Interview Editorial Consultant: Tai-Ping Liu
Interviewers: Tien-Yien Li (Li), Jann-Long Chern (Chern), Bau-Sen Du (Du), Yi-Chiuan Chen (Chen)
Interviewee: James A. Yorke (Yorke)
Date: May 17th, 2005
Venue: NCTS, Hsin-Chu, Taiwan
Professor James A. Yorke was born in USA in 1941. After graduated from Columbia University in 1963, because there was a cross-fields research opportunity offered by the Institute for Physical Science and Technology (IPST) of the University of Maryland, he continued further study in the University of Maryland. He got a PhD degree 3 years after and became a member of IPST. He was the research director of IPST for 16 years and currently is a Distinguished University Professor of University of Maryland (both in the Department of Physics and Mathematics). Professor Yorke was most known by his published article “Period Three Implies Chaos” with Tien-Yien Li (His PhD student in 1969-1974, graduated from National Tsing Hua University and currently is a Distinguished University Professor in Michigan State University). In this article, they first gave a clear definition and pioneered the research of chaos. Professor Yorke’s main research interests are chaos theory, weather forecast, genome research and the diffusion dynamics of HIV/AIDS virus. He has fundamental contributions in dynamical system, and won the Japan Prize in 2003 with Benoit Mandelbrot of Yale University, by their contributions in Science and Technology of Complexity.
Chen: Firstly, we thank you for agreeing to do this interview. Usually, we start from your mathematical background. For instance, what brought you into the field of Mathematics or the field of Chaos?
Yorke: When I was in high-school, there were several popular books written by well-known scientists, which were not technical books but aimed for high-school students. I read one particular collection of books by Norbert Wiener. He talked about how the atoms in the atmosphere bounce around against each other in complicated ways and this is a kind of "chaos" .....
Chen: Did he use the term "chaos"?
Yorke: No. But he talked about complicated motions. From this I became familiar with complicated motions about how two balls collide and bounce apart. When you change the angle just a little bit, the outgoing angle will change a great deal. So, life is filled with situations where small changes result in big changes. People have car accidents, for example, but if they have started the trip ten seconds earlier or later, probably they would have no accident. Therefore, a very small change makes a big change. In high-school, I like to read these popular science articles by many people, including Albert Einstein. So, I was actually much more influenced by these individuals than by my teachers. The people I thought worth emulating were the people I read about. There is a book "Men of Mathematics" by E.T. Bell that talks about many famous mathematicians and what they did. Some of what they did is a bit complex to explain, but some of them you can understand. This is how I got interested in many areas of mathematics. Later on, when I started studying papers which talked about situations that are chaotic (they didn't call it that), I recognized they are related to what I read about in high-school. So, this is the background how I got interested. We had a visitor from Poland, Professor A. Lasota. He had ideas. He talked about probabilities. When you start off, you might leave a house over a range of one minute, and as you follow forward in time, you see how the different possibilities occur. Maybe in 10 percent of the cases you have a car accident, ending up with in hospital. Another 10 percent, perhaps a boy might meet some girl whom he never met before and becomes very attracted, just by chance. So, the way it involves becomes more and more complicated. All involve probabilities. This is another thing that Wiener also talked about. Try to keep track how different things happen in different probabilities.
Du: Both Wiener and Lasota talked about probabilities, right?
Yorke: Yes. So, when Lasota came to America, talking about the probabilities, it was an idea that I was familiar with. After I had my PhD, I saw a paper by a meteorologist, Edward Lorenz. It was about a system of three coupled differential equations (now is called the "Lorenz systems") which has a very complicated behavior. In the paper, Professor Lorenz did many interesting things and came up with a number of interesting ideas. I showed it to T-Y Li, and we wanted to understand what was going on. Trying to understand this paper was our motivation for coming up with the idea of "Chaos".
