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.

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                                                                        INCIDENTS FROM MY CAREER

        My personal life is not interesting. I don't mean that I am an especially deadly dinner companion, or that I have
        not had my fair share of life's joys and miseries. What I mean is that only my friends and family are interested in
        the more intimate details of my history; nobody reading this essay wants to know about my marital or health
        problems (or if you do, it's none of your business!). What readers want to know, presumably, is how I came to be
        the particular sort of economist I am -- how I came to write the books and papers I did, and more generally how I
        arrived both at the particular ideas I have inflicted on the world and at whatever distinctive features there are in
        my intellectual style. Lives are seamless, so everything affects everything else: my economic theories have no
        doubt been influenced by my relationship with my cats (which is, I hasten to add, mature and mutually supportive)
        and vice versa. What I will try to focus on in this essay, however, are the incidents in my professional life that I
        think were important -- the experiences that in obvious ways influenced the way I write and think.

        I will also, along the way, try to convey something of the flavor of what it is to be a successful academic
        economist in late 20th-century America. No matter what we may say, none of us is a philosopher-saint, and you
        can't fully understand the development of economic ideas without a sense of the structure of rewards that
        economists face. That's why I call this essay "Incidents from my career"; I may have been in pursuit of Truth and
        Beauty, but I, like everyone, was also in pursuit of success.

        Most of this essay is a series of vignettes from my professional life, in chronological order. I follow this story of
        my life with a discussion of what I think was the point of it all: my personal assessment of what I did to and for
        economics.

        1. Becoming an economist

        I have a self-serving theory: interesting ideas have very little to do with interesting life experiences. According
        to this theory a person who has grown up in eight countries and speaks five languages, who has taken a dogsled
        across Siberia and a raft down the Amazon, is no more likely to have a deep insight into social science than
        someone who grew up in a safe middle-class suburb reading science-fiction novels.

        I hope this theory is true, because I have an utterly conventional background. I was born in 1953, at the peak of
        the baby boom. I grew up in the New York suburbs, had an ordinary education (I attended one of the many John F.
        Kennedy High Schools), and went on to four uneventful college years.

        Admittedly, there were those science fiction novels. Indeed, they may have been what made me go into
        economics. Those who read the stuff may be aware of the classic Foundation trilogy by Isaac Asimov. It is one of
        the few science fiction series that deals with social scientists -- the "psychohistorians", who use their
        understanding of the mathematics of society to save civilization as the Galactic Empire collapses. I loved
        Foundation, and in my early teens my secret fantasy was to become a psychohistorian. Unfortunately, there's no
        such thing (yet). I was and am fascinated by history, but the craft of history is far better at the what and the
        when than the why, and I eventually wanted more. As for social sciences other than economics, I am interested in
        their subjects but cannot get excited about their methods -- the power of economic models to show how plausible
        assumptions yield surprising conclusions, to distill clear insights from seemingly murky issues, has no counterpart
        yet in political science or sociology. Someday there will exist a unified social science of the kind that Asimov
        imagined, but for the time being economics is as close to psychohistory as you can get.

        And so in college I became an economics major. I didn't take all that many economics courses; in fact, I took
        only slightly more than the minimum required by the major, filling up the extra time with a lot of history courses.
        But I was very lucky to receive an early apprenticeship in doing real economic research. In the spring of 1973
        (my junior year) William Nordhaus and Tjalling Koopmans offered an undergraduate seminar on energy and
        natural resource issues. In my effort to find a topic for a term paper I happened to stumble across international
        cross-section data on the price and consumption of gasoline, and used that data to write a paper suggesting that
        long-run demand for gasoline is in fact fairly price-elastic -- contrary to the prevailing belief in the US at that
        time. On the strength of that paper Nordhaus asked me to work for him as a research assistant; and it was at that
        point that I can say that I effectively became a professional economist.

        Bill Nordhaus was and is a fine economist in the classic MIT, which is to say Robert Solow, tradition. There are
        several different ways of doing good economics. You can try to prove deep theorems; and who would deny the
        importance of the work of, say, the young Kenneth Arrow? Or you can do detailed, nitty-gritty empirical work;
        and I deeply admire the work of, say, a Zvi Griliches. But what has always appealed to me, ever since I saw
        Nordhaus practice it on energy, is the MIT style: small models applied to real problems, blending real-world
        observation and a little mathematics to cut through to the core of an issue.

        The first summer I worked for him, Nordhaus began with only a vague sense of how to think about the problem of
        appropriate pricing of energy. I was able to watch the process by which he crystallized that vague sense into a
        model, and then was able to see the way in which that model transformed everyone's perception of the issue. It
        would be several years before I was ready to try the same thing, but I was lucky to get so early a view of what
        doing economics is really about. I graduated from Yale in 1974. As Nordhaus's protege, it was only natural that I
        go on to graduate school at MIT.

