Source: McCurley website, date indeterminate
We are concerned with great research here. Work that will get wide recognition, perhaps even win Nobel Prizes. … We are concerned with research that will matter in the long run and become more than a footnote in history.
If you are to do important work then you must work on the right problem at the right time and in the right way. Without any one of the three, you may do good work but you will almost certainly miss real greatness.
choosing the problem
I begin with the choice of problem. Most scientists spend almost all of their time working on problems that even they admit are neither great or are likely to lead to great work; hence, almost surely, they will not do important work.
To illustrate, consider my experience at BTL. For the first few years I ate lunch with he mathematicians. I soon found that they were more interested in fun and games than in serious work, so I shifted to eating with the physics table. There I stayed for a number of years until the Nobel Prize, promotions, and offers from other companies, removed most of the interesting people. So I shifted to the corresponding chemistry table where I had a friend.
At first I asked what were the important problems in chemistry, then what important problems they were working on, or problems that might lead to important results. One day I asked, “if what they were working on was not important, and was not likely to lead to important things, they why were they working on them?” After that I had to eat with the engineers!
About four months later, my friend stopped me in the hall and remarked that my question had bothered him. He had spent the summer thinking about the important problems in his area, and while had had not changed his research he thought it was well worth the effort. I thanked him and kept walking.
A few weeks later I noticed that he was made head of the department. Many years later he became a member of the National Academy of Engineering. The one person who could hear the question went on to do important things and all the others — so far as I know — did not do anything worth public attention.
There are many right problems, but very few people search carefully for them. Rather they simply drift along doing what comes to them, following the easiest path to tomorrow.
Great scientists all spend a lot of time and effort in examining the important problems in their field. Many have a list of 10 to 20 problems that might be important if they had a decent attack. As a result, when they notice something new that they had not known but seems to be relevant, then they are prepared to turn to the corresponding problem, work on it, and get there first.
Hard work is a trait that most great scientists have. Edison said that genius was 99% perspiration and 1% inspiration. Newton said that if others would work as hard as he did then they would get similar results. Hard work is necessary but it is not sufficient. Most people do not work as hard as they easily could. However, many who do work hard — work on the wrong problem, at the wrong time, in the wrong way, and have very little to show for it.
You are aware that frequently more than one person starts working on the same problem at about the same time. In biology, both Darwin and Wallace had the idea of evolution at about the same time. In the area of special relativity, many people besides Einstein were working on it, including Poincare. However, Einstein worked on the idea in the right way.
… as Pasteur pointed out, “Luck favors the prepared mind.”
A great deal of direct experience, vicarious experience through questioning others, and reading extensively, convinces me of the truth of his statement. Outstanding successes are too often done by the same people for it be a matter of random chance.
For example, when I first met Feynmann at Los Alamos during the WWII, I believed that he would get a Nobel Prize. His energy, his style, his abilities, all indicated that he was a person who would do many things, and probably at least one would be important.
Many times a discussion with a person who has just done something important will produce a description of how they were led, almost step by step, to the result. It is usually based on things they had done, or intensely thought about, years ago. You succeed because you have prepared yourself with the necessary background long ago, without, of course, knowing then that it would prove to be a necessary step to success.
There traits are not all essential, but tend to be present in most doers of great things in science. First, successful people exhibit more activity, more energy, than most people do. They look more places, they work harder, they think longer than less successful people. Knowledge and ability are much like compound interest — the more you do the more you can do, and the more the opportunities are open for you. Thus, among other things, it was Feynmann’s energy and his constantly trying new things that made one think he would succeed.
This trait must be coupled with emotional commitment. Perhaps the ablest mathematician I have watched up close seldom, if ever, seemed to care deeply about the problem he was working on. He has done great deal of first class work, but not of the highest quality. Deep emotional commitment seems to be necessary for success. The reason is obvious. The emotional commitment keeps you thinking about the problem morning, noon and night, and that tends to beat out mere ability.
… what I call the “extra mile.” I did more than the minimum, I looked deeper into the nature of the problem. This constant effort to understand more than the surface feature of a situation obviously prepares you to see new and slightly different applications of your knowledge. You cannot do many problems such as the above needle problem before you stumble on an important application.
Courage is another attribute of those who do great things.
Without courage you are unlikely to attack important problems with any persistence, and hence not likely to do important things. Courage brings self-confidence, an essential feature of doing difficult things. However, it can border on over-confidence at time which is more of a hindrance than a help.
Great steps forward usually involve a change of viewpoint to outside the standard ones in the field.
While you are leaning things you need to think about them and examine them from many sides. By connecting them in many ways with what you already know…. you can later retrieve them in unusual situations. It took me a long time to realize that each time I learned something I should put “hooks” on it. This is another face of the extra effort, the studying more deeply, the going the extra mile, that seems to be characteristic of great scientists.
The evidence is overwhelming that steps that transform a field often come from outsiders. In archaeology, carbon dating came from physics. The first airplane was built by the Wright brothers who were bicycle experts.
Thus, as an expert in your field, you face a difficult problem. There is, apparently, an ocean of kooks with their crazy ideas; however, if there is a great step forward it probably will be made by one of them! If you listen too much to them then you will not get any of your own work done, but if you ignore them then you may miss your great chance. I have no simple answer except do not dismiss the outsider too abruptly as is generally done by in the insiders.
You need a vision of who you are and where your field is going. .. The particular vision you have is less important than just having one – there are many paths to success. Therefore, it is wise to have a vision of what you may become, of where you want to go, as well as how to get there. No vision, not much chance of doing great work; with a vision you have a good chance.
Another obvious trait of great people is that they do their work in such a fashion that others can build on top of it. Newton said, “If I had seen farther than others it is because I stood on the shoulders of giants.” Too many people seem to not want others to build on top of their work but rather they want to hoard it to themselves. Don’t do things in such a fashion that next time it must be repeated by you, or by others, but rather in a fashion that represents a significant step forward.
the question of whether greatness is worth the large effort it requires. Those who have done really great things generally report, privately, that it is better than wine, the opposite sex, and song put together. The realization that you have done it is overwhelming.
Of course I have consulted only those who did do great things, and have no dared to ask those who did not. Perhaps they would reply differently. But, as is often said, it is in the struggle and not the success that the real gain appears. In striving to do great things, you change yourself into a better person, so they claim. The actual success is of less importance, so they say. And I tend to believe this theory.