傳播數學知識．促進數學教育

Interview with Prof. Michael Aizenman

** Tai-Ping Liu
Interviewer: Tai-Ping Liu (TPL)
Interviewee: Michael Aizenman (MA)
Date: July 15th, 2011
Venue: Institute of Mathematics, Academia Sinica
**

Prof. Michael Aizenman was born on August 28, 1945 at Nizhny Tagil, Russia. He received his B.S. in 1969 from the Hebrew University at Jerusalem, and his Ph.D. in 1975 from Yeshiva University. He was a faculty at the Courant Institute of Mathematical Sciences of New York University and Rutgers University, and since 1990, at Princeton as Professor of Mathematics and Physics. He has made distinct contributions to mathematical physics, statistical mechanics and probability. He was awarded Norbert Wiener Award, Dannie Heineman Prize in Mathematical Physics. He is a member of National Academy of Sciences and Academia Europaea.

TPL: Thank you for taking your time off for this. Are you trained as a physicist first?

MA: You know people sometimes ask me whether I am a physicist or a mathematician, and my standard answer is that I work the Fifth Amendment. I have always been at the boundary of the two, and I made an effort to be at boundary of the two. As an undergraduate, I tried to major in physics, mathematics and philosophy, philosophy was dropped very early on. My PhD is formally in physics but then the first post-doctoral appointment was at Courant Institute to be the mathematics. When I arrived at Princeton, it was always between the two departments. Princeton as you know has this tradition of joint appointments in the two fields, which suited me perfectly.

TPL: Was your undergraduate degree also on both?

MA: Undergraduate, I think it was a double major. I do not remember which of the two was stressed. Basically, my tendency was more mathematical from day one. So when I go back in my mind into what attracted me and what to spend my time and fascination it was more mathematics, but when I learned fundamental mechanics and quantum mechanics, it became physics that I very much relate to and was fascinated by. So it’s always been on the border.

TPL: When you look around your mathematical friends, I would imagine most of them have somewhat less physical background, right?

MA: With some exceptions, Lieb for example, is in physics, is also between physics and mathematics. I have this world view of the relation between the two disciplines which fits what I see. I feel that the physicists try to relate to the nature and what we see around, the physical reality of nature and, I’m not quite sure, but, it’s a very rich multi-faceted entity which always surprises you with richness and aspects which you have not expected before. Then locally, it’s amenable to mathematical analysis and in this respect, mathematics to me is a bit like tangents, to talk in mathematical analogy. It’s like tangent spaces to something which is much more complex. And as you know, tangent space, not in the sense that things are linear because mathematics can be very non-linear and so forth, but the strict rules of mathematics apply for very local parts, which always surprises you in some other aspects. And this interplay between these two is very important for me.

TPL: I see, so from what you have just said, it seems not easy to identify the kind of mathematical questions which one can do something about and yet also reflect the significant physical phenomenon.

MA: It’s not difficult. For example, a theme which has attracted my interest has been critical phenomena in statistical mechanics. So this starts from physics, it’s really given by experimental observations that you have universality of critical exponents to a degree not expected, surprising and works marvelously. And then when you try to explain mathematically, people formulated the models of statistical mechanics, formulated the question of critical behaviors, phase transitions, the nature of singularities and then the stage where I entered some of the discussion; I was trying to clarify this in specific models. And then a particular problem which I found fascinating was the notion of scaling limits of critical systems, and once you formulated mathematically of what you are after, you discover on one hand, you open a door for precise mathematical structure which gives rise to beautiful mathematics, you also discover the limitation to some extent of our mathematics. So you know, topics like Stochastic Loewner Evolution, SLE, a subject to which itself I did not contribute but I did contribute to the formulation of the questions which led answers to, and these are very natural for mathematical physicists, and led to tremendous enrichment of mathematics and probability, modern probability. It’s not difficult to find those questions.

TPL: At least not for you! From what I can gather, perhaps there are two kinds of person. The first kind starts from physics and try to formulate mathematical problems, like the ones you just mentioned; you are simply happy to formulate the mathematical problems and some other mathematician may pick up. There are, say the second group where they are looking for problem which they are told has physical relevance and with their analytical tools to do something with it. Suppose we just crudely classify into these two categories, what is the disadvantage of the second category if my classification make any sense?

