An Interview With Martin Rotemberg
Martin Rotemberg is an economist at NYU. He studies the organization of firms, here and abroad.
Why did you choose to be an economist? How has being the son of an economist affected your career? Did you ever have any doubts about what you wanted to do?
My college majors were the caricature of a modern econ PhD student, which is to say econ and math. But I don’t think I did it strategically, I just enjoyed math classes (Williams, where I went, is fairly unique among modern colleges in that math is a very common major). After college, I went to work for Innovations for Poverty Action in Bolivia. It was a research job, though the reason why I searched for it was more “place where I can work abroad” as opposed to a sense that it would help me with graduate admissions. At IPA, at least at the time, there were two common paths from my entry-level position - some went the NGO/multilateral agency route, and some went academic. Now I think the job is called a “pre-doc” and the vibe is different and more academic.
It’s a great place to work (both the country and the organization). I highly recommend doing something similar if it's at all possible - I learned a lot, I feel like I was helpful in contributing to knowledge and improving people’s lives. Doing the job, I thought there were open questions where I could make some progress, and so I applied to PhD programs. At the time, there weren’t so many people with my kind of experiences in the applicant pile, so I think that made my application stand out a bit.
Having Julio1 for a dad has affected me in all sorts of ways, probably only some I recognize (since, obviously, I don’t actually know what it’s like to have a non-academic parent). Here is a small one: it was a great day when searching for myself on Google Scholar pulled up one of my papers, and not one of Julio’s where he thanks Martin Eichenbaum. More seriously, being a professional economist is a great job - there’s a reason why many economist’s children (academics in general, but particularly true in econ) follow in their parents footsteps. I did like my dad very much. He was also broadly liked in the profession. I always appreciate when people tell me stories of his interactions with them, or how much he inspired them. We aren’t in the same field - some of this is by my choice - but I do try to be kind and generous like him, especially since I have *always* wondered how much of my getting into Harvard was nepotism, and so I want to make sure that I live up to that privilege.
2. What’s your favorite paper (not your own)? When did you read it? What sort of effect did it have on you? And what would you say that all young economists simply must read?
In the spirit of the question, I won’t name a paper written by my friends/colleagues/students/blood relatives either, though of course those are my favorites. The academic writing that I most recommend to students is Nature’s Metropolis, by William Cronon, which I read in my last year of grad school after I finished the job market. It’s an amazing chronicle of the evolution of the American economy in the 19th century, centered around Chicago. It’s not an economics book per se, but it’s an amazing read. In addition to being generally an interesting time, the book shows how various changes are connected - a technological innovation over here leads to a market developing over there, which in turn creates new tasks and occupations, and encourages complementary innovations. Economics papers are by their nature narrow, but the economy is fundamentally not.
My dissertation was about Indian industrialization. A natural question is if performance there is disappointing or not - it wasn’t a manufacturing powerhouse at the time, but it was growing quickly (and still is). So is that good or bad? I wanted to read about a country that actually industrialized - how should we expect the process to actually work? Reading the book started me thinking about many of the questions that I work on now, even though I never took an economic history class.
I think young economists should read current job market papers (and go to job market talks). Job market candidates have spent years figuring out what the important open questions are, how to push the methodological frontier in order to answer them. And I think it’s very inspiring - in just a few short years, people in a similar position can produce the most amazing research, and you can do it too! (It’s also motivating as a faculty member, because I want to keep up). To give an example from my field (so that I name an actual paper in this response), I recommend Tishara Garg’s Can Industrial Policy Overcome Coordination Failures? Theory and Evidence. One of the most important questions in economics is if and how an industrial zone might increase activity. In addition to providing fundamental infrastructure that firms want, a classic answer is that it provides coordination - enterprises like being near other ones, so that they can share workers, inputs, knowledge, and so on. She collected comprehensive data on a massive number of industrial zones in India, and shows that their effect is consistent with multiple equilibria: many change very little, while others have large effects, with little in between. Models with multiple equilibria are considered horrible to work with, obviously, because who can say what equilibrium gets selected? She provides some identification and computational results, and shows that about a third of the total effect of the programs was switching equilibria. It’s an amazing project, and I’m looking forward to seeing how I can adapt her results to settings that I work on.
My other main advice to (applied) students is they have to go do stuff. Being an academic is great, but we can’t really learn about the world by just reading papers. We can’t write relevant papers by meditating in a cave until ideas come to us. It’s important to go to factories/archives/etc. to get a feel for what actually seems to be mattering on the ground.
3. What is your process for identifying something that you want to write about? How quickly do you know if an idea is good and should be pursued? Do you look for data first, and then ask questions, or do you ask questions and find data to answer it? Do you start writing immediately, or do it only at the end?
I got my job market paper idea from teaching. I wanted to cover a particular topic (how should policymakers allocate limited credit) and I couldn’t find any good material, so I went about trying to figure out how to make it. And in general that’s my process for figuring out if I want to work on a question: is there a class where this would be the kind of research that I would want to teach my students? For any reason - the data, the question, the method, etc. But it’s hard to triage ideas, and I’ve been excited about plenty of projects that I could never figure out how to convince other people to be excited about. I also invite my PhD students to present their work to my undergraduates, which I think is helpful to both sides. Sometimes it’s easy to get lost in the academic part of research, but actually the point is say things that are generally interesting.
