some thoughts on institutional logics, in three parts
Last week I was finishing up a volume introduction and it prompted me to catch up on the last couple of years of the institutional logics literature. This gave me some thoughts, and now I can’t sleep, so I’m putting them out there. This is long so it’s broken into three parts. The first two reflect my personal saga with institutional logics. They set up the rest, but you can also skip to the third and final section for the punchline.
My first book (now in paperback) was framed explicitly in terms of institutional logics. I wanted to understand why universities started to understand the purpose of science in a new way—more in terms of its economic value, and less purely about either knowledge or solving other kinds of problems—and how that lined up with the spread of activities like faculty entrepreneurship and tech transfer offices and so on.
The development I was interested in explaining was easy to characterize in terms of institutional logics, and fit pretty closely with two of Friedland & Alford’s originals: the logic of science and the logic of capitalism. I called it market logic because I wanted to sound less Marxist (sorry Marxists), and characterized the project as trying to understand why practices grounded in a new logic spread in academic science.
There was always a little difficulty with the definitions. If science logic is about valuing the pure pursuit of knowledge, well, there was always a lot of stuff in the university that didn’t fit that—like all the science produced in service of the Cold War. And “market logic” seemed a little imprecise for talking about a new valuing of science for the economic contributions it could make. It wasn’t exactly the logic of accumulation, which is how Friedland and Alford described the logic of capitalism. Still, for the most part the concepts lined up pretty well with what I was trying to do: look for common factors that could explain the spread of a variety of new practices focused on the economic value of science in universities.
So that is how I framed the book. The book was pretty successful, I wrote a theory paper on how new logics could spread in one field when another, resource-providing field changed (i.e. the state), which the sociology of science people liked but didn’t really get picked up by the institutional logics people, and that was that.
In the process, I got very interested in how policymakers came to think of science in terms of its economic value, which was new (for them) in the 1970s and prompted many of the policy decisions that changed academic science. This shift toward the economic seemed common to a range of policy domains—think about how policy conversations now treat education as an investment in human capital, or see the environment as important because of the economic effects of climate change—and closely tied to how we define policy problems and the range of solutions that get considered. This led to my current book-in-progress, which looks for common threads across multiple policy domains that have seen such a shift.
The two projects are structured in analogous ways: using historical cross-case comparisons (of policy domains, this time, rather than organizational practices) to gain insight into a broader cultural development—in the first project, university science becoming more entrepreneurial; in the second, policymaking becoming more focused on economic goals.
But the institutional logics perspective that worked well for the first project didn’t map neatly onto the second. It sounds like it might, right? Explaining the rise of an economic logic (market logic seems less and less the right term) in different policy areas.
But things quickly get blurry if you try to operationalize what it means for an economic logic to gain strength in a policy domain. Does it mean seeing the policy area in terms of its macroeconomic contribution, as when policymakers started to see technological innovation as a driver of economic growth? Is it about rethinking its purpose in microeconomic terms, as when education became an investment in human capital that would pay off in higher wages? How does that fit with the changes in environmental policy, which became more focused on the economic costs and benefits of protecting the environment, and on designing markets that could help do the job?
All these could be characterized as “economic logic”: as I defined market logic earlier, treating something as “worthwhile because it, or what it produces, has specifically economic value.” But this seemed to hide more than it revealed.
For example, you can talk about antitrust policy as having become more economic. Before 1970 it had competing and often contradictory legal purposes, which included encouraging competition and promoting efficiency, but also limiting the concentration of (nonmarket) power and protecting small business. After that, the field was increasingly defined in economic terms (the first two) and court decisions and changes in practice gradually defined the other goals as beyond the scope of antitrust policy.
Is this a story about the rise of economic logic in antitrust policy? Well, yes, sort of. But characterizing it as such misses important complexity. For example, although economists championed the idea that antitrust policy should only be used to achieve economic goals, there were very different schools of thought within economics about what policy should look like, and the “center” position evolved significantly over time. You can’t understand the evolution of antitrust policy by talking about “an” economic logic that gained influence in straightforward way. What economic logic implied was itself contested and changing.
