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Interview with Dani Rodrik

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Dani Rodrik is the Rafiq Hariri Professor of International Political Economy at the John F. Kennedy School of Government, Harvard University. Among his latest publications is the book, The Globalization Paradox: Democracy and the Future of the World Economy. He has a weblog here, and syndicated columns here.  He recently answered the following questions for the WEA Newsletter:

1. How would you briefly state your perspective on economics?

I would say I am pretty conventional and mainstream on methods, but generally much more heterodox on policy conclusions.  I have never thought of neoclassical economics as a hindrance to an understanding of social and economic problems.  To the contrary, I think there are certain habits of mind that come with thinking about the world in mainstream economic terms that are quite useful: you need to state your ideas clearly, you need to ensure they are internally consistent, with clear assumptions and causal links, and you need to be rigorous in your use of empirical evidence. Now, this does not mean that neoclassical economics has all the answers or that it is all we need. Too often, people who work with mainstream economic tools lack the ambition to ask broad questions and the imagination to go outside the box they are used to working in. But that is true of all “normal science.” Truly great economists use neoclassical methods for leverage, to reach new heights of understanding, not to dumb down our understanding.  Economists such as George Akerlof, Paul Krugman, and Joe Stiglitz are some of the names that come to mind who exemplify this tradition.  Each of them has questioned conventional wisdom, but from within rather than from outside.

A typical complaint against mainstream economics is that it is too limiting in the conclusions it leads to. Mainstream economists are often seen as ideologues of the market economy. I would concede that most of my economist colleagues tend to view markets as inherently desirable and government intervention as inherently unwelcome.  But in reality what we teach our students in the classroom – the advanced students if not the undergraduates –and what we talk about in the seminar room are typically much more about the myriad ways in which markets fail.  I love an old quote from Carlos Diaz-Alejandro who once said something along the lines of “by now any graduate student can come up with any policy conclusion he desires by building appropriate assumptions into his model.” And that was some thirty years ago! We have plenty more models that generate unorthodox conclusions now.

One reaction I get when I say this is the following: “how can economics be useful if you have a model for every possible outcome?” Well, the world is complicated, and we understand it by simplifying it. A market behaves differently when there are many sellers than when there are a few. Even when there are a few sellers, the outcomes differ depending on the nature of strategic interactions among them. When we add imperfect information, we get even more possibilities. The best we can do is to understand the structure of behaviour in each one of these cases, and then have an empirical method that helps us apply the right model to the particular context we are interested in.  So we have “one economics, many recipes,” as the sub-title of one of my books puts it. Unlike the natural sciences, I think economics advances not by newer models superseding old ones, but through a richer set of models that shed ever-brighter light at the variety of social experience.

However, contemporary economics in North America has one great weakness, and that is the excessive focus on methods at the expense of breadth in terms of social and historical perspective. PhD programs now train applied mathematicians and statisticians rather than real economists. To become a true economist, you need to do all sorts of reading – from history, sociology, and political science among other disciplines – that you are never required to do as a graduate student. The best economists today find a way of filling this gap in their education. I consider myself very lucky that I was a political science major and did a master’s in public affairs (as it is called at Princeton) before I turned to economics. I say lucky, because some of my best work – by my judgement, at least – was stimulated by questions or arguments I encountered outside of neoclassical economics.

2. How does this compare to the mainstream?

As I said, where I tend to part company with many of my colleagues is with the policy conclusions I reach. Many of my colleagues think of me as excessively dirigiste, or perhaps anti-market. A colleague at Harvard’s Economics Department would greet me by saying “how is the revolution going?” every time he saw me.  A peculiar deformation of mainstream economics is the tendency to pooh-pooh the real-world relevance of all the theoretical reasons market fail and government intervention is desirable. This sometimes reaches comical proportions.  You get trade theorists who have built their entire careers on “anomalous” results who are at the same time the greatest defenders of free trade.  You get growth and development economists whose stock in trade are models with externalities of all kinds who are stern advocates of the Washington Consensus. When you question these policy conclusions, you typically get a lot of hand-waving. Well, the government is corrupt and in the pockets of rent-seekers.  It does not have enough information to undertake the right kinds of interventions anyhow. Somehow, the minds of these analytically sophisticated thinkers turn into mush when they are forced to take seriously the policy implications of their own models.

