Timeline for How to find a topic to do research with as a Post-Doc? [closed]
Current License: CC BY-SA 3.0
25 events
| when toggle format | what | by | license | comment | |
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| Sep 11, 2013 at 13:04 | review | Reopen votes | |||
| Sep 11, 2013 at 13:06 | |||||
| Jun 5, 2013 at 11:53 | comment | added | Fernando Muro | Answering some of the comments above: it's easy to be kind, but it's much harder to be honest. | |
| Jun 5, 2013 at 4:06 | comment | added | Emerton | ... easier to know if they really are open, and if they are, to begin working on them; whereas if you are working by yourself, it's harder to know whether your questions about the field are open, and even if you find out that they are, it can be harder to get started thinking about them even if you find them interesting, because you don't have command of all the basic tools in the area.) Regards, Matthew | |
| Jun 5, 2013 at 4:05 | comment | added | Emerton | ... inspiration and motivation. Also, talking together you can ask each other questions --- to begin with, about your respective areas of expertise, as you learn from each other; but such back-and-forth can often quite serendipitously lead to new research questions. (because if you are new to a field, but are discussing it with a friend in a context where you feel relaxed and able to ask basic questions, you can often find yourself asking "basic" questions which are actually open! And then thinking about these questions with someone who already knows something about the field makes it ... | |
| Jun 5, 2013 at 4:01 | comment | added | Emerton | ... mentors will provide guidance on research problems. I don't know how common this is in Germany, but it is another possible resource. One approach that many successful people have taken is to find an area that seems interesting but not in the exact centre of activity and pursue it for a while, using it as a chance to build up your knowledge and expertise. Then you can try drifting towards more central topics, rather than approaching them head on. I already mentioned collaborating, but let me mention it again --- discussing mathematics with a friend/collaborator can provide ... | |
| Jun 5, 2013 at 3:56 | comment | added | Emerton | Dear Timo, I understand how you feel; arithmetic geometry can seem pretty overwhelming as a field when your viewing it from the vantage point of a graduate student. The advice of Andreas Blass is very good. Also, will you doing a post-doc in Germany? If so, my understanding (perhaps wrong) is that you will be associated with a professor's group, that there will be an oberseminar, and so on. You should use your connection with the professor and the seminar to learn about interesting topics, possibly find collaborators, and expand your areas of expertise. In the US, often postdoctoral ... | |
| Jun 5, 2013 at 1:31 | comment | added | Sniper Clown | Seems like OP unleashed a barrage of attacks just by asking this question. This is why I happily avoid MO. Politesse >> intellect. | |
| Jun 5, 2013 at 0:56 | comment | added | Andreas Blass | The moral is that research doesn't have to begin with the idea "I want to prove such-and-such (new) result"; it may well begin with the idea "I want to clearly understand such-and-such (known) result." With luck, it will lead to new results, and even if it doesn't, you'll have learned something that can be useful later. | |
| Jun 5, 2013 at 0:54 | comment | added | Andreas Blass | My research ideas sometimes originated in the following "oblique" way. I wanted to understand some (known) results, so I started reading the relevant papers. I got the feeling that, though the proofs are perfectly correct, they could be arranged more clearly, so I started writing out (or at least thinking through) such a rearrangement, not with any idea of publishing it but just for my own benefit. But if I really did have a clearer view, it led to generalizations that included new, publishable results. The moral of this story is --- in the next comment as I'm out of space. | |
| Jun 4, 2013 at 22:38 | history | closed |
Misha user6976 Todd Trimble Vladimir Dotsenko Felipe Voloch |
off topic | |
| Jun 4, 2013 at 22:35 | comment | added | Eleanor Von Hohlandsbourg | Why is everyone so mean-spirited? Just some small words of encouragement and generic advice from more experienced colleagues and the OP would have gone on happily ever after :) More seriously isn't it very important to choose problems smartly to have a nice career rather than randomly investing time in the first thing that catches your fancy? | |
| Jun 4, 2013 at 22:13 | comment | added | Fernando Muro | Let me be completely honest, if you don't known the answer to this question you should consider giving up research. | |