Li: In the two dimensional system, we have the Poincare-Bendixson theorem. It says that, roughly, a bounded trajectory will eventually become periodic. Traditionally, people believed we should have similar things such as quasi-periodic or almost periodic trajectories in higher dimensional systems, but nobody could prove it. In other words, people basically believed that bounded trajectories can be followed in a regular way. The main point of the Lorenz equations is that, in the three dimensional case, there are bounded trajectories which are eventually totally untraceable. These orbits are attracted into the so called "Lorenz strange attractor", a set that attracts some 'strange' orbits. From the paper, Jim is the one who came up with the idea of chaos: it is not some computational error but can be prove rigorously that trajectories can eventually be untraceable.
Chen: So, the term "chaos" was inspired by the Lorenz equations.
Yorke: Right. I was inspired by Lorenz.
Chen: Now Dynamical Systems has become a very big field. Could you provide some advices for students who are interested in entering this field?
Yorke: I think people in Dynamical Systems have a big advantage over people in certain areas of pure mathematics. In order to come up with new ideas, people have to imagine something new that no one has imagined before. In those areas, there have been many people trying to imagine these things before, so it is very hard to figure out how you can come up with something new. What I recommend is doing numerical studies. Gauss in the early 19th century spent huge amounts of time making numerical studies. Now, we can make studies millions of times faster, but many people don't do numerical studies. This is absurd. Two people are working on the same problems, and one is trying to find out what is happening by using numerical studies. That person is much more likely to be successful if other things are equal. When you make numerical studies, you often see surprising results (results that surprise you). You are challenged to understand these surprising things that you see. This becomes a way of doing research. One way of thinking about research is trying to find ideas that surprise people. I find working with computers is a very big help in getting new ideas. This is just like when Penicillin was discovered. Fleming did not start out trying to discover Penicillin. He noticed something which was surprising to him, not something he thought in his own mind, but something he saw outside, then he pursued the idea and discovered that the mold, the Penicillin mold could kill bacteria. In fact, other people took this idea much further than he did, but nonetheless it was stimulated by something he saw. How do mathematicians see things in the external world? The answer is by making numerical studies. So this is what I recommend. There are computer programs like Matlab, Maple, Mathematica, etc, you can make many kinds of investigations.
Chen: So, in this direction, would you think that having collaboration with experimenters is also important?
Yorke: That could be. But experiments are slow. It is much faster to do numerical experiments. So, I would emphasize that people do their own numerical experiments. And I would recommend that if they don't want to do numerical experiments, then they find a field in which they don't have to, something easy, like Brain surgery (all laugh)
Chen: Even in the very pure areas of Dynamical Systems or Mathematics..
Yorke: Gauss worked on the prime numbers in the number theory, and he did a lot of computations. There has been no greater mathematician than Gauss, but he had no computers. Why did Gauss do these? Was he stupid? I don't think so. Now it is so easy to do computation, but many people do not. Perhaps they feel that mathematics is a field in which they could avoid computers. I don't believe that. But, they have to understand the results the computer is producing, the graphics, pictures or numbers. They have to work very hard to understand what is going on. If they see something strange, they have to try to understand that. So the computer is not doing the research; they are doing the research. Gauss came up with some formulas and he tried to experiment different kinds of formulas to see what kind of properties he had, then he found some particular formulas which have interesting properties. It would be so much easier for Gauss if he had a computer.
Chen: What are your opinions about developing ideas in Dynamical Systems?
Yorke: One of the things about Dynamical Systems is that all scientists should understand Dynamical Systems is about how things change. But not all mathematicians have to know this, only very few mathematicians have to know how things change. So, when a mathematician starts trying to find ideas, the natural audience is the audience of chemists, engineers and physicists. So you should try to develop ideas that help scientists. Physicists may come up with a formula that they think it is true, and they go on. Then mathematicians try to prove this formula. After a couple of years, he or she proves the formula is true, but the physicists don't care. The physicists say that they thought it is true anyway (so they did not need a proof). So, the role of mathematicians should be to lead the scientists, not to follow the scientists. Our goal should be to help the scientists, tell the scientists some things that the scientists don't know. That is my view. It is often very useful for mathematicians to work together with someone in other areas, to collaborate. If a mathematician is going to write a paper for chemists, then it helps to collaborate with a chemist to find arguments that chemists can understand. If a mathematician tries to write a paper to interest biologists, how does the mathematician know what to say? A mathematician thinks one way, but a biologist thinks another way. He may have the ideas he wants to express, but he doesn't know the way of writing to interest biologists. For this reason, it is very worthwhile to collaborate with scientists.
