You and your research

a stroke of genius: striving for greatness in all you do by R.W. Hamming

Little has been written on managing your own research (and very little on avoiding other people managing your research); however, your research is much more under your control than you may realize.

We are concerned with great research here. Work that will get wide recognition, perhaps even wine Nobel Prize. As most people realize, the average published paper is read by the author, the referee, and perhaps one other person. Classic papers are read by thousands. 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.

Greatness is a matter of style. For example, after learning the elements of painting, you study under a master. While studying you pay attention to what the master says in discussing your work, but you know that if you are to achieve greatness then you must find your own style. Furthermore, a successful style in one age is not necessarily appropriate for another age. Cubism would not have gone over big during the realism period.

Similarly, there is no simple formula for doing great science or engineering, I can only talk around the topic. The topic is important because, so far as we have any solid evidence, you have but one life to live. Under these circumstances it seems better to live a life in which you do important things (important in your eyes, of course) than to merely live out your life. No sense frittering away your life on things that will not even appear in the footnotes.

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. Note that importance of the results of a solution does not make the problem important. In all the 30 years I spent at Bell Telephone Laboratories (before it was broken up) no one to my knowledge worked on time travel, teleportation, or anti-gravity. Why? Because they had no attack on the problem. Thus an important aspect of any problem is that you have a good attack, a good starting place, some reasonable idea of how to begin.

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.

Some people work with their doors open in clear view of those who pass by, while others carefully protect themselves from interruptions. Those with the door open get less work done each day, but those with their door closed tend not know what to work on, nor are they apt to hear the clues to the missing piece to one of their "list" problems. I cannot prove that the open door produces the open mind, or the other way around. I only can observe the correlation. I suspect that each reinforces the other, that an open door will more likely lead you and important problems than will a closed door.

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.

The first person to produce definitive results generally gets all the credit. Those who come in second are soon forgotten. Thus working on the problem at the right time is essential. Einstein tried to find a unified theory, spent most of his later life on it, and died in a hospital still working on it with no significant results. Apparently, he attacked the problem too early, or perhaps it was the wrong problem.

There are a pair of errors that are often made when working on what you think is the right problem at the right time. One is to give up too soon, and the other is to persist and never get any results. The second is quite common. Obviously, if you start on a wrong problem and refuse to give up, you are automatically condemned to waste the rest of your life (see Einstein above). Knowing when you persist is not easy -- if you are wrong then you are stubborn; but if you turn out to be right, then you are strong willed.

I now turn to the major excuse given for not working on important problems. People are always claiming that success is a matter of luck, but 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. Einstein, around the age of 12 or 14, asked himself what a light wave would look like if he want at the speed of light. He knew that Maxwell's theory did not support a local, stationary maximum, but was what he ought to see if the current theory was correct. So it is not surprising that he later developed the special theory of relativity - he had prepared his mind for it long before.

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.