The Economics Nobel Prize winner this year was Jean Tirole, the superstar of the game theory revolution in industrial organization (that has ended). Jean departed MIT just as I arrived 1991. No doubt, it played a role in my hire. Jean was already a legend at MIT. Two years later, when he made his departure for France permanent, I inherited his fake potted plant in 1993 when I got his office at MIT.
Starting out at the game theory revolutionary year of 1981, as sequential equilibrium was circulating, Tirole had teamed initially with Fudenberg, Maskin, Laffont, and others on an array of problems, mostly in industrial organization. Tirole’s MIT secretary, who was just outside my door, showed me how he transcribed Tirole’s papers from long hand. That may have helped him be so stunningly prolific, but it was not the bigger part of the story. Most theorists find themselves struggling with hard proofs at one time or another. When he once asked me how I was doing, I expressed frustration at being stuck for two years deriving the conditions for assortative matching with search. He replied "Lones, when I write down a theorem, the proof is just details." I cracked my problem one year later. It was not just "details".
Yes, much of his work shared a principal-agent focus, but his style was the essence of "MIT theory". As best as I can formulate it, this means that the paper's triumph is not in the logic or depth, but the construction of the model. A long struggle with a proof is simply a sign that the model has not been set up properly. I was told that this was Paul Samuelson’s imprint on the department. But even he apparently struggled for years on the option pricing problem, before losing out to Black and Scholes. I feel that this label was surely earned in the 1980s, perhaps starting with the 1982 Diamond Coconuts model, before blossoming in Tirole’s work. By then,the “MIT Theory” style was in full swing in the local culture, and heavily rewarded – most usefully with favorable treatment by the in-house Quarterly Journal of Economics. The new masters of MIT Theory were Abhijit Banerjee, Daron Acemoglu, Michael Kremer, and Thomas Piketty. Elsewhere, among many others, specialized in the style – especially, Andrei Shleifer at Harvard and Matthew Rabin at Berkeley. Banerjee, who was my next door office mate at MIT, even told me that he usually picked author or story teller as his occupation of choice when asked on airplanes. And there was more than a grain of truth in this cheeky reply.
As I struggled with my theory proofs, I have had to come to terms with what I was doing. After all, the goal of any theory is to make sense of the world. It must explain the variation we see though time or cross-sectionally. We construct models to make sense of the world around us without appeal to magic. Crucially, any theory simplifies. It over-identifies reality, and thus almost must be wrong. George Box – the chairman of the statistics department at my University of Wisconsin – once bluntly wrote, “Essentially, all models are wrong, but some are useful.” Physics gets this wrong, and deceives itself for centuries at a time – from Ptolemy, to Copernicus, Galileo, and Newton, to Einstein, to Witten and string theory – into confusing a model with “the truth”. The genius of our models is seen in anyone who seeks to tell a lie that matches the facts. It is damn hard! A lie with more twists and turns can hit more facts. Occam’s famous Razor nicely reflected this tradeoff, clearly counting simplicity as a good.
I have come to understand theory as a dialectic of two extremes, from “theory as science” to “theory as art”. The former takes models as primitives and seeks implications; the proofs here can be very hard. The other takes desired conclusions as primitives and pursues models that deliver them. The proofs tend to be easy, because one naturally lays out assumptions designed to yield the conclusions. All theorists find themselves somewhere on this spectrum – either unwilling to sacrifice elegance for "applicability", or the opposite. “MIT theory” is heavily weighted toward theory as art, while (say) Princeton or Northwestern theory is near the opposite end. The profession is still seeking a role for theory, and I feel part of the backlash was against abstract deep theory lacking meaning. But the way theorists respond to this is often to toss out elegance in favor of “economics”. This will not stand the test of time.
I feel that few of us make good artists, but (most) of us understand what solid logic is, which is the primary ingredient in theory as science. But there is something more. Suppose we all shared Tirole’s amazing genius for theory as art. Should we do it? I strongly feel the answer is no. For the scientist theorist tosses out or adds in one or two assumptions at a time to the edifice of theory. In the spirit of a controlled scientific test, we are able to see the logical import of each assumption. We must keep in mind that the map from models to outcomes is not invertible. A wealth of models can explain any set of facts. So can MIT Theory bring us to the best models?
The case for theory as art is the paradigmatic dynamic described by Thomas Kuhn. How otherwise can we ever move way from entirely misdirected models towards new models? Theory as science is an incremental process, slowly adjusting the rational edifice. Theory as art is about revolution. But constant revolution leaves nothing standing. If economics is simply an assortment of “ad hoc stories that work for ad hoc cases”, then the simplifying role of theory is lost. Nothing is ever tested. An encyclopedia of clever stories is nothing better than one incredibly complicated theory. The improvement dialectic is lost. Writing in his blog after Tirole’s Prize, Of all people Paul Krugman recently wrote of Tirole's Prize: “Of course, there came a later phase when things were too liberated – when a smart grad student could produce a model to justify anything. Time for empirical work! But by then a lot had been achieved.”
Science is largely a continuous process. It requires an improvement dialectic of models. I feel that a little MIT Theory is good, but too much of it is the death of science. Perhaps we see that in now in behavioral economics, which is the current major playground for MIT Theory. Time will tell. The science of economics also requires an ongoing effort to test models with new data. I feel that too is sadly lost in our field. We cannot blame that on MIT Theory, but perhaps if the canon of stories were smaller, we could hope for a stronger dialectic here too.
So congratulations to Jean Tirole on his Prize! Let us hope that he creates models that stand the test of time precisely because traditional "non MIT" theorists are left to question his logical edifice, or empirically-minded economists can figure out how test and refute his models.