Li: I do not know if you all agree with what Lasota says. He said “You can solve a stupid problem to get a Fields medal." I think he tried to emphasize that the so called "difficulty" of a problem doesn't mean the problem is significant. A difficult problem, which might be important, is not equivalent to a significant problem. I have met many outstanding mathematicians, and my experience is that Professor Yorke probably is the one whom I trust most in determining what sort of problems are the most important and most worthwhile to pursue. So I would like to ask, how do you judge what problems are worthy pursuing or what problems are the most significant?
Yorke: I think you would agree that mathematicians feel that there is a shortage of good problems. So, if there is a shortage of good problems and someone wins a prize for solving a good problem, why not give a prize to the person who came up with that question? Don't give it to the person who solved it. (All laugh!) We should have a prize for Fermat even though he has been dead for three hundred years. Many people think that a great mathematician's work is to solve unsolved problems. If it was the case, then no new problems would ever come about. Instead, the way I think is that one has to come up with questions, simple questions, and you try to understand the situation. But you must continuously change the problem that you are trying to solve. You must put together what you understand. Putting together what you understand means putting together a question and an answer. You really only have a good question when you have a good answer. This is very different from the idea of working on famous unsolved problems. Coming up with new questions is what scientists really have to do. All scientists, all mathematicians have to come up with new questions. You come up with new questions by understanding some ideas that you try to put together. You try to put together two halves of a coconut which contains the kernel of the idea. One half is the statement of the question, the other half is the proof, but inside is some understanding that has been incorporated inside the coconut - two halves of the coconut, and whole the idea. You must find both halves of the coconut. You must find the question to ask and the method of answering it. You may start off one question and come up with some idea for answering, but it may not really answer that question, so then you change the question. At the same time, you have to say "What do I really want to know?" I say that people should spend half the time asking themselves "What should we be asking?" Not the first half, but on-going questioning. You never settle on a question until you have the final answer. That is the way I think mathematics should be done.
Li: This is just the first half, how about the second half? Usually, what kind of intuition makes you decide which ones are most worthwhile to pursue among so many problems. For example, at that time you said finding Brouwer's fixed points by numerical methods is definitely worth pursuing. To be pretty honest (laugh), at that time I didn't know why this problem was so important, I just followed your suggestion to do it.
Yorke: I have asked myself a number of times, and I several times changed my answers of what a good question is. One answer is: can you come up with an idea that surprises people? That's one. Or can you come up with an idea that people need?
Li: For the Brouwer's fixed point problem, when we published our results, I thought perhaps we would be the only persons doing this, but, it turned out that there have been a bunch of people working on this problem now. How did you know .....
Yorke: Some people do researches by looking at the works of famous persons, then, they try to do better.
Li: This is definitely wrong, according to you.
Yorke: Right, this is not a good approach, because the famous person may not write down why they think this question is interesting. In mathematics, there is a big shortcoming that they do not write down why they think a problem is interesting. They often just write the results. So, then somebody tries to follow it without understanding why the question is interesting. Often, the question is not a simple question. So, they do better than the famous person, and get no one to pay any attention. I call this "one-ups-man-ship". It means that, for example, you jump 8 meters, I try to jump 9 meters. If there is no importance to jump 8 or 9 meters but I try to do better, this is called one-ups-man-ship - do one more. There is no content to this. I think it is important to try to work on questions which you feel are important to answer. Now, as T-Y Li said, maybe no one will pay attention, but at least you believe there is a reason for studying it. Now, if someone jumps 8 meters and becomes famous, and you jump 9 meters and you don't become famous. Well, perhaps there was a stream that was 7 meters wide, and he wanted to jump 8 meters to cross it, then there is no point to jump 9 meters. OK? If you jump 9 meters just to do one meter more than someone else, and if no one pays any attention, then you are lost. Because you've done something which has no real purpose and no one pays attention. So, I think trying to convince yourself that you have important problems to work on, important things to say to a big audience, is quite important for being able to continue doing research. So you must always ask what your audience is. Some people who do mathematical biology say their audience should be biologists and mathematicians when they write a particular article. That almost guarantees failure. Because they cannot write something that both audiences will understand and appreciate. It is better to write two articles, one for the biologists, and one for the mathematicians, saying somewhat similar things but in a way that is appropriate for the audience.
