Toward the end of his long and storied career, Richard Hamming gave a speech at Bellcore where he passed along personal observations directed toward the question: "How does one build a career as a first-rate scientist?"
Your time is well spent reading the full speech, though personally I find in it a good many statements that are distracting, or dubious, or at least left-footed. Still, if the basic question interests you, it is useful to review and to distill what Hamming had to say.
To focus my comments, I'll quote two of last paragraphs:
"If you really want to be a first-class scientist you need to know yourself, your weaknesses, your strengths, and your bad faults, like my egotism. How can you convert a fault to an asset? How can you convert a situation where you haven't got enough manpower to move into a direction when that's exactly what you need to do? I say again that I have seen, as I studied the history, the successful scientist changed the viewpoint and what was a defect became an asset.
In summary, I claim that some of the reasons why so many people who have greatness within their grasp don't succeed are: they don't work on important problems, they don't become emotionally involved, they don't try and change what is difficult to some other situation which is easily done but is still important, and they keep giving themselves alibis why they don't. They keep saying that it is a matter of luck. I've told you how easy it is; furthermore I've told you how to reform. Therefore, go forth and become great scientists!"
In the first paragraph Hamming suggests there is a necessity to "know yourself." That notion does ring a bell, and, even since the Greeks, no one has dared to advocate the contrary.
Still, even by Shakespeare's day, a more artful phrase was "to thine ownself be true," although Shakespeare found it wise to put these words into the mouth of Polonius, a pretentious buffoon who would later be stabbed through a curtain. Recent scholarship links the character Polonius (Corambis in the First Folio) to the Latin for "reheated cabbage."
Hamming's suggestion that one should somehow convert a fault to a virtue is better than reheated Greco-Roman cabbage, though it is hard to say how much better.
Still, there is a science of personality, and one of the facts that emerges from years of research is that personality is remarkably stable. The personally you have as a young adult will be with you for many years, and it makes sense to take that fact into account. To the extent that there is honest professional career advice, it focuses substantially on matching personalities and job requirements. Enough people have found value in that process that What Color is Your Parachute? has gone through forty editions.
I am more baffled by Hamming's second paragraph. How did he convince himself of the truth of any of these assertions?
As I recall Pasture, Poincare, Hadamard, Feynman, Ulam, Alvarez and a many others with compelling records of success have had high praise for luck. Clearly, there is more scholarly work to be done here.
Also, what were the "important problems" investigated by Mendel or by Brown? It's not overly unfair to say the friar was fiddling about with peas (and fudging some of his data). Brown tells us exactly what he had in mind. Over a few days in August of 1828, the country gentleman was looking though his new microscope to see what he could see.
I prefer the advice: Enjoy your garden, record --- but don't fudge --- your data, do tell people about what you have seen. Let the career stuff take care of itself.
Hamming was present at the birth of modern numerical analysis --- even computational science. He made notable contributions, and he wrote interesting, highly-readable books. He also gave many thought provoking speeches.
One should not make too much of a few pages of his off-the-cuff comments to a room full of young (and old) fiends at Bellcore in 1986.
I doubt that Hamming expected his remarks to be subjected to much examination. He was an experienced author who would surely would have presented a far more nuanced view if he had been writing for formal publication.
Adam Kapelner brought Hamming's speech to my attention, and he asked for my comments. Thinking and writing are intertwined for me, so for the rest I am solely responsible.
One does well to question the validity of an essay that offers advice that relies mostly on the personal perceptions of the author. In particular, a good author will know that the world experienced by an old man is much different than the world faced by a young person today.
A good author also knows that time and place do matter.
Hamming's view of the world was more informed by Tom Watson than by Bill Gates or Steve Jobs. The success of Mark Zukerberg would have not been imaginable. Time and Place are not destiny, but it is easier to be lucky if you are in the right place at the right time.
Hamming would have been more endearing to me if he had said:
"I'm tremendously lucky to have been in the right place at the just the time of the creation of several technologies that have changed the world. I did not have a substantial role in the creation of those technologies, but I did have the pleasure of riding the wave.
I did some things of which I am personally proud, but I am not so naive as to believe that there were not others on the team who could have done the very things for which I got credit. Some probably could have done better. The world has no shortage of hard-working people with enough talent for the task.
The mere existence of science in industry is a blessing and a miracle. Ten years earlier and ten miles away --- and nothing that I have done would have been done by me --- though essentially equivalent work is likely to have been done --- a little later or a little earlier --- in the same place."
Anyone who believes that there is an a priori clear line between the "important questions" and the "unimportant questions" needs to review the concept of Whig history. The actual "path of progress" has wiggles, twists, turns --- even erasures and forgeries --- plus lots of laziness, forgetfulness, and wishful thinking.
The distinction is anything but direct or inevitable.
The historical truth of scientific discovery can be pulled out of the record of the past only by applying the steel pliers of hard-slogging scholarship. Few of us have the time or talent to do this work. Still, to be honorable, we should at least read some of the work that has been done. Even a little reading of the scholarly work on scientific discovery puts healthy breaks on overly idle musings about how "great work" is done.
Obviously, we all need to form views about what we regard as important or unimportant. Even then, it's not written in stone that one must work on the problem one acknowledges to be the most important.
My personal perspective is that there is no shame in saying, "Yes, that problem is important, but the field is crowed and much of the literature is polluted --- nobody knows which of the published results is right or not. I'd rather work on problems where I can set the pace and where I know that I am not chasing ghosts. If I find a problem where I know I have an honest audience, then I have something for the 'acceptable' pile. Naturally, I'll keep looking for candidates for the 'great' pile, but I can't just nap (or pretend to be working) until I have populated the 'great' pile."