| Jun 4, 2013 at 20:11 | comment | added | Alexander Woo | Of course you don't know what is promising. Neither does anyone else. Most of us have a dozen failed projects for every successful one. | |
| Jun 4, 2013 at 20:10 | answer | added | Alexandre Eremenko | timeline score: 8 | |
| Jun 4, 2013 at 19:12 | comment | added | Todd Trimble | @Timo: let me put it this way. If you land a post-doc, it will presumably be on the strength and interest of your work done as a PhD student. In that case, there will be a circle of problems and ideas that are related to your areas of expertise and things you've worked on, that will be of ready-made interest to others. And in that case, you'd naturally be able to build on your strengths. But I'm afraid your question is not really specific enough to answer in better than vague generalities. I'm sorry, but at this point I'll have to vote to close as "not a real question". | |
| Jun 4, 2013 at 18:36 | comment | added | user19475 | @Todd + Stefan: The problem is that I should do something different that I did in my PhD thesis, and that I don't know in advance what is promising. | |
| Jun 4, 2013 at 17:38 | comment | added | Suvrit | I think a practical way to start may be: make a list of all possible open, (semiopen, improvable) questions of interest to you. More importantly, try to see what can you do with your theorems. Applying one's ideas to problems in related areas can lead to cool new stuff. If you are completely short on ideas, take a break for a few weeks; let your mind rejuvenate---it'll help things clear up in your head! But if you feel that you are not yet experienced enough to recognise what problems are important, then you might benefit from collaborating more widely and trying to become more independent.. | |
| Jun 4, 2013 at 17:14 | comment | added | Todd Trimble | I would like to temper my earlier comment somewhat (I fully realized how it might have sounded harsh). It's true that even the greats can feel somewhat dried-up on occasion, and particularly so after a very intensive and consuming effort. Even Richard Feynman reported such feelings after his work on the Manhattan Project! His own diagnosis was that theoretical physics had come to feel like a serious and solemn business, and that he needed to play again at his physics. I don't know if that would apply here, but it's true that if math is no longer fun, then do something else! :-) | |
| Jun 4, 2013 at 17:11 | comment | added | Deane Yang | Although I agree with the earlier comments, I can see a possible point to the question. It's likely that the questions you know you want to pursue are ones that better and more experienced mathematicians have already attacked and probably are still attacking. So how do you choose something that you have a chance at solving but will be worth publishing in a good journal? | |
| Jun 4, 2013 at 17:09 | comment | added | Yemon Choi | While my instinctive response is the same as that of the previous commenters, let me put it slightly differently: try to have some of the courage of your own convictions; look at the problems which you either did not manage to completely resolve in your thesis work, or which perhaps seemed interesting but off-topic, and see what turns up. | |
| Jun 4, 2013 at 16:39 | comment | added | Stefan Kohl♦ | I would say, if you are interested in mathematics, you know about what you want to find out more. -- If not, why do you want to do mathematics at all? | |
| Jun 4, 2013 at 16:34 | comment | added | Todd Trimble | I don't understand. You've been doing research in a deep and wide field of mathematics, and your head isn't filled with questions and topics and ideas you're really itching to pursue once the headache of the PhD requirements is over and done? I like Ricky's "extraverted" advice, but me, I'd also introspect and think of all those juicy loose ends that must have cropped up and are left unresolved. Surely you can find something this way? | |
| Jun 4, 2013 at 16:07 | comment | added | Ricky | You can still talk to other people! For example other post-doc, but mathematicians are usually happy to discuss about their research. Of course is not the same ad having an advisor, but you are note alone at all! For example you can explain your thesis to someone that works on a related area and ask him to do the same with his research topic. And of course you can simply try to improve/generalize the results of your thesis. | |
| Jun 4, 2013 at 16:04 | history | edited | user19475 | CC BY-SA 3.0 |
added 50 characters in body
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| Jun 4, 2013 at 15:55 | history | asked | user19475 | CC BY-SA 3.0 |