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I'm thinking of applying to do a PhD in String Theory, starting in September 2013. I'm gradually learning more about the subject through external reading, but still most papers are impenetrable! Could anyone give me a description of the areas of current String Theory research that would be accessible for a doctoral student? Are there any particular open problems that might be worth getting to know?

Also any general advice on how to choose a PhD topic would be most welcome! Many thanks in advance!

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When you apply, don't say you want to study strings--- usually this is a sign you don't know any real physics. Say your joy is writing complicated code to simulate electronic structure of Fe superconductors. Condensed matter has a strong experimental component, so it never floats completely into fantasy-land, and this is real physics that is always fruitful. All you have to do to make friends with a professor is read more than one of their less famous papers with comprehension, and ask them about something obscure. To do research, though, you always have to do it indepedently yourself. –  Ron Maimon Jul 26 '12 at 16:32

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The papers are impenetrable because you are lacking the background, and it is carefully kept hidden from students, so that only the ones that read the old literature can enter the field. The only way to learn it is semi-historical (meaning historical but with hindsight, so you don't learn the stuff that's bogus). Work through at least a good chunk of Green/Schwarz/Witten, Polchinsky and Polyakov's Gauge-fields and strings, without thinking, just to learn what the calculation methods are. Afterwards or simultaneously, read the 1960s articles on bootstrap to understand where all this is coming from, so that you understand the philosophy and founding notions.

The original papers are absolutely essential if you want to understand the subject in any nonsuperficial way. There are no substitutes (except review articles from the same era). The boostrap becomes taboo in 1976, so nothing from this point on will be pedagogically or philosophically correct or persuasive (except to the converted). The later literature has huge gaps in explanation, the lacunae correspond precisely to the bootstrap ideas that are left out. You can read a superficial description here: What are bootstraps? and in one of my questions: Are There Strings that aren't Chew-ish? . Without bootstraps, you won't really understand why strings interact by topology, or why they are unique (or even why they are unitary, although Polchinsky has a discussion of this). The Dolen Horn Schmidt paper on finite energy sum-rules is extremely interesting collider physics by itself, but is dismissed in GSW by calling it an "accident"!

The literature I found most helpful for unlocking the mysteries of the 1960s were Gribov's 1967 classic "Theory of Complex Angular Momentum" (this is the Rosetta stone for all this literature, although Landau's QM has a Regge theory section which helps too), Veneziano's string review of 1974(or 75) Scherk's review of strings (and generally all his articles), and Mandelstam's review of string theory (also mid 70s, he's like the Bohr and Kramers put together), and the articles in Superstrings I/II then become clear. Then you can follow by reading Witten and reading whoever Witten cites (this is sort of considered standard practice).

The articles of t'Hooft on holography from 86-91, Susskind from 90-97, are pretty much self-contained, and require no elaborate string machinery, but they make you understand why the theory looks the way it does. They allow you to understand the physical leap in 97 with Maldacena's work and AdS/CFT. The general rule in string theory is that the mathematics is straightforward (altough difficult), but physics can be completely opaque. You can learn to calculate, but without the historical literature, you won't know why you're getting the right answer or what are the correct generalizations.

Open questions

There are so many, it's impossible to list them. You won't get a good one from an academic advisor, you probably want to find your own, and quickly. If you read the original and 1990s literature, you will see a million open problems, although in the modern literature (past 2000) you will see only one really:

  • What is the correct formulation of the KLT relations?

It is becoming obvious that N=8 SUGRA is finite, and nobody has a proof. It's coming soon, and this is what so many of the best people are working on. This is more mathematics than physics, but it's important in understanding what the perturbative structure of strings are.

This is the major concern right now, because it relates string theory to perturbation theory calculations that are important for LHC.

The questions in traditional string theory are unfortunately affected by large-extra-dimension disease. This was the free-for-all that ended the second string revolution and led it to degenerate into fantasy (see here: )

Here are some other open problems. I will try to avoid repeating my previous list: What is currently incomplete in M-theory? :

  • What is the precise swampland volume field-number sum-rule?

There should be a swampland constraint on the total number of fields from some measure of the volume measure of the compactification. If you have a tiny compactification, there is a central charge constraint and modular invariance, that picks out the gauge group size in heterotic and type I strings. You can't make too much low-energy stuff without violating consistency. As the dimensions get larger, you can stuff more crap in and get more low-energy matter. But there is a heuristic that the more matter you get out, the bigger the compactification. But there is no precise relation known. What is it? How much stuff do we expect total in our universe, including dark matter, and the Higgs sector?

  • How do you prove the mass charge inequality?

This is a spectral constraint on string vacua that tells you the lightest charged particle must be lighter than it's mass. There are heuristic arguments that persuade one that it must be true, but it should be provable in any holographic theory. Yet the proof is just out of reach. Simeon Hellerman has a paper on mass bounds for neutral black holes which is a large step forward.

