Interview with the 2022 economic sciences laureate Douglas Diamond on 6 December 2022 during the Nobel Week in Stockholm, Sweden.

Where does your passion for economics come from? 

Douglas Diamond: I started in high school really liking physical science. I got interested in doing research from taking an advanced biology course in high school and went off to college planning to be a molecular biologist. I’d been interested in economics partly because I was interested in some history. I took a course in economics in my junior year in high school, which is highly unusual. It was called “Seminar on Capitalism” or something like that, and read a book by Milton Friedman called Capitalism and Freedom.  That’s where I first experienced economics. 

Then in my senior year in high school, I helped co-run this economic seminar that I took in my junior year. I read a textbook by Paul Samuelson, who was the second prize winner in economic sciences in memory of Alfred Nobel, and that was like an amazingly good textbook. I read that, but I had no thought of ever doing economics because I didn’t really know any economists. I got interested in science and research through biology. I went to college, Brown University, started to take some organic chemistry and some of these sciences. At least at a low level, a lot of memorisation was required. The science courses were less experimental than I was used to and memorisation is not my thing. So I actually dropped organic chemistry three weeks into the term at my freshman year, and then needed something that met at the same time. There was an intermediate microeconomics course that I took and it was an amazing, very advanced course, as it turned out. It didn’t have a prerequisite, but I already had this reading of the Paul Samuelson textbook, so I didn’t have to take the “what is economics” course.  

By that term I wasn’t thinking about being an economist, but I sort of liked the economics course. The second part of my freshman year, the second semester, there was a continuation of the course that was more mathematical economics taught by a mathematical economist. At that point I was thinking, “hey, this stuff is actually pretty interesting.” And I thought it was very easy. I learned that easy is good; there is this thing in economics called comparative advantage “you do what you’re relatively good at.” You may not be the smartest person, but you list the things you’re relatively good at and you should be in the one that you’re relatively best at. That’s how I sort of got into economics. Then it was sort of random what types of economics I was interested in for a while after that. 

What advice would you give to a student or young researcher? 

Douglas Diamond: If I wanted to give advice to someone just starting to think about going into research of some sort, any type of science, I would tell the students that there’s a great joy in understanding something that the world completely misunderstood in the past. The benefit of being a researcher is resolving a puzzle. If we want to get more people to go into doing research in the sciences, expressing to people what you actually do day to day, is important. The joy of understanding something that was confusing, that’s what motivates me. I think it motivates a lot of scientists. That would be my advice; to realise that that’s the whole point of this. It’s very easy to treat this as a regular job, where you just want to get a lot of people to cite your work. But you want to change people’s minds about things. That’s fun. You can’t always do it though. Sometimes you say ”yep, what people thought before, they’re exactly right. Okay, I’ll move on to another question.” 

Do you ever feel pressure knowing so many people have read, cited or built upon your work? 

Douglas Diamond: I think it’s safe to say when either of my highly cited papers, Diamond-Dybvig, which is the bank run model from 1983, or my Financial intermediation and delegated monitoring 1984, I didn’t even think about citations as something that mattered at that point, or something that would ever be measured. When I was writing the paper on my own, which was from my doctorate dissertation, or the paper with Philip Dybvig, we were basically thinking “okay, we want to try to explain what’s going on. It’d be nice if we could get this thing published”. We were thinking more about getting people to read it and getting it published than having it cited. Certainly, for the bank runs paper, we were hoping that policymakers read it. 

The paper got a lot of attention, but the number of citations in that paper, surprisingly, is like relatively constant year by year. It doesn’t tend to go up. It went up a little bit during the financial crisis of 2008, but basically it sort of keeps getting cited today at more or less the same rate it was cited 10 years after it was published. Normally papers that are huge hits get lots of their citations very fast, particularly in empirical work where people are trying to either refute it or extend it. Since ours was about trying to help people think about something I would not have guessed that this would’ve been a tremendously cited paper. We were actually pretty proud of that paper when we wrote it because it came out so clean. People that we presented it to, including my mentor Steve Ross, was clear to us that the paper was going to have a big impact. We probably thought it would’ve had 50 or 60 citations or something like that. It had a few more than that. 

