Jens Hainmueller joins the MPIPS as a Visiting Scholar
We are delighted to welcome Jens Hainmueller, Kimberly Glenn Professor and Professor of Political Science at Stanford University, who is joining the MPIPS as a visiting scholar for one year. Professor Hainmueller’s research brings together statistical methods, causal inference, migration and political economy. His work has made important contributions to the study of migration and integration as well as to the development of new approaches for empirical research. During his stay, Professor Hainmueller will engage with researchers at the Institute, contribute to our academic activities, and pursue his own research. We are very pleased to have him with us and warmly welcome him to our research community.
Jens Hainmueller, you grew up in Freiburg and studied at the University of Tübingen, Brown University, and the London School of Economics before completing your PhD at Harvard. You then held a faculty position at MIT before joining Stanford, where you are a professor of political science and co-direct the Immigration Policy Lab. Your research combines questions about immigration and integration with quantitative analysis and causal inference, and you have developed methods now widely used across the social sciences.
Today, you are among the most highly cited researchers of your generation. Your research spans immigration, citizenship, refugee resettlement, public attitudes and political behaviour, with an influence that extends well beyond academic debate into policy. We are delighted to have you with us in Göttingen this year as a visiting scholar, and grateful for the opportunity to talk with you about the questions, methods and ideas that have shaped your work.
We are living through a period of overlapping transformations, from migration and demographic change to technological change and political polarization. You work on a remarkably wide range of questions, often in close partnership with policymakers and practitioners. How do you decide which problems are worth pursuing?
I'd love to say there's a grand strategy. The truth is, I'm intellectually very curious, and they say novelty slows down time. So for me it's important to take on new questions from time to time, to stay fresh.
But there is some method to it. Broadly, my research falls into two groups, and I choose problems differently in each.
The first is methods research, where I develop new statistical tools. My approach there is simple. Every methods paper I've written came out of a problem I ran into while analyzing a real dataset, where the existing methods couldn't give me the answer I needed. When that happens, I ask whether other researchers are likely to run into the same problem. If they are, it's worth solving properly. I learned this from one of my mentors, Don Rubin, who always said that the best methods papers come out of real research problems with real data.
The second group is substantive research, often done together with policymakers and practitioners. There I ask three questions. Does the answer matter scientifically, beyond one specific setting? Does it matter to people making real decisions, or to the people affected by those decisions? And can we answer it credibly, rather than just tell a plausible story?
It's surprisingly hard to meet all three. The projects I'm proudest of are the rare ones that do.
In your teaching, you tell researchers to start by imagining the ideal experiment they would run, and then work backwards to find a feasible way of pinning down the effect. You have used that approach to tackle some of the most difficult questions in migration and integration. Are there questions you would like to answer now that you still do not see a convincing way to study?
Well, many of the most fundamental questions in life can't be answered by science at all. What is the purpose of life? What is love? I wouldn't want to randomize those to find a scientific answer.
But within my own field, yes, plenty. To explain why, it helps to say what most of my work is really about. It's about counterfactuals, things we can't observe. What would have happened if a government had chosen a different policy?
In the best case, we can answer that rigorously with a randomized experiment. One group gets the policy and a control group doesn't, and the control group shows us, without ambiguity, what would have happened without it.
But the bigger the counterfactual we ask about, the further we move from the data we actually observe. And the further we move, the bigger the assumptions we have to make about what would have happened otherwise. At some point it becomes more guesswork than science.
So I like to ask questions that are big enough to be interesting, but not so big that scientific evidence can no longer answer them.
And it's sometimes tricky to know where that line is. I recently served on a National Academies of Sciences panel on global forced migration and refugee resettlement and integration. We had many of these debates: what can the evidence actually support, what conclusions can we draw, and what remains more speculative? I think drawing that line carefully is an important responsibility for a scientist.
In your New York citizenship experiment, you found that people who became citizens tended to have better economic outcomes, but that this difference disappeared when you used the randomized experiment to isolate the effect of citizenship itself. Still, the earlier findings were plausible, statistically significant and influential. Is there a point where you have the confidence that a finding is telling you what we think it is telling you?
Never completely, and I think that's the right attitude. But let me give a concrete answer, because David Laitin and I just published a study on exactly this in the Proceedings of the National Academy of Sciences.
We collected every study we could find on whether citizenship raises immigrants' earnings: 60 estimates from 31 studies, over four decades. If you simply average them, citizenship appears to raise earnings by about 10 percent. That's the number that has shaped policy thinking.
But then we sorted the studies by how they try to separate the effect of citizenship from the fact that people who naturalize are different to begin with. And the method turned out to explain more of the variation in results than the country, the citizenship rules, or anything else. The randomized fee-waiver lottery in New York gives an effect close to zero. Some observational approaches give effects of 50 percent. Same question, very different answers, depending on the design.
The part that worried me most came from the New York data itself. When we set the lottery aside and analyzed those same people with a standard observational method, we got a gain of about 10 percent. And the usual checks researchers run to detect bias didn't flag anything. So a result can be plausible, statistically significant, and pass the standard tests, and still be wrong.
Science depends on what Robert Merton called "organized skepticism." We don't take anyone's word for it, and we don't judge a claim purely on how plausible it sounds. We need actual, reliable evidence. So when do I have confidence? Not when a result is significant, and not when many studies agree, if they all share the same weakness. As the political scientist Karl Deutsch put it, truth lies at the confluence of independent streams of evidence. I gain confidence when designs with different weaknesses point to the same answer, and when the most credible design agrees with the rest.
On citizenship we have made a lot of progress, but we're not quite there yet. It may well matter in some settings. But we shouldn't treat the average as a forecast of what a policy will deliver.
Hainmueller, J. & Laitin, D. D. (2026). "The economic returns to citizenship: Evidence from a meta-analysis." Proceedings of the National Academy of Sciences.
You are spending a full year at the MPIPS. What are you hoping to explore during your time here, and how are you enjoying your time at the Institute and in Göttingen so far?
Right now, I'm very focused on writing up several studies that are in their final stages. One is a paper on a new method for studying how people make trade-offs in complex survey experiments, where respondents evaluate options with many different features. I'm also finishing papers that examine the impacts of private hosting on the integration of Ukrainian refugees, using detailed register data.
What is valuable about being here is the combination of quiet time, intellectual breadth, and the chance to interact with the great researchers at MPIPS and the Max Planck Society more broadly. It gives me space to finish ongoing work, but also to think about what the next decade of research should look like.
And I'm having a great time in Göttingen so far. The city is steeped in history, and I'm trying to soak it all up. I recently got to visit the observatory of one of my scientific heroes, Carl Friedrich Gauss. Walking through it, I kept wondering: would Gauss be thrilled to know that his method of least squares is still so dominant more than two hundred years later? Or would he wish we had moved on by now? I guess that counterfactual remains unobserved.
Thank you very much for taking the time to speak with us, Jens. We are delighted to have you at the MPIPS and look forward to the ideas, conversations, and collaborations that will grow from your time here.
Interview by Chris Kofri, MPIPS, October 2026
Learn more about Jens Hainmueller and his research here:
Jens Hainmueller at Stanford University