MA: Well, um, most of the time I do work on mathematical analysis problems, whose motivation is in some way coming from physics or ideas which physicists can open the window to without having the mathematicians to analyze it. Most of the time that is what I do, most of the time I work in mathematics, it is not formulating conjectures which I would pass to my colleagues in mathematics. When I mentioned SLE (Stochastic Loewner Evolution), on one hand, it was a success story in the sense the question to which I contributed to formulating and putting precisely under the microscope with some initial steps were taken over and mushroomed into beautiful mathematics, but I regarded this to some extent as a failure of a mathematician, because my ambition was to actually solve it myself. But I learned, with time I learned that your contribution in solving a problem of mathematics, related that may be, it’s great, I don’t want to diminish it but to some extent, there’s not less but perhaps more value in formulating a good question.

TPL: So your so-called failure actually gives you a lasting satisfaction.

MA: A certain amount. But I would have liked to solve this one. This is a problem which escaped from me. I once told my colleagues, that a mathematician who solves an outstanding conjecture should regard it as a certain duty to formulate another one.

TPL: Right, so that you leave something for the future generation. I guess it must be because of age, I found that having identified a good problem gives me sufficient satisfaction already; one doesn’t have to solve the problem. Now, talking about formulating problems, I was told that this person, Parisi, he has done some of that.

MA: Not formulating problems. Giorgio Parisi had the insight to see, formulate a structure and see an answer to a problem which is easily posed more or less, the answer was totally surprising and the logic by which he arrived was initially very hard to comprehend. As a friend told me, I think it was Parisi who said, at the Toulouse meeting when he presented it. Parisi consulted with him to know zero dimensional representation to infinite dimensional groups as a motivation for what he was about to say. He was proven to be correct, but not by following his steps. In general what I find, often in mathematical physics, is people tend to work on structures and possible solutions which were envisioned by physicists and usually when you succeed it is not by checking the path taken by the person who saw it first actually can be justified, but rather developing your own perspective on the subject and seeing echoes of what is done.

TPL: Mathematicians have to follow their own intuitions.

MA: Absolutely, I mean the tools are very different. This is actually one of the misconceptions of the work of mathematical physicists. Physicists often feel that mathematical physicists would be just checking the epsilons, dotting the i’s and crossing the t’s, which is usually not the case.

TPL: In fact, I would imagine that good physicists would appreciate the actual happening of how mathematicians go around it right, instead of making rigorous of their thinking. They are happy we have actually found different mathematical structure, which is considerably useful in other situations as well. There is certain universality of our creation.

MA: Yeah, physicists need to be continually educated on that, and one of the frustrating aspects of the interactions between mathematicians and physicists is that physicists usually do not see it this way or the way I described. Often they are very defensive. They arrived at the conclusion using some insight based on intuitive grasp of what’s of essence and they feel that they leaped over early aspects which they cannot quite see through. But when mathematicians approach the subject by means which they do not understands, they tend to be very defensive about this and they do not see this aspect which we have just said, that a different structure emerging.

TPL: Do you mind giving an example of that?

MA: One of the early examples of renormalization group theory in physics was in works of Phil Anderson, which was a beautiful paper in 1972 roughly, related to the Kondo effect, in which a renormalization group flow equation was described, for two or three degrees of freedom, of a rather complicated system, and by studying it, they derived (it was jointed with Hamann and Yuval), they answered the problem, but beyond this thing they introduced the idea for renormalization group pictured in a very concrete way, which led to concrete non-trivial results. But from that point on, the authors of their work, the main author, Anderson, was not particularly welcoming of mathematicians trying to dig into this subject in a mathematical way; it took many years to actually verify that some of the key conclusions are correct. Now what is the value of that, well the value is that once you formulate the phenomena in the mathematical language, it’s transportable to various other disciplines. For instance, appreciation of critical phenomena and universality of phase transitions, actually, once you formulate it mathematically, spread into other areas, of discrete mathematics, of information theory, well beyond the specific condensed matter problem that this was formulated on. Mathematics language permits to connect views which are very different, and some people made major contribution by just pointing out in other areas, that ideas which work here once you formulated in certain mathematical levels actually open a door for an insight in different area. Jennifer Chayes was extremely successful with the group which she led, Microsoft research, working with Bollobas and others. Our friend, Joel Spencer, bringing insight of statistical mechanics and critical phenomena to graph theory, problems which were of interest for mathematicians because of coding and information theory.