  • What's going on with extremal black holes?

If you make a stack of D-branes, and pull one away, there is no restoring force. For appropriate branes, this is described by an N=2 gauge theory with a modulus. If you let the brane slowly collide with the others, it makes oscillations in the field theory, and the collision is described by a geometry analogous to Atiyah and Hitchin monopoles. But this is a black hole collision model now.

The point is that it is classically reversible and leads to oscillations, brane bouncing in and out. But you naively expect that in a true black hole collision that this leads to irreversible absorption. What are the near extremal black holes doing classically? Are they irreversible? Are they reversible? I think they're reversible.

This is related to the question of recovering the classical geometry from AdS/CFT. The correspondence is very hard to take the classical local limit on, where it is supposed to recover supergravity. You know it works, but this doesn't mean you can trace what happens to classical matter starting far-away going into a stack of branes. Does it come out again (if they are reversible than it must)? But how?

  • Are there calculable non-SUSY vacua?

There is a paper on SO(16)xSO(16) heterotic strings which is quickly reviewed in Polchinsky Alvarez-Gaume/Ginsparg/Moore/Vafa. This model is notable, because it is not SUSY, but it has zero vacuum energy at zero coupling. This is a relic of the fact that it is a projection of a SUSY model. Are there other such projections? What's the general idea here?

There are also a lot of unorthodox vacua found in the 1980s that were swept under the rug, because people wanted strings to be more unique than they are. This work one should read (although I didn't read enough, just one or two papers, so that I know these exist).

Anyway, you will get better ideas than these just from reading, but to do this, you need to quickly go over the old literature, and this only takes a few months if one knows where to look. The key for me was Gribov.

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The way things work in academia is it's your adviser who will pick your topic for you. Most students have no choice in the matter.

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As I understand it I'll have to have a pretty good idea of a particular area I'm interested in when I apply though, won't I? (Disclaimer: I'll be applying to UK universities, and I understand the system is quite different in the US...) –  Edward Hughes Jul 25 '12 at 10:38
    
I think this is not right. Most students I knew chose their own topics, sometimes from a suggested list. –  user1504 Jul 25 '12 at 11:49
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If your advisor picked your topic without any input from you then you were very unlucky in your choice of advisor. They should not have done that. But of course it varies greatly by field and by institution. If you have a really good idea for a project, you might even be able to pitch it yourself in your application - that's what I did. (I'm in the UK if it makes a big difference.) –  Nathaniel Jul 25 '12 at 13:27
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Apropos, @hgbreton, your choice of PhD supervisor is really important. If at all possible, try to meet potential supervisors before applying, and make sure you're on the same wavelength. Try to find out what they're interested in - do they ask the same kind of questions as the ones you're interested in? - and ask what they look for in an application. –  Nathaniel Jul 25 '12 at 13:36

If you want some idea of what's going on in string theory right now, have a look at the talks given at summer conferences: Strings 2012 and the upcoming Simons summer workshop, for example. (Note also that the Aspen Center, Les Houches, & TASI, which have often focused heavily on strings in the past, don't seem to be doing so this year.)

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Note, if you're coming into string theory cold, and actually get a Ph.D. position, it is likely to take you 5+ years to get a decent thesis together (one that pushes boundaries) not 3+ years. This is due to the massive learning curve you will forego and the current rate of publication. Also, it is not easy, and comprises a great number of mathematical disciplines. Also, it is unlikely that you will have an abstract that solves an major problem in the field, the abstract will be given to you by a prospective supervisor and will be likely one that will help the funding dept./research group. –  Killercam Jul 26 '12 at 7:53
    
@Killercam - Is the massive learning curve peculiar to string theory or is it the case for just about any area in physics? (Assuming the person has a standard graduate core background i.e. classical mechanics, quantum mechanics, electrodynamics and statistical physics) –  Joebevo Aug 23 '12 at 16:18
    
String theory is very complex (as many other diciplins are) however, I am not aware of another that incorporates so many different facets of both physics and mathematics. For instance, to get to a position where you can start understanding string theory, you will first need to have studied (to a relatively high undergraduate level) Differential Geometry, Group Theory, QM, Classical Field Theory and Canonical Quantisation, Partical Physics, General Relativity and Riamannian Geometry - then after the undergraduate study (depending on the uneversity and how good you are) you will need... –  Killercam Aug 24 '12 at 8:37
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a good understanding of Homology, Homotopy & Cohomology Groups, Path Intergral Quantisation, Quantum Field Theory, Orbifolds, bundles et al. from Riemannian Geometry. Index Theorems - supersymmetric QM. Familiarise your self with some relevent algebras; Lie, Grassmann and Clifford Algebras. A good book to get you started would be Geometry, Topology and Physics by M. Nakahara. As you can see there is much to learn just to be able to start thinking about string theory. I hope this helps... –  Killercam Aug 24 '12 at 8:46

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