What Should I Work On?

I haven’t done much blogging lately (or arguably ever). I have been pretty busy, went to a great workshop in Seattle and another in Madrid, and trying to get details of my travels next year straight (I am on sabbatical for a year). Let’s see if I can get back on track, blog-wise.

Recently a student who took my first-year physics class sent me an email. She is now at a high-powered university and is considering graduate school.

This student has strong interest in both physics and mathematics. She asked me a few difficult questions. Can she make contributions to physics by getting a math degree? Should she become a mathematician? Should she just get a degree in physics? Note: she has done some experimental work, but her inclination is towards theory. This is a talented student who probably has a bright future, so I took the question seriously.

I did not give this student complete answers to her questions, because I am not certain of what they are. I did offer some opinions instead. I offer these again below, after a little more contemplation.

I think that the question, “what should I work on?” is one that all people in our field, not just students, should be asking ourselves. Sometimes we continue an obsession with a mathematical or physical question, long after the reason for the question is obsolete.

Here are my attempts to answer the questions:
1. No, do not get a math Ph.D., if you really want to do theoretical physics. I repeat, do not do it. I know people who say math is better, mainly because you are far more likely to get an academic job. If not risking your future is the issue, I agree that math is better. I don’t see many effective advances in physics coming out of PURE mathematics, however. There is an important role for rigorous methods in theoretical physics, namely in traditional mathematical physics, where theorems are actually proven. Few math departments focus on this subject however. There are connections between analysis, algebra, differential geometry and algebraic geometry (whose usefulness is roughly in that order) and physics, but the typical math Ph.D. advisor will not direct you towards these connections. Or at least, I think he/she won’t. The only math people I have met who do this sort of thing are a minority. There is an emerging tradition of using physics to solve questions in mathematics. If you are interested primarily in physics, however, these may not be the questions YOU want to solve.

2. Having said all I did in 1., let me not dissuade you from doing mathematics. If you pursue a degree in math, do math and enjoy it.

3. Suppose you decide to go to graduate school in physics. Don’t focus just on high-energy theory and especially not exclusively on quantum gravity. The more specialized you are, the less likely you will do something of general interest. You will gain insight into your own research problems by being familiar with concepts in other subfields. Look at other areas of theoretical physics. These are probably more useful to you than pure mathematics, at least in the short term. Learn the math you need, as you need it.

As I wrote above, I think it is beneficial for all of us to ask what we should work on. By this I don’t only mean the choice of physics or mathematics, but what problems to attack. I can’t say much about the experience of others, but I have asked this of myself: and more than once. I did not completely change fields each time I tried to answer it, but I did change my approach on several occasions. During this evolution, I learned a lot of physics (and some mathematics too).

Why is the question “what should I work on?” important?

A. Let’s say you are a practicing theoretical physicist, studying some class of models. Why do you do it? Is it an attempt to answer one of the big questions? Is it because you hope it will lead to an answer of a big question? Or is it because you like it for its own sake? If you answered yes to the last question, I think you are in (figurative) trouble. I enjoy doing technical things, and love solving abstract problems. But it’s not enough. Solving a problem with no greater purpose gives satisfaction, but it is a hollow satisfaction.

B. Maybe you have a clear goal for your research. Macheteing your way through the technical rainforest may not lead you to the fabled City of Precious Metals and Wild Parties. If you have no map of the forest, you need to make one; you can only do this by pushing in many different directions and making trails.

C. Suppose you’ve published lots of papers on some problem and it’s going nowhere. You don’t have a clearer picture of the whole business than you did at the beginning. Know when to give up and try something new.

D. Don’t get too confident that you are on the right path. For example, if you and your friends are working on the same thing, it doesn’t make you or them right in doing so. Are you really doing something significant or are you experiencing the euphoria of conviviality? Don’t take publicity (including self-publicity) seriously.

E. At the back of your mind, remember that there are people out there who do experiments and make observations. What do you have to say to those people? You do not have to be a phenomenologist (god knows, I am not), but you should have some notion of what the scientific implications of your work are.

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Hubris

Now and then, a sense of accomplishment is welcome in my tiny existence. In the greater scheme of things it means little – as Kafka is reputed to have said to Brod, “there is hope, but not for us.” Still, it is nice, if only for a moment. If you are interested, you can find the reason here, or here.

Working on the confinement problem for Yang-Mills theories in lower dimensions, led me to the problem of the principal chiral model in one space and one time (1+1) dimensions. This is a model of an N by N unitary matrix field, of determinant one. Axel Cortes Cubero and I studied this problem at large N, when he was my Ph.D. student (he is now a postdoc at SISSA).

So what is large N? There is a special limit which some problems of high-energy or condensed-matter physics can be solved with. This is the large-N limit, where the number of species of particle is taken to infinity. Actually, there are a few of these large-N limits:

  • The large-N limit of an isovector field with N species. This sometimes goes by the name  “random-phase approximation”. Lots of interesting problems have been solved this way. The Feynman diagrams have a chain-like or linear structure.
  • ‘t Hooft realized that for models of matrices (like the principal chiral model above) the Feynman diagrams became planar. The 1/N-expansion is an expansion in the genus of Feynman diagrams. The original motivation was an approximation scheme for QCD, 1/N=1/3 being approximately zero.

It turns out that it is much harder to calculate anything in ‘t Hooft’s large-N limit than in isovector case. Perhaps that is because the problems ‘t Hooft was considering are potentially much more interesting.

Since the late 90’s, much of the activity in supersymmetric quantum field theory concerns ‘tHooft’s limit. I don’t want to just wax poetically about this, but there has been a lot of progress in superconformal field theories and their deformations.

The principal chiral model is in only two spacetime dimensions, whereas the supersymmetric theories above are in three or four spacetime dimensions. Nonetheless, this model is interesting, because it shares features with QCD that the supersymmetric theories do not. Most important, it is asymptotically free and has massive particles in its spectrum. Furthermore, the solutions Axel and I obtained are complete, going beyond both perturbation theory and strong coupling approximations. These solutions are valid at all length scales.

But there was a difficult snag in all of this. Axel’s and my methods heavily use integrability and the “form-factor bootstrap”. It’s pretty easy to see how correlation functions (or renormalized propagators) look at large distances. Unfortunately, it was not obvious how they would behave at short distances. Moreover, there is a prediction for the short-distance behavior from the perturbative renormalization group; the two-point function behaves like logarithm of the separation squared. I was not at all confident that the form-factor bootstrap in Mr. ‘t Hooft’s limit would obey this prediction (and behave like the logarithm squared). There was no straightforward way to check it, and there were other things for me to do. I felt, however, that I was failing to put the ideas to the test.

Last July I asked an elephant in the Copenhagen Zoo to step on my head, should I be unable to solve the problem. She did not agree, because we could not shake on it (her trunk was too far from the fence). The entire summer, I worked only on this problem. It turned out that the mathematics is related to ideas well-known to statistical mechanicians (Levy flights) and mathematicians (non-integer powers of Laplacians).

In the end, the answer fit the prediction. It’s kind of magical that it worked, since the prediction was made using very different mathematics.

For a few more days, I will feel good about myself. Then I’ll get tired of my hubris. O Goddess Nemesis, mine eyes search for thine sword and shield amongst the constellations.