I don’t always start with data, but I do analysis pretty early in the process: I want to make sure that the patterns I think should exist actually show up. I think quantitative theory is valuable, but I don’t want to get over my skis - I try to only include ingredients in the theory that I can actually measure and evaluate.
My goal is to give interesting & interactive presentations and circulate good & complete papers, so I try to present papers many times before writing. Otherwise, at least for me, it’s hard to know how to structure the results, and to figure out exactly what exhibits a paper needs.
4. What is your comparative advantage as an economist?
I’m going to give you a non-answer to this one too - I don’t think comparative advantage is a static thing. I’m constantly learning from conferences, students, seminars, lunches with colleagues, etc. The me starting out as an assistant professor could never have written the papers that I’m working on now.
5. Why is economic history important?
I don’t think there is only one answer to this question, so I’ll give you an answer about why I am excited about my particular papers. It is important to understand the forces underpinning growth, such as capital/infrastructure investment and the spread and development of new technologies. Studying the long-run implications of these large scale changes is relevant, since almost tautologically we don’t have long time frames to study contemporaneous economic changes.
And I’ve never written a paper like this, but I said it was my original motivation for studying economic history: I think there is value in directly comparing the past to modern economies, to provide benchmarks.
6. With Kim and White, you challenged the claims of misallocation made by Hsieh and Klenow, among others, in India. India’s statistical bureau does not “clean” their data, and this leads to errors and outliers in productivity. Bils, Klenow, and Ruane (2021) acknowledge the justice of the critique, but come to much smaller estimates of how much misallocation is due to mismeasurement. Are you convinced by their reply? What are your current opinions on the debate?
One beauty of Hsieh and Klenow’s paper on misallocation is how absolutely simple their measure is, and therefore how portable it is to a variety of datasets. I think everyone now agrees that you can’t just calculate their statistic and call it a day, but I’m not sure there is a consensus on what to do next. There are many interesting modern papers developing a variety of economic & statistical techniques to correct for measurement error
The other beauty of their result is it’s obviously correct. There are many factories in India who lose money every year, and it’s hard to explain how they exist just with market forces. This doesn’t happen in the US. It’s true that in the uncleaned enterprise data there appears to be more misallocation in the United States than in India (and, actually, also in the current cleaned data - it’s only in the past that simple measured allocative efficiency was higher in the US). But I think that’s a measurement problem.
Hang and Kirk and I have some new results that I think are fairly compelling, though the most results aren’t cleared yet. I think my teaser for the new draft is: the measurement of dispersion is crucial for answering a variety of important empirical economic questions, such as understanding the allocation of factors across enterprises and over time. I don’t think it’s only the misallocation literature that should be concerned about measurement. I should also emphasize that I don’t think that Bils, Klenow, and Ruane was a response to our project - we wrote our papers at more or less the same time.2
7. A recent paper of yours (on educational investment when child labor is available) uses a rainfall IV. What do you think about rainfall IVs generally? When are they appropriate to use? How does your paper avoid the pitfalls?
Rainfall affects many things, especially in poor agrarian societies. Output, of course, but also conflict or people’s moods or a variety of things (Jonathan Mellon has a nice graphic that maybe you’ve seen, here). The idea of our paper is that early life investment increases education because of dynamic complementarities (the more skilled you are, the easier you find school, and therefore the more school you go to), but conversely decreases education because of opportunity cost complementarities (more skilled kids are also more useful on the farm / helping out at home / etc.). To understand empirically which force is more important, our goal was to find something that shifted early life investments & skills, without otherwise affecting the school/work tradeoff.
I think in modern papers that use rainfall researchers are broadly careful. Good rainfall is good, and so can be used to understand the effects of good shocks (and similarly for bad shocks). I haven’t seen any recent papers that really interpret their results as rainfall mattering through only specific mechanism.
That is to say, we’re not formally using rainfall as an IV. That would require one causal pathway from rainfall to the thing we care about, which is early life investment and therefore human capital as an adolescent. For us, what matters is that rainfall does predict early life investment (probably mostly because of its effect on income), and our measures of pre-school skills, and that it doesn’t otherwise directly affect schooling choices (which I think is particularly plausible because we are comparing across ages within a place, so everyone is faced with the same shocks to the broader economy). But, for instance, one question we get asked is if we can split our results into the effects of cognitive and physical skills (e.g. brain vs. brawn). And for this project we can’t really answer it, because rainfall affects both.
8. What does economics need to do more of? Are there things it is doing too much of? Is the allocation of researcher attention optimal?
Industrial policy is back on the policy agenda worldwide, as a response to geopolitical and economic events. I don’t think that economics research all needs to be directly policy-relevant, but I do think that there is a large gap between the practice of economics research and what policymakers care about. Charlatans will always be happy to call themselves economists and give useless advice, and it’s a shame when they get the floor.
Julio Rotemberg was an economist at Harvard, who sadly died in 2017. He is best known for his work on New Keynesian models of the economy.
From talking to Prof. Klenow at the AEA conference, his personal view is that most of the measured misallocation is due to measurement error. I was erring in thinking that the papers were conflicting with each other.