The First 50 Years and the Next 50 Years of A Behavioral Theory of the Firm

It is our great pleasure to interview Jim for the 50th anniversary of BTF. Thank you Jim, again, for supporting our initiative.

Thank you. It’s a pleasure for me to be able to do it. I’m sorry that I can’t be in Orlando playing with the Disney folks and talking to all of you good people. But at least this piece of work will demonstrate that I’m still alive-a fact that surprises me as much as it probably surprises most of you. But it is a pleasure, and thank you for inviting me.

Thank you Jim. Based on the voting result, we have seven sets of questions in two broad categories. The first category is about BTF, and the second category is about doing research in general. So let’s begin with the first set of questions. Jim, can you tell us about your collaboration with Richard Cyert on BTF?

Well that goes a few years back. So you’ll have to trust my memory, which is probably no better than anyone else’s. Back in 1953, I was a fresh new PhD, and at the age of 25 went to the Graduate School of Industrial Administration at the Carnegie Institute of Technology. This was an extraordinary institution. It was presided over by Dean George Leland Bach who was then 37 years old, and the intellectual life very much surrounded three critical people: Bill Cooper who was then about 39, Franco Modigliani who was then about 37, and Herb Simon who was then about 35. So it was a bunch of young Turks. And I was one of the young squirts who worked with the young Turks. You know, it was an extraordinary group. That group, the faculty—it was quite small—but the faculty and students of GSIA (Graduate School of Industrial Administration) generated something like 7 or 8 Nobel laureates, and about 8 or 10 members of the National Academies, and I think five people who won the Scholarship Award from the Academy of Management. So it was an extraordinary group. It was a group for which intellectual life was paramount—arguments, debates. And work was intense. Most people worked 7 days a week. The joke was the dean came down on Sunday to see who was there. The presumption was that work mattered. So I fell into that group, became part of that group, and Dick Cyert, who was then about 32 or so, and I became friends. And we not only became friends, we became colleagues, and we started writing. So in I think 1955 we published a paper in the American Economic Review. ² In 1956, we published a paper in the Quarterly Journal of Economics. ³ In 1958, we published a paper in Econometrica ⁴ and another one in Administrative Science Quarterly. ⁵ These papers basically became the base for BTF.

At the same time, I was working with Herb Simon writing Organizations, and both of us were publishing other papers. So it was an intense, very productive group, and very productive period. It was a very arrogant group. We believed that we knew what the answers were, and that the rest of the world was not very bright. And we had to fix them. And so that propelled that particular little school into a fury of intellectual academic work. Dick and I became friends, our families became friends, and we wrote and played together. We used to go over to Forbes Field, which used to be the playing field for the Pittsburgh Pirates, who were a miserable baseball team, but after the top half of the seventh inning, if you went to Forbes Field you got in free. So we would walk over there and carry on our conversations in the bleachers, overlooking the latest failure of the Pittsburgh Pirates. Now I should add that we also lived to witness one of the great events of all time, which was the 1960 World Series, in which the Pirates defeated the New York Yankees against all odds, and which was finished in the last half of the ninth inning of the seventh game when Bill Mazeroski hit a home run over the left field wall. Forbes Field is long gone—well, it’s where the University of Pittsburgh Business School is now. The Business School is located in right field, which is perhaps appropriate, but a portion of the wall in left field is maintained as a monument to that victory in 1960. If you were there you would know how important it was. But that was the climate in which Dick and I wrote.

Thanks Jim. I think it’s fair to say that we all hope to have a research partner like him, or like the research group over there. To have the ambition to change the world.

Well, we knew we were going to.

The second set of questions about BTF is about looking forward. What needs to be done about BTF? And in particular, we have three questions in this set.

First, moving forward, what are the most important unresolved theoretical questions that the literature that builds upon BTF can tackle?

Next, what themes identified in BTF still need development: like search, routine, attention, and others?

Third, how is BTF related to the theory of organizational evolution and adaptation?

Well let me set the scene a little bit. When we wrote this book, microeconomics had two major projects, and it’s still substantially true of microeconomics.

The first project was to educate people how to make intelligent choices of a particular sort. A sort that calculated the probable consequences of alternatives, and select the alternative that maximized present value. Much of the discipline, much of the effort, was directed to persuading people “that’s the way one ought to act.”

