Nobel laureate Steven Weinberg had a piece back in the Nov. 27 Nature (p. 389) offering advice to people just starting their scientific careers. It's useful stuff, and the lessons aren't just for beginners, either.
His first of "Four Golden Lessons" is No one knows everything, and you don't have to. (This came from his early paralysis at not knowing the whole field of physics.) That one gets more true every year, as the pile of scientific knowledge increases. I'm a reasonably good organic chemist, but there are big swaths of the literature that I'm not familiar with. Unusual steroid reactions? They're legion, but I don't know 'em. Sesquiterpenoid biosynthesis? (Half my readership just said "Gesundheit!") They're wild-looking compounds (PDF), but I've never needed to know much about how they're made. Mechanistic organometallic complex chemistry? Go ask Greg Hlatky (and while you're there, check out his piece on the compounds these things can make by reacting with stopcock grease).
No, I don't know these things too well, and (so far) I haven't had to. If I need to, I'll learn them. That's the best way to deal with the size of a scientific field, I think: get the fundamentals down, and that will give you the tools to learn what you need to know. Then let your own curiosity and your circumstances take you from there.
Weinberg's second lesson is aim for rough water. Try to work in a field where things are contentious and unsettled - "go for the messes." There's still room for creativity there, as opposed to the more worked-out fields. Of course, that presupposes that the reader is interested in doing creative work, but advice like this is wasted on anyone who isn't. Not that there aren't plenty of such people around - any research department is full of them. They can make contributions, as long as both they and their supervisors know the score. Trouble ensues when they don't.
His third lesson is forgive yourself for wasting time. He classifies that as "probably the hardest to take" of his lessons. This is a consequence of the go-for-the-messes advice, and will be most applicable to those that have followed it. What he means is that it can be very hard to know if you're working on something that's even solvable, or if you're working on the right problem at all.
That certainly applies to my area of research, where there are long stretches where it seems like nothing's happening, and perhaps never will. Even when things are moving along, you're never sure if that light off in the distance is reflecting off a pile of gold, or is a bare bulb put there to scare the rats off a garbage pit. So, we're searching for an agonist of receptor XYZ - who knows if such a thing exists? Or if we're going to stumble across it? Or if it'll do what we think it will, assuming we know how to test it in the correct way and assuming that we can understand the results? Working like this, there's going to be a lot of wasted effort, and you're just going to have to come to terms with it.
Weinberg's final lesson is learn something about the history of science. The least important reason to do that, he says, is that it might help out your research. To use his example, without knowing the historical record, you might come to believe that Thomas Kuhn or Karl Popper really understood how science works. But the larger reason is that an appreciation for history puts your work in perspective. Weinberg believes, as I do, that science is one of the highest activities of civilization, and that we should be proud of our parts in it. A real discovery can live longer, and with greater impact, than almost any other human work.