So ironically, I think my heterodox approach has stronger foundations in mainstream economic methods than the views of many of the mainstream economists themselves.

3. Do you think that a more pluralist approach might gain traction? What factors constrain and support such a development?

It depends on what you mean by pluralism. Pluralism on methods is much harder, and I will come back to it. Pluralism on policy is already a reality, even within the boundaries of the existing methods, as I indicated. There are healthy debates in the profession today on the minimum wage, fiscal policy, financial regulation, and many other areas too.  I think many critics of the economics profession overlook these differences, or view them as the exception rather than the rule. And there are certainly some areas, for example international trade, where economists’ views are much less diverse than public opinion in general. But economics today is not a discipline that is characterized by a whole lot of unanimity.

Now that doesn’t mean that Economics is a pluralist paradise. There are powerful forces having to do with the sociology of the profession and the socialization process that tend to push economists to think alike. Most economists start graduate school not having spent much time thinking about social problems or having studied much else besides math and economics.  The incentive and hierarchy systems tend to reward those with the technical skills rather than interesting questions or research agendas. An in-group versus out-group mentality develops rather early on that pits economists against other social scientists. All economists tend to imbue a set of values that tends to glorify the market and demonize public action.  What probably stands out with mainstream economists is their awe of the power of markets and their belief that the market logic will eventually vanquish whatever obstacle is placed on its path.

As a result, economists tend to look down on other social scientists, as those distant, less competent cousins who may ask interesting questions sometimes but never get the answers right. Or, if their answers are right, they are so not for the methodologically correct reasons.  Even economists who come from different intellectual traditions are typically treated as “not real economists” or “not serious economists.”

So the hurdles for the economists that want to depart from the conventional path are pretty high. Above all, they must play by the methodological rules of the profession.  That means using the language of mathematics, the standard optimizing, general-equilibrium frameworks, and the established econometric tools. They must pay their dues and demonstrate they remain card-carrying members in good standing.

For those who, like myself, find considerable value in these methodological predilections, these dues are worth paying. I find that these methods keep me intellectually honest; they are a way of convincing myself that I know what I am talking about.  My attachment to these methods has not been for instrumental reasons – that is, for acceptance within the mainstream (although it has presumably helped – my intellectual opponents cannot so easily dismiss me by saying “he is not a real economist…”). But I also understand those who find mainstream methods too constraining or unhelpful. I think they offer something of value too, in providing a critique from outside. I often find myself in agreement with those critics on substantive grounds, but find a lot to criticize in their work on methodological grounds.

The criticism of methodological uniformity in Economics can also be taken too far. Surely, the use of mathematical and statistical techniques is not a problem per se. Such techniques simply ensure our arguments are conceptually and empirically coherent. Yes, excessive focus on these techniques, or the use of math just for its own sake, are a problem – but a problem against which there is already a counter-movement from within. In the top journals of the profession, I would say most math-heavy papers are driven by substantive questions rather than methods-driven concerns.

And things change. The two most exciting developments in Economics in the last two decades are the behavioural and experimental revolutions.  The first of these has made a significant dent in the rationality postulate of neoclassical economics, while the latter has taken the profession in a profoundly empirical and policy-oriented direction. These are significant changes in how one does mainstream economics, and the fact that they have happened suggests there is room for methodological changes. Not plurality, perhaps, but some degree of evolution in methods. I am not necessarily a great fan of either of these methodological innovations, but they show the profession is able to adapt and change.  Note also that both sets of new methods came from outside Economics — psychology and medicine, respectively.  Young economists made these methods their own, and changed the discipline from within.

4. What lessons, if any, have been learned from your experiences challenging the conventional wisdom?

If you want to be successful as a scholar, you have one of two paths. Either you come up with a new technique or piece of evidence to shore up conventional wisdom. Or you challenge the conventional wisdom. The latter is a high risk, high return strategy. It is high risk for all the reasons I have mentioned previously. But it is high return because anything that has turned into conventional wisdom is almost by definition wrong, or at least, overstated.  So done right, challenging conventional wisdom is a successful research strategy that is bound to pay off. In my own case, every piece of conventional wisdom I challenged had already become a caricature of what sounds economics teaches us. I wasn’t doing anything more than reminding my colleagues about standard economic theory and empirics. It was like pushing on an open door. I wasn’t challenging the economics, but the sociology of the profession.

