comments on krause’s “model cases: on canonical research objects and sites”

Monika Krause recently published a fascinating new book at the intersection of sociology and philosophy of social science: “Model Cases: On Canonical Research Objects and Sites.” I had the chance to comment on the book at the Social Science History Association meetings this week, alongside Fiona Greenland and Julian Go. Below are my comments for those interested in learning more about the book.

Near the beginning of graduate school, I took a preliminary examination on economic sociology and organizations. The reading list for the exam covered a wide range of topics – from the power structure of the Medici in 15th century Florence to the end of socialism in Eastern Europe in the 1990s. But the thing I learned the most about was the boards of directors of Fortune 500 companies in the 20th century United States. Paper after paper in economic and organizational sociology analyzed the history and dynamics of these boards and especially the connections between them – the network of “interlocking directorates.” I learned about the history of this network, the now-declining centrality of banks in the network, how innovations in corporate governance diffused through the network, competing theories about the network’s functioning and significance, and more. In Monika Krause’s felicitous framing, this network was clearly the “model case” for much research in economic and organizational sociology in the 1980s to 2000s. This one network – a particular “material research object” in Krause’s terms – stood in for a more general “epistemic research object”, something like “the role of networks in economic life.” Why? What about this case made it stand out? And why does it matter that so many of our subfields are constituted around model cases in precisely this fashion?

Model Cases: On Canonical Research Objects and Sites identifies this pattern in the social sciences and begins to offer a theory for how and why researchers rely on model cases, and why such reliance can limit the reach of our inquiries if we do not reflect on these choices. The cover of the book fantastically hints at the main argument, showing a painting of the French Revolution (the model case for historical sociologies of revolution and political change), a street map of Chicago (the model case for urban sociology), and the 1969 Cordobazo uprising in Argentina (the model case for studies of populism in political science).

Model Cases

The basic structure of the argument, which I’ve hinted at already, is something like:

1. First, the book offers a definition of model cases via analogy to model systems in biology. Model cases are “privileged material research objects” – that is, specific things-in-the-world that are made central by some community of scholars (typically a disciplinary subfield) and seen as correct, appropriate, and useful for learning about the larger “epistemic research object” of interest (e.g. Chicago stands in for cities).

2. Second, Krause then argues that many social science subfields, most notably those in sociology, make extensive use of model cases. That is, model cases structure the production of knowledge in these subfields. Not everyone who studies cities studies Chicago, but iconic past and prominent present research focuses on Chicago, and other work in urban sociology is compared to work on that model case.

3. Third, Krause argues that unlike in Biology, the social sciences do not recognize the extent to which they are reliant on model cases. While biologists have an explicit conversation about what organisms should serve as model systems for different biological processes, and the pros and cons of relying too heavily on a narrow set of such model organisms, social scientists have mostly relied on model cases without realizing they are doing so. (I should note that one strength of the book is its detailed engagement with actual research practice in biology – that is, Krause grounds her comparison in the history and sociology of biology rather than some idealized notion of the field.)

4. Fourth, and finally, Krause argues that the social sciences would be much improved if they were reflexive about their reliance on model cases, and her book offers tools for starting just such a conversation. Note that the point here is not to argue against the practice entirely; Krause recognizes that some privileging of material research objects is probably beneficial and maybe even necessary. There’s real virtue in having a collective depth of expertise on particular cases. But there are limits too; our theories may be “overtuned” to features that are idiosyncratic to particular cases, for example. And our reliance on particular model cases may privilege those with particular sets of expertise – knowledge of French, understandings of European and American history, etc. – that reinforce other forms of inequality in the field. Thus Krause argues not for abandoning model cases, but for making explicit our collective deployment of such cases, and perhaps in so doing, opening up space for a conversation about which cases we should rely on in a given field, rather than permitting inertia to keep us locked into our current patterns.

The book is structured into an introduction and six short chapters followed by a short conclusion (the main text is just 125 readable pages; perfect for consumption on a cozy fall or winter afternoon). The introduction lays out the basic structure of the argument. The next four chapters offer the core of the argument, offering a clearer definition of model cases, an incredibly useful discussion of how subfields come to rely on the logic of model cases (and importantly, potential alternatives) and how they select particular cases, and how the current organization of the disciplines into subfields interacts with this reliance on model cases. The final two chapters dig deeper into the model cases of two particular subfields: social theory and global sociology.

(As a first kind of question or comment, I’d note that these are somewhat curious choices, especially social theory where the conversation around the politics of the canon is much more developed than parallel conversations around, say, the centrality of the Fortune 500 in studies of economic networks. In some ways, social theory seems quite anomalous, and while I very much appreciated the chapter’s take on how “colleagues” (actual flesh and blood academics) are turned into “authors” (objects of analysis for social theorists), I don’t know that it was the best subfield for demonstrating the importance of Krause’s argument.)

