“Why do so few scientists make significant contributions and so many are forgotten in the long run?”

“What is the biggest problem in your field? And why are you not working on it?”

Richard Hamming

Richard Hamming was a mathematician and computer scientist who worked on calculating machines for the Manhattan Project and for Bell Labs.

He worked alongside some of the greatest scientists in history including Von Neumann, Feynman, Fermi, and more.

In his talk You and Your Research (1986) he reflects on why some scientists he worked with like Claude Shannon went on to do Nobel Prize level work and others in the cubicles right next to them were forgotten.

What does it take to do Nobel Prize level work?

I’m not talking about ordinary run-of-the-mill research; I’m talking about great research. And for the sake of describing great research I’ll occasionally say Nobel-Prize type of work.

I became very interested in the difference between those who do and those who might have done.

Here are some of his tips for doing Nobel Prize level work:

Stop being modest and decide to do great work

Great work is never done by accident. You need to have the confidence and courage to make it happen.

Drop modesty and say to yourself, “Yes, I would like to do first-class work.”

Our society frowns on people who set out to do really good work. You’re not supposed to; luck is supposed to descend on you and you do great things by chance. Well, that’s a kind of dumb thing to say. Luck will not cover everything.

One of the characteristics of successful scientists is having courage. Once you get your courage up and believe that you can do important problems, then you can. If you think you can’t, almost surely you are not going to.

Choose to work on important problems

If you do not work on an important problem, it’s unlikely you’ll do important work. It’s perfectly obvious.

Great scientists have thought through, in a careful way, a number of important problems in their field, and they keep an eye on wondering how to attack

Richard Hamming liked discussing problems with scientists from other fields.

During lunch, he would sit with scientists from different fields and ask them questions about their work.

One of his famous questions is: “What are the biggest problems in your field and why are you not working on them?”

Many of his fellow scientists, when pressed, admitted they didn’t really believe the problems they were working on were important.

I started asking, “What are the important problems of your field?” And after a week or so, “What important problems are you working on?” And after some more time I came in one day and said, “If what you are doing is not important, and if you don’t think it is going to lead to something important, why are you at Bell Labs working on it?” I wasn’t welcomed after that; I had to find somebody else to eat with!

“Hamming, that remark of yours got underneath my skin. I thought about it all summer, i.e. what were the important problems in my field. I haven’t changed my research,” he says, “but I think it was well worthwhile.”

I noticed a couple of months later he was made the head of the department. I noticed the other day he was a Member of the National Academy of Engineering. I noticed he has succeeded. I have never heard the names of any of the other fellows at that table mentioned in science and scientific circles. They were unable to ask themselves, “What are the important problems in my field?”

The obstacle is the way

Don’t shy away from obstacles.

Obstacles in the path of your short term goal are often the tip of the iceberg of truly great problems.

Early on it became evident to me that Bell Laboratories was not going to give me the conventional acre of programming people to program computing machines in absolute binary. It was clear they weren’t going to. But that was the way everybody did it. I could go to the West Coast and get a job with the airplane companies without any trouble, but the exciting people were at Bell Labs and the fellows out there in the airplane companies were not. I thought for a long while about, “Did I want to go or not?”

I wondered how I could get the best of two possible worlds. I finally said to myself, “Hamming, you think the machines can do practically everything. Why can’t you make them write programs?” What appeared at first to me as a defect forced me into automatic programming very early.

What appears to be a fault, often, by a change of viewpoint, turns out to be one of the greatest assets you can have. But you are not likely to think that when you first look the thing and say, “Gee, I’m never going to get enough programmers, so how can I ever do any great programming?‘

Have tremendous drive

Hamming is a big believer in deliberate effort. He believes you need to both work hard and apply your effort sensibly.

He also doesn’t shy away from the fact that you need to make sacrifices to do Nobel Prize level work. He admits it didn’t help his relationship with his wife.

You observe that most great scientists have tremendous drive.

I discovered that John Tukey was slightly younger than I was. John was a genius and I clearly was not. Well I went storming into Bode’s office and said, “How can anybody my age know as much as John Tukey does?” He leaned back in his chair, put his hands behind his head, grinned slightly, and said, “You would be surprised Hamming, how much you would know if you worked as hard as he did that many years.” I simply slunk out of the office!

Given two people with exactly the same ability, the one person who manages day in and day out to get in one more hour of thinking will be tremendously more productive over a lifetime.

“Knowledge and productivity are like compound interest.” Given two people of approximately the same ability and one person who works ten percent more than the other, the latter will more than twice outproduce the former. The more you know, the more you learn; the more you learn, the more you can do; the more you can do, the more the opportunity - it is very much like compound interest.

I don’t like to say it in front of my wife, but I did sort of neglect her sometimes; I needed to study. You have to neglect things if you intend to get what you want done. There’s no question about this.

Drive, misapplied, doesn’t get you anywhere. I’ve often wondered why so many of my good friends at Bell Labs who worked as hard or harder than I did, didn’t have so much to show for it. The misapplication of effort is a very serious matter. Just hard work is not enough - it must be applied sensibly.

Tolerate ambiguitity

Great scientists have the confidence to put forth a theory and the humility to notice the flaws in the theory.

Most people like to believe something is or is not true. Great scientists tolerate ambiguity very well.

They believe the theory enough to go ahead; they doubt it enough to notice the errors and faults so they can step forward and create the new replacement theory.

If you believe too much you’ll never notice the flaws; if you doubt too much you won’t get started. It requires a lovely balance.

Darwin writes in his autobiography that he found it necessary to write down every piece of evidence which appeared to contradict his beliefs because otherwise they would disappear from his mind.

When you find apparent flaws you’ve got to be sensitive and keep track of those things, and keep an eye out for how they can be explained or how the theory can be changed to fit them.

Conclusion

I appreciate his unique insight from working with the greatest scientists in history, and what makes them different. I think there’s a lot of good advice in this talk about what it takes to become a great scientist.