What skills are important for students or researchers to develop? 

Douglas Diamond: I’d say the most important skill for a researcher is keeping an open mind about what the answer to a question might be. It’s very easy, particularly as you get more senior as a researcher, to have your mind focused on certain answers that you found in the past, and trying to look for either new data or new theories that are consistent with your old views. A lot of what we learned from research is overturning old ideas with either slightly better or very much better ideas. Trying to be open-minded about the way one does research and what the answers are, and not bringing your preconceived notions about the world or your political views and things like that, that’s probably the most important. 

Why do you think it’s important for students and researchers to approach and explain complicated subjects? 

Douglas Diamond: When writing a paper, as well as building the theory that the paper will ultimately be based on, I think about what the key feature that we want to try to understand here is. I tend to make it as simple and one feature at a time-analysis as possible. One reason why Phil and I tried to make our paper on bank runs relatively clean and simple, was that some of the audience someday might be central bankers and bank regulators and the public, as opposed to other economists. We made that paper relatively straightforward for that reason, for the audience reason. The second thing is that we originally thought about a somewhat more complicated model. Not that it was so difficult to solve, but that it had an unnecessary feature in it.  

The basic idea in the Diamond-Dybvig model is that the bank’s assets, like its loans, are illiquid. If you tried to sell them or liquidate them or get rid of them in a hurry before they matured, you would get a tiny fraction of what they’re worth. We originally started with an idea explaining why bank loans in particular were illiquid assets. It was some complicated story that the bank, to sort of commit a small fraud, would be having loans that were not likely going to be repaid, “bad loans”, and that instead of foreclosing on them, they’d roll them over and keep lending money to the firm to hide the fact that the loan was not going to be repaid. That by itself would make it illiquid because people are buying a used loan from a bank. It’s one of these bad ones that they’re just keeping around for fraudulent purposes.  

Then we realised that the main point that we had about borrowing short term and lending long term illiquid, was true for almost any reason that a loan was illiquid. Putting in a particular reason why the loan was illiquid was counterproductive. If we want to make the point, generality and simplicity went together, for whatever reason the bank loan is illiquid. There are lots of reasons you couldn’t sell it for what it’s worth. 

If that was true, the bank would be subject to a run and subject to a run for good reasons. Because you’d like to issue short-term debt against long-term illiquid loans for the purpose when there’s not a run, you create an asset that’s more liquid than other assets out there. On the other hand, if you’re doing that, if you’re creating this liquid asset, and if everybody thinks that everybody else is going to withdraw, that is a self-fulfilling prophecy. 

Was there a person who influenced you? 

Douglas Diamond: Steve Ross was definitely a mentor and role model to me and to all of his students. All of Steve Ross’s students set up this foundation called the Foundation for Advancement of Research and Financial Economics. We all donated money to it, fairly significant amounts of money, so it could set up something called the Steve Ross Prize. We all contributed to a volume explaining what a great mentor Steve Ross was. Steve Ross was a person who was particularly gifted at helping individuals figure out what they were good at. He didn’t produce lots of little Steve Rosses. He produced lots of people who do various, different things. Without Steve, I don’t think I would’ve succeeded in learning how to build simple models that had new ideas to them, but at the same time were quite applied. Doing what’s applied theory, which sounds like a contradiction in terms, is an art. Steve was very good at teaching people how to do that art. He was a very encouraging, strong advocate for all of his students. Even if we were all feeling awful about our work, he would point out the one good part of it and we could focus on that one good part. He’s probably the biggest influence.  

My other advisors, James Tobin and Martin Shubik, were my advisors for the whole time. But Steve Ross appeared in year three of my PhD. In the years one and two, I actually got my interests in banking and finance cemented. Both James Tobin who was a Nobel Prize winning macro economist and Martin Shubik, who was a game theorist, micro economist, were both very clear that the financial system wasn’t well integrated into the rest of economics. From them, I sort of learned where the holes were in economic theory and they had their own ideas on how to fill those holes. I had different ideas, but learning where the holes are, that’s invaluable when you’re trying to figure out what to do research on. They were also very strong mentors, but I think I’d probably still be in graduate school trying to finish my thesis if it wasn’t for Steve Ross. 