Li: You told me that you have seen in your career a lot of things coming up and down, up and down. For example, in the beginning of your career, there were 'control theory', 'meta-stability', 'bifurcations', 'delay equations', etc, etc, then `chaos'. I remember that in 1982 I asked you that the chaos is so popular now, will it last? And I remember clearly that you said "I do not see any reason it won't last".
Yorke: People will get the basic ideas and those ideas will be applied. There might be other ways which people can continue doing research, but the ideas of chaos will remain valid, and they will have to be used.
Li: Let’s change the topic. Nowadays, for example, the financial mathematics is a `hot' field, but how long do you think this (hot field) will last?
Yorke: Right, if people want to know what I think are some good hot areas, they can look at my web-page, which is "yorke.umd.edu". On there, I have current projects that I am working on. One of our topics is 'weather prediction'. Weather prediction is taking the current world atmosphere and trying to extrapolate the future. That is what weather prediction is. Our group is trying to come up with better ways of figuring out what is the weather NOW all over the world. This is our main idea. And to use nonlinear dynamics not just to do that but also to come up with better ideas of weather prediction. This is an important problem, but this is also a hard problem. So, we work in a group. There, the ideas of chaos are certainly present. We hope that we will produce in the next couple years important ideas people use worldwide for figuring what the initial condition is. There are other people working in this field too, they will certainly contribute their ideas, but we hope to have a really impact on how this is done. Another project is about HIV virus. Earlier this year my collaborators and I wrote a paper on how infectious HIV virus is. In our paper, we completely revised the answer, and we published it in a medical journal. This is an important area. We tried look at this as an epidemic breaking out, so it is growing very rapidly, and tried to understand the properties as it grows rapidly. There is a little bit chaos-like behavior over there, but it is mainly the growth, the exponential growth. Another topic we are interested in is how to figure out what genomes are like, trying to understand the sequence of genomes. People are already doing this, but we want to find better methods. And we hope in a year or two, to be able to figure out what genomes are with fewer errors than other people. Maybe we will succeed, maybe we won't. And we work in pure mathematics areas. So, I am working in many different things, many different topics at the same time. This, I do not recommend, because it means each area goes relatively slowly. But this is the way I work. This year is the hundredth anniversary of Einstein's famous year of 1905, in which he wrote four very famous papers. His four papers are very different from each other. So, these were some stuff I read since I was in high school, not the papers, but about Einstein and what he did, the non-technical parts. So I always feel that, well, maybe I could work in different areas at the same time, certainly not at Einstein's level, but just work on different things at the same time. Working on different things, you get different ideas, and the ideas help each other. If you are going to work on cell dynamics in biology, and you will find that when you are working on cell dynamics, what you have previously learned will be helping you. It will bring new ideas into this area, but other people in that field don't know. Of course, there are a lot of things that you don't know, but they do know. So, it becomes tricky. I just like to find some interesting problems that I think I can say something about and get people interested in them.
Li: With regard to the so called 'hot' fields, what you said is not to bother about the hot fields .....