And there’s the rub. What worked fairly well as a way to characterize the justification for a handful of specific new practices in a pretty well-defined field (U.S. research universities) worked much less well for characterizing an analogous cultural shift that took place in a much broader social space—across whole domains of public policy. The practices of bioscience entrepreneurship, university patenting, and university-industry research centers seemed to have enough cultural similarity that they could usefully be compared. But the shift toward seeing education as a producer of human capital, antitrust policy as efficiency-promoting, and environmental policy as best determined through cost-benefit analysis seemed less usefully characterized as reflecting the spread of an institutional logic—even though I did, and still do, think they are related shifts.
Instead, what they share is economists: a particular expert group with its own style of thought that is influential, but not uniform; that evolves over time; and that plays out differently as it approaches different questions and is applied in different political contexts. So the new book is framed in terms of the spread of a particular—but not fixed—kind of disciplinary expertise: how its bearers gained organizational footholds and displaced competing experts; how their way of thinking was institutionalized through laws, court decisions, and regulations; and how they influenced other disciplines (law, public policy) in ways that facilitated this process. At least for the moment, I’m not thinking about the changes I’m interested in in terms of the spread of a particular institutional logic.
So that’s that. My first book came out in 2012 and I haven’t paid a lot of attention to the institutional logics literature since then, although it has exploded in size. Getting up to date for the piece I was writing, though, made me revisit it.
And it kind of made my head hurt. And I think the clue as to why is buried in that long and self-involved story about my own wrestling with the concept.
I still believe the concept of institutional logics is useful as an orienting framework. A lot of the big insights—that there are broad institutional orders, like market, family, profession, religion, etc., and that they compete and combine at local levels—seem fundamentally correct. And the proliferation of institutional logics research in management journals has made culture and practices much more central to the study of orgaizations—which I see as a good thing.
But in the last couple of years, research on institutional logics has been all about understanding the microdynamics of how institutional logics play out locally—within particular organizations or groups of them. And because it’s published in management journals (not that sociology journals would be any different), the authors have to use these studies to generate theory. And so there is a proliferation of work that identifies mechanisms through which competition/displacement/hybridization takes place locally, and which is presumed to be at least potentially generalizable.
The problem is that institutional logics are ideal types, not real things in the world. And while you can find useful ways to measure them in particular contexts, there aren’t a lot of useful ways to measure them across contexts—in part because they instantiate differently across fields and organizations, and hybridize in practice, and evolve, and so on.
And so the institutional logics literature has seen this very recent proliferation of increasingly abstruse theory that isn’t really “theory” in the sense of being testable, generalizable, and so on, but is more about the case-based identification of mechanisms that are hoped to be more general.
I don’t think this is terribly generative. These theory-building papers, of which there are many, are never going to be more general, because institutional logics are not real things: they’re not solid enough to make cross-case comparison useful except at fairly local scales. Which is why the framework worked for explaining the origins of some specific practices in academic science, but was less useful for explaining how an economic way of thinking spread in multiple policy domains.
None of this is to say that there isn’t considerable value in the concept of institutional logics. It’s great for understanding what is going on in particular important contexts, and some of the more recent papers that I really like use it to explain just such cases. But these are papers not focused on building general arguments about how institutional logics have effects. (They also, not incidentally, tend not to focus on the broadest logics of the inter-institutional order—market, corporation, profession, religion, and so on—but on more local logics that do not map neatly onto those broader logics.)
Explaining cases—like descriptive results—is a real contribution, and I think we should value it much more highly. But the institutional logics perspective does not work well as a Lakatosian research program, and a lot of recent work seems to try to shoehorn it into that box.
I don’t think a Lakatosian research program was the intent of Thornton, Ocasio and Lounsbury, who in their 2012 book called institutional logics a “perspective.” And it certainly wasn’t the intent of Roger Friedland, whose bemused reflections on how his 1991 essay took on a life of its own are well worth the read.
But that seems to be where we are. There are plenty of useful things that can be done with the institutional logics perspective. Lots of particular important cases are begging for explanation. And we can carry insights we take from one case to give us new intuition into other, analogous cases.
By the very nature of the concept, though, studies of institutional logics are not going to produce the scientific cumulation of knowledge that appears to be the current goal. No matter how much we might wish it would.