《HOW I WORK》Krugman

[LCFwentao]

HOW I WORK My formal charge in this essay is to talk about my "life
philosophy". Let me make it clear at the outset that I have no
intention of following instructions, since I don't know anything
special about life in general. I believe it was Schumpeter who claimed
to be not only the best economist, but also the best horseman and the
best lover in his native Austria. I don't ride horses, and have few
illusions on other scores. (I am, however, a pretty good cook). What I
want to talk about in this essay is something more restricted: some
thoughts about thinking, and particularly how to go about doing
interesting economics. I think that among economists of my generation
I can claim to have a fairly distinctive intellectual style -- not
necessarily a better style than my colleagues, for there are many ways
to be a good economist, but one that has served me well. The essence
of that style is a general research strategy that can be summarized in
a few rules; I also view my more policy-oriented writing and speaking
as ultimately grounded in the same principles. I'll get to my rules
for research later in this essay. I think I can best introduce those
rules, however, by describing how (it seems to me) I stumbled into the
way I work. ORIGINS Most young economists today enter the field from
the technical end. Originally intending a career in hard science or
engineering, they slip down the scale into the most rigorous of the
social sciences. The advantages of entering economics from that
direction are obvious: one arrives already well trained in
mathematics, one finds the concept of formal modeling natural. It is
not, however, where I come from. My first love was history; I studied
little math, picking up what I needed as I went along. Nonetheless, I
got deeply involved in economics early, working as a research
assistant (on world energy markets) to William Nordhaus while still
only a junior at Yale. Graduate school followed naturally, and I wrote
my first really successful paper -- a theoretical analysis of balance
of payments crises -- while still at MIT. I discovered that I was
facile with small mathematical models, with a knack for finding
simplifying assumptions that made them tractable. Still, when I left
graduate school I was, in my own mind at least, somewhat
directionless. I was not sure what to work on; I was not even sure
whether I really liked research. I found my intellectual feet quite
suddenly, in January 1978. Feeling somewhat lost, I paid a visit to my
old advisor Rudi Dornbusch. I described several ideas to him,
including a vague notion that the monopolistic competition models I
had studied in a short course offered by Bob Solow -- especially the
lovely little model of Dixit and Stiglitz -- might have something to
do with international trade. Rudi flagged that idea as potentially
very interesting indeed; I went home to work on it seriously; and
within a few days I realized that I had hold of something that would
form the core of my professional life. What had I found? The point of
my trade models was not particularly startling once one thought about
it: economies of scale could be an independent cause of international
trade, even in the absence of comparative advantage. This was a new
insight to me, but had (as I soon discovered) been pointed out many
times before by critics of conventional trade theory. The models I
worked out left some loose ends hanging; in particular, they typically
had many equilibria. Even so, to make the models tractable I had to
make obviously unrealistic assumptions. And once I had made those
assumptions, the models were trivially simple; writing them up left me
no opportunity to display any high-powered technique. So one might
have concluded that I was doing nothing very interesting (and that was
what some of my colleagues were to tell me over the next few years).
Yet what I saw -- and for some reason saw almost immediately -- was
that all of these features were virtues, not vices, that they added up
to a program that could lead to years of productive research. I was,
of course, only saying something that critics of conventional theory
had been saying for decades. Yet my point was not part of the
mainstream of international economics. Why? Because it had never been
expressed in nice models. The new monopolistic competition models gave
me a tool to open cleanly what had previously been regarded as a can
of worms. More important, however, 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. The models I wrote down that winter and spring
were incomplete, if one demanded of them that they specify exactly who
produced what. And yet they told meaningful stories. It took me a long
time to express clearly what I was doing, but 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. To get this system or
aggregate level description required, of course, accepting the
basically silly assumptions of symmetry that underlay the Dixit-
Stiglitz and related models. Yet these silly assumptions seemed to let
me tell stories that were persuasive, and that could not be told using
the hallowed assumptions of the standard competitive model. 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. Finally, the
simplicity of the models may have frustrated my lingering urge to show
off the technical skills I had so laboriously acquired in graduate
school, but was, I soon realized, central to the enterprise. Trade
theorists had failed to address the role of increasing returns, not
out of empirical conviction, but because they thought it was too hard
to model. How much more effective, then, to show that it could be
almost childishly simple? And so, before my 25th birthday, I basically
knew what I was going to do with my professional life. I don't know
what would have happened if my grand project had met with rejection
from other economists -- perhaps I would have turned cranky, perhaps I
would have lost faith and abandoned the effort. But in fact all went
astonishingly well. In my own mind, the curve of my core research
since that January of 1978 has followed a remarkably consistent path.
Within a few months, I had written up a basic monopolistic competition
trade model -- as it turned out, simultaneously and independently with
similar models by Avinash Dixit and Victor Norman, on one side, and
Kelvin Lancaster, on the other. I had some trouble getting that paper
published -- receiving the dismissive rejection by a flagship journal
(the QJE) that seems to be the fate of every innovation in economics
-- but pressed on. From 1978 to roughly the end of 1984 I focussed
virtually all my research energies on the role of increasing returns
and imperfect competition in international trade. (I took one year off
to work in the US government; but more about that below). What had
been a personal quest turned into a movement, as others followed the
same path. Above all, Elhanan Helpman -- a deep thinker whose
integrity and self-discipline were useful counterparts to my own
flakiness and disorganization -- first made crucial contibutions
himself, then talked me into collaborative work. Our magnum opus,
Market Structure and Foreign Trade, served the purpose of making our
ideas not only respectable but almost standard: iconoclasm to
orthodoxy in seven years. For whatever reason, I allowed my grand
project on increasing returns to lie fallow for a few years in the
1980s, and turned my attention to international finance. My work in
this area consisted primarily of small models inspired by current
policy issues; although these models lacked the integrating theme of
my trade models, I think that my finance work is to some extent
unified by its intellectual style, which is very similar to that of my
work on trade. In 1990 I returned to the economics of increasing
returns from a new direction. I suddenly realized that the techniques
that had allowed us to legitimize the role of increasing returns in
trade could also be used to reclaim a whole outcast field: that of
economic geography, the location of activity in space. Here, perhaps
even more than in trade, was a field full of empirical insights, good
stories, and obvious practical importance, lying neglected right under
our noses because nobody had seen a good way to formalize it. For me,
it was like reliving the best moments of my intellectual childhood.