Yorke: Hot fields..... Yes, you see in genomes what we are trying to do is called 'whole genome shot-gun assembly'. You take a big genome, perhaps with 3 billion letters of A, C, G and T, and you break it into lots of overlapping pieces of DNA; then you have to try to put these pieces together. This is not a hot field, even though people have spent huge amounts of money using this technique. It is not a hot field because many people feel it is a solved problem. But it should be a hot field:. Cetera Genomics was a company that used this technique to put together a.'"draft” of human genome, meaning there are errors in what they did. Some people say it is a solved problem as how to put these pieces of DNA together. This is like saying that when the Wright brothers in 1903 flew an airplane for two hundred feet, they solved the problem of heavier-than-air flight. But, of course, flying two hundred feet is not too useful, so now we have made progress AFTER the problem is solved. So, as T-Y said, this is not a recognized hot problem, so there is NOT a lot of competition. Perhaps I should have said that people can look at my web page to see. some examples of what I think should be hot problems
Chen: So, whether a problem is hot or not depends upon competitions.
Yorke: Yes. Very often in biology, people will say, oh, something is a great problem, without looking at available answers. But I want to put answers and questions together at the same time One of the things we have been working on in the past year is when somebody takes these genome pieces and puts them together, how correct the job has they done. And we come up with a new approach that detects hundreds of errors. When we detect the errors then we know something that nobody else knows; where the errors are. We can then find out why we made errors there, and can try to fix these. But this is a question which is not asked in any detail: how you find the error in the draft genomes.
Li: But why did you choose this problem?
Yorke: (Laugh ....) Well I read a newspaper about how a group had put together the genome of a species of bacteria for the first time. It was a news article, saying they have done this. And I figured that, well, see they broke the DNA into lots of overlapping pieces, and then they put them together. And I felt possibly they didn't do the best possible job, while they did a great job. There is a difference between doing a great job and the best possible job. So, I felt if my students would find this interesting, then we could try to do a better job. So, it was initiated simply by reading some newspaper. I try to read all popular articles about many kinds of sciences, to try to find out what is going on, and try to come up new ideas, that way.
Chen: This is your second time visiting Taiwan, how do you think the research in Dynamical Systems or in Nonlinear Dynamics here?
Yorke: It is getting better, and is making considerable progress.
Chen: Could you give some advice on how Taiwan can build a strong group in dynamical systems, or in nonlinear dynamics?
Yorke: They must do numerical experiments on whatever interests them, and the same as groups of people in number theory and other fields.
Chen: Do you mean numerical simulations?
Yorke: Numerical studies, of some kind relevance, perhaps simulations.
Chen: Why do you think so?
Yorke: It is because it is very hard for people to come up with new ideas. People can look around and see things and try to explain them. What we do as a mathematician is to do numerical studies and see what comes out with numerical studies. Think it this way, when you are running a marathon, will you wear shoes? Doing mathematics without computers is often like running a marathon without shoes. You don't get very far.
Li: In 1960, a marathon Olympic champion, Abebe Bikila, run without shoes. However, four years later, he got the gold medal again with shoes. (All laugh.)
Yorke: There was another marathoner named Emil Zatopek, who is a very famous marathoner and also an Olympic champion; He wore army boots. People tried to copy his technique, and they simply got sore feet. So, it may not be good to copy what other people do, either running without shoes or running with army boots.
Li: Here is a related question. If here comes a group of students with very high potential to become big shots in the future. If they are brought to you and ask you to lead or guide them, what is your best suggestion?
Yorke: I have no idea about the best suggestion. But, one should not try to be in one field. See, in nonlinear dynamics, it seems like there are so much you have to know, then you cannot start. You have to know Probability Theory, you have to know Numerical Method, and you have to know Topology, all kinds of areas. But, if wait until you learned all those things, then you would not get started. So, I think people should start trying to work on small research projects before they know all of the 'required areas. They should just try to come up with their own ideas. Unfortunately, in America and most other places, when a student becomes a graduate student, they must spend a number of years studying old ideas before they can start exploring new ideas. I would prefer people start trying to explore new ideas to surprise themselves as early as possible, not wait until they have learned a huge number of materials.
Li: I have been repeating to my students all the time what you said to me, "If you want learn it, do it."
