How to escape the inclination to be a universalist or: How to learn to stop worrying and do some research. As an undergraduate we are trained as mathematicians to be universalists. We are expected to embrace a wide spectrum of mathematics. Both algebra and analysis are presented on equal footing with geometry/topology coming in later, but given its fair share(save the inherent bias of professors). Number theory, and more applied fields like numerical analysis are often given less emphasis, but it is highly recommended that we at least dabble in these areas.
As a graduate student, we begin by satisfying the breadth requirement, and thus increasing these universalist tendencies. We are expected to have a strong background in all of undergraduate mathematics, and be comfortable working in most areas at a elementary level. For economic reasons, if our inclinations are for the more pure side, we are recommended to familiarize ourselves with the applied fields, in case we fall short of landing an academic position.
However, after passing preliminary exams, this perspective changes. Very suddenly we are expected to focus on research, and abandon these preinclinations of learning first, then doing something. Professors espouse the idea that working graduate student should stop studying theories, stop working through textbooks, and get to work on research.
I am finding it difficult to eschew my habits of long self-study to gain familiarity with a subject before working. Even during my REU and as an undergrad, I was provided with more time and expectation to study the background.
I am a third year graduate student who has picked an area of study and has a general thesis problem. My advisor is a well known mathematician, and I am very interested in this research area. However, my background in some of the related material is weak. My normal mode of behavior, would be to pick up a few textbooks and fix my weak background. Furthermore, to take many more graduate courses on these subjects. However, both of my major professors have made it clear that this is the wrong approach. Their suggestion is to learn the relevant material as I go, and that learning everything I will need up front would be impossible. They suggest begin to work and when I need something, pick up a book and check that particular detail.
So in short my question is: 

How can I get over this desire to take
  lots of time and learn this material
  from the bottom-up approach, and
  instead attack from above, learning
  the essentials necessary to move more
  quickly to making original
  contributions? Additionally, for those of you advising students, do you recommend them the same as my advisor is recommending me?

A relevant MO post to cite is How much reading do you do before attacking a problem. I found relevant advice there also.
As a secondary question, in relation to the question of universalist. I find it difficult to restrain myself to working on one problem at a time. My interests are broad, and have difficulty telling people no. So when asked if I am interested in taking part in other projects, I almost always say yes. While enjoyable(and on at least one occasion quite fruitful), this is also not conducive to finishing a Ph.D.(even keeping in mind the advice of Noah Snyder to do one early side project). With E.A. Abbot's claim that Poincaré was the last universalist, with an attempt at modesty I wonder

How to get over this bred desire to work on everything of interest, and instead focus on one area?

I ask this question knowing full well that some mathematicians referred to as modern universalists visit this site. (I withhold names for fear of leaving some out.)
Also, I apologize for the anonymity.
Thank you for your time!
EDIT: CW since I cannot imagine there is one "right answer". At best there is one right answer for me, but even that is not clear.
 A: I think that, for the majority of students, your advisor's advice is correct.  You need to focus on a particular problem, otherwise you won't solve it, and you can't expect to learn everything from text-books in advance, since trying to do so will lead you to being bogged down in books forever.
I think that Paul Siegel's suggestion is sensible.  If you enjoy reading about different parts of math, then build in some time to your schedule for doing this.   Especially if you feel that your work on your thesis problem is going nowhere, it can be good to take a break, and putting your problem aside to do some general reading is one way of doing that.  
But one thing to bear in mind is that (despite the way it may appear) most problems are not solved by having mastery of a big machine that is then applied to the problem at hand.  Rather, they typically reduce to concrete questions in linear algebra, calculus, or combinatorics.  One part of the difficulty in solving a problem is finding this kind of reduction (this is where machines can sometimes be useful), so that the problem turns into something you can really solve.  This usually takes time, not time reading texts, but time bashing your head against the question.  One reason I mention this is that you probably 
have more knowledge of the math you will need to solve your question than you think; the difficulty is figuring out how to apply that knowledge, which is something that comes with practice.  (Ben Webster's advice along these lines is very good.)
One other thing: reading papers in the same field as your problem, as a clue to techniques for solving your problem, is often a good thing to do, and may be a compromise between working solely on your problem and reading for general knowledge.
A: One thing that might help is to think about this advice as saying you need to develop new skills rather than being about the one true way to do mathematics.  That is, you have a lot of experience and skill at learning math systematically from the ground up like you did in your classes, but that's only one skill out of many that are necessary to be an effective researcher.  You also need to hone your problem solving skills, you need to learn how to identify appropriate interesting problems and research programs, you need to learn how to efficiently wade through the literature to find what you need, etc.  You have less practice at these things, so naturally you're not as good at them and so it's going to feel uncomfortable, but that's normal when you're learning new skills.
In other words, you're focusing too much on being well-rounded in terms of subject matter, but you're missing out on being well-rounded in terms of your skills.
That said, I do think it's worth following your interests, provided you still have enough time for your main research program.  There's more time in a day than my brain can handle working hard on my main research program, and the more of the rest of the time that was spent learning other mathematics, filling in gaps in my background, or working on a side project, rather than say playing 2048, the better.  So keep learning broadly and deeply, but don't let it eat into the time you're getting your main work done.
A: My best advice is just to do it.  of course, that's not helpful, so let me suggest something more concrete: do an extremely easy case of a more interesting problem.  While research problems can often seem quite daunting (and the ones worth doing take a while), try to chip off a piece of one you're pretty sure you can do, and do it.  Older mathematicians may be able to help point you to some kind of appropriately non-difficult problem.  It may not be worth publishing, but it may help get you rolling.
A: 
>
  How to get over this bred desire to work on everything of interest, and instead focus on one area?
  >