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. My work on
geography seems, at the time of writing, to be leading me even further
afield. In particular, there are obvious affinities between the
concepts that arise naturally in geographic models and the language of
traditional development economics -- the "high development theory"
that flourished in the 1940s and 50s, then collapsed. So I expect that
my basic research project will continue to widen in scope. RULES FOR
RESEARCH In the course of describing my formative moment in 1978, I
have already implicitly given my four basic rules for research. Let me
now state them explicitly, then explain. Here are the rules: 1. Listen
to the Gentiles 2. Question the question 3. Dare to be silly 4.
Simplify, simplify 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. I have now described my basic rules for research.
I have illustrated them with my experience in developing the "new
trade theory" and with my more recent extension of that work to
economic geography, because these are the core of my work. But I have
also done quite a lot of other stuff, which (it seems to me) is also
in some sense part of the same enterprise. So in the remainder of this
essay I want to talk about this other work, and in particular about
how the policy economist and the analytical economist can coexist in
the same person. POLICY-RELEVANT WORK Most economic theorists keep
their hands off current policy issues -- or if they do get involved in
policy debates, do so only after the midpoint of their career, as
something that follows creative theorizing rather than coexists with
it. There seems to be a consensus that the clarity and singleness of
purpose required to do good theory are incompatible with the tolerance
for messy issues required to be active in policy discussion. For me,
however, it has never worked that way. I have interspersed my academic
career with a number of consulting ventures for various governments
and public agencies, as well as a full year in the US government. I
have also written a book, The Age of Diminished Expectations, aimed at
a non-technical audience. And I have written a pretty steady stream of
papers that are motivated not by the inner logic of my research but by
the attempt to make sense of some currently topical policy debate --
e.g., Third World debt relief, target zones for exchange rates, the
rise of regional trading blocs. All of this hasn't seemed to hurt my
research, and indeed some of my favorite papers have grown out of this
policy-oriented work. 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. Paying attention to newspaper
reports or the concerns of central bankers and finance ministers is
just another form of listening to the Gentiles. Trying to find a
useful way of defining their problems is pretty much the same as
questioning the question in theory. 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. So doing policy-relevant economics does not, for me,
mean a drastic change in intellectual style. And it has its own
payoffs. Let's be honest and admit that these include invitations to
fancier conferences and speaking engagements at much higher fees than
an academic purist is likely to get. Let's also admit that one of the
joys of policy research is the opportunity to shock the bourgeoisie,
to point out the hollowness or silliness of official positions. For
example, I know that I was not the only international economist to
have some fun pointing out the absurdities of the Maastricht Treaty,
and was not above some wicked pleasure when the ERM crisis I and
others had long predicted actually came to pass in the fall of 1992.
The main payoff to policy work, though, is intellectual stimulation.
Not all real-world questions are interesting -- I find that almost
anything having to do with taxation is better than a sleeping pill --
but every couple of years, if not more often, the international
economy throws up a question that gives rise to exciting research. I
have been stimulated to write theory papers by the Plaza and the
Louvre, by the Brady Plan, NAFTA, and EMU. All of them are papers that
I think could stand on their own, even without the policy context.
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. Once
you start down that road, once you begin to think that David Mulford
matters more than Bob Solow, or to prefer hobnobbing with the
Ruritanian finance minister to talking theory with Avinash Dixit, you
are probably lost to research. Pretty soon you'll probably start using
"impact" as a verb. Fortunately, while I love playing around with
policy issues, I have never been able to take policy makers very
seriously. This lack of seriousness gets me into occasional trouble --
like the time that a gentle parenthetical joke about the French in a
conference paper led to an extended diatribe from the French official
attending the conference -- and may exclude me from ever holding any
important policy position. But that's OK: in the end, I would rather
write a few more good papers than hold a position of real power. (Note
to the policy world: this doesn't mean that I would necessarily turn
down such a position if it were offered!) REGRETS There are a lot of
things about my life and personality that I regret -- if things have
gone astonishingly well for me professionally, they have been by no
means as easy or happy elsewhere. But in this essay I only want to
talk about professional regrets. 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. Every year I promise to try to do
some real empirical work. Next year I really will! A more important
regret is that while the MIT course evaluations rate me as a pretty
good lecturer, I have not yet succeeded in generating a string of
really fine students, the kind who reflect glory on their teacher. I
can make excuses for this failing -- students often prefer advisers
who are more methodical and less intuitive, and I all too often scare
students off by demanding that they use less math and more economics.
It's also true that I probably seem busy and distracted, and perhaps I
am just not imposing enough in person to be inspiring (if I were only
a few inches taller ...). Whatever the reasons, I wish I could do
better, and intend to try. All in all, though, I've been very lucky. A
lot of that luck has to do with the accidents that led me to stumble
onto an intellectual style that has served me extremely well. I've
tried, in this essay, to define and explain that style. Is this a life
philosophy? Of course not. I'm not even sure that it is an economic
research philosophy, since what works for one economist may not work
for another. But it's how I do research, and it works for me.