The second project was trying to understand how collections of people, like firms or societies and so on, made decisions, and worked. Now it’s obvious that if the first project is totally successful, the second project is simply the derivative of it. And most of economic theory at that time assumed that the first project was largely successful, and therefore one could have a theory of the firm that was basically derived from decision theory. Our commitment was that you had to understand the actual processes that firms use, the search procedures they have, the decision procedures they have, the way they learn. And that if you understood those, you would in fact discover that not every firm all the time followed the rules of decision theory. We set out to do that, and I wouldn’t say we accomplished our goal but we were pretty consistent in trying to do that. But most of that still remains to be done, and the project of understanding the actual processes of firms is still a minor part of contemporary economics, and therefore falls more and more on students of organizations. So we have a kind of curiosity where the most important work in economics is being done outside of economics—at least, that’s my picture of it.

Now if you ask “what are the critical domains,” different people would answer different things on that, but I would think that one is to understand adaptive processes. And adaptive processes include the processes by which you filter through alternatives to find some rather than others, and the processes by which new alternatives, new options, are generated. But those we need to understand much better.

The second thing that is really quite different in many ways, is that if we are going to think of decisions as being somehow related to preferences or utility functions or whatever you want to call them, then we need to attempt to understand where preferences come from, how they change, how to one extent they are endogenous to decision-making, and things of that sort.

And the third thing that I put on the list is to understand rules and how they develop and how they are implemented. One of the major points of BTF is that firms follow standard operating procedures. They follow rules. Subsequently, people have done a good deal of work identifying how that is linked to identities, and how it is linked to something we call the Logic of Appropriateness. But there is still a lot of work to be done on rules, how they change, how they develop, and how they are spread through an organization. So those are the agenda that I would push on.

Next is on how BTF relates to organizational evolution and adaptation. Well, clearly, it’s intimately related. The idea that firms follow rules is fundamental to at least the Nelson and Winter (1982) version of evolutionary economics. In the Nelson and Winter version of evolutionary economics, the genes, effectively, of evolution in firms are the rules. The rules are the invariant things that are passed on from one generation to another. And so a theory of evolution is a theory of how rules change and develop. And more generally, I would say that anyone who wants to understand firms as we try to do has to understand selection processes, and has to understand evolutionary processes.

The third set of questions relating to BTF is looking backward. In particular, two questions got high votes in our survey.

First, after 50 years of research since BTF, is there anything that you think has been proven incorrect in the original work?

Second, is there anything you wish you had done differently when developing BTF?

Well, those are really in some sense the same question, because in the kind of theorizing that is involved in BTF, you do not have the precise point predictions that are going to be precisely disconfirmed. So you ask what was not as well developed in the theory as might have been? And, there I think we were too cautious in our treatment of rules. We did not see how important the rule-based nature of human behavior was to economics. I say that particularly because over the years, and having nothing to do with BTF particularly, economics has gone further and further from an understanding of behavior because it has simply not understood the importance of rules, of identities, of obligations, things of that sort. And that, what I think is essentially a failure of microeconomics, is partly due to the fact that we were too cautious about pointing this out. Perhaps we were too cautious because we didn’t realize it.

The other thing it seems to me we didn’t do as well as we might have done is to develop the ideas of learning and adaptation. We identified that they were important, we said that you had to understand learning of goals, learning of knowledge and so on, but we did not attempt to develop theories of learning. And particularly, we did not do the kind of work that’s been done more recently, where one identifies the mistakes of learning and similarly the mistakes of evolution. We suffered from I think a sense that learning was relatively efficient and evolution was relatively efficient, and we now know of course that they aren’t particularly efficient. So those two things seem to be things that we could have done better.

Thanks Jim. Having heard that, we still believe we are in the best of all possible worlds.

Jim: Well I don’t know. I think it’s perfectly possible to believe in the best of all possible worlds. It is a belief that will be continually buffeted by experience, but that’s what experience is for.

The fourth set of questions is about the current work related to BTF. In particular, what recent developments in behavioral theory of the firm are you personally most excited about?

Well I think it’s obvious from what I said. I am most currently interested in the work on learning and adaptation. Particularly that part of it that focuses on the possibilities that learning may lead you astray, and particularly on those parts that try to deal with where novelty comes from. The sources of novelty are a great mystery in evolutionary theory. Well, evolutionary theory has two sources of novelty—one, which it understands fairly well, the genetic combinations. One it doesn’t understand at all, which it calls mutation. And mutation is basically a label for “what you don’t understand.”

