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«ADVENTURES IN PHYSICS AND MATH Edward Witten From a young age, I was fascinated by astronomy. This was not exceptional because the late 1950's were ...»

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Edward Witten

From a young age, I was fascinated by astronomy. This was not exceptional because the late 1950's were

the start of the space race and everyone was excited about space. I really cannot remember how much my interest in

astronomy predated the space race. At the age of about nine or ten, I was given a small telescope (a three inch

reflector) and one of the highlights of my growing up was to see the rings of Saturn. Something that puzzles me in hindsight is that in those days I thought Saturn was hard to find. By now, having assisted several children with their own small telescopes, I am quite aware that Saturn is one of the most obvious objects in the sky and easy to find from almost anywhere on Earth in any small telescope on any clear night when it is above the horizon. It will not look like it does in a professional photo, but it is a striking sight through any telescope.

As a youngster, I dreamed of growing up to be an astronomer, but I was also very much afraid that by the time I was an adult, astronomers would have to live and work in space. This sounded dangerous to me. Looking at how things turned out half a century or so later, we see that space satellites play a very important role, but the astronomers who develop them and use them stay safely on the ground. I suppose that the repair of the Hubble space telescope by astronauts is one of the very few cases in which work related to astronomy has been done by humans actually working in space. Incidentally, though space telescopes play a substantial role, ground-based astronomical observations are certainly still very important.

At about age 11, I was presented with some relatively advanced math books. My father is a theoretical physicist and he introduced me to calculus. For a while, math was my passion. My parents, however, were reluctant to push me too far, too fast with math (as they saw it) and so it was a long time after that before I was exposed to any math that was really more advanced than basic calculus. I am not sure in hindsight whether their attitude was best or not. However, the result was that for a number of years the math I was exposed to did not seem fundamentally new and challenging. It is hard to know to what extent this was a factor, but at any rate for a number of years my interest in math flagged.

Eventually, however, I understood that math and theoretical physics were the fields in which I had the most talent, and that I would really only be satisfied with a career in those fields. I was about 21 years old when I made the decision between mathematics and theoretical physics, and I made this decision based on very limited knowledge about either field. My choice was theoretical physics, in large part because I was fascinated by the elementary particles.

This was in the early 1970's. For a twenty-year period, beginning roughly when I was born, there had been an amazing succession of discoveries about elementary particles. At the beginning of this period, the proton and neutron and the atomic nucleus had been the smallest things known. The modern concept of elementary particles barely existed. But beginning around 1950, there had been an explosion of discoveries. This had resulted mostly from new technologies, especially but not only the ability to make particle accelerators in which elementary particles are accelerated artificially to very high energies.

In short, when I started graduate school at Princeton University in the fall of 1973, the study of elementary particles had been in a state of constant tumult going back at least two decades. But beneath the surface there was the potential for change. What we now know as the Standard Model of particle physics had been written down, in essentially its modern form, in a long process that had been essentially completed, just a few months before I started graduate school, by David Gross, Frank Wilczek, and David Politzer. (David Gross was later to be my graduate advisor.) The period of perpetual revolution in the world of elementary particles actually continued during my graduate days. One of the biggest discoveries of all was announced on November 11, 1974. This was the discovery of the J/ψ particle. Though its lifetime is far less than a nanosecond, it was astonishingly long-lived for a particle of its mass and type. It was such a dramatic discovery that it led to a remarkably speedy Nobel Prize for the heads of the teams that made the discovery, and people used to talk about the November revolution in physics. To those of you who are too young to remember the Cold War or who might want to brush up on your history books, let me just say that there is another event that used to be called the November revolution.

Anyway, by November 1974, I had just about learned enough about elementary particles that I could understand what the excitement was all about and what people were saying, but not quite enough to participate prominently. After what looked to me like some initial confusion, it was realized in a few days that the J/ψ particle

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I have gone into so much detail about this to try to explain what my interests were as a graduate student in the mid-1970's. In short, when I was a graduate student, the era of perpetual revolution in particle physics was still in full swing. I assumed it would go on and I was hoping to participate in it. But in hindsight, the quick success in understanding the J/ψ maybe should have been a hint that the scientific landscape was going to change. In fact, it turned out that the surprising properties of this new particle made perfect sense in the Standard Model, and even had been predicted before, though I don't know how well known the papers making this prediction had been. Certainly I had not known about them.

Meanwhile, I developed another interest as a student, which in a way contained seeds of some of my later work. Here I should explain to those of you who are not physicists that one side of what theoretical physicists do is to try to understand the laws of nature, and the other side is to try to solve the equations in different situations and work out predictions for what will happen. The separation between these two sides of the subject is not always so clear. For example, there is no hope to understand what are the correct laws of nature without at least some ability to solve them and find their predictions. But in practice, much of what physicists do is to try to understand the behavior of matter in situations in which, at least in principle, the appropriate equations are known. This can be easier said than done; for instance, it is one thing to know the Schrodinger equation, which describes the behavior of electrons and atomic nuclei, and another thing to solve the equations and understand the behavior of a piece of copper wire.

As a particle physicist, my main goal in principle was to understand what are the fundamental equations.

However, the emergence of the Standard Model created a novel situation. Some very new fundamental equations were in the process of being established just as I began my graduate studies, and some of them were really very hard to understand. In particular, the Standard Model said that protons, neutrons, pions, and other strongly interacting particles are made from quarks, but no quarks were to be seen. To reconcile the contradiction, one had to believe that quarks are “confined,” meaning that no matter how much energy one pumps in, quarks can never be separated.