Yorke: Right, if you want learn it, do it. When you try to work in a problem, it is important to learn what you need to know. When you take a course, often you don't understand why it is important. It doesn't really become a deep part of your brain. It doesn't get deeply embedded, it is surface embedded. Whereas, if you are working on a problem, then you need these ideas and they become part of your understanding. So, it is much better to learn things as you go, as you are working on problems.
Chen: So, you get at least a reason why it is important.
Yorke: Understanding why it's important, yes. Of course, it might be important for different reasons, but just being taught in the course may not be adequate. You really want to know how it relates to everything you know, rather than how it relates to a little bit of what you know.
Chern: For our readership, can you give some further descriptions about what the "chaos" is.
Chen: Since you are the namer of the term "chaos".
Yorke: Chaos is what you see all round you, every day, where small changes will produce big changes. What we saw in our mathematics was that the same kind of things could be true. In simple dynamical systems, we could see the same thing that small changes result in very big changes. People have been used to be thinking about mathematical trajectories as bullets shot out of a gun. If you change the direction of the gun a little bit, the direction of the bullet changes a little bit, and where the bullet goes changes a bit, but there is not a big difference. Whereas in billiards, when you bang one billiard against another, if you change how you send a first billiard ball off a bit, the way the second billiard ball goes is very different. So we say that chaos is "sensitivity to initial data" — small changes in initial situations produce big changes. We saw in the mathematical situation the same kind of thing as we saw in the world around us. That's why we called it chaos. Just think about how big a change it would have been when you were conceived to have become an opposite sex. Think how different the world would be if all the people we know had been born the opposite sex. A little change can result in a big difference in outcome.
Li: In other words, it is difficult to predict or unpredictable.
Yorke: So, it is predictable in the short run, but not predictable in the long run. I sometimes say that people who are successful are good at "plan B". You may have a plan for what you want to do, and very likely something will happen which prevents you from succeeding in plan A. Chaos theory is saying that your complicated plan may fail for some reason, therefore you must be ready to change the plan to plan B. So chaos theory implies that it is important to plan, but your plan should be very simple, and you should be ready to change the plan. That's why I said "successful people are good at plan B", because they would often have to change their plans.
Chern: Interesting, it is a very interesting and good idea.
Yorke: I try not to predict very far the future. What is the future in ten years? What I will be going in five years? I don't know. I don't try to plan that far ahead. Li and I got into Chaos by changing our area of interests, then he changes area much into numerical methods, and I change my area another ways. In 1990, my collaborators and I got the idea of working in 'controlling chaos', which many people have been interested in since then.
Chen: A hot area! (All laugh)
Yorke: A hot area, yes. We stopped working in it in about 1994, but other people continue working on it. If I would work on it now, I have to understand all areas of what other people are doing. (All laugh.) So, I think it is better to work on genomes, on HIV (all laugh), or computer networks, or...
Chen: So, when there are many followers, maybe you will change to another area.
Yorke: Right (laugh).
Chern: So, I can say that you have a very "dynamic" research career, right?
Yorke: I tend to like dynamic questions. The genome may not be so dynamic. But, it is interesting and important. I try to say, if you keep asking yourself “Why is this area that I am working on important”, you will probably not be too happy, because you will not be able to get a very good answer to why it is important. Still, it is important to ask. I see people who don't ask, and then ten years later, they are very unhappy. So, it is better to be a little unhappy knowing your work is not as important as you would like it to be than to wind up ten years later realizing that it is not important at all. Important to whom? That is up to you. Why it is important is also up to you. There is no single answer. I like to see if I can get other people interested in these questions. I think it is sad for a mathematician if he or she is working in areas that don't interest people, because science is creation and communication of ideas. I feel that you must be able to communicate your ideas to others; the more people you can communicate with, the better. So, I emphasize communication, not just working on problems and solving problems, but communicating the ideas, because they are important, because they interest people, because they may make people laugh..... I don't care, but so that people would be interested.
Chen: It's really a very nice and invaluable opinion. Maybe we could stop our interview here. Thank you very much again.