In this piece, originally published in 2011 by the American Economic Association’s Committee on the Status of Women in the Economics Profession, Esther Duflo, co-recipient of the 2019 Nobel Memorial Prize in economics, reflects on her academic career.

Although today my research agenda is closely associated with randomized control trials (RCT) in development economics, the truth is that randomized trials did not start with me, and I did not start with randomized trials.

When I was a graduate student at MIT, Michael Kremer (who was then an assistant professor) was already engaged in what was to become the first of a new generation of RCT in development economics—the now-famous Kenya textbook study—and in another RCT with Abhijit Banerjee.

I saw both of them struggle as they learned the ropes the hard way, and although I found the approach incredibly promising, I did not think it was one I could take as a graduate student. In fact, at the end of my second year, I got two offers of a job for the summer: Michael offered me to work on a second RCT he was thinking of starting with a women’s group in Kenya, and Abhijit suggested I work with him on a survey of the software industry in India. I thought the software industry project was more likely to work out, so I went to India, and missed my first opportunity to work on an RCT. I had clearly not seen where the trend was going.

Kenya was that I felt that the RCT would likely absorb too much of my time and energy, leaving me little space to get started on my own research. I was very keen to develop a research agenda that would really be mine, in part to judge whether I was really cut out to do research. I was well prepared for the coursework at MIT, because the master’s degree I had completed in France was much more technical than what most American students go through before the Ph.D.

So that part had been easy. But I had experienced a brush with despair when trying to write a required term paper for the econometrics class. My first idea for a topic had been rather vague; I had run some regressions, but I was stuck when it came to interpreting what they meant. Two or three weeks before the paper was due, I decided that it could not possibly be a paper, and I had to either find an interpretation or change topic. For about a week, I could not do either and I was totally paralyzed. Finally, I decided to replicate a paper using a different data set. But that week had left a strong doubt in my mind that I could really do research for a living.

“I am always surprised by the fact that many young researchers do not seem to know why they are researching a particular topic, or, when they do know, seem to have picked it for the wrong reason.”

My older brother Colas—who is a professor of philosophy in France and, despite that, one of the most down to earth and practical persons I have ever met (at least in academia)—gave me two pieces of advice when I asked him how one goes about starting a career as an academic.

The first was, “write one page every day.” This was literally how he wrote his dissertation. He would mark the days off a calendar with a cross, so writing two pages on a given day would give him a respite for the next. He also allowed some borrowing. But the system meant that he would write on average 365 pages in a year, and hence a dissertation in two. (French philosophy dissertations are long!) Of course, the principle needs some adjustment when applied to economics, since the writing itself is not as important as the analytical work that precedes it. But the underlying principle is essential: slow and steady progress. Writing one page a day leaves plenty of time for preparation, primary research, or thinking about the overall plan for the book. But it gives a structure to enforce continuous progress. One does not create a research agenda by waiting endlessly till the Big Idea comes, but by starting to work on a topic, learning more about the topic (and neighboring ones in the process), and progressively connecting the dots. (Voltaire, my brother’s favorite philosopher, famously enjoins us in the conclusion of Candide, a book where he makes fun of aimless abstract reasoning, “Cultivate your garden.”)

The second thing Colas said was, “Write the book (or the article) that you would have liked to read, but you could not find.” This may sound fairly obvious, but I am always surprised by the fact that many young researchers do not seem to know why they are researching a particular topic, or, when they do know, seem to have picked it for the wrong reason. They just stumbled upon a data set and then searched for a question; they wanted to try out some particular technique and this seemed to be an appropriate setting to do so; or they discarded all the questions they thought of answering because these appeared to be too “small.” In general, this is a recipe for, at best, a very boring life, and at worst, disaster. You will soon discover (if you haven’t already) that working on your research is the reward for all the other things you have to do in life: writing referee reports, teaching and advising, serving on various committees, etc. So first and foremost, your research has to excite you enough for it to be a treat! And what better treat than reading a good article at the same time you’re working on it?

That said, I was extremely lucky to be handed, not just one or two articles that I would have liked to read but did not exist, but a whole collection of them. When I was in my second year in the Ph.D. program, John Strauss and Duncan Thomas started to circulate, in manuscript form, their review chapter on human resources economics for the Handbook of Development Economics.

This is a masterful survey of the literature on health, education, labor markets, and household behavior in development economics until about 1993. To a student trained in labor economics by Joshua Angrist and Stephen Pishke and in development economics by Abhijit Banerjee and Michael Kremer, it made two things very apparent: the questions could not be more important, and the answers were mostly unsatisfactory. Strauss and Thomas were very explicit about the limitations of the papers they were covering, but they had to deal with the material that was there.