        The mid-1970s at MIT were a heady time. For one thing, those were the days of the rational expectations
        revolution in macroeconomics. MIT's senior faculty were a bit skeptical, and Keynesian ideas continued to be
        taught -- a fortunate thing, because by the 1980s equilibrium macro would become a faith held in the teeth of
        adverse evidence. Nonetheless, for students it was a time when everything seemed up for reinvention. Saddle-path
        diagrams were still new and exciting, not the tired cliche they have since become; I still remember a bunch of us
        working out the geometry of anticipated shocks on a lunchroom table. For those who were interested in
        international macroeconomics -- and the arrival of Rudi Dornbusch at MIT in 1975 meant that many students were
        -- there was the additional excitement of trying to figure out the new world of floating exchange rates, at a time
        when the question seemed to be who would win the glory of having the winning theory. (Again, the empirical
        debacle still lay in the future).

        Finally, at MIT I got my first sense of the wider role an economist can play in the world. When he arrived at
        MIT, Rudi Dornbusch was an economist's economist, known for the didactic clarity of his papers. As I watched,
        he was transformed into a policy guru, his advice sought by governments and bankers around the world. I don't
        know whether the possibility for that kind of enlargment of role was truly new, but it was new to me.

        In the summer of 1976 I got a first taste of the policy world myself, as part of a small group of MIT students sent
        to work for the central bank of Portugal for three months. At the time Portugal was in considerable chaos, in the
        aftermath of a revolution and an attempted coup; much of the challenge was simply to figure out what was going
        on. What I learned from that experience was the power of very simple economic ideas and simultaneously the
        uselessness of theories that cannot be given operational content. In particular, my experience in a country in
        which it was a major challenge even to decide whether output was rising or falling gave me a lasting allergy to
        models that tell you that a potentially useful policy exists without giving you any way to determine what that
        policy is.

        Although I learned an immense amount at MIT, however, I did not exactly leave trailing clouds of glory. I was
        anxious to get out of graduate school, for no better reason than that I was still very shy and lonely, and that I
        hoped that getting out into the real world would help me break out of my personal shell. (For the same reason, I
        turned down Bob Solow's offer to nominate me for the Harvard Society of Fellows; I was afraid that I would
        simply sit alone in my office for three years). As a result, I rushed out with a hastily written thesis, which didn't
        even include the one really good paper I had written (more on that below). Luckily Yale offered me a job
        nonetheless. But it was not until the middle of my first year of teaching that I found my feet as an economist.

        2. Finding a vision

        I wrote the first paper I think of as characteristic when I was still in graduate school. "A model of balance of
        payments crises" emerged while I was spending two months as an intern at the Federal Reserve, where I realized
        that the stories Steve Salant was telling about speculative attacks on commodity stockpiles could be applied to
        currency crises as well. Both my craftsmanship and my self-confidence were still, however, a bit weak. The
        model contained unnecessary complications, and the writing was somewhat unclear. Perhaps as a result, Rudi
        Dornbusch, by now my thesis adviser, didn't get the point of the first draft (neither did the referees when I finally
        submitted it); and instead of standing up to his doubts, I simply buried the paper until Rudi suggested I look at it
        again a year later.

        I now think that I was lucky that I put speculative attacks on hold, since I might easily have ended up devoting
        my next few years to rational-expectations models of international finance. Instead, I spent my first semester of
        teaching at something of a loss, and then found something much bigger: a vision that continues to guide my
        research more than 15 years later. The vision was, of course, of the importance of increasing returns and
        imperfect competition in trade.

        I had learned about monopolistic competition from a short course given by Bob Solow in 1976, and I guess the
        idea of applying the new models to trade had been percolating in my mind ever since. I have, however, a typical
        pattern in my work: I will have a foggy idea that I play with occasionally, sometimes for years; then some event
        will suddenly cause the fog to lift, revealing an almost fully developed model. In this case, in January 1978 I paid
        a visit to Rudi Dornbusch to talk about my work, and prepared a list of possible ideas, including as an
        afterthought the idea of a monopolistically competitive trade model. When he flagged the idea as interesting, I
        went home to work on it the next day -- and knew within a few hours that I had the key to my whole career in
        hand. I distinctly remember staying up all night in excitement, feeling that I had just seen a vision on the road to
        Damascus.