For example, when I first began to criticize the Washington Consensus, I thought I was doing the obvious. The simple rules-of-thumb around which the Consensus revolved had no counterpart in serious welfare economics. Neither were they empirically well supported, in view of East Asia’s experience with heterodox economic models. When you questioned supporters closely, you first got some very partial economic arguments as response, and then as a last resort some political hand-waving (e.g., “we need to get the government to stop doing such things, otherwise rent-seeking will be rife…”). My argument was that we should take economics (and political economy) more seriously than simply as rules of thumb. Economics teaches us to think in conditional terms: different remedies are required by different constraints.  That way of thinking naturally leads us to a contextual type of policy-making, a diagnostic approach rather than a blueprint, kitchen-sink approach.

Similarly, when I questioned some of the excessive claims on the benefits of globalization I was simply reminding the profession what economics teaches.  Take for example the relationship between the gains from trade and the distributive implications of trade.  To this day, there is a tendency in the profession to overstate the first while minimizing the second.  This makes globalization look a lot better: it’s all net gains and very little distributional costs.  Yet look at the basic models of trade theory and comparative advantage we teach in the classroom and you can see that the net gains and the magnitudes of redistribution are directly linked in most of these models. The larger the net gains, the larger the redistribution. After all, the gains in productive efficiency derive from structural change, which is a process that inherently creates gainers (expanding sectors and the factors employed therein) and losers (contracting sectors and the factors employed therein). It is nonsensical to argue that the gains are large while the amount of redistribution is small – at least in the context of the standard models.  Moreover, as trade becomes freer, the ratio of redistribution to net gains rises. Ultimately, trying to reap the last few dollars of efficiency gain comes at the “cost” of significant redistribution of income. Again, standard economics.

Saying all this doesn’t necessarily make you very popular right away. I remember well the reception I got when I presented my paper (with Francisco Rodriguez) on the empirics of trade policy and growth. The literature had filled up with extravagant claims about the effect of trade liberalization on economic growth. What we showed in our paper is that the research to date could not support those claims. Neither the theoretical nor empirical literature indicated there is a robust, predictable, and quantitatively large effect of trade liberalization on growth.  We were simply stating what any well-trained economist should have known. Nevertheless, the paper was highly controversial.  One of my Harvard colleagues asked me in the Q&A session: “why are you doing this?” It was a stunning question. It was as if knowledge of a certain kind was dangerous.

Years earlier, when I wrote my monograph Has Globalization Gone Too Far? I had been surprised at some of the reaction along similar lines. I expected of course that many policy advocates would be hostile. But my arguments were, or so I thought, based solidly on economic theory and reasoning. A distinguished economist wrote back saying “you are giving ammunition to the barbarians.” In other words, I had to exercise self-censorship lest my arguments were used by protectionists! The immediate qestion I had was why this economist thought barbarians were only on one side of the debate. Was he unaware of how, for example, multinational firms hijacked pro-free trade arguments to lobby for agreements – such as intellectual property – that had nothing to do with free trade? Why was it that the “barbarians” on one side of the issue were inherently more dangerous than the “barbarians” on the other side?

But ultimately, the reward of challenging conventional wisdom that has gone too far is that you are eventually proved right.  The Washington Consensus is essentially dead, replaced by a much more humble approach that recognizes the importance of locally binding constraints. And many of the arguments I made about the contingent nature of the benefits from trade and financial globalization are much closer to the intellectual mainstream today than they were at the time. I do not think of this as a great achievement. These changes were bound to happen, and I essentially rode the wave.

I suppose there is a lesson here for younger researchers: Identify an intellectual consensus that has gone beyond what the theory and empirics can support and chip away at it. But do so without departing too much from the discipline’s accepted methods!

From: Pp.9-12 of World Economics Association Newsletter 3(2), April 2013

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