Well, we have a similar problem. As you look at people trying to understand where novelty comes from, there are a number of people who are looking essentially for combinatorics of existing rules, or whatever it is. Some of that is very interesting research. John Padgett’s research on chemical analogs of that process are very interesting, but I don’t think we’ve unlocked the key. I don’t think we have anything comparable to Mendel. And until we get to something like that, we can hand wave a good deal about combinations, but we don’t understand them very well. So the sources of novelty are a domain that excites me and concerns me.

The last question related to BTF is, “Do you think that BTF has influenced mainstream disciplines like economics, psychology, and sociology? Why do you think it has or has not?”

Well, Chengwei, that’s a question for an intellectual historian, and I’m not an intellectual historian. I like sometimes to imagine that I’m an object for their study, but I’m not part of them. So basically I would look at the people who have tried to study that kind of question. Mie Augier has done some work on that. She, for example, has looked at all of the journals that reviewed BTF and the articles in those journals that cite BTF and said, what are the words in the titles of the articles—it’s a very interesting idea. Well what she finds is that BTF is cited very generally for process notions, and it’s cited very generally across all these fields, but the more specific things are different for the different fields. Economics would have a different take on BTF according to that kind of analysis. The other thing I’ve done—just for you—is I’ve read a very new handbook of organizational economics, by Bob Gibbons and John Roberts. ⁶ And that’s a big book. It has 28 chapters and 1,181 pages. Written by 45 authors, and about 90% of the authors are economists. The Cyert and March book is cited on precisely 8 pages on those 1,181. Now, that number is exceeded 10-fold by people like Bengt Holmstrom, or Jean Tirole, or Paul Milgrom. On the other hand, it compares favorably with the numbers recorded for Joseph Schumpeter, who appears on only one page of this handbook; Ludwig von Mises, who appears on only one page; Alfred Marshall, who appears on only one page; Gérard Debreu, who only made two pages; Jacob Marschak, who made six pages; and Adam Smith, who made seven pages. So it’s about like Adam Smith.

In this whole handbook, neither John von Neumann or Oskar Morgenstern ever got any mention. March and Simon [Organizations] was mentioned on five pages. So basically, if you take that handbook, contemporary economists working in the organizations field have no history. They don’t cite anyone who hasn’t written in the last 10 years. There are some exceptions—they do cite Ronald Coase on 32 pages. They cite Herb Simon on 26 pages and Kenneth Arrow on 23 pages. But basically, they don’t do much.

The Cyert and March citations are focused entirely on conflict and the strategic nature of information. So anything else from Cyert and March you don’t find, and in fact if you look in the subject index, bounded rationality is cited on five pages, politics is cited on five pages, but on no page is there any mention of aspirational levels or organizational slack or satisficing. On the other hand, incentives are mentioned on 193 pages, property rights on 89, contracts on 81, incomplete contracts on 35, and agency theory on 68. So you can see that the thrust of BTF has not made a major impact on that corpus.

Now the exception might be the transaction cost analysis, and we’d have to talk about, if we say why has it or has it not spread, and so we need a theory of diffusion—how do ideas spread? And almost any theory on the spread of ideas talks about the carriers of ideas. Who are the disease carriers? And who are they—they’re students! Oliver Williamson gets cited an awful lot in economics. He owes a lot to BTF, and he would happily acknowledge that. And in fact if you go to the back of this handbook, seven of the eight references to Cyert and March come in chapters co-authored by Bob Gibbons, who was once a student of mine. So it hasn’t spread very much through economics.

On the other hand, if you look at the field of strategic management, it’s a fair amount through that. And there we have quite a few students. We have people like Dan Levinthal, Henrich Greve, Anne Miner, William Ocasio, Theresa Lant, Stephen Mezias, Claus Rerup, Mark Zbaracki, and Christine Beckman. Ideas spread through students. Now, when you start talking about epidemiological models of the spread of ideas, you have to be careful. Because when ideas spread, they transform at the same time that they transfer. And that makes intellectual history very difficult. Because occasionally they use an idea that sounds an awful lot like an idea that I’ve heard before, but they label it something else. And that’s part of the story. But I think the punch-line is most of modern organizational economics are not conscious of any influence by BTF. There are parts of it that have been influenced by it, but the history is lost by the generational change.

Thank you Jim for responding to all these questions relating to BTF. In addition to the questions submitted about BTF, we also have some questions submitted about doing research in general, and they got high votes, so we thank Jim again for agreeing to address these questions also. And these questions will be asked by my colleague, David Maslach.

The first question that I have is especially relevant to those of us who are in a business school, or who are junior faculty like myself or Chengwei. As business schools have a pressure to provide incremental publications, how do we go about developing big theory as BTF?