        Of course it took a while to convince anyone else of the truth of that vision. In fact the next year and a half was
        deeply frustrating: rejections by journals, lack of interest by most of my senior colleagues (though much support
        from Carlos Diaz-Alejandro), and a decision by the Yale department not to give me a research fellowship. I
        persevered, however, and in the spring of 1979 another patch of fog lifted, and I saw my way clear to integrate
        monopolistic competition and comparative advantage. (I can again describe the moment of revelation very
        precisely: the analytical trick that made the model possible came to me at Boston's Logan Airport, where I was
        waiting for a flight to Minneapolis).

        I presented the new paper at the National Bureau of Economic Research Summer Institute that July -- an ideal
        locale, because it guaranteed exposure to an influential group of international economists. I still think, with all of
        the things that I have done since, that the hour and a half in which I presented that paper was the best 90 minutes
        of my life. There's a corny scene in the movie Coal Miner's Daughter, in which the young Loretta Lynn performs
        for the first time in a noisy bar, and little by little everyone gets quiet and starts to listen to her singing. Well,
        that's what it felt like: I had, all at once, made it.

        Made it to what? In the modern academic world there tends, in any given field -- whether it is international
        finance, Jane Austen studies, or some branch of endocrinology -- to be a "circuit", the people who get invited to
        speak at academic conferences, who form a sort of de facto nomenklatura. I used to refer to the circuit in
        international economics as the "floating crap game". It's hard to get onto the circuit -- it takes at least two really
        good papers, one to get noticed and a second to show that the first wasn't a fluke -- but once you are in, the
        constant round of conferences and invited papers makes it easy to stay in. By the summer of 1980, with five or so
        really good papers either published or in the pipeline, I was pretty much guaranteed a lifetime place.

        It seems to me that in the next couple of years, assured of a solid place in the academic world, I actually did
        slack off a bit, although I continued to work on the economics of trade and imperfect competition, and wrote some
        papers that I can still read without embarassment. What I mostly remember from that time, however, is going to
        conferences. These were not lavish affairs: we are talking about flying economy class, taking the bus in from the
        airport, and staying on the sixth floor of a hotel with no elevator or in a conference center with bathrooms down
        the hall. Nonetheless, people were now paying my way to travel to England, France, Italy, Germany, Spain,
        Finland, Sweden, Switzerland, Israel, Mexico. I was finally having the exotic experiences that I had missed when
        younger -- except, of course, that I kept meeting the same people wherever I went!

        I have never left the academic circuit, and I never will. I have been a bit cynical about how that circuit works,
        but its members constitute a true, and wonderfully unpretentious, elite. A few weeks before writing this piece I
        attended an international trade conference held in a classroom in Milan. The room was shabby, with seats so
        uncomfortable that several older participants ended up with back problems. The hotel was decent but austere. Yet
        I can assure you that there was more real insight in the discussion than you will find in a dozen G7 summits. I
        hope that I never forget that it is young economists in blue jeans, not famous officials in pinstripes, who really
        have interesting things to say. And yet I was not satisfied. No doubt this had a lot to do with personal issues of
        the kind that I won't discuss here, but after three years of academic conferences I was jaded and a little bored. I
        was ready to jump at the opportunity to do something different, if not in the end better.

        3. Washington

        In August of 1982 I flew home from a conference in Sweden to find a message to call Martin Feldstein. Two
        weeks later I had arranged for a leave from MIT and was on my way to Washington, to be the chief staffer for
        international economics at the Council of Economic Advisers.

        It was, in a way, strange for me to be part of the Reagan Administration. I was then and still am an unabashed
        defender of the welfare state, which I regard as the most decent social arrangement yet devised. I am also unable
        to pretend to respect "policy entrepreneurs", the intellectually dishonest self-proclaimed experts who tell
        politicians what they want to hear. The Reagan Administration was, of course, full of people who hated the
        welfare state and had very little interest in the truth. But the summer of 1982 was a moment of near-panic among
        the Reaganauts, as the recession and the debt crisis seemed to threaten catastrophe. They not only hired
        Feldstein, they gave him the freedom to bring in a politically incorrect team of whiz-kids (which included Larry
        Summers and Greg Mankiw) in the hope that he could turn things around. By 1983, with a recovery well under
        way, the political types were back in charge and Feldstein was ostracized for worrying publically about the
        budget deficit; but that came later.

        Washington was first thrilling, then disillusioning. It is the capital of the world, and for a young person it is
        wonderful to think that you can really have an effect on decisions of global importance. I can still recite from
        memory the long list of prohibitions on the front page of each classified document ("Secret/No foreign
        nationals/No contractors/Proprietary information/Origin controlled"). Some people get addicted to that thrill, and
        will do anything to stay near the center.