The catch was that the Standard Model equations that are supposed to describe quark confinement are opaque and difficult to solve. So it was hard to understand if quark confinement would really happen.

Understanding quark confinement became my passion as a student and for a number of years afterwards.

But it was a very hard problem and I did not make much progress. In fact, in its pure form of demonstrating quark confinement using the equations of the Standard Model, the problem is unsolved to this day. To be more precise, from large-scale computer simulations, we know that the result is true, but we do not really have a human understanding of why.

I gained a couple of things from this experience, even though I was not able to solve the problem I wanted.

One was negative. I learned the hard way what I regard as one of the most important things about doing research.

One needs to be pragmatic. One cannot have too much of a preconception of what problem one aims to solve. One has to be ready to take advantage of opportunities as they arise.

Reluctantly, I had to accept that the problem of quark confinement that I wanted to solve was too difficult.

To make any progress at all, I had to lower my sights considerably and consider much more limited problems. (As I will explain later, I eventually made a small contribution to the problem, but this was almost 20 years later.) On a more positive note, in accepting this and making what progress I could on more limited problems, I began to get some experience thinking about what physicists call the strong coupling behavior of relativistic quantum systems – the behavior of these systems when the equations are hard to solve by standard methods. This experience became important in my later work.

Here I should again explain to those of you who are not physicists that when the coupling is weak, everyone who goes to graduate school in physics learns what to do. When the coupling is strong, a large variety of questions and methods come into play. As a result, I am not sure that there is any such thing as being an expert on how quantum systems behave for strong coupling, and in any event certainly I myself never have become such an expert. I have learned quite a bit while always feeling like a beginner.

In 1976, I completed my Ph.D. at Princeton University, and moved to Harvard University for what proved to be four years of postdoctoral work. It was also a very eventful time personally. Chiara Nappi, whom I married in

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At Harvard, I learned a lot from many of the senior professors, originally the physicists and then some of the mathematicians as well. I do not want to go into too much technical detail but I will try to give a flavor.

One senior colleague at Harvard was Steven Weinberg, who was a Standard Model pioneer (and 1979 Nobel Laureate). There were certain fundamental topics in physics that I had had trouble understanding as a graduate student. I think Steve thought that many of the physicists had some of the same confusions I did. Whenever one of these topics came up at a seminar, he would give a small speech explaining his understanding. After hearing these speeches a number of times, I myself gained a clearer picture.

I also learned a lot from Sheldon Glashow and Howard Georgi. Glashow was a senior professor and another Standard Model pioneer and 1979 Nobel Laureate. Georgi was a junior faculty member, just a few years older than I was. In fact, office space was scarce at Harvard and Georgi and I shared an office.

Glashow and Georgi, among other things, were experts at building models to explain the results coming from particle accelerators. I learned a lot from them, and had the age of perpetual revolution continued, I probably would have aimed to learn to do what they did. But as I have already hinted, the nature of experimental progress was changing at just this time. Great advances have continued, in areas ranging from neutrino physics – which is well developed here in Japan, by the way – to cosmology. Important new particles have been discovered, most recently the Higgs particle. But rather than perpetual revolution, the surprise coming from particle accelerators during these decades has been the fantastic success of the Standard Model. It works much better, and at much higher energies, than its inventors must have anticipated.

Although I certainly did not realize this at the time, the changing landscape meant that I would find more opportunity in somewhat different directions. That is why my interaction with yet another senior physicist at Harvard, Sidney Coleman, proved to be important. He was a legendary figure for his insights about quantum field theory, and was the only one of the physicists I have mentioned who was actively interested in strong coupling behavior of quantum fields. The others appeared to regard such questions as a black box, not worth thinking about.

On a number of occasions, Coleman drew my attention to significant insights that I think I would otherwise just not have heard about, or at least not until long after. Often these insights involved fundamental mathematical ideas about relativistic quantum physics, or its relationship with other areas of modern mathematics. There are many topics that were important in my later work that I had simply no inkling of until I learned about them from Coleman.

At the time I could not make much sense of what I was hearing, but luckily I remembered enough that it was useful later. Just to give one example, I can remember Coleman explaining to me an insight, originally due to the Soviet mathematician Albert Schwarz, that certain surprising results of physicists working on the Standard Model actually had their roots in the “index theorem” of Michael Atiyah and Isadore Singer. This was actually a major theorem of 20th century mathematics, but I had never heard of it, or even of the concept of the index, or of the names Atiyah and Singer.

I should explain that although in the seventeenth, eighteenth, and even much of the nineteenth centuries, mathematicians and physicists tended to be the same people, by the twentieth century the two subjects had appeared to go different ways. This happened because mathematics made advances that seemed to take it far away from physics, but also because physics after around 1930 had moved in directions – involving relativistic quantum field theory – that seemed too difficult to understand mathematically.

My graduate education in physics had occurred at a time when there was not much engagement between cutting edge mathematics and physics. Like the other physics graduate students I knew, I had not learned the sort of things one would want to know if one wished to grapple with contemporary questions in mathematics. It was typical of a physics graduate education of the time that I had never heard of the Atiyah-Singer index theorem or most of the other things that I heard about from Coleman.

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