As part of our interview series, we ask renowned experts in the field for their advice for young researchers. For our second interview, we got the opportunity to talk to Mushfiq Mobarak himself!
Ahmed Mushfiq Mobarak is the Jerome Kasoff ’54 Professor of Management and Economics at Yale University with concurrent appointments in the School of Management and in the Department of Economics. Mobarak is the founder and faculty director of the Yale Research Initiative on Innovation and Scale (Y-RISE). Mushfiq has pioneered much of the literature in Development Economics through field experiments exploring ways to induce people in developing countries to adopt technologies or behaviors that are likely to be welfare-improving.
ETRM: How would you define development economics right now and where do you think the frontier is at currently?
MM: In the last 20 years development economics has moved heavily towards program evaluation and the use of randomized control trials to evaluate programs. But presumably we run those evaluations because we want to answer the question- “if this program were to become at-scale policy would it continue to have a positive effect on people’s lives?” Program evaluation is a useful input for that policy question, but it’s not the only thing we need to know. We need to think about what new changes occur as programs scale up to policy. And there’s a set of second generation questions that appear.
For example, the political economy complexities of scale up. When we’re running a program at a pilot scale, often the governments don’t notice or care. But if there’s a chance these become policy at some point, of course they’re going to react to it. This could be as simple as: “oh you’re providing that service to this population, so I’ll redirect my resources elsewhere”. Or it could be the opposite: you are providing skills training in place x, the policy maker might use industrial or trade policy to site factories to take advantage of the skilled workers in this location. In that case the original program effects might even be magnified at scale, given the complementary investments.
And if people like a particular program, politicians may try to associate themselves with it and that might muddle the information environment for voters. For example, it could become more difficult for voters to distinguish good politicians from strategic politicians. If the program thereby undermines political accountability, the political economy questions may turn out to be the biggest issues because politics may be the fundamental cause of underdevelopment in that area.
We’ll have these complications not only in the political economy sphere, but also in terms of general equilibrium changes. Any new program will interact with the pre-existing set of policies, and we’ll have complications with respect to what are the indirect effects on not just the program beneficiaries but all the people that they interact with in the labor market and food markets and informal insurance markets etc. So I think the frontier for development economics is really thinking through those complexities and using rigorous research methods to also generate evidence on those complexities.
ETRM: Do you think the emphasis right now is on RCTs? And should grad students going forward also make use of secondary data and or combine the two?
MM: I think the fact that we’re even asking that question, and framing that question in terms of methods is just not the right starting point. I don’t think methods should drive what questions we answer. You need to think about the fundamental causes of underdevelopment and figure out what the important questions are and only then figure out the research methods and datasets that will allow us to generate the highest possible quality answer, and the most rigorous possible answer to our question.
ETRM: What advice would you give to current grad students?
MM: Just like any other muscle, your research muscles also require exercise. The big piece of advice is that if you’re stuck, try to take a bite-sized piece of a problem. Don’t get stuck just reading for two years without actually trying out something on your own. Note that this is very practical advice, as opposed to me trying to give conceptual advice on what you should be working on. Another piece of practical advice is to not get too focused on methods like: “I need do a randomized control trial” or “I need to go and find administrative data”. Instead, let the importance of the question guide you.
ETRM: Finally, you’ve written a lot of papers, how do you get inspiration or where do you get your ideas?
MM: Many of the papers I’ve written in my life that I actually like the best including the agenda on seasonal deprivation that I just presented at Cornell, other papers on water pollution across jurisdictions in Brazil, or the effects of electrification – these were all ideas that had come to my mind in some vague form when I was around Middle School age in Bangladesh. Not that I knew anything about economics or identification strategies or research methods back then! To give you an example, in one paper I use the fact that you need certain Geographic topographic characteristics to generate hydropower, because that requires intercepting water at high velocity. That idea came to me because I was living in Chittagong in Bangladesh, near the only hilly area in our flat country. We were living through a really bad drought that summer (around 1989), and as a result we had a lot of “load shedding” or no access to electricity for maybe 16-17 hours of the day. That was a transformative experience for me because it was extremely unpleasant to be in a place that was like hundred-degree Fahrenheit weather with 100% humidity and no electricity. That’s when I was first exposed to the idea that when there’s a drought in any hilly area, we might lose access to electricity if you rely on hydropower. I implemented this insight two decades later in a research project in Brazil.
Related to my work on seasonal deprivation, this is what we grew up with, in that every year during that season there were newspaper articles about how bad that period of seasonal deprivation (‘Monga’) was. And then related to my work on trans-boundary river pollution and externalities- I wrote my 10th grade social studies paper on India building a dam on rivers that flow into Bangladesh upstream of the Bangladesh border, and this was one of the causes of the massive floods we experienced in the 1980s. So the upshot of all of that is that students should just go out and have experiences, and learn what’s important to people. That’s also something I advise my kids: travel, have experiences, think.
ETRM: So if you’re having a bad day, it may just be an idea for a paper!
MM: Haha, if you’re having a bad day, it’s better if a research idea comes out of it, than if it’s just a bad day and you have nothing to show for it!