        After a little while, however, I began to notice how policy decisions are really made. The fact is that most senior
        officials have no idea what they are talking about: discussion at high-level meetings is startlingly primitive. (For
        example, the distinction between nominal and real interest rates tends to be regarded as a complex and useless
        bit of academic nitpicking). Furthermore, many powerful people prefer to take advice from those who make them
        feel comfortable rather than from those who will force them to think hard. That is, those who really manage to
        influence policy are usually the best courtiers, not the best analysts. I like to think that I am a good analyst, but I
        am certainly a very bad courtier. And so I was not tempted to stay on in Washington.

        I did, however, discover a new talent: that of writing serious economics in seemingly plain English. I got to
        practice that talent in writing classified memos, and proved good enough at it that I ended up writing most of the
        1983 Economic Report of the President. Ever since, I have used non-technical writing about economics as the
        basis for a sort of parallel career, one that keeps me on the fringes of the policy world though rarely at its
        center. I made a good start on that parallel career just after leaving Washington, by writing a paper for a major
        conference on industrial policy. That paper was deeply critical of some of the industrial policy proposals that
        were circulating at that time, and was critical in particular of what I considered the foolish proposals of a policy
        entrepreneur by the name of Robert Reich. In so doing I had planted a time bomb which only went off nine years
        later.

        4. Consolidation and crisis

        I spent one year in Washington, and was then faced with the problem of reintegrating myself into academic life --
        not an easy task. Often a period of work in policy seems to destroy the capacity to do academic research. It's not
        just that writing papers lacks the thrill of directly influencing events. It's also that once you've seen the primitive
        nature of real policy discussion, you start to wonder whether third-order conditions or likelihood-ratio tests can
        really matter. But I was lucky, because a colleague took me in hand.

        During the academic year 1983-4 Elhanan Helpman of Tel-Aviv University was visiting at MIT, and he persuaded
        me to work with him on a magnum opus synthesizing the work on the "new trade theory", the merger of industrial
        organization and trade that he and I had helped pioneer. What followed was a ten-month period of total
        immersion, out of which emerged Market Structure and Foreign Trade, which served all the purposes Elhanan had
        in mind: not only did it synthesize the field, but by offering a single, comprehensive reference it was a great
        advertising device. That is, from that point on, if anyone asked "What's this new trade theory about?", he could
        simply be told to read our book. That was good for the new trade theory, and not incidentally good for our own
        careers.

        After this huge effort, I fell into something of a work slump. In fact, from my point of view I went into a
        three-year professional crisis. From the outside this may not have been obvious. After all, I was by now a tenured
        professor at the world's leading economics department, and was still a very active member of the conference
        circuit. I even wrote several pretty good papers during that time. Yet from the inside, I felt that I had lost my
        sense of what I was supposed to be doing; the good papers felt like isolated stunts, not like part of an ongoing
        quest.

        To be honest, I also felt underappreciated. At one level, this was petty: I had a very pleasant job that paid quite
        well and received lots of invitations to conferences around the world. Compared with 99.9 percent of humanity, I
        had nothing to complain about. But of course that isn't the way the human animal is constructed. My emotional
        reference group consisted of the most successful economists of my generation, and I was not generally counted
        among their number.

        I hit an emotional low point in the spring and summer of 1987. I was turned down for several grants, substantially
        complicating my plans to take an academic leave the next year; and I didn't seem to have any real momentum
        going on in my research. I went to conferences, but it seemed like going through the motions. And then, somehow,
        it all fell into place again.

        5. Getting back on track

        In the second half of 1987 I suddenly experienced an explosion of research productivity. I'm not quite sure why,
        but I can think of several reasons.

        One was that I took a year's leave from MIT and spent it sitting at the National Bureau of Economic Research.
        The NBER is a cramped environment, with several dozen smart young economists crammed close together. It isn't
        very comfortable, but at any given time there is nearly always an interesting conversation about economics going
        on in the coffee room; I don't know anyplace else as stimulating.

        Another reason was that I had, without quite knowing it, been accumulating material. Over the previous two
        years, lacking fundamental research ideas (and needing money), I had gone to many policy-oriented conferences:
        conferences that would provide an honorarium for a sensible but not necessarily innovative paper on the dollar, on
        developing country debt, on the trade deficit, and so on. I was pretty good at this, because of the skill I had
        developed at writing serious economics in non-technical language. Not many theorists are able or willing to
        participate in this somewhat different conference circuit, so I was in the fairly unique position of being a clever
        model-builder who had a good sense of what the trendy international economic issues of the day were, of what
        was on the minds of people who cared about policy.

        Finally, it may sound silly, but I think that the advent of improved software for personal computers, and
        especially the availability of laptop machines that could come with me on my international travels, encouraged
        me to write technical papers. I am an extremely fast but disorganized and impatient worker; a technology that
        lets me produce a paper -- equations, simulations, and all -- in a hotel room somewhere over a weekend perfectly
        fits my style.

