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July 19, 2005

Advice to the Young

Looking back at my response to Marty Tysanner, it occurs to me that, perhaps, he deserves a more lengthy explanation of why I found the notion, that the panel discussion at String 2005 would affect his choice of what to work on, so utterly wrong-headed.

Update (8/1/2005):

On the off-chance that I’ve failed to convince Marty that he’d be better off throwing I Ching sticks, he can read Dennis Overbye’s summary of the panel discussion.

First of all, one ought to dispel the notion that choosing a speciality to work on is akin to taking Priestly Vows. You should be prepared, indeed even expect, to radically change course, perhaps several times during your career. This is not, contra Luboš Motl, following fashion. It is an appropriate response to new information. Revolutions (or, at least, small coups d’êtat) do occur, occasionally and unpredictably, in physics. And you should be prepared to change course accordingly.

My own decision, which so disappointed Luboš, to change directions midway through graduate school came about as follows. Soon after starting graduate school, I went to see Howard Georgi. “What are you thinking about?” he asked me. I rattled off several things that seemed interesting to me, ending with, “… and quantum gravity.” “Don’t waste your time!” he barked, “There’s no decoupling limit in which it’s sensible to consider quantum gravity effects, while neglecting other interactions. Unless you know particle physics all the way up to the Planck scale, you can never hope to say anything predictive about quantum gravity.” Howard was, of course, completely correct1. And so I bit my lip and dropped quantum gravity from my list of problems to think about.

Later, when string theory came along, it promised a unique (or nearly unique) UV completion of a theory which could accommodate both gravity and the known interactions of particle physics. In a surprising and nontrivial way, Howard’s objection was circumvented. Quantum gravity, at least in the context of string theory, became something sensible to think about. So I reordered my list of priorities…

There are lots of things which could, just as radically, reorder your list of priorities. If we knew what the “Next Revolution” was going to be, you could, perhaps, prepare yourself for it. Since we don’t, the best you can do is work on what’s seems interesting and important now, while educating yourself as broadly as possible, so that you’ll at least have a fighting chance when some new and unexpected development comes down the pike. I’m not saying that any significant new development should lead you to up-end your research plans. But it should, at least, lead you to re-examine them.

How do you decide, after all, what to work on? It’s somewhere in that magical intersection of the set of problems which are important with the set of problems on which reasonable progress can be made in the short term. New developments can change either of these sets, by making previously intractable problems seem tractable, or by lending new importance to previously uninteresting (or, perhaps, un-thought-of) questions.

But, again, revolutions which radically alter these sets are inherently unpredictable. The best you can do is focus on those topics that seem most promising, now. For figuring out what those are, I would hope that the talks at Strings 2005 (if not my woefully inadequate summaries thereof) would be suitable food for thought. Idle speculation about future developments in the field won’t serve you very well2.

I chatted with several people about their overall impressions of Strings 2005. The consensus was very positive. There were no great surprises, but there was clear progress on a broad array of fronts. My reportage from the conference was spottier than it might otherwise have been, if only the percentage of boring, pointless talks were higher, affording me more “downtime” in which to blog.

And people are very upbeat about the LHC, and what it might tell us. The participant list for the LHC Olympics is studded with well-known young string theorists. If you want my personal opinion about what would be good for you to be thinking about, that would be one place to start.

But, then, you should probably be wary of advice proffered on the internet…

Instead, maybe you should just listen to the Strings 2005 Song, composed and performed by Brian Wecht, Brook Williams, Nelia Mann, Ted Erler, Matt Lippert, and Nick Jones.

1The principle of Universality — that the same infrared physics allows for multiple, distinct, ultraviolet completions — is what makes effective field theory possible. But it also, ultimately, dooms any attempt to study quantum gravity in a field-theoretic context. Anyone who tells you, “First, I’m going to quantize pure gravity, and then we can add whatever matter and gauge interactions we need, later.” is trying to sell you a bill of goods. Nothing sensible can come from such an approach.

2 Frankly, I’m not sure what purpose they do serve. Some people professed to find the panel discussion entertaining. Personally, I left midway through. Perhaps with a few beers, I would have found it more amusing. Some grimly sat through the whole thing and were depressed by it.

Posted by distler at July 19, 2005 9:54 AM

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