For example, there were many papers regressing various outcomes (wages, fertility, children’s health) on people’s education. But while the literature in labor was full of attempts to correct for an “ability bias” that did not seem really present in rich countries, there was not a single paper doing this convincingly in the development literature, although the selection of who gets to go to school could, prima facie, be expected to be more severe in developing countries. There were very interesting papers showing that men and women seemed to be spending resources differently, but women who had more resources in their control were likely to live in different families, and this was not really dealt with.

This was fabulous; there seemed to be a whole field open in front of me. I just had to work my way through Strauss and Thomas’s review and identify important questions where it was possible to productively apply the methods I had just learned in labor economics (natural experiments, instrumental variables, etc.) to improve the answer. There was a lot of work to do, but it all seemed rather manageable: this was my “one page a day” agenda.

I was lucky again, because I was actually wrong in how easy the job was going to be, but I did not discover it till much later. I made a long list of questions to look at. I then started trying to make progress on the first one on the list, the “returns to education” question, and proceeded to look for a suitable instrument. I had decided, on a priori grounds, that the best instrument would be a policy that had exogenously reduced the cost of education for some people, and left it high for some (comparable) people. I had also decided that a top-down school construction program was probably a good place to start looking for such a policy, and I proceeded to search the MIT library’s collection of World Bank reports for a country that had had a big increase in school building at some recent point. I started with Indonesia. I had used Indonesian data for my (ill-fated) econometrics paper, so I had learned enough about Indonesians to know they were into large-scale policies. It turned out that they had indeed gone on a school-building spree in the 1970s, and they had done this very differentially in different regions.

This was perfect for my purpose. I traced the reference for the document that said where the schools were built. All that was needed was a trip to Indonesia to copy that book, and some money to get hold of a large data set that I knew existed. Someone at the World Bank who had some money lying around was kind enough to arrange the latter, and I took the trip in a detour from India, where I was researching the software industry. When I returned to MIT in the fall, I followed the one-page-aday principle (one regression a day) and by November the paper was written.

I found out later, of course, that research is usually much bumpier than that, and things don’t usually work out quite so simply. I also learned that the Indonesian case was unusual, and there is not a natural experiment for every question you want to ask. Governments haven’t always nicely implemented some large-scale policy in a way that makes it possible to look at its effects. There were still a number of these large-scale policies to look at, so at this point I could have decided to reverse the order of priorities, and search around for policies that could be evaluated. But I was too committed to my brother’s second principle, and to the list of questions that I had written out after reading Strauss and Thomas’s chapter, to which I had been continuing to add new ones in other domains. (What is the effect of microcredit on welfare? Why are people not using fertilizer even when it is very cheap?)

“What drives me remain simple questions: what makes poor people tick, what keeps them stuck, and how economic policy can help them.”

This is why RCT imposed itself as a very natural next step. With RCT, we do not need to wait for a government to implement a program in a sufficiently quirky way to try and answer our questions. All we need is a partner willing to work with us: it can be an NGO that is already implementing a similar program, willing to randomize its allocation in a new area; or it could be an organization open to try out something entirely new. This, of course, takes work.

Each experiment requires much more effort than it takes to download a data set. But the reward is that the substantial agenda, the real question, can now be main driving force behind the projects we choose.

Of course, I continue to exploit natural experiments when they present the key to questions I want to answer. But in the meantime, RCT gives me much more freedom to write the books that I would like to read, but are not written yet.

Because I rely mostly on RCT in my research, and because I have contributed, with Abhijit Banerjee and Rachel Glennerster, to setting up and nurturing the growth of the Abdul Latif Jameel Poverty Action Lab, RCT itself has started to be seen as my research agenda. But I am not an experimentalist or an econometrician: I love RCT, I am interested to push the method as far as it will go, and I am very happy to see it adopted widely and in new and interesting ways by many researchers. But what drives me remain simple questions: what makes poor people tick, what keeps them stuck, and how economic policy can help them. This is what helps me get out of bed, even when I am jetlagged and feeling quite sorry for myself.

Esther Duflo is the Abdul Latif Jameel Professor of Poverty Alleviation and Development Economics at the Massachusetts Institute of Technology. Together with Abhijit Banerjee of MIT and Michael Kremer of Harvard University, she is the recipient of the 2019 Nobel Memorial Prize in Economic Sciences. This text originally appeared in the winter 2011 issue of the American Economic Association’s Committee on the Status of Women in the Economics Profession (CSWEP).

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