big theory, little problems or big problems, little theory

What makes a study interesting? Is it the problem (e.g., financialization; boycott success) or is it the theoretical question that the problem is meant to address? For many organizational theorists, I would expect the answer would be the theoretical question. Organizational research, and much of sociology for that matter, is driven by making contributions to theory, no matter how small or seemingly mundane is the problem itself.  I don’t think that’s necessarily a bad thing. Teppo and I called this blog orgtheory and not orgresearch for a reason. We like theory. I like the big abstract puzzles that seem pointless to outsiders but that keep many of us up late at night.

The emphasis on “big theory” poses some constraints for getting published in our field. Some, including Don Hambrick, have lamented this trend as the feeling is that it causes scholars to push beyond their data and to make claims that are unjustified.  Scholars, the critics claim, have replaced theorizing with a “theory fetish.” Whether they intend to or not, scholars sometimes turn theory turns into neat packaging without any real attempt to integrate or replicate.

But not all areas of scholarship are equally focused on “big theory.” Some subfields pride themselves for doing little theory and instead examine the “big problems.” Take demography as an example. Nope, not much theory there, but the problems (e.g., changes in the divorce rate; immigration patterns) are big. Of course, it’s not as if demographers are just descriptive. They are interested in explaining problems and may use a little theory as they search for mechanisms that explain the big problems at the heart of their analysis. It’s just that the starting point for their analysis is more about the problem than the theory. Being able to shed light on a really big problem is given more weight in the review process than making a big theoretical contribution.  Although demography may be on the extreme side of the continuum, I think that some branches of historical sociology and strategy research are like this as well.

Why are demography and strategy research more problem oriented than economic sociology or organizational theory? My sense is that it’s because there is more consensus in those subfields about what the big problems are. Demographers may not agree with one another about which theories matter, but they do have high consensus around what big problems they ought to be interested in explaining/solving. This is similarly true in strategy research. You can pinpoint strategy’s focus to one set of DVs – performance.  If you can shed some light on explaining this problem – how to improve financial performance – I don’t think it really matters what theory you use or if you have much of a theory at all. But in organizational theory, there is much less consensus about what the big problems are, and so we instead focus on generating consensus around what the big theoretical questions are.  It turns out that there are a handful of big theoretical questions (e.g., institutional change; network effects vs. cognition) but people who are in the subfield develop a sense for what these are and then figure out how to develop research projects to address those questions. Sometimes, and probably way more often than is useful, scholars start with the topical problem and then, after they’ve done some analysis or finished their ethnography, try to cram their research problem into a theoretical question. Sometimes it works and sometimes it doesn’t. When it doesn’t work, the resulting paper has all of the problems associated with “theory fetish” – e.g., superficial contribution, weak mechanisms.

Is there a place for more problem-oriented research in organizational theory? I’d like to think so. But to get there we need to start talking more about what the big problems are in the organizational world and to get over the false idea that “little theory” is bad.  Little theory doesn’t mean no contribution at all; it just means that we arrive at them as a consequence of a detailed examination of a big organizational/social problem.  I take Jerry Davis’s and Greta Krippner’s books as great examples of problem focused work that also happen to make nice theoretical contributions along the way. I think we need more research like this.

Written by brayden king

May 16, 2011 at 2:46 pm

Posted in brayden, research

12 Responses

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  1. “Take demography as an example. Nope, not much theory there, but the problems (e.g., changes in the divorce rate; immigration patterns) are big.”

    You may be very surprised.



    May 16, 2011 at 3:39 pm

  2. I’m not so sure about this distinction between Big Theory (questions) and Big Problems. Doesn’t having a Big Problem already imply that your Theory fails to explain something, and therefore also has a problem? Conversely, what use is contributing to Big Theory if there’s no Big Problem that this theory is supposed to solve? That said, I very much prefer to have a problem in need for a theory (nail seeking hammer) than vise versa (hammer seeking nail). Sadly, in sociology, my own work included, it is most often the latter.



    May 16, 2011 at 4:41 pm

  3. Rense – Of course the distinction blurs in many cases, but at their extreme these two styles represent very different ways of approaching social science. Another way to conceptualize the distinction is that Big Problem research tends to be more inductive – let the data guide your judgments, draw theoretical implications later – while the Big Theory approach is typically more deductive – the whole reason for studying this setting is because presents an ideal case of a Type X phenomenon.

    After sufficient study a Big Problem can generate Big Theories particular to that phenomenon. The study of income inequality, for example, has spawned a set of theories. But there are some problems that will likely never generate a whole theoretical body around them simply because the initial interest in the phenomenon was generated by a theoretical question of more general application (e.g., microbrewery foundings; the rise of nouvelle cuisine). These small problems, of course, can be the best places to generate theoretical insights, but that doesn’t necessarily elevate the status of the problem.

