Please don't, but if you need to read a shorter summary of Vassar's text: http://lesswrong.com/lw/gdz/michael_vassars_edge_contribution_summary/
Also there is a text by Paul Graham which gives very interesting advice in the same direction:
In his famous essay You and Your Research (which I recommend to anyone ambitious, no matter what they're working on), Richard Hamming suggests that you ask yourself three questions: What are the most important problems in your field?
Are you working on one of them?
Why not?
Hamming was at Bell Labs when he started asking such questions. In principle anyone there ought to have been able to work on the most important problems in their field. Perhaps not everyone can make an equally dramatic mark on the world; I don't know; but whatever your capacities, there are projects that stretch them. So Hamming's exercise can be generalized to: What's the best thing you could be working on, and why aren't you? Most people will shy away from this question. I shy away from it myself; I see it there on the page and quickly move on to the next sentence. Hamming used to go around actually asking people this, and it didn't make him popular. But it's a question anyone ambitious should face.
The trouble is, you may end up hooking a very big fish with this bait. To do good work, you need to do more than find good projects. Once you've found them, you have to get yourself to work on them, and that can be hard. The bigger the problem, the harder it is to get yourself to work on it.
Of course, the main reason people find it difficult to work on a particular problem is that they don't enjoy it. When you're young, especially, you often find yourself working on stuff you don't really like-- because it seems impressive, for example, or because you've been assigned to work on it. Most grad students are stuck working on big problems they don't really like, and grad school is thus synonymous with procrastination.
But even when you like what you're working on, it's easier to get yourself to work on small problems than big ones. Why? Why is it so hard to work on big problems? One reason is that you may not get any reward in the forseeable future. If you work on something you can finish in a day or two, you can expect to have a nice feeling of accomplishment fairly soon. If the reward is indefinitely far in the future, it seems less real.
Another reason people don't work on big projects is, ironically, fear of wasting time. What if they fail? Then all the time they spent on it will be wasted. (In fact it probably won't be, because work on hard projects almost always leads somewhere.)
But the trouble with big problems can't be just that they promise no immediate reward and might cause you to waste a lot of time. If that were all, they'd be no worse than going to visit your in-laws. There's more to it than that. Big problems are terrifying. There's an almost physical pain in facing them. It's like having a vacuum cleaner hooked up to your imagination. All your initial ideas get sucked out immediately, and you don't have any more, and yet the vacuum cleaner is still sucking.
You can't look a big problem too directly in the eye. You have to approach it somewhat obliquely. But you have to adjust the angle just right: you have to be facing the big problem directly enough that you catch some of the excitement radiating from it, but not so much that it paralyzes you. You can tighten the angle once you get going, just as a sailboat can sail closer to the wind once it gets underway.
If you want to work on big things, you seem to have to trick yourself into doing it. You have to work on small things that could grow into big things, or work on successively larger things, or split the moral load with collaborators. It's not a sign of weakness to depend on such tricks. The very best work has been done this way.
In a recent discussion a friend was telling me how he felt he was not as smart as the people he thinks are doing the best research on the most important topics. He said a few jaw-dropping names, which indeed are smarter than him, and mentioned their research agenda, say, A B and C.
From that, a remarkable implication followed, in his cognitive algorithm:
Therefore I should research thing D or thing E.
Which made me pause for a moment. Here is a hypothetical schematic of this conception of the world. Arrows stand for "Ought to research"
Humans by Level of Awesome (HLA) Research Agenda by Level of Importance. (RALI)
HLA RALI
Mrs 1 --------> X-risk #1
2 --------> X-risk #2
3 --------> Longevity
4 --------> Malaria Reduction
5 --------> Enhancement
1344 --------> Increasing Puppies Cuteness
Etc...
It made me think of the problem of creating match making algorithms for websites where people want to pair to do stuff, such as playing tennis, chess or having a romantic relationship.
This reasoning is profoundly mistaken, and I can look back into my mind, and remember dozens of times I have made the exact same mistake. So I thought it would be good to spell out 10 times in different ways for the unconscious bots in my mind that didn't get it yet:
1) Research agenda topics are polygamous, they do not mind if there is someone else researching them, besides the very best people who could be doing such research.
2) The function above should not be one-to-one (biunivocal), but many-to-one.
3) There is no relation of overshadowing based on someone's awesomeness to everyone else who researches the same topic, unless they are researching the same narrow minimal sub-type of the same question coming from the same background.
4) Overdetermination doesn't happen at the "general topic level".
5) Awesome people do not obfuscate what less awesome people do in their area, they catapult it, by creating resources.
6) Being in an area where the most awesome people are is not asking to "lose the game" it is being in an environment that cultivates greatness.
7) The amount of awesomeness in a field does not supervene on the amount of awesomeness in it's best explorer.
8) The Best person in each area would never be able to cause progress alone.
9) To want to be the best in something has absolutely no precedence over doing something that matters.
10) If you believe in monogamous research, you'd be in the akward situation where finding out that no one gives a flying fuck about X-risk should make you ecstatic, and that can't be right. That there are people doing something that matters so well that you currently estimate you can't beat them should be fantastic news!
Well, I hope every last cortical column I have got it now, and the overall surrounding being may be a little less wrong.
Also, this text by Michael Vassar is magnificent, and makes a related set of points.