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Thursday, October 16, 2008

What can we learn from Nobel laureates in economics? According to Krugman: Listen to the Gentiles

For a while, I've been prone to skipping most of Paul Krugman's columns in the NYT, finding them a bit on the shrill side for my taste. Still, as he was basking in his recent Nobel-generated glow, I was directed, via Gordon Smith, to a great set of links by Tyler Cowen at Marginal Revolution that describe Krugman's work in economics. Especially interesting to me was an essay Krugman wrote about how he works and goes about finding useful projects in economics. He develops a few rules of thumb to try to guide his research. Here they are, with the discussion after the jump. I wonder which of these might apply cleanly or with some minimal translation to the academic law context. As far as I know, the closest legal analogue to this "How I Work" series is Kim Ferzan's instantly-classic interview with Ian Ayres, Paul Robinson, and Carol Sanger. To my mind, some of Krugman's notions regarding "question the question" and "dare to be silly" are a bit similar to Ian Ayres' advice to embrace perversity. Of course, question the question is an old philosopher's trick...

1. Listen to the Gentiles

2. Question the question

3. Dare to be silly

4. Simplify, simplify

Here is more of Krugman's essay with elaboration on these four key points.

Listen to the Gentiles

What I mean by this rule is "Pay attention to what intelligent people are saying, even if they do not have your customs or speak your analytical language." The point may perhaps best be explained by example. When I began my rethinking of international trade, there was already a sizeable literature criticizing conventional trade theory. Empiricists pointed out that trade took place largely between countries with seemingly similar factor endowments, and that much of this trade involved intra-industry exchanges of seemingly similar products. Acute observers pointed to the importance of economies of scale and imperfect competition in actual international markets. Yet all of this intelligent commentary was ignored by mainstream trade theorists -- after all, their critics often seemed to have an imperfect understanding of comparative advantage, and had no coherent models of their own to offer; so why pay attention to them? The result was that the profession overlooked evidence and stories that were right under its nose.

The same story is repeated in geography. Geographers and regional scientists have amassed a great deal of evidence on the nature and importance of localized external economies, and organized that evidence intelligently if not rigorously. Yet economists have ignored what they had to say, because it comes from people speaking the wrong language.

I do not mean to say that formal economic analysis is worthless, and that anybody's opinion on economic matters is as good as anyone else's. On the contrary! I am a strong believer in the importance of models, which are to our minds what spear-throwers were to stone age arms: they greatly extend the power and range of our insight. In particular, 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.

Question the question

There was a limited literature on external economies and international trade before 1978. It was never, however, very influential, because it seemed terminally messy; even the simplest models became bogged down in a taxonomy of possible outcomes. What has since become clear is that this messiness arose in large part because the modelers were asking their models to do what traditional trade models do, which is to predict a precise pattern of specialization and trade. Yet why ask that particular question? Even in the Heckscher-Ohlin model, the point you want to make is something like "A country tends to export goods whose production is intensive in the factors in which that country is abundant"; if your specific model tells you that capital-abundant country Home exports capital-intensive good X, this is valuable because it sharpens your understanding of that insight, not because you really care about these particular details of a patently oversimplified model.

It turns out that if you don't ask for the kind of detail that you get in the two-sector, two-good classical model, an external economy model needn't be at all messy. 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! (One drawback of this trick is that it often gets people angry. An academic who has spent years on a hard problem is rarely grateful when you suggest that his field can be revived by bypassing it).

Dare to be silly

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. After all, your assumptions will surely look peculiar: a continuum of goods all with identical production functions, entering symmetrically into utility? Countries of identical economic size, with mirror-image factor endowments? Why, people will ask, should they be interested in a model with such silly assumptions -- especially when there are evidently much smarter young people who demonstrate their quality by solving hard problems?

What seems terribly hard for many economists to accept is that all our models involve silly assumptions. Given what we know about cognitive psychology, utility maximization is a ludicrous concept; equilibrium pretty foolish outside of financial markets; perfect competition a howler for most industries. 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.

Consider the example which some economists seem to think is not simply a useful model but revealed divine truth: the Arrow-Debreu model of perfect competition with utility maximization and complete markets. This is indeed a wonderful model -- not because its assumptions are remotely plausible but because it helps us think more clearly about both the nature of economic efficiency and the prospects for achieving efficiency under a market system. It is actually a piece of inspired, marvellous 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.

Simplify, simplify

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.

Fortunately, there is a strategy that does double duty: it both helps you keep control of your own insights, and makes those insights accessible to others. The strategy is: always try to express your ideas in the simplest possible model. The act of stripping down to this minimalist model will force you to get to the essence of what you are trying to say (and will also make obvious to you those situations in which you actually have nothing to say). And this minimalist model will then be easy to explain to other economists as well.

I have used the "minimum necessary model" approach over and over again: using a one-factor, one-industry model to explain the basic role of monopolistic competition in trade; assuming sector-specific labor rather than full Heckscher-Ohlin factor substitution to explain the effects of intraindustry trade; working with symmetric countries to assess the role of reciprocal dumping; and so on. In each case the effect has been to allow me to tackle a subject widely viewed as formidably difficult with what appears, at first sight, to be ridiculous simplicity.

The downside of this strategy is, of course, that many of your colleagues will tend to assume that an insight that can be expressed in a cute little model must be trivial and obvious -- it takes some sophistication to realize that simplicity may be the result of years of hard thinking. I have heard the story that when Joseph Stiglitz was being considered for tenure at Yale, one of his senior colleagues belittled his work, saying that it consisted mostly of little models rather than deep theorems. Another colleague then asked, "But couldn't you say the same about Paul Samuelson"? "Yes, I could", replied Joe's opponent. I have heard the same reaction to my own work. Luckily, there are enough sophisticated economists around that in the end intellectual justice is usually served. And there is a special delight in managing not only to boldly go where no economist has gone before, but to do so in a way that seems after the fact to be almost childs' play.

Posted by Administrators on October 16, 2008 at 11:25 AM in Current Affairs | Permalink


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