    A side note – one of the main problems that PhD students have when formulating research questions is that they’re often drawn to problems that seem big to them but that seem quite small to most other social scientists. The student needs to figure out how their phenomenon is really an instance of a big theoretical question or risk being completely irrelevant. A safer strategy is to find a problem that is widely regarded as big (e.g., income inequality) and develop a new way to study it with a big theory idea.


    brayden king

    May 16, 2011 at 5:41 pm

  4. Brayden, I sure do recognize your distinction in the practice of social science. But from an ideal-type, Popperian perspective the distinction should not be there – Big Problems ought to motivate Big Theory, which is then developed in a deductive fashion. Then also small problems (with lab experiments as an extreme case) can play an important role in solving the Big Problems, as an aid to testing and refining the Big Theory. Unfortunately, as you say, there is too little consensus (at least in sociology) on what the Big Problems are for this ideal-type approach to take off. Perhaps a nice topic for an orgtheory poll? :)



    May 16, 2011 at 6:27 pm

  5. @Rense, I think there some confusion of labels happening here. Like in your ideal scenario, Big Theory is in fact motivated by significant questions. If I’m understanding Brayden correctly though, they are just a different set of questions from the ones Brayden calls “Big”. It’s the distinction between basic and applied research, or between general questions and pertinent questions. The questions behind “Big Theory” are big in the sense that they affect very broad ranges of phenomena: e.g., how are patterns of stratification perpetuated? how does the structure of social networks affect the diffusion of ideas? how does culture influence action? These questions are big because they have the potential to transform what sociologists think about many aspects of the social world. The questions called “Big Questions”, on the other hand, are questions that are big because they themselves matter, perhaps not only to sociologists but to policy makers or the general public. A lot of them are of the form “What’s the cause of social problem X,” or “What’s the effect of policy Z on important phenomenon Y?” These questions are Big in their immediate implications, but they do not have to have big effects on general understandings of society. Some questions are both Big and big, but it makes sense why questions that are just Big or just big would still be of interest to sociology.


    Andrei Boutyline

    May 16, 2011 at 10:10 pm

  6. Brayden identifies a really important problem for organization theory as a field: what is the source of our coherence, if anything? Strategy researchers are unified by a dependent variable. In strategy, as long as “performance” is on the left hand side of the equation, you can put anything on the right – industry structure, IP, routines, CEO charisma, board interlocks, alliances, Satan worship, state of incorporation, whatever. Organization theory is united by its unit of analysis and by its devotion to theory, and specifically a handful of theories that mostly originated in the 1970s (and a few constructs updated since then, like status). But the phenomena to be explained are left open, and we lack common standards on what count as important problems. (Isomorphism? Patent citations? Time to IPO?) As a result, reviewers seem to fall back on a nebulous “contribution to theory” (and the slightly less nebulous “econometric fanciness”) as standards of evaluation, and we end up with 100 papers on patents in biotech (only modestly important in the real world) for every paper on Walmart (fantastically important in the real world). The biotech papers feature time-series data and the Huber-White sandwich estimator, which certifies their importance; the Walmart paper is merely a case study.
    Matters are made worse by the near-universal availability of WRDS, SDC Platinum, Execucomp, and Stata. In the absence of a compelling problem sense at the field level, it’s easy enough to regress first and ask questions later; as Stinchcombe noted long ago, any competent grad student can usually generate three explanations for any observed pattern of results.
    So Brayden: how do we come up with a shared sense of what the important problems are? And how do we persuade reviewers that important problems are worth addressing even if they don’t involve status or fixed effects models?


    Jerry Davis

    May 17, 2011 at 1:57 am

  7. Good questions Jerry. I don’t know how to come up with a shared sense of the important problems when it seems like the trend of the OT world is that we’re becoming more fragmented and diverse. Coherence is less attainable now than it might have been 10 or 15 years ago. My guess is that developing consensus about the importance of certain problems is most likely to take place in smaller groups/clusters within OT. We generate interest in an issue by holding a small conference or workshop, one of the purposes being to recruit new adherents. It’s good old fashioned coalition building.


    brayden king

    May 17, 2011 at 2:14 pm

  8. An key question from a sociological point of view is: who defines what a problem is? If we are to believe the constructivists, such as Becker (1966) , Berger and Luckmann (1966), and Spector and Kitsuse (1977), not to mention Mills with his distinction between “troubles” and “issues” in The Sociological Imagination, the definition of what a problem is is determined by social relationships within society. You see it in demography already: research into fertility was funded by Western institutions whose main interest was to reduce the number of births in developing countries. If, likewise, org research were to open up to “problems”, what kind of problems would be on the agenda? Those that favour the perspective of grant donors? Consequently, would a shift in focus to “problem-oriented research” really result in more critical studies of Wal Mart?



    May 18, 2011 at 4:19 pm

  9. […] big theory, little problems or big problems, little theory « (tags: epistemology academia:profession) Filed under: Linkage   |  Leave a Comment LikeBe the first to like this post. […]


  10. Either way, I’m for “Big”, theory or problem. While I value being circumspect about what our studies allow us to say, I also value tackling topics that are important but thorny enough that they challenge our ability to say anything as precisely as we might like to.

    For example, yesterday’s Piers Morgan show on CNN featured several takes on our “financial culture.” I’m not sure I know what that is, or if it’s more than a tagline for a show that’s ultimately selling its sponsors products (insurance, pharmaceuticals, etc.), but I thought it was very interesting. In particular, it lent momentum and legitimacy to the nascent re-thinking of the relationship between organizations and markets. The part with the CNBC hos and author of “You Teacher Said What?” drove me absolutely batty.

    And yet, it’s hard to say much that’s precise about these things, at least at first.

    Embracing the tension between these two values is healthy, I think, and perhaps a strategy for both good research and increased relevance.


    Mark Kennedy

    May 20, 2011 at 4:57 pm

  11. […] those of who are really paying attention (and I applaud you if you are), you’ll notice that I’ve asked this question before. It’s become a sort of obsession of mine.  For the field of organizational theory, […]


  12. […] of argument goes, is grand theory. The fact that the grand theory may be latent, unarticulated, or embedded in a discipline doesn’t change what it is; in fact, latent and unarticulated grand theory may be dangerous if […]


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