How do you cope with failure? 

Douglas Diamond: The older I get, the easier it is to push forward when something doesn’t work. In my own personal experience, most times when something doesn’t work, if I just keep working on it, eventually it does. Maybe fewer than 20% of the projects that I started ended up nowhere with just having to go into the trash. But more often than not, the project starts out as trying to understand or build a model of some phenomenon. Then I build a model – sometimes with co-authors, sometimes by myself – of the thing I was trying to build a model of. Sometimes it doesn’t quite deliver what I expected. Often what I can do is figure out what this model I just built is a model of and say “well, that’s the answer to some other question”. 

Other times I’ll change the model a little bit to make it go back to what I was originally trying to get at. I’ve learned two things. One, the second model is the model of what I wanted. The second thing I learned is, if you just change these assumptions from where I started to where I finish, I got a totally different economic outcome. Sometimes just the change in the assumptions to the change in the outcome is informative in itself. Former Nobel Prize winner Bengt Holmström has a name for this called “a conversation with the model.” Normally you think you learn in the world from putting the model, taking it to data and seeing what the data tell you. But it turns out that if you know something about the world already and you’re good at looking at models, you can sometimes learn from a model. 

Sometimes learning about that mapping from assumptions and conclusions is interesting and informative in and of itself. That’s been true on multiple occasions. As a result, I haven’t had to trash too many projects. Most of the projects I’ve trashed, is once I actually finished the model. I realised that it was just a model of something I already knew. I said “okay, I produced something that isn’t original”. Who wants to do unoriginal research? 

What are the key implications of your research? 

Douglas Diamond: My research is in a few areas. The main area, and the area that the prize committee highlighted, is on thinking about what banks do in the economy. Why do they do it? Why do they provide some good or bad elements to the economy? And what are the implications for things, like financial crises or the proper allocation of capital across firms or access to liquidity for people? There’s sort of several types of implications. One type of implication is for just understanding if something goes wrong in the financial system. Why the contracts that people write – that sometimes have bad outcomes, like a financial crisis or a bank or something – why they wrote those contracts in the first place.  

A lot of the questions that I ask are “why” questions? Why do we do it this way as opposed to that way? Why don’t we do it this other way? “Why” questions sound like they’re very unapplied.  We want to know how much to do it, or what to do, rather than why we do it. But for novel experiences, like a financial crisis or a new type of financial institution or a huge change in the economy because of like a war, knowing why certain things are done or are not done, turns out to be somewhat important.  

Phil Dybvig and I did research on bank runs, and the question we ask is, why do banks or other financial institutions that are similar to banks, write contracts which leave them subject to a run or panic, where everybody’s rushing to get their money out because other people are rushing to get their money out. 

That means the banks that are perfectly healthy can be going out of business just because fear of fear itself, or a panic stepped in. If you’re a policymaker, you need to know why a panic is occurring and what you can do to help resolve it, if you hadn’t fixed it in advance by like deposit insurance or something. In addition, I say the most useful thing that came out of the research that Phil and I did was to make very clear that bank runs aren’t just about banks. They’re not about how much currency you have in the vault, like they say in the movie It’s a Wonderful Life. It’s not about money in the vault. That certainly is a problem, but it’s about issuing short-term debt to finance long-term illiquid businesses or loans. It could be Lehman Brothers, it could be a cryptocurrency exchange, it could be stable coins, things like that. The key thing is that this problem of runs and crises, which are self-fulfilling problems, could be in many parts of the economy. 

What made you think that there was more to uncover with bank runs? 