TPL: When did you get your PhD, when did you publish your first paper?

MA: My very first paper is related to Master’s Degree, which never got finished. It was at the Hebrew University, I interrupted the Masters studies to come to the US for the PhD program. And I think my first paper was with Joel Lebowitz and Sheldon Goldstein, Giovanni Gallavotti, on dynamics of infinite particle systems. We were interested in dynamical systems perspective on topics of statistical mechanics.

TPL: So that was what year?

MA: I got my degree in 75, it was around that time.

TPL: You have traveled not along a straight line for quite a while. What are the scenery or the personalities you have come across? Do you want to describe some of that? Certain people you have met?

MA: People I had a chance to interact with? Well, coming to the US, I was initially interested in foundations of quantum physics, but then I interacted with David Finkelstien, who had this vision, the main message of quantum mechanics is that the logic of the physical reality is different than the classical logic we are used to. And he thought this one is very consistent and sticking with that, one should construct some structure from which even space-time would emerge by the rules of quantum logic. It took me a year to realize that it was fascinating, but I wanted to have more tangible growth, and then I also realized the richness of the mathematical physics, which was taking place around Joel Lebowitz. Now Joel’s office, being a graduate student with Joel Lebowitz was quite an experience, because it was in a very loose environment, the course was not too structured, it was steady flow of fascinating people that one had direct contact with. So I had chance to get impromptu explanations and seminars to a very limited audience by David Ruelle, Oscar Lanford. Excellent people, and one thing which struck me then as a young graduate student is that it is not there are smart people and smarter people, but that people have really different qualities and different sensitivities. Someone would be brilliant in capturing mathematical structure and presenting it in a very ordered way, where you would see it beautifully, but he would be uncomfortable with too chaotic set up. And I saw Joel listen through a seminar where he would get lost in the details of the mechanism of mathematics and towards the end would be asking very penetrating questions which took by surprise, some of the people who had followed perfectly well the mathematical structure which was presented. Then I came to interact with Elliott Lieb who was my postdoctoral mentor at Princeton.

TPL: Very different personality.

MA: Yes, still the same time a very friendly circle and Elliot I think is a mathematical physicist who comes from physics but has an eye to formulate the results, in a very mathematical language, and again, his work has spun off very interesting mathematics, while he was always insisting on trying to keep connection with mother physics.

TPL: Something comes to my head: it’s always somewhat a mystery to me that there must be, maybe it doesn’t apply to your case at all, but what is mysterious to me is how the culture can have an effect on a person. For example, the Chinese culture, may I say you come from a Jewish culture, is that true or not?

MA: Yes, I’m Jewish.

TPL: That’s very different, and they give us a different set of values and so on. You and I both have exposed to two kinds of cultures and other kinds of cultures. Do you mind talking about this?

MA: I think that I, I recognize some elements of what you are saying. I think that if you look at the work of Chen-Ning Yang, Tsung-Dao Lee; some Chinese physicists I think, have been stressing a certain global view of the landscape and crossing bridges between specific studies of models and related problems which can be formulated like implications of symmetry, role of symmetry. But this is not unique to Chinese culture, to Chinese physicists, it does have to be exposed to, the culture you are exposed to does affect your work, but only up to some point. For example, I think that you can see British Imperialisms which also somehow affects American approach to questions of quantum mechanics, coming from a European or German tradition where there was a bit of encouragement in discussions of foundational aspects of quantum physics. And Richard Feynman’s answer: “Shut up and Calculate!”, conveys a certain spirit that we associate perhaps with American youth and energy. But these divides are not absolute, they enrich the subject.

TPL: The Japanese, they are also different. But we are basically individuals.

MA: No, we are affected by culture, definitely. All what I’m saying is that it is not that some have zero sensitivity to one aspect of the approach which is more important to others. It is a question of mixture.

TPL: Now, what is your interest lately? This is a bad question. Joel Keller, once I ask him this question, he responded: “Are you talking about yesterday afternoon or this morning?” So what would you really like to be able to do? What would be your dream?

MA: Well, it’s embarrassing to pronounce one’s dreams because there is a certain element of immodesty about that. But it’s also important to have high goals. Sometimes I feel that the issues in analytic number theory present the next frontier for probability and statistical mechanics and interesting things happen in that area, but there is plenty on my hands in the study of random Schrödinger operators where one combines probability theory with analysis. And we are not totally disconnected from the other areas which I mentioned.

