights, sexuality and cultural change. Scholars and journalists have noted dramatic changes in recent years, in general public opinion toward gay rights in general, and same-sex marriage in particular. A number of important legal cases have received extensive attention; a number of recent ballot initiatives, including the California initiative, have been analyzed; and indeed a range of explanations have been offered for this wave of developments, from post-materialist “modernization” theory to cultural theory to social movement theory (Of particular note is Michael C. Dorf and Sidney Tarrow’s “Strange Bedfellows: How an Anticipatory Counter-Movement Brought Same-Sex Marriage into the Public Arena,” in Law and Social Inquiry, vol. 39, no. 2 [2014] ). None of these streams of research are even mentioned in the LaCour and Green paper.

The paper does mention, in passing, that “the Los Angeles LGBT Center [is] our nongovernmental organization partner.” But LaCour and Green say nothing else about this organization, which seems important to them mainly because they were able to use some of its activists as canvassers in their study. A simple perusal of its website indicates that: “The Los Angeles LGBT Center traces its roots to 1969 when the founders of the organization first began providing client services. Today the Center’s more than 450 employees and 3,000 volunteers provide services for more LGBT people than any other organization in the world through programs that span four broad categories:  health; social service & housing; culture & education; leadership & advocacy” ( ). The Center also organizes an extensive series of adult education classes called “Learning Curve: Cool Classes for Queers, our Friends and Allies” ( ). The center traces its roots to 1969. Is there a connection between this “partner” organization and the famous New York City “Stonewall riots” of 1969—basically a response to anti-gay police brutality—that sparked the modern GLBT movement? Have the long-term, sustained cultural efforts of groups such as this “partner” organization had any important impact on the evolution of public opinion in Southern California on gay rights and same-sex marriage? Does it matter that this organization is practicing not simply a “rights politics” but a self-styled “Queer politics?” LaCour and Green are silent on such things. They report the results of their single experimental study as if these questions are not even worth considering.

For these reasons, it is hard to regard the piece as a serious contribution to major scholarly debates in political science. It may represent a small contribution to the social psychology of “prejudice” and to the micro-dynamics of modifying “prejudicial” beliefs. But such inquiry represents a very small part of serious social science inquiry into the sources of gender and sexual identity and the contentious politics of gender and LGBT rights.

To observe this is not to disparage this kind of work. The piece’s intuitions about canvassing may have validity, even if the data deployed to support this intuition appears to be fraudulent. But can such canvassing be so easily bracketed off from the broader and sustained priming of the public on this issue, in the U.S. and more broadly, and especially in Southern California, by Hollywood popular culture, and by political and cultural organizations like the Los Angeles LGBT Center? Is it possible to significantly advance political science knowledge by avoiding any discussion of politics and ignoring virtually all research on the politics of the issue in question?

The article engages no macro-political concerns. It is also rather inconclusive. LaCour and Green conclude: “Our experimental results demonstrate that active contact is capable of producing a cascade of enduring opinion change. Further research is needed to assess the extent to which the strength, diffusion, and persistence of active contact’s effects depend on how groups come together, the salience of their identities, the issues they discuss, and the manner in which deliberation takes place.”

I would agree with this. Much further research remains to be done. Some of this research may benefit from the use of the experimental survey methods employed by LaCour and Green. Some will involve more conventional forms of opinion research. Much of this inquiry will involve a broad range of methods and perspectives on politics, from queer theory to social movement theory to analysis of political parties to analysis of the diffusion of norms about sexuality and state regulation across an increasingly transnational and global public sphere.

Political science is a very rich, broad, and diverse discipline. The scandal surrounding the LaCour and Green article surely demonstrates that research ethics are important and that they can be egregiously violated. One can go further: published research that does nothing but report the results of particular empirical studies ought to be held to a very high standard of data accessibility and transparency. For such work, in the end, is nothing more than its data analytics. The LaCour and Green episode demonstrates that current practices do a good job of enabling mistakes and misrepresentations to be identified and critiqued. But it also demonstrates the narrowness of the kind of research that tersely reports “findings” rather than offers serious analysis, the kind of work that can command three or four pages of Science magazine—and can say almost nothing of interest about politics.

Most important work in political science involves more than the reporting of experimental or survey or even ethnographic results. It involves serious engagement with alternative interpretations of political problems, and serious analysis of such problems in historical time and space. The dramatic political ascendancy of the same-sex marriage agenda in the U.S. and in many other advanced liberal democracies is an exciting and interesting development. Political scientists have much to say about this development—about its historical conditions and causes and its variations (one very interesting account is Omar Encarnacion’s new book Out in the Periphery: Latin American Gay Rights Revolution, being published by Oxford this Fall); about the strengths and limits of “identity politics” and indeed of a movement politics centered around the institution of marriage, and about the complex intersections of sexuality, gender, race, and class; and about the concurrent ascendancy of a very sexually repressive politics, in parts of Africa, in parts of the Middle East (especially those parts now controlled by ISIS), and even in parts of Eastern Europe.

The LaCour and Green episode no doubt raises important questions about the rush to publish in the contemporary academy; the problems of intellectual responsibility that attend some forms of lab-style “team research”; and the ways that senior faculty sometimes connect with graduate students and junior colleagues doing this kind of research, signing onto projects in which they may not have been very active participants, thereby taking credit and also offering a kind of “scientific imprimatur” on such work.

But these questions do not implicate most of the important work being done in political science. And the kind of findings presented by LaCour and Green’s piece do not represent major contributions to the serious work being done political scientists on the pressing questions of our time, whether or not these findings rest on fraudulent data.

Two scholars have been caught cheating or at least misrepresenting their data. That is embarrassing for them and some of their associates. Science magazine was apparently enamored of a seemingly clever experimental study, and published the piece. That is embarrassing for the journal. And it is too bad that so much attention is being paid to this narrow experimental study, and so little attention is being paid to the fine work being done by so many others. Most of this work cannot be reduced to a research report or three-page article. And most of it is rather more interpretive, historical, humanistic, and seriously political, than the work published in Science magazine. Science is many things. But it is not a journal of serious political inquiry. And it does not loom large in the thinking of most political scientists. Most political scientists thus have no reason to get caught up in the current brouhaha. For there is truly important work being done that warrants our attention, and more work yet to be done.

The author would like to thank the following for their helpful comments: Ira Allen, Terry Ball, Nancy Hirschmann, Mala Htun, Mary Katzenstein, Peter Katzenstein, Rafael Khachaturian, Marc Lych, Jenny Mansbridge, Adrian Miroiu, Mihaela Miroiu, James Moskowitz, Anne Norton, Rogers Smith, Joe Soss, Dara Strolovitch, Sid Tarrow, Kathy Thelen, and Brendon Westler.

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Amanda Murdie is Professor & Dean Rusk Scholar of International Relations in the Department of International Affairs in the School of Public and International Affairs at the University of Georgia. She is the author of Help or Harm: The Human Security Effects of International NGOs (Stanford, 2014). Her main research interests include non-state actors, and human rights and human security.

When not blogging, Amanda enjoys hanging out with her two pre-teen daughters (as long as she can keep them away from their cell phones) and her fabulous significant other.