Problems, Puzzles, and Questions

24 January 2006, 1305 EST

One of the perennial issues for academics, and perhaps especially for academics studying social phenomena (although I can easily see how this would be of concern for those of my colleagues in the physical sciences as well), is the relationship between the issues and topics that we choose to study and the concerns of politicians, bureaucrats, and the electorate as a whole. This is a perennial issue in part because, whether we teach at public or private institutions, we are in large measure supported by social surplus — whether in the form of governmental funding, alumni donations, tax breaks, or some combination thereof. [I am not including tuition payments under the heading of “social surplus,” because tuition is a fee for a service, unlike alumni donations and the like.]

The question thus arises: what does society as a whole get for its support of academic institutions and the academics who populate them? Obviously, the teaching that we academics perform is part of it, but that’s not all that we do. Indeed, professional advancement in academia is, for better or for worse, largely dependent not on teaching but on research, and in particular on the publication of that research. Hence, the more precise question is: how should academics choose the topics of their research? A popular answer to this question, and one that was often articulated this weekend at the conference that Dan and I organized, is that scholarly research ought to be “problem-driven.” I’ve always been a little uncomfortable with this response, and I’d like to take a few minutes here to publicly think through why I am uncomfortable — and what I would prefer to see instead.

At first glance, the notion of problem-driven research has a lot to recommend it. Calling something a problem implies the existence of a solution of some kind, which would suggest that problem-driven research would, in principle, provide such solutions. The social benefit here is relatively clear: in return for their occupation of a relatively privileged place in the contemporary market economy (including tenure, which essentially guarantees academics a job in perpetuity), academics are expected to solve pressing social problems. Implicit here is a definition of a problem as a matter of public concern, as something “important” to the populace as a whole or to some significant portion of it; otherwise, the solution would have little public value. So the idea here is that academics should be working on themes and topics suggested by the broader public.

An opposing point of view might locate the sources for research topics not in the broader public, but instead in the narrower realm of the academic community: in the particular discipline within which the academic works, or perhaps even more specifically within the academic’s own particular intellectual school or theoretical camp. Following Thomas Kuhn, we might call this “puzzle-driven” research, where a puzzle is defined as something that appears strange or inexplicable to adherents of a given set of conceptual or theoretical assumptions. What this means is that the relevant community whose members immediately recognize the importance of the topic is not the public at large, but the community of researchers who share a series of assumptions with the researcher.

Both of these views have something to recommend them, but also have some significant drawbacks. The advantage of a problem-driven selection criterion is that the topic thus chosen has immediate practical relevance, and stands in no real need of further justification — since everyone basically already accepts that the issue is important, simply saying that one is working on “poverty” or “war” or “human rights” is quite sufficient. And of course, working on a topic that everyone already acknowledges is important means that whatever insights or remedies one generates will also be of more or less immediate applicability.

But there are two important costs associated with this kind of popular resonance: the tyranny of the present, and the disappearance of “problematization.” The first of these stems from the fact that the public isn’t always concerned about the same things, and (democratic triumphalists to the contrary) what holds the public’s attention at any given point in time might easily not be the things that are most in need of research. The cheap shot here is “terrorism,” which not many people considered all that important an issue for American researchers to focus on before 9/11, but which has now crowded out several other topics on the popular agenda. So being problem-driven means, in a way, being unable to deviate very far from the public’s already-expressed preferences.

The second cost of problem-driven research is that every popularly-perceived problem comes along with and arises from a problematization, a socially sustainable way of approaching a topic so that it appears problematic rather than ordinary or acceptable. Michel Foucault’s studies of “sexuality” are among the best examples of what a problematization is and does; Foucault argues that the various issues associated with sex in the last couple of centuries (including incest, homosexuality, repression of trauma, etc.) were only held to be “problems” standing in need of social regulation and therapeutic intervention because of the broader framework within which they were (often implicitly) discussed and perceived. Something similar can easily be said for problems like poverty, unemployment, war, and the like — at any given historical juncture, a problem comes along with a problematization that stresses certain aspects of the problem as problematic, and provides a general heading under which to address them. Take war: if one thinks that wars are inevitable, then war isn’t a problem! It’s only if one thinks that peace, or a balance of power equilibrium, is the natural condition of things that war becomes problematic. Or take unemployment: if one believes in a “natural” level of unemployment, as many Chicago School economists do, then unemployment isn’t a problem any more than objects falling to the ground when dropped is a problem.

Problem-driven research thus runs the twin risks of accepting the public’s definition of what is a problem and how it is problematic. Together, these commitments blunt the critical function of academic research and make it more difficult for such research to place things on the public agenda — either new problems, or new approaches to problems that emphasize very different aspects of the relevant topics. It’s hard not to engage in pandering if one is trying to be problem-driven.

Puzzle-driven research, while free from these specific issues by virtue of its orientation towards an academic discipline rather than the public at large, nonetheless encounters similar drawbacks. Problematizations (I suppose that we might technically call them “puzzleizations” or something, but that’s an ugly, ugly neologism) exist within academic disciplines as well, and research that is oriented towards them has to, by definition, accept a given way of attacking or approaching some topic. And the list of topics for research within a discipline consists of those things that existing theoretical models and constructs can’t adequately explain, regardless of how trivially narrow and technically mindless they are. For example: if one is a rational choice theorist, gift-giving is a “puzzle” because the benefits do not appear to balance the costs. (Actually, if one is a rational choice theorist, virtually every cooperative social activity is a “puzzle”; this is why rational choice theorists have developed theories of “collective action” in an effort to explain something that appears perfectly ordinary and obvious to people who are not working within that intellectual tradition.) Ditto every academic puzzle one might imagine, from the overextension of great powers (“overextension” assumes some notion of correct or reasonable extension) to the absence of global free trade arrangements (which is only a puzzle if one assumes both that people act on their narrow self-interest and that free trade creates benefits for everyone) to the presence of laws of war (which is a puzzle only if one assumes that war is the breakdown of social order rather than a social activity in itself).

Hence: problem-drivenness requires academic researchers to give up too much to the public’s current preferences, while puzzle-drivenness requires academic researchers to give up too much to their discipline’s current preferences. However, in order to go on doing the work that we do, academic researchers have to somehow speak to both the public and their discipline, unless they are independently wealthy or have a patron of some kind. But I think that this is a slightly different issue; what we have to do to justify ourselves and our work is not the same thing as how we ought to generate the topics on which we are working.

My preference, then, is for question-driven research, where a question arises at the conjunction of the researcher’s personal preferences and the broader cultural values in which s/he is embedded. I am interested in what I am interested in partially because of some unique, idiosyncratic experiences that I have had; these experiences are of course shaped and made meaningful by my own deployment of the cultural materials that I have come into contact with. In other words, there’s a biographical aspect to how we select topics of interest. And that’s not a weakness — it’s a strength, because it gives individual researchers the drive and commitment to persist until they find answers to their questions.

But once we have our topics, I think that we have to make an effort to demonstrate both that they are problems and that they are puzzles. Shifting the terms of the situation such that “being-a-problem” and “being-a-puzzle” are effects of how we introduce and deal with our questions means that the critical function of academic research is restored: we are no longer strictly beholden to existing socially-sustained definitions of what and how something is worthy of being researched. In articulating our questions as problems and puzzles, academic researchers are both empowered to shift the agenda of both their discipline and the public at large, and also able to engage in conversations with other academics and with members of the public. But there’s an important difference between this kind of critical engagement on the one hand, and being driven by either problems or puzzles on the other.

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