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.
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.
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.
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.