I want to briefly highlight the first chapter’s discussion of different potential logics for justifying particular choices of research objects. This chapter will be incredibly useful for graduate students in methods courses, and other contexts where scholars are trying to understand how to choose what to study, and then justify those choices. Krause identifies five distinct, if not always opposed, logics of selection: the logic of model cases (we should focus on studying specific, privileged cases), the logic of coverage (we should study X because it has not been studied before), the logic of application (we should study X to see if theory Y applies there, often a theory built on studies of a model case), the logic of representativeness (think of how population-based surveys are usually discussed as representative samples), and the logic of formal models (think abstract, theoretical systems and hypothetical data and simulations, in contrast to how model cases use details from one real case to infer dynamics in others). This language nicely captures variation in how social scientists do their work, and how they justify those choices.  

At the end of each chapter Krause offers an assessment of what the social sciences are already doing enough of and an unabashedly normative claim about what we need more or less of. For example, the first chapter argues that we have enough studies trying to “apply” the insights from model cases to other cases, but not enough studies of neglected cases. Chapter six argues that we have enough non-comparative work on the US & UK, but need more studies of non-Western contexts, especially ones that are not postcolonial. And so on.

As I hope I’ve demonstrated, Krause’s approach offers some incredibly useful vocabulary for making sense of the current organization of the social science. The book is also full of specific insights. For one example, her approach offers specificity to discussion of the “Eurocentric” tendencies of the social scientists. Yes, the social sciences are Eurocentric – but they are also quite narrow within their studies of Europe. We know an awful lot about industrialization in Britain and the politics of 18th and 19th century France, but much less about, say, Prussia. Eurocentricity is an accurate critical description, but one that can at times give too much credit to the social sciences, which are even more parochial than that label implies.

Ok, with all that in mind, I’d like to conclude my remarks with three sets of questions or concerns.

First, I fear that some of the normative observations come a bit too quickly and are not thoroughly justified. What are the criteria for making these claims? How should we judge success? I do appreciate that the recommendations, in some sense, tell us where to cut and not just where we need more. But I would have liked a bit more of an explicit discussion of what the goals of this whole social science endeavor are, and how the normative recommendations flow from those goals.

Second, I would have liked to see a bit more systematic data and research underpinning the claims about how model cases are shaping one or more specific subfields. I should say that I am thoroughly convinced of the overall argument – I think I can identify model cases for every subfield I’m part of, like the interlock network in economic sociology – but I still expected to see a bit more substantiation of this claim. Again, here, I think the chapter on social theory, while interesting in its own right, did not do the work of supporting the overall argument that a more robust study of one of the cases named in earlier chapters (urban sociology, historical sociology, etc.) might have done. Such an empirical analysis of the dynamics of model cases in the social sciences might also reveal subfields where other logics really are dominant. Here I am thinking especially about quantitative fields like stratification research in American sociology. In this context, I think (and have elsewhere argued) that data availability and “knowledge infrastructures” play a central role in shaping what kinds of questions are asked and where, but I don’t think the logic follows the pattern of model cases. I would be curious to hear if Krause agrees, and how we might go about empirically studying the dynamics of model cases and other logics across subfields (which in turn, might help to justify the normative recommendations).

Third, and finally, I worry that the book does not pay quite enough attention to what you might call the political economy of academic knowledge production. That is, while the book does foreground how model systems in biology and model cases in the social sciences can facilitate knowledge production by streamlining and “infrastructuring” the research process, I do not think it goes quite far enough in building on that insight to understand the barriers to implementing the suggestions at the end of each chapter. Put another way: doing things different might be costly. Costly collectively as we have to learn more, and costly individually as scholars who wish to deviate from existing model cases and logics of justification must work to both understand their own objects of study and to prove the value of insights gleaned in non-canonical places. If enough people read this book, the latter part may get a bit easer! But still, I worry. I especially worry given the context of contemporary academia – whatever you want to call the current moment of funding cuts and research assessments (here, I am thinking especially of JP Pardo-Guerra’s forthcoming book The Quantified Scholar on how the British research assessment framework encourages more conventional knowledge production, and militates against work that’s further afield from established norms). In other words, I fear we may be fighting to keep as much heterodoxy as we have right now, and are unlikely to be able to make gains to open things up much further. In any event, I would love to hear more about how Krause thinks about the contemporary political economy of academia and what that applies for the struggle against the tyranny of model cases.

Thank you very much again for the opportunity to read and think with this fantastic book. I look forward to today’s discussion!

Author: Dan Hirschman

I am a sociologist interested in the use of numbers in organizations, markets, and policy. For more info, see here.

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