Apologies in advance for this a soft question which has no closed, correct answer. This is probably the best forum to ask my question.

I am a third year graduate student in theory group of a top-15 school in US. So far, I've been doing decently well. I have a first author theory paper and a first author practical paper so far. My advisor has been superb in helping me honing my skills but I feel stuck (and helpless).

So far, my advisor has been a helping hand and a guiding force to always point me right directions and pose the right questions (not too abstract, not too concrete) which have been instrumental in me finding the answers to research problem. As I try to be more "independent", i.e, ask the right questions and prove results, I feel I have failed miserably and quickly feel overwhelmed. I feel that I don't have the maturity of a theory PhD student yet where I can ask myself the right questions and come with answers. In other words, given the right definitions and some hand holding, I am able to do things but otherwise, it becomes very hard. My sloppiness when it comes to writing proofs doesn't help either.

I am looking for advice on how can I sharpen my skills and be more "theory-minded" where I can grasp things quicker and require less hand holding. While one answer is simply to keep working and hope that experience makes me wiser, I am not sure how this will work out. The only solution I have is to actually go through come recent papers in my area and write down proofs by hand in as much detail as possible to help me nail proof writing skills and build intuition.

Any advice would be extremely helpful. Please let me know if question is unclear or needs more detail.

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    $\begingroup$ I think around the third year is when you can expect to start becoming independent and it's quite premature you have failed at it. I am not going to attempt an answer to your general question right now, but as far as proof writing (which I think is a separate question) you should think of a written proof as an attempt to convince a very sceptical audience. You can ask a fellow PhD student to act as a sceptical audience. Or you can do it yourself by playing devil's advocate and trying to "stress-test" and break your own proofs. $\endgroup$ Commented Dec 15, 2017 at 18:24
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    $\begingroup$ Dont' theoretical papers in computer science always list authors in the alphabetical order? So it doesn't make a lot of sense to speak about "first authorship" in that context. Otherwise, what @SashoNikolov said. It's too early for you to worry. And also, the feeling of helplesness and ignorance is a constant in the life of a scientist. $\endgroup$ Commented Dec 16, 2017 at 18:02
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    $\begingroup$ @AndrejBauer My advisor and me are the only people on both the papers. So I am the "main" student contributor. All I wanted to convey was that I have been decently productive so far. $\endgroup$
    – karmanaut
    Commented Dec 16, 2017 at 20:16
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    $\begingroup$ I am a third year graduate in theory ... I feel I have failed miserably and quickly feel overwhelmed — So, right on schedule, then. $\endgroup$
    – Jeffε
    Commented Dec 21, 2017 at 15:26
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    $\begingroup$ My advice: read ONLY the statements of results, try understand them. Then close the paper. Try to think on your OWN proof for 1-2 hours, maybe for 1-2 days. In any case - have you found a proof or not - it will be a real satisfaction to see the GIVEN proof. Independent of whether yours was better, or not, or even if you have had no clue. Doing this many times, I'd became more “theory-minded” (I hope). $\endgroup$
    – Stasys
    Commented Dec 22, 2017 at 22:28

4 Answers 4


One way I have often found theory problems to work on is by reading about an area and trying to figure out exactly what the state of the art is on a problem. Invariably, some basic questions end up being left unanswered, and that’s where I will start my research. Such questions are sometimes left unanswered not because they are too difficult, but because nobody formalized things properly, and this is something that can come naturally to a theorist who is just trying to understand what’s known and what’s not. And the ability to formalize problems is a key aspect of doing successful theory.

Another natural way to do successful theory is by trying to solve known open problems, for example those found in the discussion sections of recent papers. There, the key is having a good enough understanding of your own strengths and interests that you choose problems where you might make progress. This takes some experience and also some self-awareness, which you can actively think about and cultivate as you go through your PhD.

