Should one attack hard problems? When I applied for a PhD student position I had an interview with two professors. Somehow we touched the problem if $P$ is $NP$ and, once we got there, for some reason both professors made it clear that in their opinion there is absolutely no point attacking such a hard problem. Of course this is the case for a starting student, it is more fruitful to build the basis first. But they basically stated that the problem has been studied by so smart researchers that no mortal could do better anyway.
This makes me wonder should one attack such hard problems at all? If one should, why and when? Will studying hard problems span new ideas? Is it even a necessity to understand some hard problems and, especially, why they are hard to solve? Or is it just pure waste of time? Or is it that one should learn some hard problems to educate oneself but not spend time attacking them?
 A: Actually, I think trying a "hard problem" may be a good idea IF
1) You have a fair evidence that you are strong enough to tackle things other clever people gave up on. The evidence should be tangible. The best evidence is, of course, having solved at least one hard problem already, but that, obviously, cannot be applied to your first hard problem ever. Sometimes a good indication is other people saying something like "You should stop stealing other mathematicians' daily bread and do some real thing that no one else can do!" (Note that you shouldn't follow the first part of this advice.)  
2) You have an escape strategy. That may be thinking of something else in parallel, making sure that your plan is such that even a partial progress can be of value, etc.
3) You are not afraid to fail and are used to the feeling of being a hopeless idiot (meaning you can calmly admit this frustrating fact about yourself without any reservations, excuses, or other kinds of self-deceit and still push ahead at your full strength). 
4) You have enough free time and do not care too much of your career ups and downs.
5) You are sufficiently open-minded to see things at unusual angles and are trained to figure out reasonably quickly whether any given idea may possibly work or it certainly won't. Note that both  are tough skills, which are almost completely untouched in most standard treatises on problem solving.
6) You love the problem. This should, actually, be #0 rather than #6, and it is hard to explain what it means in rational terms, but you can feel it when it happens.  
If those conditions are satisfied, go ahead and try shooting the Moon. If not, you'd better make your way up slowly step by step like most of us, picking the fight just slightly bigger than your own size every time. 
I'm not a great believer in "having a new idea from the start". The new idea or a combination of ideas usually comes eventually when working on the problem and the moment it comes is often very near the end of the story. The trail of failures that precedes it is well-hidden, but we all start with "I have no method, no feeling, no tools, no clue, and no hope" and proceed through "twisting this, we can get a bit more or something a bit different, however the main difficulty remains untouched". You have to figure out not only what doesn't work but also how exactly it doesn't work. Most of the time is spent on constructing examples and counterexamples to the steps in your initial plan, digressing into simpler models, checking that no information is lost at each particular step, i.e., that if the original theorem is correct, then the intermediate lemma you want to try is at least very plausible, and so on, and so forth. I do not know how it works for others, but for me any non-trivial problem is a scattered jigsaw puzzle, not an originally blurry but complete picture I merely need to focus the camera on. 
I'm not sure how much credibility I can claim myself when talking like this about solving hard problems, but, fortunately, most of these claims aren't my creations: I merely believe they are true and the opposites are false. So, take all this with a healthy grain of salt and keep in mind that out of 100 mathematicians, at most 5 are qualified to shoot the Moon in principle and, out of those 5, at most 1 will score a hit when making this long shot, so don't judge us, professors, too harshly when we just know our limitations and are unwilling to try to jump above our heads. There is a lot of stuff at the knee level that needs to be done and some of us (including myself) just feel that it will be more efficient to spend most of our time doing it there. One becomes a loser not when he aims and shoots lower than the Moon but when he stops seeing it in the sky :). 
As to the formal question list, I would answer as follows:
Should one attack such hard problems at all? 
Yes. The gods won't do it for us, so it'll have to be one of us, poor mortals, who should try.
If one should, why and when? See #1-#6 for "when". As to "why", if one asks this question, one shouldn't.
Will studying hard problems span new ideas? 
Possibly. It can work out either way.
Is it even a necessity to understand some hard problems and, especially, why they are hard to solve? 
No, nothing is absolutely necessary. You can live and work perfectly well without it. 
Or is it just pure waste of time? 
This depends on who and what you are.
Or is it that one should learn some hard problems to educate oneself but not spend time attacking them?
That works for some people too.
A: What did Polya say.....
That if one can not solve a hard problem, then solve a similar but easier problem.  I like thinking about the hard problems in my field, knowing that it doesn't take tons of creativity to solve something easier after seriously studying those.    
A: Here is what both    Feynman,  Grothendieck (and my father)  said: have several   projects in mind at all times. 
Grothendieck   explains  a two year  state of depression he went through at the beginning of his career  to the fact  he single mindedly followed one goal which turned out to be very illusive. 
Feynman explained his success  on  the fact that the he always  had several questions in his mind  and  kept an open eye  for anyting that might relate to this. That is why  he found attending seminars so much more helpful.
As for successful  PhDs dissertations I read somewhere, long ago,  that there are of two types


*

*the type where you find a new method for an old question,


and 


*

*the type where you find a new  question for an old method.


Statistically, the 2nd type is more prevalent.   Obviously that is a rough classification and  dissertations are  cocktails  of both types.
So to answer your question, should you  try to solve hard problems, my answer is yes, but remember that, even if you do not get the whole dinosaur   in you dissertation,  his tail may be  good enough to  make you a Doctor in Sciences.
A: When thinking about attacking a hard problem one should ask: Do I have a tool or an idea that other people who attacked the problem did not have? If so, one should give it a try. If not, one will be most probably not better than others.
A: Let me quote Ennio De Giorgi on this: "If you can't prove your theorem, keep shifting parts of the conclusion to the assumptions, until you can"
A: I think Markus Redeker's answer captures the essential point. If the problem is hard and famous (at least in the relevant sub-field), so a fortiori for a problem like P≠NP, I would add the further restriction that you should consider attacking it only if that new idea you have allows you to solve an easy or average (but still new) related problem or at the very least allows you to reprove in a completely different way a known result. If this works, then 1) you now know that this new idea is not completely crazy or just a variant of an old one 2) you have a worthy PhD. 3) you can think about making math history. In fact, if you skim through math history, recent or otherwise, you will see that because of point 1) (testing that you idea is indeed new and worth pursuing) many historical breakthroughs were preceded by an easy (or at least much easier) variant relying on similar techniques.  
A: As I understand, you are only beginning your graduate studies.
At this stage you should get a problem from your adviser, a problem that you are likely to solve.
If you want to become a professional mathematician, you should publish regularly, and for this
you need problems which you are likely solve in reasonable time.
What kind of problems you are likely to solve, you will gradually learn from experience.
But in the very beginning, rely on the experience of your adviser. 
But of course, you should also learn about "big and famous" problems, and think about them too.
Then, if you are lucky, you have an idea how to make a progress in one of them. 
My main advise for the beginner: choose a right adviser, and do what s/he recommends.
In the remaining time, read and think on other problems. 
A: As an amateur, I'd say yes, just for the fun of it (and perhaps to provide new potentially useful though rather sketchy ideas to professionals). I think one can't make breakthroughs in any area if he or she doesn't find it cool enough to spend most of their (free or not) time on it.
On the other hand, I can easily understand that people who got involved in a long and difficult career can't take too high a risk trying to tackle a long-standing open problem that might be intrinsically unsolvable (like the Continuum Hypothesis).
My advice would thus be: if you have no real career issues, no family to feed and find math extremely exciting, just go for it!
