Prof. James Glimm was born in Peoria, Illinois on 24 March, 1934. He received his BA in 1956, MS in 1957 and the PhD in 1959 from Columbia University. Afterwards, he was a faculty at Massachusetts Institute of Technology, Rockefeller University, and New York University. He served, during 2007-2009, as the president of the American Mathematical Society. He has been interested in various mathematical fields, including C*-algebra, shock wave theory, quantum field theory and scientific computing. He is a member of the National Academy of Sciences and awarded Dannie Heineman Prize and Stelle Prize. In 2002, he was awarded National Medal of Science for “his original approaches and creative contribution to an array of disciplines in mathematical analysis and mathematical physics.”

ILC: I would like to know your experience in learning mathematics, from childhood to graduate school.

JG: That was a good question. I always did well in mathematics. But, In fact, I didn't study mathematics professionally until I got to graduate school. In college I was an engineering major. And in fact, I was an average student. I was not a brilliant student in college. (Laugh.)

TPL: Really!

JG: And, I think I probably specialized more in a lot of other things, like having fun. (Laugh)

TPL: I was told that you won a poetry contest!

JG: That is correct! In fact, my other interests included writing poetry. I belonged to a fraternity, which is a literary fraternity. I was probably considered as the most unliterary member of the fraternity. They were very surprised that it was Glimm that won the contest.

ILC: The discipline of poetry is very different from mathematics.

JG: I think there is a common element. They both need great concentration and intense focus. But I think there are many differences also.

TPL: You were having fun, then you went to graduate school.

JG: Then I had a very narrow focus. Focused just completely on scientific works. The change was like day to night. I focused very deeply on the science when I was in graduate school.

TPL: You just decided to do that.

JG: It was very engaging, I think. Undergraduate mathematics didn’t interest me that much. I did not approach it as a mathematician, I approached it as an engineer.

TPL: How could you get into a good graduate school, if you... (Laugh)

JG: Well, That was a little bit of luck. Because I was in Columbia, which had a good graduate school. But, they are not really very strict about admission. (Laugh.) So, I was very very lucky in that. If I had been an undergraduate in Princeton, they would not accept me in graduate school. I might not be a mathematician as I have been.

SHY: I am interested in how did you decide which field you wanted to jump into and you wanted to devote yourself to.

JG: Well! There were many aspects of luck in my life. One of the lively professors at Columbia was Dick Kadison. And, I got connected with him. He was doing operator algebras. So that was my early work, with operator algebra. I was quite interested in the connection of the mathematics to its application. So operator algebra connected up to quantum mechanics. I studied quantum mechanics. That's the way I was pursuing applications. Then I went to NYU and I talked to Peter Lax, I asked Peter Lax to suggest some good problems. He suggested hyperbolic conservation laws. So I studied hyperbolic conservation laws. That led to the discovery of what's called Glimm's method, which is a solution method. So people often ask how that method came about. In fact, there are two parts to it, which are the numerical algorithm and the estimate. The estimate definitely came first. And I thought of them conceptually as power series. And power series was expanded in units of wave interactions. So the waves will interact once, then twice, three and four times. If the wave is small then the second interaction will be smaller than the first one. Then the fourth smaller than the third. So the series would be expected to converge, which is very much like a Neumann series. With a linear problem, you can solve it with a Neumann series. With a nonlinear problem, you generalize the Neumann series. So then, I needed an estimate to prove this conceptual picture, which is certainly a correct picture and the basis for the proof. I needed a numerical estimate. To do that, I worked extremely hard. Basically those estimates failed. One idea after the other failed all summer. I was using the idea of a contraction operator. So I thought of the estimate in terms of a sphere: after the interaction, the solution should be in a smaller sphere. And they would always stay inside a sphere; that would be the bound. Of course, being a nonlinear problem, you have a choice of the definition of what you mean by a sphere. So you have all different kinds of topology. The problem is to define the metric in which the interaction makes things smaller. There just were not any. I tried one after the other. All these spheres, all these definition of spheres, but nothing worked. And finally at the end, I was just about to give up; then I tried nonlinear functionals. That was a completely different definition. And the nonlinear functional did actually get smaller as you get more interactions, because everything that has to be there you can build into it. When the interaction occurs you know how to count it. And so those estimates converge very nicely. The estimates actually work very well. It's a very simple set of estimates. When that they were all finished, I needed the constructive procedure. These are estimates for some procedure but I didn't have the procedure. So I found the estimate but I did not have the procedure to apply the estimates to. The procedure was the probabilistic scheme, which was actually very easy. At that point, it came out in a day or two. Because you took all the ideas which went with the estimate. What is the vehicle that produced these estimates? That was actually easy. That was the random choice method.

