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 Sometimes we continue an obsession with a mathematical or physical question, long after the reason for the question is obsolete.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.


2 thoughts on “What Should I Work On?

  1. Your A seems implicitly too restrictive. Lots of people work on little problems that are useful in other parts of Physics. Surely one can even work on something for its own sake (not useful to anyone?) if you are careful to keep up your skills and knowledge of other fields.
    Your C needs expansion, I think, to note that doing something else for a while can let you come back to the problem able to see why you couldn’t make progress, see holes in the argument as you had it, etc..
    B and D are closely related in my experience. One realizes that the current path is not so good, it’s all a little depressing (more than a little if it’s been six months one could almost call wasted), goes back a few steps, figures out a new path, … It’s nice to have several paths forward at once, but I’ve not often had more than a couple that I’ve been able to see. Something also to take into account is that having machete’d a long way through a rainforest, one has to be able to motivate other people to come to a hidden temple (or to a newly discovered orchid, or something of even more specialist interest) and to lead them there; having a map will definitely help with that. I like the rainforest analogy as a complement to Lee Smolin’s mountain tops and foggy valleys. I particularly like that the reasons for something interesting in the rainforest being where it is are more subtle than it just being a high place (it’s good to have more than one wild analogy to avoid being too carried away by any one of them).
    As important as E is, my perception is that in most fields there are those useful people who span the gap between theorists and experimentalists; certainly physics seminars can be almost anywhere on the spectrum, as each person’s preference and experience takes them (although research groups can get in a rut towards one or the other in their invitations to give seminars). Also, E can be difficult insofar as the further a new theoretical approach is from current experimentalists’ phenomenological thinking, the more useful its reconceptualization might be (given that its models /are/ useful), even as it becomes more difficult to show people how it can be useful.
    Thanks for the post.


    • Hi Peter,

      Perhaps I should have emphasized that the list I gave was not very rigid. I basically agree with what you say. I suppose that both A and E mean that you have something big in mind
      for your research. It doesn’t mean that you have to follow fashion. In fact, looking at big questions often means you can’t follow fashion entirely. I didn’t mean that occasionally doing a problem just for fun is a bad idea either.

      I completely agree with the value of returning to a problem that previously eluded solution.


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