        Anyway, whatever the reason, in 1987 and 1988 I began writing a torrent of papers. I actually don't know how
        many -- there were about eight serious theory papers that remain relevant, and probably another fifteen topical
        conference papers, not to mention two co-authored books. (By the way, the times and ways in which ideas float up
        remained fairly strange. My basic model of exchange rate target zones, arguably my most successful single paper,
        came to me during a flight from Tokyo to London).

        The papers I wrote during that spurt were different from those I had written during my first few years after
        graduate school. My earlier work had tended to draw its motivation entirely from the logic of economic research,
        addressing enduring questions like "why is there international trade?" Now I found myself writing papers that
        took a current policy concern -- Third World debt reduction, the working of the EMS, the apparent trend toward
        trading blocs -- as a starting point. From there I would develop a small, elegant model that would in effect
        provide a language for discussing the issue. Some of the issues I worked on have faded into obscurity; but it turns
        out that the models tend to live on.

        The work I did in 1987 and 1988 ended my own self-doubts about research. And I would be dishonest if I didn't
        admit that there was also a gratifying change in my professional standing. The conference invitations got fancier
        -- although, as I suspected, it turned out that the lavishness of a conference and its intellectual quality are almost
        perfectly negatively correlated. More important, there seemed to be a growing appreciation outside of
        international trade of what the new trade theory had achieved. This appreciation was eventually reflected in some
        serious academic gongs: Elhanan Helpman received the Israel Prize, an all-academic honor that is at least as
        hard to get as a Nobel Prize, and I got the American Economic Association's John Bates Clark Medal. The
        important point is that in 1987 and 1988 I had, once again, made it past a sort of barrier. And I was again not
        satisfied: I wanted to try something new.

        6. A broader audience

        In the fall of 1988 Michael Barker, a former Congressional aide now working for The Washington Post,
        approached me about a book project. He wanted me to write a primer on the US economy for a new series of
        "briefing books" the Post was planning to issue. Rather casually I agreed, and after much procrastination I spent
        most of a summer on Martha's Vineyard pounding out The Age of Diminished Expectations. It turned out that I
        wrote a different sort of book than either Michael or I had expected. It was, indeed, a primer on the US economy;
        but it was also a kind of stealth textbook on economic theory, turning the real economic problems of the United
        States into a series of parables that illustrated economic principles, with sophisticated models hidden under the
        seemingly plain prose. It wasn't to everyone's taste, but it quickly became a sort of cult book, with a devoted
        following.

        Diminished Expectations never became a true best-seller. I like to blame the marketing and distribution, over
        which I never had any control. But the book did reach a much larger audience than anything else I had written,
        and did a lot to open new doors to me. Journalists read Diminished Expectations and then called me for stories;
        businessmen read it and asked me to speak at conferences. And of course each interview in the press or business
        speech led to further calls.

        This was not all to the good. The pace of my life changed; I had always been busy, but now I found myself in
        constant and unhappy overdrive. I signed with an agency to negotiate speaking deals, not for the business they
        could bring but for their ability to demand high fees and thus ration my time. (I got pretty good at the speaking,
        however, and the fees started to get high enough to tempt me into doing too much of it). I found that an hour or
        two of each day was spent on the phone with reporters. Luckily for my sanity and future productivity, however, I
        did not break through into a role as TV personality. If I had, I do not know if I could have found the
        self-discipline to continue with research.

        My role as a public person soared during the 1992 Presidential campaign, then took a nosedive soon afterwards.
        What propelled my visibility upwards was my role in a bitter public dispute over income distribution. It is a fact
        that income inequality in the US soared during the Reagan years, but it is a fact that conservatives are reluctant
        to admit. I had included a chapter on inequality in Diminished Expectations -- over the objections, by the way, of
        my editors, who didn't think it was important. I came back to the issue in some Congressional testimony early in
        1992. In particular, I thought up a useful way to dramatize the extent of the inequality: some 70 percent of the
        increase in average family income from 1977 to 1989 had gone to the top one percent of families. This number
        made a good sound bite, and was eagerly seized upon by the Clinton campaign.

        The next few months were a strange time, as I, with a little help from friends in the press, waged what amounted
        to a propaganda war with the editor of the Wall Street Journal. I think I won that war -- in the end, the point was
        that inequality had indeed increased sharply, and efforts to deny that eventually looked silly. But it meant that for
        much of that year I was playing a far more public role than ever before. Inevitably this brought me into some
        contact with the Clinton campaign. I wrote an op-ed piece endorsing their economic plan, and met the candidate
        once. In the newspapers, of course, I was touted as a likely chairman of the Council of Economic Advisers.