Why on earth would you want to get over your "bred desire"?  We all know very talented people who spend many years working in a narrow direction, doing hard things, but their papers are read by almost no one (sometimes not even by referees who recommend acceptance, but that is another story...).  When I was younger I would work on ten problems at a time, figuring that batting .100 was fine.  Now I am down to four or five, so I have to bat a higher number, but I would never work on only one.  I have great respect for people who devote years to solving one important problem (Wiles and Enflo come to mind), but for every successful mathematician like that I can name many others who have reduced their productivity by being too narrowly focused.
A: To me, the question sounds like, "How do I get over the bred desire to meet everyone in sight, and instead work on the desire to fall in love with a specific person?"
So my personal answer is:  It is just so THRILLING to solve an interesting open problem.  Learning material is very nice, I like it a lot.  But when I have gotten new results, those have been the among the happiest and most memorable moments of my life.  (And I don't think that that is an unusual sentiment.)  I don't just mean "big" results; even "small" results feel wonderful.
Maybe the bred desire that you mention is (or is related to) the emphasis on "theory building".  Yes, theory building is great, but I personally see it through the lens of problem solving.  The best solution of all to a problem is one that is short and sweet, and doesn't use an excessive amount of theory.
Of course, unless you're Erdős (who would not have asked the question), you wouldn't solve open problems all the time.  If you're a graduate student, the experience may seem inaccessible.  So I might suggest answering a few questions on MathOverflow, in a certain frame of mind.  Take some relatively rigorous MO questions (related to your thesis topic, say) and work on them as if they're open.  Or, another good method is to collaborate with someone who has that problem-solving itch.  Or watch such people work; see what animates them.
A: I agree with your advisor. With the "bottom up" approach you can study mathematics all your life, and have great fun in the process, but to start a successful research career you need to focus on a specific problem even if you do not know everything about it yet. In fact, many people learn much better that way, motivated by specific problems, which is why the earlier one starts doing research, the better. 
Becoming a well-rounded mathematician will pay off in the end but at the moment you just need to stay in the game. There are indeed some remarkable people who can cover different areas with continuous research output, but for many of us this strategy won't help to find a job, get a first grant, and honestly, won't help to make a significant contribution. There is good reason mathematicians specialize: one deep paper has more impact than 10 mediocre ones. You have to really get noticed in some subfield
in order to succeed careerwise. 
Again, there are a number of prolific people doing deep work, and if you realize you are one of them, stop worrying. Till then, it is better to focus.
A: Dear Anon:
I really sympathize with your position. And be aware that this tension between (for want of better words) curiosity and performance will be even more critical if you want to make a living out of doing math past graduation. What it means in particular is that it is important for you to find the right balance between doing research and satisfying your curiosity, and then trying to educate yourself on the types of jobs that would be the best fit. (Yes, I know, as if you didn't have enough to do already, you're learning math research, but educating yourself on the job market is critical too.)
I will not be afraid to argue both sides of the issue: I think it is very important to continue to satisfy your curiosity. Eventually, you will graduate, and one of the first things you'll feel like doing is broaden your horizons. Going in a totally different field is probably not recommended, but apart from that, new ideas of research problems can come from unlikely sources, as noted in the comments.
So I would encourage you to stick to your universalism. After all, it's not for nothing that math folks, as a rule, get most excited about results that connect different disciplines. But I would encourage you to exert this curiosity mainly outside of your own field of research. This is a bit trickier to explain, especially since this will depend enormously on how technical your field is. You do have to read some in your field, but targeted reading works really well in research, and this might improve your productivity tremendously. Your long term goal is to become deeply knowledgeable in your field, of course. But in the meantime, trying to be broad in your field is a time sink that could work against you. Also, you may find better return on time invested after you've grappled with the subject without a net for a while.
By the way, you mention your REU: one of the things you may want to work soon after graduation is finding problems that are suitable for undergraduates (a big career plus these days, unlikely to change in the foreseeable future). These problems will not come from your thesis work, so a wider perspective will pay off here. 
A: What's the goal?
If you have the resources and the (at least tacit) agreement of the institution whose resources you are using, follow your own lead.  Of course, you may run out of one resource or another before accomplishing anything more than personal indulgence.
If you have to get a result, and you do not understand something (and have limited resources such as time), go to someone and ask for understanding, or at least a different perspective.  If the question is focussed enough and still evasive, ask on MathOverflow.  Even if the question is eventually deemed inappropriate, some will notice and give you advice toward understanding.  (Don't stop there.  Ask department faculty, etc., as appropriate.)
In short, to avoid the desire for universalism, pretend that you don't get paid if you don't deliver product in a timely fashion.  That way of thinking will at least help you focus on producing something worthwhile for your efforts.  If you are interested, I can suggest a few strategies to adopt.
Gerhard "Ask Me About System Design" Paseman, 2010.08.17