TPL: So the hard part was the estimates and the functional. As a result you found the scheme.

JG: The scheme itself is the easy part. But it was easy only because the hard part was done.

TPL: And by that time you had a lot of insights.

JG: Yes!

TPL: A lot people would wonder how James Glimm could come up with this probabilistic argument. What is the answer?

JG: Well! The solution was really easy. But it is easy only because it was the vehicle to contain the estimate. And the estimate was already there. It was not the other way around. So the estimate came first. And the estimate had to estimate something. I did not know what it could estimate. So I was looking at an inverse problem. I was looking at something that this estimate could estimate.

ILC: Let me tell a story of mine. Once, I met Ron DiPerna. He told me that he was doing compensated compactness for nonlinear elasticity. He suggested that I can sue Glimm’s scheme to study this problem. He asked me whether I had read Glimm's random choice method. I said yes. I said that I have read your paper, Glimm-Lax and Tai-Ping’s papers. I told him that I have read 3 times. He said: “Only 3 times? Not enough. You should read more times.” So I went back and studied hard.

TPL: I am not sure this is always correct advice.

JG: Well, I should also say that other people, you, Tai-Ping, and Bressan, they took these ideas and took them much further. The original idea that I worked on with Peter Lax: we did very complicated estimates. But there is always something very simple behind an idea. There was an ODE, a decay rate ODE. If you thought about the ODE, it was all very simple. You just needed to do a lot of technical estimates to carry out these ideas. There was another problem; I tried very hard and did not ever solve it. That was the uniqueness, well-posedness of the problem. So those came later. The elaboration of the method definitely introduced the idea I didn’t have.

TPL: Jim, let us go back to Shih-Hsien’s earlier question. Implicitly, that question seems to be this: When you go to a new field, you seem to be completely fearless, right?

JG: Yes!

TPL: In fact, Peter Lax told me a little bit different story than what you just said. Peter Lax said you went there to ask him what is the hardest question in conservation laws. (Laugh.) So you are completely fearless. It was a field you were not familiar with. You seem to have no psychological problem. “This is the field. I do not know anything about it. No trouble!’’

JG: Actually, I have more trouble with easy problems. (Laugh.) Because there are too many choices, too many ways, to do them. They are not highly disciplined. Difficult problems have their own route. If you pick the wrong route, then you are off the track.

SHY: So, how can you be so sure that you have picked the right route.

JG: Well, in fact, I didn’t. I spent the whole summer on the wrong route. I was close to giving up. But, I just tried a little more. That was good, because, when I was close to giving up, then I knew that there were something very fundamentally wrong with what I was doing. That gave me the freedom to try a different approach. But, the hard work was all the preparation, which put my mind in the right framework for understanding everything. I had it all in my head. And, at that point, I could see how to do it.

SHY: That means, before you worked out the estimates, you already realized what would be the solution, the whole picture of the solution in order to build up those estimates.

JG: Well, basically I thought of it as a power series in the wave interactions. I thought the waves themselves are fundamental. So, the solution should be expressed in terms of wave interactions. I thought of it as power series. A succession of powers in the small waves had to be convergent, because higher order interactions had to have a smaller effect compared to basic interactions.

TPL: Waves and interactions.

JG: Yes.

TPL: Can I turn to quantum field theory? How did you get into that?

JG: Well, that was the consequence of the thesis work in C* algebras. Looking for where they are useful, basically, led to quantum field theory. So those were being used for the study of quantum field theory. Having got into quantum field theory, the C* algebras were suitable tools, but probably not the most suitable tools. Other methods were really better. So I started out down the path, and found that although that is a path you can follow, there were better paths. So, we switched the methods, basic methods, that is to use path space integrals, which were more fundamental, more friendly to the solution of the problem than the operator algebras. There were many controversies between operator-algebra people and path-space people. In fact, there were many other approaches beyond those. Among the functional analysts in those days, there were five or six people; each one had their own theory and how to go about it. I learned from every one of those people. They all had a piece of truth, and instead of arguing, I just said yes. I said I learned from you. Then, I went to the next person and I learned from that person. I learned from five or six people. All of them were at each other’s throats . But, I learned from all of them and put all the ideas together. And added some new ideas. Nobody had thought of doing that.

TPL: I see. Then those fermented in your head.

JG: Yes. Yes. Friedrichs is very profound with very good ideas.

TPL: He wrote a book, right?