And as you do your PhD, you’ll develop these skills and more, including the ability to grasp proofs in papers quicker, and if things go well, you’ll be coming up with your own directions naturally by the end.


Another avenue for interesting exploration is when you're trying to understand the proof of a theorem or lemma. If you dig really deep into the proof to understand exactly how it works (and I don't mean literally, in the $A\Rightarrow B$ sense, but intuitively), you'll often realize that the proof is more ungainly than it needs to be. Asking whether it can be simplified often leads to new explorations.


I agree with Sasho Nikolov's comment: there are two issues here, whose outcomes might influence one another, but they really are two separate issues: writing better proofs, and coming up with good research questions.

(1) For writing better proofs, practice practice practice. But also get feedback. If you know this is a weakness, don't be afraid to ask for help, and when you practice and write things down, ask someone (your advisor, or a friend who you think is better at writing crisp proofs than you are) for feedback on your practice. (In other words, remember: it's not just 10000 hours of blind practice that makes an expert, but 10000 hours of deliberate practice.)

(2) As for coming up with better research questions, that is one that people struggle with for a long time. While we may get better at it, I think it is something realistically most of us will are still working on in some form or another for most of our careers. I was once given the advice that if you get one good idea out of every 10 ideas, you're doing well. (Now, in order for that to work out, you have to realize relatively quickly which ideas are bad ones so you don't waste too much time going down blind alleys.)

(3) Know yourself. Learn your strengths and your weaknesses. Work on your weaknesses, leverage your strengths. Always stick to what truly interests you.

(4) In terms of specific strategies for coming up with better questions, one thing to realize is that there are many different kinds of researchers out there, and different research strategies will work well for different people. If you haven't see it, and although it is somewhat of a caricature of reality, check out Dyson's Birds and Frogs. That shows you that there are at least two different kinds of researchers, but in reality there are probably dozens of different categories of theory researcher. (And I don't just mean by topic, but by research style.)

With that huge caveat in mind, here's at least one strategy for trying to find good queestions to work on.

I think you already partially know the answer. Read a lot. A friend once gave me advice in grad school: you are reading and learning so much at such a rate at that point in your life that if something is hard to read now, put it down and come back to it in a few weeks - it will be easier just by virtue of all the stuff you've learned in those few weeks. (Okay, maybe a month. Maybe two. Depends on the subject and what you're doing in between. Also, take this with a grain of salt: obviously don't just put something down because it's hard.)

Try to see to the heart of the matter. If there's a question that interests you, what is the heart of that question - the part of the question that, without resolving that, you could get nowhere. Try to make whatever progress you can on the heart of the question. (This also goes back to knowing your strengths.)

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    $\begingroup$ smbc-comics.com/comic/the-fox-and-the-hedgehog $\endgroup$
    – Jeffε
    Commented Dec 23, 2017 at 18:54
  • $\begingroup$ @Jeffe: Nice :). (Though, to be precise about it, I kind of think of fox/hedgehog as related to but not the same as frog/bird. So, at the very least, you can have foxy birds, foxy frogs, hedgebirds and hedgefrogs, though perhaps some of these combinations are more prevalent than others.) $\endgroup$ Commented Dec 23, 2017 at 22:11

Finding good problems to work on is a very difficult task, almost every graduate student struggle with it. That is one of the main reasons you have an adviser who can use his experience and help you find problems that worth working on and can lead to some results in reasonable time.

It is also a matter of trial and error. You have to fail a lot till you get an intuition about what is a good problem to work one. Keep trying and over time you will gain the intuition and skill to pick good problems to work on. Until then use the experience of your adviser.

Another practice that helps in gaining the skill is reading the abstract and conclusion sections of a lot of the papers in topics you find them intellectually intriguing. Try to understand why the author think the problem is interesting.

It often happens that a PhD student graduates without demonstrating complete independence from their adviser. That is one of the reasons people go for postdoc: to demonstrate that they are capable of research independent without their adviser.


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