TPL: Have you tried your hands on Riemann Hypothesis?

MA: Well, who hasn’t.

TPL: Why is that problem so hard?

MA: In a way, it touches on pseudo-randomness, which leads to random behavior. Somehow, prime number theorem is at the level of law of large numbers, looking at it from probabilistic perspective. The Riemann Hypothesis is somehow the next level which in probability would be the central limit theorem if you wish, except there is nothing random about prime numbers, and yet when you look at fluctuations, for example the Mobius function, you are trying to capture what a bit of randomness would make a trillion. Many systems actually are also related to statistical mechanics. Boltzmann’s formulation of statistical mechanics, for example, equivalence of ensembles, is related to the emergence of robust probabilistic description for a non-probabilistic non-random system. The development of mathematical tools for that, that’s our challenge and we find that in many situations.

TPL: So Riemann Hypothesis is important at least for that?

MA: It’s often good to have a target and I do not know whether the target itself is all important but the road there is fascinating, although in this case, the Riemann Hypothesis happens to be one that is recognized to have many implications so that it will be of value I guess to prove it, mathematically speaking. But often the target, it is good to have a target for one’s dreams and work, which does not mean the most important result would be the proof of that but rather the understanding and spin-off one develops. When I entered the field of mathematical physics, constructive quantum theory was viewed as a worthy target and many good things evolved from the effort of mathematical physicists, not because the goal was accomplished but realized to be, it was realized that the goal originally planned actually was not quite... Let me put it this way, when I was entering as a post-doc, the problem which was presented as an urgent target for mathematical physicists was the crisis in theoretical physics, where physicists used the notion of Field Theory as a basic tool for description of physical reality, whereas mathematically it was not really clear what Field Theory is. The goal was to produce some models in four dimensions and the models which were proposed actually do not produce the result. But trying to understand what goes into this structure has led to many interesting insights and many spin-offs.

TPL: There was the effort of Glimm and Jaffe, which is a very rich endeavor, right?

MA: Right. It’s again, an interesting question of how to divide one’s effort, should one direct one’s effort to proclaimed goal like constructing Field Theory in four dimensions, solving the Riemann’s Hypothesis, or reaching the moon, versus encouraging research on topics which emerge from grassroots up. I think either exaggeration is not the best way to go.

TPL: In that sense, democracy is important in academic environment.

MA: Absolutely, yes. On the other hand, it is also good to proclaim goals, worthy goals, without being too draconian about cutting off work on other fields, in other directions, which in the long run, probably more contributions emerge from that grassroots further inside. On the other hand, without any set of examples of worthy goals, most people who have the inclination to produce interesting work look a bit aimlessly around.

TPL: So, Europe has been leading the scientific development since the Renaissance. And for many years, the intellectuals in Orient keep asking oneself, what’s wrong with this old civilization? The same thing can be said about Arabian culture. They also have their glorious days which overlap with the glorious days of the Eastern civilization during Chinese Tang dynasty and so on, then somehow become stagnant. Of course, the cause for that could be very complex, but this grassroots thinking, is it true that this really, there’s a precondition for that, namely the society has to have certain freedom.

MA: Absolutely, yes, freedom to follow one’s inclination, one’s creativity is absolutely essential. The intellectual pressure is also important in motivation and stimulation. You mentioned Jewish culture, Jews in Europe for a long period were not given free access to universities, it was very limited in certain countries, certain areas. It varied. And I have the impression that there was an explosion of presence of Jewish talent in the American science in part from this generation which hoped their children would succeed, motivated them to open the doors which were closed, so the generation of Feynman, I can make a long list, are often people who came from background where they themselves were not children of professors but they brought on the scene with a lot of energy and enthusiasm for breaking the barrier although they would not formulate it this way, on occasions you see such moments.

TPL: So their home education in the early generations valued intellectual pursuit and so on very much.

MA: There was intellectual pressure present but there were also limits on the road forward and when conditions were relaxed and this opened up, this makes results.

TPL: What makes them, is that the religion or what, what makes them value this intellectual pursuit with such a high priority?

MA: I do not think it’s the religion but it’s the culture of valuing scholarship and thinking and debating and questioning.