        In fact, however, key advisers to Clinton knew me from way back, and the memories were not friendly.
        Immediately after the election, Robert Reich -- the same policy entrepreneur I had attacked in 1983 -- was named
        head of the economic transition team. And to my dismay, it quickly became clear not only that I would be
        excluded from influence, which didn't bother me too much, but that the Clinton Administration was going to
        systematically prefer policy entrepreneurs to real experts. In particular, it became apparent that the dominant
        ideology of the new administration would be what I call "pop internationalism", a foolish analogy between
        international trade and corporate competition. And because no first-rate economists would or could accept this
        doctrine, the key positions were filled by second-rate people.

        I did not take this development gracefully. I said what I thought, in letters and interviews. And of course the
        press -- as always deferring to a new President, and impressed by his articulateness -- ridiculed my complaints,
        ascribing them to sour grapes over not having received an appointment myself. A few months later everyone was
        complaining about the quality of the new Administration's personnel, but there is no memory in these matters; I
        was more or less disgraced, and my public profile was and still is much lower than at its peak.

        This story may not be over. I have another plain-English book in the works, and do not plan to stay out of public
        controversies forever. But I do not expect or want to have the kind of fever-pitch political involvement I had in
        1992 again. I was able to face the unpleasantness of how my venture into politics turned out with considerable
        equanimity, for two reasons. One was that my personal life had taken a turn for the better. The other was that I
        had once again gotten hold of a grand research project that I found inspiring and absorbing.

        7. Back to the vision

        There is a rhythm in my professional interests. When I have been concentrating on academic research for several
        years, I tend to get a bit bored and want to get involved in policy; when I have done policy for a while, I start to
        have the itch to do real research again. (I get tired of policy much more quickly than I get tired of research).
        True to this rhythm, soon after I finished Diminished Expectations I was anxious to do some real thinking again. I
        found the clue to a new project when Michael Porter, the business strategist, sent me a manuscript of his
        forthcoming book The Competitive Advantage of Nations. It's a mammoth book, and I never did read it all, but I
        was very taken with his emphasis on the role of regional industrial clusters in international competition. Soon I
        started thinking about trying to develop models of economic geography. I started with complicated ideas, then
        gradually boiled them down. I distinctly recall filling many sheets of scrap paper during a sleepless night at the
        faculty club at the University of British Columbia, and calculating many numerical examples in a hotel room in
        Hawaii. After a few months I had a basic model ready to submit for publication; by the fall of 1990 I was ready
        to give a set of lectures on the subject, Geography and Trade, which has become another cult classic.

        Economic geography has turned out to be a richer research vein than the subjects I mined in the late 1980s; I
        have written six serious papers on the subject already, and do not feel that I am close to exhausting its potential.
        I have also engaged in a systematic process of proselytizing on its behalf; my intention is to establish economic
        geography as a branch of economics that is taken as seriously as international trade, and I believe that I will
        succeed in that plan.

        Coming up with a good idea, with an insight into the way the world works that is really new and that you really
        believe in, is a deeply satisfying experience. The only thing that is even more satisfying is when one idea leads
        on to another, when you find yourself making a whole series of related discoveries. When that happens, never
        mind if you are a shy and mild-mannered professor: you feel like some archetypal hero on a mythic quest. I count
        myself very lucky to have had that feeling even once, during the development of the new trade theory. It is little
        short of a miracle that I have been able to experience it a second time, as the new economic geography has taken
        shape.

        What makes it even more satisfying is the relationship between the two quests. Economic geography, like the new
        trade theory, is largely about increasing returns and multiple equilibria. The technical tricks needed to make the
        models tractable are often the same. There is a difference in emphasis -- the trade models were largely focussed
        on internal economies of scale, while geography is largely about external economies -- and in policy relevance.
        Nonetheless, it is clear that the two lines of research are in some sense part of a larger project. So I have the
        satisfaction of being able to feel that I have done more than written two dozen or so clever papers: I have been
        engaged in some kind of cumulative enterprise. In the remainder of this paper I will try to explain what I think
        the nature of that enterprise has been -- that is, to justify myself as an economist.

        8. What have I been up to?

        Anyone who does creative work must, of necessity, be something of a sleepwalker, because future creative work
        is by its nature unpredictable. You can't know what you're going to do over the next few years, because if you did
        you would in effect already have done it. It's only when you look back that you can see the shape, grasp the
        pattern. The pattern in my own work has two main aspects. One is its substance, the core set of ideas that have
        informed many of the papers worth remembering. The other is its style -- a distinctive way of approaching
        problems that is closely linked to the substance.

