As part of our interview series, we ask renowned experts in the field for their advice for young researchers. We are starting off this series in-house with Prof. Chris Barrett!
Chris Barrett is Stephen B. and Janice G. Ashley Professor of Applied Economics and Management, and an international professor of agriculture at the Charles H. Dyson School of Applied Economics and Management, as well as a professor in the Jeb E. Brooks School of Public Policy, and a Senior Faculty Fellow of the Cornell Atkinson Center for Sustainability, all at Cornell University. He is co-editor-in-chief of the journal Food Policy and edits the Palgrave Macmillan book series Agricultural Economics and Food Policy.
The Economics That Really Matters blog was developed by graduate students and staff in Chris’ research group in 2014.
ETRM: In your opinion, what is the definition of development economics at the frontier as it is right now?
Chris Barrett: Development economics is the study of how we improve the human condition. It’s pretty broad, so that necessarily encompasses poverty reduction and reducing food insecurity, reducing the incidence of conflict, improving women’s empowerment, improving productivity, and the functioning of markets, all of which go into improving the human condition. The common denominator is, we worry about improving the human condition for those who suffer relatively low living standards. So one could, I think, make the case that a lot of development economics could be applied to under-resourced and disadvantaged populations in high-income countries, like Native American populations in the United States, or the homeless population in the United States. Typically, those are a different literature, and there is not as much intersection between development economics and economists who work on those problems as might be optimal. But the vast majority of the variance and living standards around the world is determined by the country in which one lives, so defining development economics as in the economics of improving the human condition by focusing study on low and lower middle income countries, I think, is a reasonable start.
ETRM: What do you think is the future of agricultural economics? Should young researchers prioritize the intersection of it with climate change, for example, or should they focus on some other topics?
Chris Barrett: Agricultural economics will remain important so long as humans continue to want to eat. It’s that simple. We take it for granted, just like you take for granted the fact that you’re likely to be able to eat your dinner tonight, if you choose to eat dinner tonight, but that doesn’t make it unimportant. If anything, it’s becoming more important. As we’re starting to push up against planetary boundaries the challenge of sustainable agricultural production grows, and that raises a host of questions that cross the lines of virtually every subdiscipline within economics. There are environmental questions surrounding water and land management, even gene flow. There are health economics questions around not just obesity, but infectious disease management because agricultural development is the main source of introduction of zoonoses into humans. The agri-food value chain is the largest employer worldwide. So it’s central to understanding labor and labor market functioning around the world. It’s also a source of enormous amounts of technological change. Even though it slowed for a while it seems to be accelerating again now. So for those who are interested in the economics of productivity and productivity measurement, agriculture is important. The way in which the value chain functions from upstream concentration in seed and fertilizer companies, for example, through downstream concentration in supermarkets and fast-food chains has huge IO implications. At a time when economics became very theoretical, agricultural economists remained deeply committed to using data in ways that many other subfields of economics did not, and to using those data to inform public policy and the behavior of firms throughout the value chain in ways that other fields did not. So I very much believe agricultural economics remains relevant. I think its relevance is only expanding as time goes by and we start to realize that the problems are very complicated and poorly understood. And again, as long as we’d like to eat we’re going to need a functioning agrifood system.
ETRM: Yeah, that was a really good answer. And we do really like to eat, so I’m convinced! I’m asking more of a question on behalf of graduate students. What advice do you have for graduate students who want to be in academia or not?
Chris Barrett: Well, first figure out whether you like to teach or not so that you can sort between going on the academic track or not. The non-academic track basically trades teaching for some other sort of advisory service. If one goes to work for a CGIAR center or the World Bank or the IMF or a business one is going to wind up spending a lot of non-research time; it just won’t be teaching. It’ll be advising clients or advising operational folks, or any of a whole host of other activities. So there are very few pure research jobs because research is expensive. It’s a cost center for most organizations. So figure out what you like to do to complement your research. You get a Ph.D. because you want to do research. That’s how you want to have impact, and that’s what you’d like to spend some of your time doing for the rest of your professional career. But you’ve got to figure out what you like to complement it with. That’s one of the two most fundamental questions I think graduate students have to ask themselves. What do I like doing besides research? And then let me get good at that. So if you think you’d like to teach, you’d like to be an academic, then get yourself into the classroom. Get teaching assistantships; better yet get yourself a primary instructor role at some point to find out: am I actually good at this? Do I actually enjoy it?
The other big question you have to ask yourself is “what excites me in way of research such that I wake up in the morning and I want to think about this problem? I so want to know the correct answer that I’m willing to persevere through what will inevitably be very hard parts of any meaningful research project.” I’ve never been a part of a research project that didn’t hit some tough patches along the way. There are times when you can be tempted to give up if you’re not genuinely interested in learning the right answer. You can be tempted to cut corners. But you have to really make sure you genuinely want to know the correct answer, that you’re not just trying to get something published. There’s lots of work that’s publishable because they have cute or seemingly clever answers; but they are just noise. They aren’t meaningfully informative. Unfortunately, journals are full of noise, and that’s part of the scientific enterprise, sorting the noise from the signal, and advancing the signal, so that steadily, as a community, we learn more and more about things that really matter. We get more confident in the results others have come up with previously by replicating in some fashion their core findings. But that’s hard work to do right. So figure out what really excites you.
I get really excited about trying to figure out things that matter to help improve standards of living for very poor people. How can we make sure that moms can feed their kids? How can we make sure that a family that’s presently very poor isn’t condemned to being poor for very long periods of time, just by their circumstances? Those sorts of questions really motivate me. So I wake up wanting to figure out answers to those questions; it gets me very engaged.