TPL: It is very difficult to know why they value particular values, all one can say is that it has been their tradition.

MA: Yes, but this tradition, if you look at the number of scientists and mathematicians who emerged from this community as a function in time, it has not been uniformly strong, and in the 20th century, certainly in the United States and also Europe, you saw bursts from that direction.

TPL: It seems to me that this intellectual pursuit, and indeed all the other human activities, a lot of time it is motivated by financial gain. But that’s definitely has to be non-sufficient because everybody works hard for financial gain and intellectual pursuit may not be the most easy, direct way to achieve this gain. So this could be one of the motivations, but the Jewish culture had to have other motivation.

MA: Any culture, I don’t want to be specific with Jewish, it’s any culture. Individuals seek a certain sense of self-satisfaction not only self-satisfaction but recognition. Yes, financial gain may be part of it but especially in the culture which actually values ones’ intellectual contributions, that’s also a strong motivation.

TPL: The Chinese, for example, has particulars, they have always wanted to make poetry, which is supposed to be the highest form of your expression. Even Jiang Zeming, the previous leader of China, when he goes somewhere and he makes poetry. He is no poet, unlike Abraham Lincoln, who is a true poet, but he cannot help it.

MA: Yeah, but I think that, the younger generation pays attention to that. When I was growing up, the literature the high school kids were exposed to stressed improvement in the world in just technological process. The message was that somehow if you were good, you should mobilize yourself for that, and some felt that with my poor understanding and knowledge I could not solve technological problems but still it felt good spending time on solving the math problems or whatever the technical issues that came up. Not because you thought that you were really solving that particular problem, but it does give some incentive, some encouragement.

TPL: It feels as if you were part of the effort.

MA: Yes, It’s a very satisfying feeling to succeed in an area, where you feel also in some broad sense. Although I think that in our field, in the reality people are driven to do what they do by a sense of satisfaction which they derive from their work, in a way in some sense you cannot stop thinking about that. I’m talking about myself because I happen to know myself more, but I think it’s much more universal. I was thinking about problems that I found fascinating, not because of any reward or encouragement. It was difficult to stop thinking about it.

TPL: Now, I have heard from others, Michael Aizenman does certain things, he is unique in that. Instead, could I ask you, I have been asking bad questions, so let me ask one more bad question.

MA: There are no bad questions.

TPL: What are the certain things that you do, that you work hard and are different?

MA: I think that I feel that each is unique in each own way. It’s hard for me to say.

TPL: I know that it’s a bad question that puts you on the spot. But let me put it differently. There are certain things that give you real pleasure, “I travel this route and I am happy to continue” or certain things, it can be big or small.

MA: It’s too much focus on me for me to answer it easily. But overall, I feel that I have been very lucky in pursuing what fascinates me. When I started early on, I knew what kind of activity I wanted to engage in, and I was actually told, financially this may not be a very good choice because down the road university research budgets may be limited and so forth, and I did not care about that. I knew what kind of things I want to do and somehow I found I had more successes than I expected and that actually life was very rewarding and very rich. I was very fortunate to meet and interact with people of different sensitivities, inclinations and insight and that has been very rewarding for me. I like to work with collaborators. It’s normally fun to develop ideas together. But I also like to take my problems and just think about them in my own time. Early on, I was very pleased to see that actually I can make some contributions in that. Down the road, I found in more than one case, that some of my younger colleagues from left or right, actually, made further progress on problems which I started in hope to see, to deliver to them, but I learned to rejoice in that too.

TPL: Can you describe one or two things like that?

MA: Let me give you an example of what I just said where success led to joy even though I was not the one who did the last stage in that. In 82, 81, I solved some problems of Field Theory in statistical mechanics by introducing random walk representations, an insight based on probabilistic properties of non-intersection properties of random walks in high dimension. When I was asked to give lectures on this in Paris, I formulated and realized that there are problems I cannot yet solve and I formulated a much simplified version of the problem referring to non-intersection exponents in two dimensions of random curves. This has led to, actually let me not get down this path, it’s a long story of its own. Let me not get into that. Well I formulated a question: what is the power law of non-intersection of two Brownian paths in two dimensions. The simplest problem which is related to the kind of questions I was after and I could not understand it. I even promised a bottle of decent wine for the solution of that. And years later, I learned that the physicist who has since became a friend, Duplantier, found an answer to this, just by combination of numerics with reliance on predictions of Conformal Field Theory. He formulated an answer, non-trivial, some rational family of exponents, but it was done by methods which did not give any proof. He then asked me whether it’s time for me to deliver the prize, and I said as long as there is no proof there will be no prize. Eventually, the technique of Stochastic-Loewner Evolution was developed and the work of Schramm, Lawler, and Werner led to rigorous proof that, this very interesting solution which was found by Duplantier is actually correct.