JG: Yes, I read his book. It is a very nice book. That was very influential on the work I did. But the book itself fundamentally was very close to the idea of physics, not as adventuresome, as original. And that was perhaps the right direction. Because the more adventuresome people actually, in trying to be adventuresome, probably deviated from the true path.

TPL: This work, people have always regarded it in awe and consider it as a very profound thing. Can you go into a little bit of the technical aspects?

JG: Well, one of the interesting aspects to this work is related to the theory of wavelets. Now, many people invented wavelets, before they were invented. So, I don’t want to make a big deal out of that. Haar, for example, invented wavelets before anyone knew what wavelets were. But Jaffe and I were also pre-inventors of wavelets. So, we have simultaneous analysis of X and P spaces. At that point people could be in either one, but not both. By being in both, we did much deeper estimates, which we needed . But, the formal principle of physics, the power series expansion, and the ideas we learned from Friedrichs were probably already present in the ideas of Feynman and the other people. But we learned them from Friedrichs, so he was very influential to us. And, we could do the expansions, and the power series gave you the leading term in the same way that they did for the conservation laws. You have some infinities and you had to cancel them. Now we looked at the easier case which is lower dimensions. There were only a few infinities. So, you cancel the few infinities, then everything else is finite. So in Friedrichs’ formalism you could see how to do that low dimensional cancellation. It was a very interesting idea, because sometimes the answer was in a different Hilbert space. It starts off with one Hilbert space, but the answer is in another one by an infinite amount. But you can write down the Hilbert space you are supposed to be in and with the few infinities canceled or expressed properly, the rest is finite and doesn’t change the Hilbert space. So we could do all of that. Once you understood it, it just follows a certain pattern; it was rather routine, except you have to deal with an enormous number of technical issues. So, the papers are sometimes 50 pages, sometimes 150 pages. There is a unit of measure which Arthur Jaffe's students talk about. It was a unit expressed in computing papers, which in those days were rather large sheets of paper, which were maybe 2 feet by 3 feet. The question is how many of these large sheets of paper it takes you to prove certain estimates. But, there was a unified idea, an idea to follow through. One simple idea would organize this. I think many of the key developments of modern mathematics must be like that. Consider the Poincare conjecture, for example. I did not follow the details, but I am convinced that Perelman had in his head some simple ideas first. He could follow them through, but as a sequence of very complicated estimates needed to piece it all together.

TPL: I know you have many interests. When you talk to chemists, you have something to say. You talk with people who major in business, and you have something else to say. You have very wide interests. We mentioned you won a poetry contest. But, on the other hand, when you work on something, you have a deep concentration.

JG: Yes! It is necessary to be deep, to do something deep. But, it is necessary to be broad in order to understand the ideas. So you have to find a way to be broad some of the time and to be deep some of the time.

TPL: You are able to do that! (Laugh.)

JG: Well, that is part of the joy of mathematics. Mathematics allows that to happen.

TPL: You must have some moments agonizing over some difficulties, no?

JG: Of course! (Laugh.) Of course! Yes, there were many things I tried and haven’t done. It is a pleasure to beat some other people sometimes too.

SHY: Can you give us some examples that even the great Glimm feels that there are something he cannot do, to make us feel better. (Laugh.)

JG: Well. One of the great problems in analysis that is still left is the full Navier-Stokes equations. I am convinced that depends on ideas from the renormalization group. The renormalization group has several stages when it is brought up in terms of physics, but the most profound and deepest part of it is to integrate out some degrees of freedom. The problem can be solved for smaller length scales, leading to modified equations for the larger length scales only. In the case when everything is homogeneous, which you expect for turbulence in the inertial range, all those length scales are identical. By induction, if we can do one of them, then we can do all of them. That is a very simple idea; it is what Kolmogorov used to derive his 5/3 law. His analysis is based on a fixed point, the renormalization group fixed point. There is a further idea which has to do with the epsilon-expansion, actually. It is used when you get to the fixed point equation you have to solve. I think that part is not necessarily applicable to a mathematical proof of existence and regularity for the Navier-Stokes equations. Orzag tried that. I am not sure that part will actually be important. But the renormalization group and its early sense, which has to be an invariant analysis of length scales, I am sure, will be an important part of the ultimate proof of existence and regularity for the Navier-Stokes equations

ILC: Why did you jump to the computational science?