        Substance

        As the narrative above makes clear, I have worked and written on a lot of topics. It is, however, the idea of
        increasing returns that has been the most important theme in my work. And it is my work in helping to clarify the
        role that increasing returns plays in economics that is the main excuse I have for my existence. The idea of
        increasing returns is, of course, a very old one, going back at least to Adam Smith. Nonetheless, until the 1980s
        economics was heavily dominated by what we may call the Ricardian Simplification: the assumption of constant
        returns and perfect competition.

        There is no mystery or shame involved in that domination: strategic simplification is the essence of all
        understanding except in the most fundamental physics. The constant returns-competitive model offers a
        remarkable if somewhat incomplete view of how the world works; in terms of economic policy, 95 percent of the
        time it would be a blessing if politicians could understand what's right about the constant returns model, not
        what's wrong with it. Nonetheless, the world isn't really characterized by constant returns, and it was essential to
        go beyond the Ricardian Simplification, if only to be able to say to the policymakers that we had explored that
        terrain and found little of use.

        If one admits increasing returns into one's economic model, two other consequences follow. First, increasing
        returns are intimately bound up with the possibility of multiple equilibria. There can be multiple equilibria in
        constant-returns models, too, but they are rarely either plausible or interesting. By contrast, it is very easy to be
        persuaded of both the relevance and importance of multiple equilibria due to increasing returns. What technology
        will be chosen for high-definition television? Which city will be Europe's financial center? These are real and
        interesting questions. Second, once there are interesting multiple equilibria, you need a story about how the
        economy picks one. The natural stories involve dynamics -- the cumulation of initial advantages that may be
        accidents of history.

        Speaking loosely, then, traditional economic analysis has -- for very good reasons -- focussed largely on static
        models in which equilibrium is uniquely determined by tastes, technology and factor endowments. An economic
        analysis that takes increasing returns seriously will normally involve dynamic models in which the choice of
        equilibrium also reflects history.

        All of this is fairly obvious, and indeed the history of thought in economics is littered with manifestos on the
        need to take into account increasing returns, multiple equilibria, dynamics, and the role of history. Nicholas
        Kaldor, for example, delivered strident attacks on constant-returns economics in the late 1960s; Thomas Schelling
        offered elegant little parables about dynamics and multiple equilibria in a series of papers during the 1970s.
        Nonetheless, it wasn't until the 1980s that increasing returns really got into the mainstream of economics. I
        wasn't the only one in the movement: Paul Romer, in particular, wrote several papers I wish I had written (I can
        think of no higher praise!) applying increasing returns to economic growth. But I think it's fair to say that my
        work first on trade and then on geography did as much as anyone's to really put increasing returns on the
        professional map.

        In the new trade theory, the basic point was that increasing returns are a motive for specialization and trade over
        and above conventional comparative advantage, and can indeed cause trade even where comparative advantage is
        of negligible importance -- for example, among industrial countries with similar resources and technology. The
        pattern of specialization and trade caused by increasing returns is, however, somewhat arbitrary; one must appeal
        to historical accident to explain who produces what. This seems pretty obvious, yet until the new trade theorists
        got going it was not part of mainstream thinking. It is a fact of life that trained economists find it very difficult
        to see the obvious unless it has been encapsulated in a clear formal model. (That's not an attack on the enterprise
        of modeling: those who believe that by engaging in fuzzy thinking they can widen their horizons almost always
        see even less). The few existing models of trade under increasing returns were somehow too awkward to be
        persuasive. My own view is that the problem was largely one of style, something I'll turn to shortly, and that my
        big contribution was to break through an intellectual style barrier. Whatever the reason, before 1980 the potential
        role of increasing returns in international trade was virtually ignored by economists; by 1987 or so it had become
        part of the standard story. That's a pretty big intellectual shift, and I think it's fair to claim that Elhanan Helpman
        and I deserve most of the credit.

        In the area of economic geography, the basic point is that the economic landscape is covered with examples of
        agglomeration -- geographical concentrations of population and activity in general, like Los Angeles,
        concentration of particular types of business like Silicon Valley. These agglomerations are rarely explainable by
        special inherent resources of the site; they are, rather, examples of increasing returns at work. And the role of
        history in their formation is obvious: there has been no important commercial traffic on the Erie Canal since
        1850, yet the head start that canal gave to New York City has allowed New York to remain the largest US city to
        this day. Again, all of this is obvious. And yet the apparent difficulty in modeling the increasing-returns nature of
        agglomeration had excluded this obvious story from the economic mainstream. Even today, the new economic
        principles textbook by Joseph Stiglitz contains exactly one reference to cities in its 1200 pages -- a brief
        discussion of rural-urban migration in the Third World! I'm pretty sure this will change.