Douglas Diamond: There’s an interesting question about deposit insurance and whether once we have deposit insurance, do we no longer have to worry about financial crises? An interesting implication of the work that I did with Phil Dybvig is that it’s about short term debt and not about being a bank. If you are Lehman Brothers or you are a securitisation, where you put a bunch of loans or mortgages into a pool, and then issue claims against them, something called asset backed commercial paper, which is short term debt on a securitisation. Once you see that these things that are not banks can have runs, then you can’t rest as easy, saying ”oh, we have deposit insurance on the banks so the banks won’t have runs.” Well then maybe the banks won’t have runs based on deposit insurance, but you’ll have the runs elsewhere. 

The activity of creating liquidity – borrowing short term to finance long term – migrates out of the regulated sector. People knew there were bank runs, so did we, that’s the history we were trying to explain. People understood that if you didn’t keep enough currency in the vault, that a bank could be fractional reserves; if you didn’t have enough currency in the vault, there could be a bank run. But no one had really thought about “why do we write these contracts that are subject to runs? If it’s not currency in the vault, what is it”?  

Deposit insurance is a good thing to protect part of the financial sector, but it can’t protect the whole thing. I think I mentioned before a lot of the work that I do is why something happens. It’s important to reevaluate why something happens, because maybe it was done in the past for a good reason. But if things change over time in the economy or the laws or the climate, if the why reason is no longer valid, you’ve got to make sure that laws and regulations or regulators that sort of prop up a particular part of the financial system or any part of the economy, is not obsolete.  If the why is no longer relevant, it’s important to know that. 

You’ve said that you don’t like to work on the hot topics. How do you come across things that people aren’t already thinking about? 

Douglas Diamond: I definitely do not base my research on what is happening today. When my research is relevant to what’s happening today, then in some sense I address a broader audience. When the big financial crisis of 2008 occurred, I slowed down the amount of basic research that I was doing and spent more time talking to policy makers and the public about financial crises. In the early stages of that financial crisis we saw, there was no actual data. I’m a theorist, so someone who just thought for 30 years about the issues probably should speak their mind about what they think is going on.  

To that extent, I work on the flavour of the week or the issue of the day. But I basically work on what I’m interested in and what I feel like I have an insight into. The work that Phil Dybvig and I did on bank runs was not thought at the time to be very topical. In fact, the very first time I gave the paper at the University of Pennsylvania, someone in the audience said: “This paper is very interesting, but it should be in the economic history workshop instead of the economic theory workshop,” because we learned long ago that financial crises are not a problem in developed economies. We learned how to fix them. So that was completely wrong as it turned out. There’s an incentive as a scholar who wants to get attention to work on what’s currently topical. But unless you happen to have some insight into what’s the current flavour of the weak topic, it generates more bad research than good. I like to do what I know how to do, which is narrow, but deep. 

Can you tell us about the object that you are donating to the Nobel Prize Museum? 

Douglas Diamond: I actually struggled to find an artifact to donate. I’m a what’s called “a pencil and paper theorist.” I didn’t have any data. A lot of what I learned about the world, I learned from observing the world or reading books and economic history and things like that. I struggled, and I was looking through my files and archives. I had a handwritten take home exam from a course I took in college, which was a tremendously influential course to me. It was a course called “The Economic History of the United States”. It was basically an undergraduate, one semester course that was an entire book by Milton Friedman and Anna Schwartz called A Monetary History of the United States.  

The most interesting part of that book was about the 1930s when there were a tremendous number of bank runs and bank failures. Actually, in another course in the second semester, which was a PhD course, we used just that chapter of the book. I read that book very carefully twice.  

In this exam, which I didn’t remember that I had, there was an analysis of what would’ve been different in the 1930s if the Federal Reserve had pegged the interest rate at a constant level. What would’ve been different in the macro? I read my answer and, I didn’t remember this at all, and my answer said, “it looked like a lot of the predictions that normal models would have, would say the bank failures only affected the money supply. It wouldn’t affect what was going on in the real economy”. I realised in my answer, that I questioned that. I didn’t know how to model that, but I was questioning what’s the effect of banks on the real economy when I was still in college, in 1975. I was thinking, where did I get interested in this stuff? It turned out that was it. 

Watch the interview