Here.
I suddenly realized the remarkable extent to which the methodology of economics creates blind spots. We just don’t see what we can’t formalize. And the biggest blind spot of all has involved increasing returns. So there, right at hand, was my mission: to look at things from a slightly different angle, and in so doing to reveal the obvious, things that had been right under our noses all the time…
…Eventually I realized that one way to deal with a difficult problem is to change the question — in particular by shifting levels. A detailed analysis may be extremely nasty, yet an aggregative or systemic description that is far easier may tell you all you need to know.
…What I began to realize was that in economics we are always making silly assumptions; it’s just that some of them have been made so often that they come to seem natural. And so one should not reject a model as silly until one sees where its assumptions lead.
…Doing geography is hard work; it requires a lot of hard thinking to make the models look trivial, and I am increasingly finding that I need the computer as an aid not just to data analysis but even to theorizing. Yet it is immensely rewarding. For me, the biggest thrill in theory is the moment when your model tells you something that should have been obvious all along, something that you can immediately relate to what you know about the world, and yet which you didn’t really appreciate. Geography still has that thrill.
In the course of describing my formative moment in 1978, I have already implicitly given my four basic rules for research:
1. Listen to the Gentiles
2. Question the question
3. Dare to be silly
4. Simplify, simplify
…I have no sympathy for those people who criticize the unrealistic simplifications of model-builders, and imagine that they achieve greater sophistication by avoiding stating their assumptions clearly. The point is to realize that economic models are metaphors, not truth. By all means express your thoughts in models, as pretty as possible (more on that below). But always remember that you may have gotten the metaphor wrong, and that someone else with a different metaphor may be seeing something that you are missing.
…As long as you ask “system” questions like how welfare and world income are distributed, it is possible to make very simple and neat models. And it’s really these system questions that we are interested in. The focus on excessive detail was, to put it bluntly, a matter of carrying over ingrained prejudices from an overworked model into a domain where they only made life harder…The same is true in a number of areas in which I have worked. In general, if people in a field have bogged down on questions that seem very hard, it is a good idea to ask whether they are really working on the right questions. Often some other question is not only easier to answer but actually more interesting!
…If you want to publish a paper in economic theory, there is a safe approach: make a conceptually minor but mathematically difficult extension to some familiar model. Because the basic assumptions of the model are already familiar, people will not regard them as strange; because you have done something technically difficult, you will be respected for your demonstration of firepower. Unfortunately, you will not have added much to human knowledge…What I found myself doing in the new trade theory was pretty much the opposite. I found myself using assumptions that were unfamiliar, and doing very simple things with them. Doing this requires a lot of self-confidence, because initially people (especially referees) are almost certain not simply to criticize your work but to ridicule it.
…The reason for making these assumptions is not that they are reasonable but that they seem to help us produce models that are helpful metaphors for things that we think happen in the real world… inspired, marvelous silliness.
What I believe is that the age of creative silliness is not past. Virtue, as an economic theorist, does not consist in squeezing the last drop of blood out of assumptions that have come to seem natural because they have been used in a few hundred earlier papers. If a new set of assumptions seems to yield a valuable set of insights, then never mind if they seem strange.
The injunction to dare to be silly is not a license to be undisciplined. In fact, doing really innovative theory requires much more intellectual discipline than working in a well-established literature. What is really hard is to stay on course: since the terrain is unfamilar, it is all too easy to find yourself going around in circles. Somewhere or other Keynes wrote that “it is astonishing what foolish things a man thinking alone can come temporarily to believe”. And it is also crucial to express your ideas in a way that other people, who have not spent the last few years wrestling with your problems and are not eager to spend the next few years wrestling with your answers, can understand without too much effort…The strategy is: always try to express your ideas in the simplest possible model.
…Why doesn’t policy-relevant work seem to conflict with my “real” research? I think that it’s because I have been able to approach policy issues using almost exactly the same method that I use in my more basic work…Confronting supposedly knowledgeable people with an unorthodox view of an issue certainly requires the courage to be silly. And of course, ruthless simplification is worth even more in policy discussion than in theory for its own sake.
…There is, of course, always a risk that an economist who gets onto the policy circuit will no longer have enough time for real research. I certainly write an awfully large number of conference papers; I am a very fast writer, but perhaps it is a gift I overuse. Still, I think that the big danger of doing policy research is not so much the drain on your time as the threat to your values. It is easy to be seduced into the belief that direct influence on policy is more important than just writing papers — I’ve seen it happen to many colleagues.
…A minor regret is that I have never engaged in really serious empirical work. It’s not that I dislike facts or real numbers. Indeed, I find light empirical work in the form of tables, charts, and perhaps a few regressions quite congenial. But the serious business of building and thoroughly analyzing a data set is something I never seem to get around to. I think that this is partly because many of my ideas do not easily lend themselves to standard econometric testing. Mostly, though, it is because I lack the patience and organizational ability.
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