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I'm not sure if this is an appropriate question for MO, but I figured it couldn't hurt to ask. I'm a second year graduate student, currently gearing up to construct a committee and syllabus for my oral exams, and I'm struggling with some issues regarding the subject(s) I wish to study. In particular, I have found that what I am truly interested in is transcendental number theory and would absolutely love to have this as a primary area of focus for my exams, with the hope of developing a thesis in this area as well.

However, after speaking to some of my professors I now have the impression that the field is not exactly dead, but very, very cold. Not only do the open questions in the field seem to be impossibly difficult, but there are very few mathematicians out there (or so it seems) who focus on transcendence as a primary area of research. In light of these difficulties, I'd like to ask the following:

For graduate students in pure mathematics, do you recommend following your interests despite obvious challenges, or should students temper their passions and pick more fruitful areas of research for their theses? Additionally, for my particular case, where/who do I turn to to discuss transcendence and cultivate a sense for what types of problems (if any) are suitable for a PhD thesis?

Thanks in advance for your responses!


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Do both. Pick something that will be a successful thesis, and show your capacity as a researcher, and work on your passion at the same time. If in the middle of your efforts you find your passion consuming/replacing your "job", get help in restoring balance. Alternatively, if in the middle you hit on something in your passion that allows you to replace your thesis topic, ask your advisors about that possibility. Gerhard "Passion Equals Job Implies Satisfaction" Paseman, 2014.04.21 – Gerhard Paseman Apr 21 '14 at 18:40
There's been progress in transcendence theory over function fields (Drin'feld modules, T-modules), see the work of Greg Anderson and Matt Papanikolas (and others, but from their papers you'll find references to the other major players). – Joe Silverman Apr 21 '14 at 18:54

My experience shows that a graduate student on an early stage of his career is usually unable to make a reasonable judgement about areas of mathematics etc. on his own. At this stage, the crucial thing is choosing the ADVISER (among those available). The adviser must be a mathematician a) of high standing/reputation and b) the one you feel comfortable to work with. Choose the best one of those available. After you choose such an adviser, and s/he agrees to supervise you, rely completely on his/her advises instead of asking your fellow students and/or MO.

I mean you should talk to professors in YOUR department, not to MO. I mean people on MO can recommend you a an area of research, but you will be unlikely to achieve something without a good adviser in this area.

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Choose a topic where you can do something computational.

1) Your options inside or outside the academy will be greater if you have computational skills. Most graduate students in math do not end up at research universities.

2) If you want to make progress on old problems, you'll probably need tools that the old mathematicians didn't use. Computers are great tools.

3) Getting people interested in your proofs is hard, but numbers and computational results are great bait for getting others to collaborate.

For instance, consider Schanuel's conjecture in the form:

If there are $n+1$ algebraic dependencies among $x_1,\ldots,x_n,e^{x_1},\ldots,e^{x_n}$, then there is a $Q$-linear dependence among $x_1,\ldots,x_n$.

For which $n$ and which algebraic dependencies can you prove this? Can you devise an algorithm, and what numerical results does it give?

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I am sure that Andrew Wiles had wanted to work on Fermat's Last Theorem even as a graduate student, but surely John Coates advised him not to and instead wait until he has tenure somewhere to pursue this daunting task.

The ideal first research area of a graduate student (in my experience) is one where there is sufficient interest in the area, with a diverse selection of problems (so that it is extremely unlikely to be 'mined out' in the near future), and that there are problems your supervisor know of that can be fairly reasonably attacked by modifying a known method. Preferably after you have geared to solve your first problem the tools you have developed can easily be repurposed to solve a plethora of other problems so that you establish a reputation immediately.

So in summary, dip your feet into the pool first and get acquainted with the broader picture of number theory. If at some point your research naturally crosses paths with transcendence theory, pursue it then.

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What I've been doing is I've focused on tractable areas that are still related to my ideal area. As long as you can see how what you're doing still relates to, in this case, transcendence then it's not wasted time. Keep abreast of current activity and maybe spend some spare time looking into it but I'd advise only really start gunning for it once you're in a stable job.

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To answer the specific aspect of the question, about transcendental number theory, I think one thing you should do is to talk (by email, maybe) with Michel Walschmidt in Paris. I think he could give you an educated opinion about how cold is the subject, and if it is not too cold, where you can an adviser which would help you working on it.

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