TPL: Oh wow! So it goes around, back to physicists and then come back to mathematicians.

MA: Absolutely, this led to some other questions which I formulated, which led to the development of the Stochastic-Loewner Evolution, which produced marvelous mathematics in the hands of these people who proved that Duplantier’s guess was actually correct. At that point I was asked what was the prize for, I was asked the question, are you a physicist or a mathematician? Because physicists value discovery, and if you try a number of times and you miss but you get something right and you discover a new law, that’s what the prize is for. Mathematicians as you know value a proof and they strongly discourage wrong proofs and mistakes which are never forgotten. But I felt that being a mathematical physicists, I value both, so there was one award to the group of four people. This was a major success for mathematics. Werner received the Fields Medal for this set of works. Schramm should have got it earlier but he was by two weeks too old for that. Beautiful mathematics. It actually started from a problem which for me gives an example of this interaction of mathematics with physics. I may now be answering your previous question a bit better. I spent some time studying critical percolation processes. Percolation models are the simplest models where we can describe the phase transition, critical behavior in a rather, to which you can arrive in a rather simple way. It became clear that you would like to know the scaling limit of the model. Now, how do you describe the continuum limit of a discrete lattice of variables? Intuitively, you would think that every site of the continuum, it’s becoming too mathematical. To jump over details, I think our mathematics is very limited, mathematical analysis is limited by the fact that we can deal with mathematical concepts which are based on a countable collection of degrees of freedom. If you would like to take scaling limits of random functions, you may envision a function for which the value at every point in the continuum is another random variable, independent random variable. There are no such functions in the mathematical world. We cannot have uncountable collection of degrees of freedom which are independent. It’s very limited in this sense. It’s a little secret like the Pythagorean had, that’s our secret of mathematics. It enables us to describe very well but a small patch of reality, so trying to think about scaling limit of a discrete model. What is continuum? It makes one realize that a point in the continuum in a scaling limit actually encloses the entire world which collapses into that, not a single degree of freedom. I hope the idea is clear. If I start from a discrete partition of say, a unit square, for each lattice side you associate some interesting variable, for example in percolation model, a bond may be allowing conduction or not, and then you look at the paths which are formed along open bonds. If you study the global behavior of those paths, from the macroscopic perspective, you have a continuum model and the question is then how to capture it mathematically. You find that you can look at this system from microscopic or macroscopic perspective and whichever perspective you take, you lose a lot of information. Trying to formulate a mathematical language for the continuum description of this model, led to, well this was a joint work with Almut Burchard, led us to consider spaces of random curves as a description of families of random curves, as a description of scaling limit. Or that Schramm had another idea, which in two dimensions works superbly, and that has led to the Stochastic-Loewner Evolution. Nowadays, there are people who are working in the field. They are working the well formulated area of properties of random curves with some conformal invariance properties. But for me, what makes it most fascinating is the connection between the precise and beautiful mathematics and the reality which actually is the richer reality of the model which this just captures part of it. So this has been a successful story in the sense that questions which started from attempts to characterize critical behavior led to very lucid, beautiful mathematics, although this mathematics captures only a small part of what you are trying to understand.

TPL: This echoes the statement you make at the very beginning about the physical richness and the tangent space.

MA: Yes, I should mention that as you know, the last two rounds of Fields Medals were given for work in this field, Werner and Smirnov.

TPL: So this also points out the nature of Fields medal in some sense but you don’t spell it out. That is a very beautiful story you just mentioned, very beautiful and also philosophically makes one ponder. Indeed, it also echoes your statement that different people have different sensitivity.

MA: Present challenges let them peak upwards, or resonate with them.

TPL: You come back to Taiwan again, at better weather. Thank you very much.

MA: Thank you very much.

- Tai-Ping Liu is a faculty member at the Institute of Mathematics, Academia Sinica.