I think the most the most dangerous choice graduate students make is trying to follow a fashion to do what they think will sell. First of all, it’s very hard to predict what will sell even near term, much less several years down the road. And you’re playing a long game when you start your dissertation research. It’s very hard to predict what will be in fashion 3 or 4 years from now, when your papers are really ready to publish. But also because the quality of your work is a function of how passionate are you about it, not how passionate other people are about it! I’m a firm believer that the quality of one’s work ultimately drives how well one does with it.
When I came out of my PhD program in 1994 at the University of Wisconsin, Madison, development economics was thought of as kind of a dead field. Many people believe that there was just sort of one set of economics, and it applied everywhere. So why did you need a specialized type of economics for the low income world? But as Joe Stiglitz famously put it, development economics is to economics as pathology is to medicine: if you really want to understand how the human body functions, you need to study the pathological cases, you need to understand where things clearly aren’t working right in order to provide good medical care to people who are healthy right now. One can push that metaphor too far, but I think basic point he was making is exactly right that there are clearly systemic things wrong in very poor communities, and identifying and isolating those mechanisms, identifying what interventions can help to relax the constraints that hold people back systemically in those places, is really the task of development economics. And it has informed the broader discipline quite well. Pranab Bardhan had a wonderful paper on this many years ago, on what economics has learned from development economics. This was part of his vibrant defense of development economics as a field that many people thought was about to fade away. Well, lo and behold! 30 years later, development economics is an ascendant field, very prominent in the leading economics departments all over the world, with a bunch of Nobel prizes over the last 15 years. But it’s a very different field today than it was 30 years ago when I was a graduate student. Agricultural economics likewise was seen as a fading field back then. So I was fortunate my two main fields recovered robustly, and I have had the good fortune to be able to ride along with that.
But even if those fields hadn’t rebounded at the discipline’s scale, I’ve spent a lot of time working with people in other disciplines because the problems that motivate agricultural and development economics research give you far more entry points to work with other scientists – non-economists – than most fields of economics do. Environmental economics is very similar. There are lots of opportunities to work with other scientists. The marginal returns to a day spent with a non-economist is much higher than the marginal return to a day spent with an economist, in my experience. Other economists and I know a lot of the same stuff; but when I’m with a soil scientist or a hydrologist, or a nutritionist, or a parasitologist, I’m just learning at an incredible rate. And sometimes they are, too! Together you can make some real advances by working across those boundaries, if you’re willing to take the time and the risk. Real problems in the world don’t respect disciplinary boundaries. So this comes back to my earlier point about focusing on issues you’re passionate about. If you do that, you will often find yourself pulled into conversations with other fields that won’t necessarily be rewarded by your own discipline. You have to acknowledge and accept that, and be prepared to do it anyway. I have found it immensely rewarding. It’s never delivered a ‘top five’ article but it has been central to having some real-world impact through my research.
ETRM: Thank you so much. A quick follow-up: What would you recommend graduate students to do in terms of finding a niche, and specializing in that topic versus keeping their research agenda on the broader side?
Chris Barrett: So there are there are two different things you need to pay attention to at the same time. One is, for better or worse, the research community, both academic and non-academic, operates on publications as currency. So you need to develop publishable material. In economics, that’s typically journal articles, peer-reviewed journal articles. We typically don’t reward very much, at least certainly not proportional-to-effort, books or book chapters. You have to be able to generate article-length, original manuscripts that are publishable in decent journals. So that’s constraint one. If you fail to do that, then you’re not generating what is valuable to the profession. So anything you write, you should ensure it’s likely to be publishable. If you can anticipate ahead of time that this document isn’t going to be publishable, then don’t pursue it unless you’re obliged to do it – for example, producing a code book for the data set you’re developing is a necessary thing to build on, but it’s not going to be publishable. That’s the exception to the rule. So the first thing to keep in mind is, you need to generate peer-reviewed publications just to be taken seriously as a researcher because peer-reviewed journal articles are the currency of value.
The second thing is that those individual publications have to add up to something. If this is just a listing on a CV, kind of a laundry list of opportunistic publications, then it doesn’t create much of an impact nor a very favorable reputation. Rather, you’re seen as an opportunist. Then you’re somebody with a toolkit who just goes and applies the toolkit to whatever happens to come along. You’re not a genuine expert in a field. You’re an expert on a tool. Or worse.
The advice I typically give junior faculty and graduate students about writing research statements for job applications or for their tenure or promotion review packets is this. Research is akin to doing a jigsaw puzzle. Somebody who reviews your CV sees what are akin to a bunch of jigsaw puzzle pieces, the articles listed on the CV. They look at them, and they can guess at how these fit together. They may have a hard time figuring out what some of the papers or pieces really are. Your task is to provide them with the picture that goes on the cover of the box of the jigsaw puzzle box. You need to help them understand how the individual pieces will ultimately fit together to create an attractive bigger picture. A good research statement guides the reader through how all of the individual pieces one sees on a CV interlock such that the research program whole is greater than the sum of its published papers parts.
My own research objective is extremely broad, you know, reducing unnecessary human suffering. So I work on food insecurity problems. I work on technology adoption for small farmers. I work on the functioning of agrifood value chains. I work on poverty, dynamics. I work on risk management and disaster response. To a lot of people, these individual papers or clusters of papers look like little clumps of puzzle that over time, have all started to move closer and closer together, to connect into a bigger picture that I’ve long had in my mind’s eye. Does that metaphor help?
ETRM: That was so helpful, thank you so much!
