krugman--How I Work
HOW I WORK
Paul Krugman
Professor, Princeton University
My<br>formal charge in this essay is to talk about my "life philosophy". Let<br>me make it clear at the outset that I
have<br>no intention of following instructions, since I don't know anything special<br>about life in general. I believe it
was<br>Schumpeter who claimed to be not only the best economist, but also the<br>best horseman and the best lover in
his<br>native Austria. I don't ride horses, and have few illusions on other scores.<br>(I am, however, a pretty good
cook).<br>What<br>I want to talk about in this essay is something more restricted: some thoughts<br>about thinking, and
particularly<br>how to go about doing interesting economics. I think that among economists<br>of my generation I can
claim<br>to have a fairly distinctive intellectual style -- not necessarily a better<br>style than my colleagues, for there
are<br>many ways to be a good economist, but one that has served me well. The<br>essence of that style is a general
research<br>strategy that can be summarized in a few rules; I also view my more policy-oriented<br>writing and
speaking<br>as ultimately grounded in the same principles. I'll get to my rules for<br>research later in this essay. I
think<br>I can best introduce those rules, however, by describing how (it seems<br>to me) I stumbled into the way I
work.<br>ORIGINS<br>Most<br>young economists today enter the field from the technical end. Originally<br>intending a career in hard science
or<br>engineering, they slip down the scale into the most rigorous of the social<br>sciences. The advantages of entering
economics<br>from that direction are obvious: one arrives already well trained in mathematics,<br>one finds the concept
of<br>formal modeling natural. It is not, however, where I come from. My first<br>love was history; I studied little
math,<br>picking up what I needed as I went along.<br>Nonetheless,<br>I got deeply involved in economics early, working as a research assistant<br>(on world energy markets)
to<br>William Nordhaus while still only a junior at Yale. Graduate school followed<br>naturally, and I wrote my first
really<br>successful paper -- a theoretical analysis of balance of payments crises<br>-- while still at MIT. I discovered
that<br>I was facile with small mathematical models, with a knack for finding simplifying<br>assumptions that made
them<br>tractable. Still, when I left graduate school I was, in my own mind at<br>least, somewhat directionless. I was
not<br>sure what to work on; I was not even sure whether I really liked research.<br>I found<br>my intellectual feet quite suddenly, in January 1978. Feeling somewhat<br>lost, I paid a visit to my old
advisor<br>Rudi Dornbusch. I described several ideas to him, including a vague notion<br>that the monopolistic
competition<br>models I had studied in a short course offered by Bob Solow -- especially<br>the lovely little model of
Dixit<br>and Stiglitz -- might have something to do with international trade. Rudi<br>flagged that idea as potentially
very<br>interesting indeed; I went home to work on it seriously; and within a few<br>days I realized that I had hold of
something<br>that would form the core of my professional life.<br>What<br>had I found? The point of my trade models was not particularly startling<br>once one thought about it:
economies<br>of scale could be an independent cause of international trade, even in<br>the absence of comparative
advantage.<br>This was a new insight to me, but had (as I soon discovered) been pointed<br>out many times before by
critics<br>of conventional trade theory. The models I worked out left some loose ends<br>hanging; in particular, they
typically<br>had many equilibria. Even so, to make the models tractable I had to make<br>obviously unrealistic
assumptions.<br>And once I had made those assumptions, the models were trivially simple;<br>writing them up left me
no<br>opportunity to display any high-powered technique. So one might have concluded<br>that I was doing nothing very
interesting<br>(and that was what some of my colleagues were to tell me over the next<br>few years). Yet what I saw --
and<br>for some reason saw almost immediately -- was that all of these features<br>were virtues, not vices, that they
added<br>up to a program that could lead to years of productive research.<br>I was,<br>of course, only saying something that critics of conventional theory had<br>been saying for decades. Yet my
point<br>was not part of the mainstream of international economics. Why? Because<br>it had never been expressed in
nice<br>models. The new monopolistic competition models gave me a tool to open<br>cleanly what had previously been
regarded<br>as a can of worms. More important, however, I suddenly realized the remarkable<br>extent to which the
methodology<br>of economics creates blind spots. We just don't see what we can't formalize.<br>And the biggest blind
spot<br>of all has involved increasing returns. So there, right at hand, was my<br>mission: to look at things from a
slightly<br>different angle, and in so doing to reveal the obvious, things that had<br>been right under our noses all the
time.<br>The<br>models I wrote down that winter...