JG: That is a good question. I was always somewhat interested in that. Every time I looked at it, and talked to computational people, they claimed that they are likely really to solve every problem. I notice that went on for several years. They always have something else to do the next year. I thought maybe their claim that they had solved every problem was perhaps overstated. So there may be still something left to be done. So I was interested in getting into it, but also was always the problem of the big learning curve. You want to find a more friendly way to get in and to get in more rapidly. I noticed that people were using the random choice method to solve the equations numerically, whereas I had only thought of using it theoretically. I understood that. So I decided to get into conservation laws using the random choice method. That is a very good method in one dimension. But efforts to do it in three dimensions really do not succeed. People who want to study numerical Reimann problems in higher dimensions, I think, have made some artificial problems. I do not want to be negative about others’ programs, but I don’t think I should care for that. I do like these problems in the sense that there are wave interacting in higher dimensions. One can look at problems related to Mach-stem formation and shock reflections problems and so on. But anyway, from the random choice method, we did a simpler version on one dimension. It is a lower order method, but we get higher accuracy. In coarse grid, it is good in some way. You get nice solutions with nice properties. Then you try to do it in two dimensions. It is a disaster. At that point, we thought of front tracking, as a higher dimensional generalization. So that was the method we followed. It is a lot to do with wave interactions. We use the Riemann problem, but to do higher dimensional interactions, you need to solve shock polars, and they were very complicated, and so, you had to say: “well! Is it worth it?” We looked at finite difference methods; they work pretty well for shocks. So, it wasn’t worthwhile and so we stopped tracking shocks. But, we still track contacts. The question is whether it is worthwhile to track the contacts. In fact, contacts were a big disaster for finite differences. And that is a major unsolved problem. People worked a lot on contacts, but the matter is still unsolved. I think front tracking is quite viable compared with other methods. There are other ways people approach contacts numerically. But front tracking is a very viable method.

TPL: What are your non-mathematical interests these days?

JG: My non-mathematical interests? Well, one of the interests is that we enjoy going to the opera. The other interest I am pursuing more recently, is studying Italian. They are, in fact, related since many operas are in Italian, which is beautiful. So I thought I would enjoy even more of the opera if I had more knowledge of Italian. How do I learn Italian? I do that by reading Italian books and by searching on the Internet. I am moderately fluent in reading Italian. I am not learning to speak Italian, but in terms of listening and understanding, I found an Italian TV Channel. I can follow that to a certain extent, but I am not proficient in speaking Italian.

TPL: Now, as AMS president, this clearly is a job, it takes away your time from science. You must have something you feel deeply, something that you would like to do. Otherwise, you would not have taken this job.

JG: It probably would not be possible without some goals. If you have too many goals, it is like not having any. If you try to go in all directions, you might end up going in no direction. Because they all cancel. There are forces involved, and the total force is zero. So I picked two goals. I picked an intellectual goal and a more administrative goal. We will talk about the administrative goal first, which has to do with teaching. As the president of AMS, I had to be concerned about resources. People normally think about resources in terms of NSF or federal funding support for research. In fact, a major support for pure mathematics is the university budget for teachers. And for every dollar NSF puts in, the university budget is multiplied by a factor of 5 to 10. By an order of magnitude, the teaching budget is much more profoundly important. The NSF is still important, very important; but it plays a secondary role. In fact, if you do the first job, teaching, well, you will probably do better at the second, research, well. I do not think there is a conflict. I want to see teaching improve. Now, in my university, at Stony Brook, we achieved this goal, which I think is unique. As far as I know, among the research departments, the teaching is average in the following sense. We do not have a measure of the quality of learning. We study satisfaction. In terms of student satisfaction, our mathematics equals the university average. I don’t think a lot of research oriented universities can do this. But probably there are a lot of teaching oriented colleges that can do that. So it seems possible to achieve quality teaching without compromising the research. I believe we do good research in math and applied math. It does take a little bit of extra work. The extra work is perhaps level of 5 or 10 % extra. For that, certainly the university may compensate. Now, most of the methods I use, probably won’t generalize; but some of them do generalize. We are looking for methods that are usable across the board to improve the teaching ability of American mathematicians. So where is that silver bullet? I think people in Rochester were facing extinction. And the basic idea, as they say, is that the prospect of hanging serves to concentrate the mind. They developed a computer graded system for homework. Apparently, that method makes an enormous difference in learning performance. So we are going to study that. We have around 8 people distributed around different kinds of departments. We will see what ideas come up, I hope the best ideas come up. We may help promote ideas that are already promoted by other groups. Cooperating with them, we are not competing with other people, in pushing some idea. So, I am thinking of the available ideas as plotted on a plane, with all ideas in the plane. One axis is how hard the idea is to implement, how easy it is to implement. And the other axis is how effective it would be. So, our goal is at the upper left hand corner. That is both easy and feasible. But we are filling up the upper left hand corner, which is both feasible, easy, and also effective. So we push that collection of methods as the answer to the teaching problem.