        The geography models I have been writing since 1990 have inspired a growing number of followers, including a
        growing body of empirical work. It's a reasonable prediction that ten years from now the new economic geography
        will be as firmly established as the new trade theory. If so, I will have succeeded in bringing a quite large chunk
        of increasing-returns-based analysis into the heart of mainstream economics. That, I think, is my main
        achievement. What has made it possible, however, is not so much special insight -- both in trade and in geography
        it is possible to point to many people who have expressed similar ideas -- as style. Indeed, I regard the
        intellectual style I have developed as central to the whole enterprise.

        Style

        Robert Solow used to tell his students that there were two kinds of theorists: those who like to generalize, and
        those who like to look for illuminating special cases. I fall very strongly into the latter camp. Indeed, I have
        elevated the creation of special cases into a sort of personal art form. In constant-returns models, it is often
        possible once you have made the big untrue assumptions up front to derive results of considerable generality. For
        example, the Heckscher-Ohlin-Samuelson model does not depend on any assumptions about the degree of
        substitutability between capital and labor. You may want to look at, say, a Leontief or a Cobb-Douglas technology
        as an interesting example, but you don't have to. In increasing-returns models, by contrast, there are very few
        general results. Even with two goods, two countries, and one factor of production one easily bogs down in a
        complex taxonomy. So what do you do?

        My answer has been to rely heavily on those suggestive special cases. The process works like this: start with an
        informal verbal story, often one drawn from casual empiricism or from non-mainstream economic literature. Then
        try to build the simplest possible model that will illustrate that story. In the course of the model-building the
        story tends to change along with your intuition, but at the end of the process you have a simple model that is a
        very special case, but that makes a lot of intuitive sense and effectively gives you a language to discuss things
        that previously were off limits. The intuition can then also serve as the basis for empirical work, although to be
        honest I have never been a very persistent econometrician.

        How do you find special cases that work, that allow you to go where no modeler has gone before? Any way you
        can. At various times I have assumed particular functional forms; symmetry; two states of nature where you
        might expect to find a continuum, or a continuum of goods where the traditional models have two; and in some
        cases relied on numerical examples where pencil and paper fail. It's a sort of blitzkrieg approach to theory:
        instead of trying to advance on a broad front, one tries to get as far as possible along a narrow corridor of
        advance, taking advantage of any weak points you can find.

        This style is not, of course, original. For classic examples, consider some of the early work on growth and
        technical change, say Arrow's model of learning by doing or Solow's vintage capital model. In those papers all of
        the elements of the style are there: an intuitive story based on casual empiricism, embodied in a model that relies
        crucially on special functional forms to be tractable, yet which seems to offer important further insights. What I
        did was to apply the method repeatedly in the service of a cause I believed in, that of making economic theory
        safe for increasing returns.

        The style works for other things as well, however. The policy-inspired models I did in the late 1980s -- on
        sovereign debt, target zones, trading blocs, exchange rates -- followed the same approach. In these papers policy
        relevance and analytical elegance seemed to me, and to a fair number of other people, to be surprisingly natural
        allies: it turns out that a crisp, minimalist model may be just what is needed to clear out some of the nonsense in
        a policy discussion and get down to the real issues.

        One might also speculate that my relative success at writing economics in plain English has something to do with
        modeling style. After all, once you have accepted that models are metaphors rather than ultimate truth, and have
        schooled yourself to make the metaphors as simple as possible, it may be easier to find non-mathematical
        metaphors as well. Or to put it a different way: once you have stripped an idea down to its essence, it is often
        surprisingly possible to express that essence without any visible display of technique. In summary, then, whatever
        contribution I may have made to economics has involved both substance -- the integration of increasing returns
        into economics -- and style -- radical simplification as a modeling strategy. The style is essential to the
        substance but also has a life of its own, and has allowed me to make productive raids into a number of areas
        other than increasing returns.

        9. The point of it all

        Perhaps in the end the question one should ask of any scholar is what purpose he feels his work serves. I could
        claim great nobility of character and tell you that I work for the good of humanity. Or I could try to shock you
        and tell you that all I care about are the financial and professional rewards. Neither would be entirely false. I
        am, indeed, a bit of a romantic who believes, rather in the face of the evidence, that good ideas eventually
        prevail and make everyone's life better. I am also not an ascetic: I will not sneer at a nice honorarium or a free
        trip to a pleasant location.

        But the honest truth is that what drives me as an economist is that economics is fun. I think I understand why so
        many people think that economics is a boring subject, but they are wrong. On the contrary, there is hardly
        anything I know that is as exciting as finding that the great events that move history, the forces that determine
        the destiny of empires and the fate of kings, can sometimes be explained, predicted, or even controlled by a few
        symbols on a printed page. We all want power, we all want success, but the ultimate reward is the simple joy of
        understanding.