Well, David, I have a little problem with the concept of big theory, and I’m not sure that BTF quite fits it. But if you say Marx or Freud or Darwin, I suspect they qualify. But who qualifies in our domain? Does BTF qualify? Does Herb Simon qualify? I don’t know. But even more than that, it seems to me that our field develops better with powerful little ideas than by trying to go find some big overarching theory. When I read the papers that are called theoretical papers in our field, the ones that aspire to big theory seem to me almost entirely empty. I’m sorry about that.

What excites me in our field are little ideas that seem to be powerful. Things that I’ve been associated with that seem to me very useful are things like aspiration level based decision-making, organizational slack, competency traps, these have some dynamics and some power behind them I think, whereas our big theories are a little too close to metaphysics for me.

The next question is related as well. Why do you think BTF was so influential in developing organizational theory?

Well, again, I think I would prefer to leave that to the intellectual historians. And, of course, I have a bias that perhaps one factor was quality. That maybe the ideas were good. That’s possible, and of course it’s counter to the way we theorize about things. But if I were speculating in a more skeptical way about the theory, I would point out that a lot of the people who cite BTF were students of mine. So they may have been corrupted by that early unfortunate experience, but I haven’t done any systematic work. I think some of the ideas in BTF seem to me to have this quality of being little ideas with power that you can use in a lot of different situations. And it seems to me that’s really what we seek more than anything else.

Thank you Jim for those insights. The next question is for future scholars seeking to develop theories as impactful as BTF, even in unrelated areas, what advice would you have?

Well David I’m not an enthusiast for tactical advice in scholarship. I think the point is to try to contribute to knowledge as best you can. And tactical advice tends to be advice on marketing: what journals to publish in, what schools to have a job in, and things of that sort. Those seem to me to take attention away from improving the product, and move it to improving the packaging, and I just don’t like that. So I would say the point is to do your own work, do it as well as you can, and make as good a contribution to knowledge as you can, and let the world decide whether it likes that or not. And it may decide it doesn’t like what it should decide it likes—the world makes all kinds of mistakes of that sort—but I think it is destructive of good scholarship to worry about the marketing of the results.

So do your work. And if you keep trying to say, who’s going to read this paper and how can I influence them, you change to a marketing mode instead of a research mode.

The next question relates to having an impact in management practice. Which areas of research have the strongest impact on management practice, and how can those be further developed?

Well David, my own impression of the development of organization studies is that the ideas that have been most influential in management do not come from the people who were trying to help managers. They came from the people who were trying to find interesting ideas. When I talk to managers, sometimes they say they find great help from the garbage can model, or from exploration/exploitation, or from competency traps, or sampling failures. Those things seem to influence them. None of them came out of a desire to be influential or a desire to help management. And I think I can make the case that there are some good reasons why the interesting ideas in life come not from trying to solve problems but from trying to produce beauty, or produce pleasure, or whatever. I am unabashedly an advocate of ideas for their own sake.

The next question relates to managerial insights. We often find that practitioners write their own books on how they succeeded, and advanced their organizations. How can we trust these accounts?

[Laughter] Well, as you know David, I wrote a book about the ambiguities of experience, and the main lesson of that book is how easy it is to be confused by your own experience. And certainly that’s true, it’s very easy for managers to be confused by their own experience. And I think all of us have the experience of reading books by experienced managers and, depending on our mood, laughing or throwing them across the room. They don’t seem to hold up, they say contradictory things, they don’t seem to move from one point to another, they seem to say general propositions that could be true or not true, you can’t tell. But every once in a while you find a Chester Barnard, or Dale Carnegie who is my favorite—these are people who in fact have a sense of something interesting. And my sense of managers is that we treat them like we treat students. Students say a lot of dumb things, but our job is not to laugh at them, but to try to find the interesting things that they are trying to say. And I would say that with the writings of managers. Don’t treat them as true, but treat them as sources of possible ideas that can be developed, by you, in a proper way.

Well thank you so much Jim, we really appreciate your insights, and there is a lot to reflect on today. On behalf of myself, Chengwei, Peter, and Vinit, Organization and Management Theory Division at the Academy of Management, and the rest of the Academy, we sincerely appreciate you giving these insights and allowing us to be part of your celebration today.

Thank you very much DM, it’s been a pleasure, and I hope that what I have to say is not totally irrelevant, but I repeat what I think I said at the start: Old people are usually very confident of what they think they know, but they usually don’t know as much as they think they know.