TPL: Oh, this is an experimental science.

JG: Yes. That defines the administrative goal. The intellectual goal is related to ideas quite different from my own research, which grow out of engineering, physics branches, and mathematics. It occurs to me that there are a lot of investigations which are independent of physically based models. They basically derive directly from data. Just to give an example, when you do image analysis, facial recognition, finger print recognition, or statistical analysis of data. you often do not do it through intermediate differential equations. You just look at data itself, and the pattern in the data. It is what I call data driven science. Now there is a lot of science concerned with analysis of data. Even if there are some differential equations, the data driven science does not emphasize this aspect. In this approach, one just looks at data, and lets data speak for itself. And, in many cases mathematics does provide organizing principles for how to do that. I thought it would be a good thing to try to develop data orientated science, which could very well be the science of the 21st century. Not that physics based, differential equation based science is going to disappear. But, with computers, pattern recognition is an issue that has been undervalued. It will become very important for science in the next century. I want to explore that to see at least where it leads as the intellectual vision.

ILC: Is it more related to statistical sciences?

JG: Well, it certainly has a big statistical component. But it has other components, too. It is not statistics by itself, but in conjunction with other things. I was talking with several people at Yale. They are developing this set of ideas. They are interested in geometry formulated statistical equations. You have a data set. The data set is a manifold, but it is a statistical manifold. So you have to find the manifold buried in the statistical data. You have some geometry. You have some statistics. The question is how you define the curvature on a statistically defined manifold, for example. I think many problems in data driven science are defined by combinatorial identities. Again, it is a search for a statistical pattern, a pattern of the data. People have used conservation laws, for example, in image analysis, where the viscosity method is used in an attempt to converge to the pattern buried in the data. So, I think there is room for many different ideas. Certainly statistics plays a big rule, but we should not prejudge and narrow the ideas to that. We should have a broad horizon to see which areas of mathematics can contribute to this pattern recognition problem.

TPL: It is not a particular subject. It is a pattern of thought. We are at its starting point.

JG: Yes.

ILC: What kind of engineering courses did you have?

JG: I never graduated as an engineer, but I was a student in electrical engineering. That was a five-year program, but after four years, I realized engineering was really not where my heart was. But I was very confused, because I was confused between physics, mathematics, and engineering. I did not know why I was confused then, but I know why now. Because I wanted to do all three. I saw different things. But, I wanted to do all three with the intensity allowed by doing only one of them. And I couldn’t do that. Obviously, I couldn’t do that. I had to make a choice. It turns out I do it by a time average instead of a space average.

TPL: Time averaging. You are doing computations. You are talking about prediction. Now you are talking about pattern recognition. You are in contact with more and more people, right?

JG: Yes.

TPL: Suppose you were to start over again as an undergraduate student, what would you do?

JG: Well, that is a good question. As a department chairman, I could start again every year. Every year some people leave and we hire new people. So I do start again every year. My mind gets refreshed every year. What directions are we developing? We develop math-biology. We are probably going to develop a finance program. So, I guess that is the answer I can give to your question; I do start again every year.

TPL: Your ever so curious mind! Every year you start fresh.

SHY: How do you penetrate each problem when you get stuck.

JG: Well, in the biology, I think mathematics has grown a lot, and it is a very healthy subject nowadays. But I started looking at that area years ago. The mathematician’s attitude was “Well, I am not sure what biology is, but at least we know we are doing mathematics.” That was actually a disaster! You had to actually know the biology in order to do biology. And, hopefully, there is some mathematics in it. So we are very deeply into the biology. We are doing mostly molecular biology. There is atomic level modeling solving the Newton equations. There is pattern recognition trying to find molecules that are interacting with other molecules. Differential equations trying to describe the interaction between genes and other genes, with gene regulation. This is not my own works; it is work of my colleges. So, there are a lot things going on. If we want to hire people, we want to hire strong people, happy people, people who can fit in with other people who are strong and happy. Routes can be followed, we can be good and maybe better. These are the opportunities that we think we can follow.

TPL: Maybe we can stop here with this happy note. Thank you very much.

• Tai-Ping Liu is a faculty member at the Institute of Mathematics, Academia Sinica.
• I-Liang Chen is a faculty member at the department of Mathematics, National Taiwan University.
• Shih-Hsien Yu was a faculty member at the City University of Hong Kong and is a faculty member at Academia Sinica starting July 2021.