A talk by Richard Hamming for guiding you on your research. This talk is about how you individually do a great research, and how you managing your research.

Meta

• Authors: Richard Hamming
• Date: 1991
• Link: https://www.cs.virginia.edu/~robins/YouAndYourResearch.html
• Video: https://www.youtube.com/watch?v=a1zDuOPkMSw

You and Your Research” by Richard Hamming

Notes

Main Talk

Why is this talk important?

• We only have one life, why not do something significant.

First-class work or Significant work?

• Drop modesty and say to yourself, “Yes, I would like to do first-class work.”. You are not supposed to to really good work at the beginning. Luck should descend on you when you are doing the great things by chance. You should not tell yourself, “I would like to do something significant.”

What makes people do the great work?

• Luck? Once in a while a person does only one thing in his whole life, but a lot of times there is repetition. You see again and again that it is more than one thing from a good person.
• One characteristic is that usually when they were young they had independent thoughts and had the courage to pursue them.
• Good start. Great work is something else than mere brains. Brains are measured in various ways. Good start can fell away shyness, awkwardness and inarticulateness, bring you confidence and courage and making you productive and articulate.
• 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. Courage is one of the things that Shannon had supremely.
• Age. Most mathematicians, theoretical physicists, and astrophysicists do what we consider their best work when they are young. (It is not that they don’t do good work in their old age but what we value most is often what they did early. On the other hand, in music, politics and literature, often what we consider their best work was done late.) Why? In the first place if you do some good work you will find yourself on all kinds of committees and unable to do any more work. When you are famous it is hard to work on small problems. The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow.
• Defect. Often the great scientists, by turning the problem around a bit, changed a defect to an asset. Many scientists when they found they couldn’t do a problem finally began to study why not. So ideal working conditions are very strange. The ones you want aren’t always the best ones for you.
• Drive. You would be surprised how much you would know if you worked as hard as John Tukey did that many years. What Bode was saying was this: “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.
• Inspiration. “Genius is 99% perspiration and 1% inspiration.” Misapplied drive doesn’t get you anywhere. It must be applied sensibly.
• Ambiguity. 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. 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. Those are often the great contributions.
• Emotional commitment and attention. So the way to manage yourself is that when you have a real important problem you don’t let anything else get the center of your attention - you keep your thoughts on the problem. Keep your subconscious starved so it has to work on your problem, so you can sleep peacefully and get the answer in the morning, free.
• Eat with different groups of people. Learn something you are not familiar with. Ask “What are the important problems of your field?”, “What important problems are you working on?”, and “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 still working on it?” (You will not be welcomed after that.)
• Important problem. Think “What are the important problems of my field?”. Don’t be unable to ask yourself this question, which may make you succeed. If you do not work on an important problem, it’s unlikely you’ll do important work. It’s perfectly obvious. You can’t always know exactly where to be, but you can keep active in places where something might happen. Think hard about where is my field going, where are the opportunities, and what are the important things to do. Let me go there so there is a chance I can do important things.
• Reasonable attack. Phrase “important problem” carefully. It’s not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important. The average scientist spends almost all his time working on problems which he believes will not be important and he also doesn’t believe that they will lead to important problems.
• Insist on your problem. Most great scientists know many important problems for which they are looking for an attack. And when they see a new idea come up, they drop all the other things and get after it. If you don’t pursue it, you may have it in your hands but come in second. The great scientists, when an opportunity opens up, get after it and they pursue it. They drop all other things. They get rid of other things and they get after an idea because they had already thought the thing through. Now of course lots of times it doesn’t work out, but you don’t have to hit many of them to do some great science.
• Open the door. If you have the door to your office closed, you get more work done today and tomorrow, and you are more productive than most. But 10 years later somehow you don’t know quite know what problems are worth working on. He who works with the door open gets all kinds of interruptions, but he also occasionally gets clues as to what the world is and what might be important. There is a pretty good correlation between those who work with the doors open and those who ultimately do important things. Although people who work with doors closed often work harder, somehow they seem to work on slightly the wrong thing - not much, but enough that they miss fame.
• Approach rather than result. “It ain’t what you do, it’s the way that you do it.” Important work not only focus on getting the answer, but also on a better approach. (Extend reading on ‘Hamming’s Method of Integrating Differential Equations’.)
• Next year’s problem and how. “I should be concerned with all of next year’s problems, not just the one in front of my face.” How do I conquer machines and do all of next year’s problems when I don’t know what they are going to be? How do I prepare for it? How do I do this one so I’ll be on top of it? How do I obey Newton’s rule? He said, “If I have seen further than others, it is because I’ve stood on the shoulders of giants.” These days we stand on each other’s feet!
• Foundation and generalization. “It is a poor workman who blames his tools - the good man gets on with the job, given what he’s got, and gets the best answer he can.” The essence of science is cumulative. You should do your job in such a fashion that others can build on top of it, so they will indeed say, “Yes, I’ve stood on so and so’s shoulders and I saw further.” By changing a problem slightly, you can make the resolution that I would never again solve an isolated problem except as characteristic of a class.
• Selling. The world is supposed to be waiting, and when you do something great, they should rush out and welcome it. But the fact is everyone is busy with their own work. You must present it so well that they will set aside what they are doing, look at what you’ve done, read it, and come back and say, “Yes, that was good.” When you open a journal, as you turn the pages, you ask why you read some articles and not others. You should have better write so that when the readers are turning the pages they will stop and read yours. If they don’t stop and read it, you won’t get credit.
• Three things to sell. You have to learn to write clearly and well so that people will read it, you must learn to give reasonably formal talks, and you also must learn to give informal talks. You should not be a “back room scientists”, keeping quiet in a conference and submitting a report after a decision been made. You should stand up right in the middle of a hot conference, in the middle of activity, and say, “We should do this for these reasons.” You need to master that form of communication as well as prepared speeches.
• Spend time on great thought. Try to committed 10% of your time trying to understand the bigger problems in the field, i.e. what was and what was not important. You may find you believe “this” and yet had spent all week marching in “that” direction. Ask yourself if you really believe the action is over there, why do you march in this direction? You either had to change my goal or change what I did.
• Manage time and urgent tasks. You may not get the power to control what you have to work on at the first beginning, but once you are moderately successful, you have some incomplete power to choice when there are more people asking for results than you can deliver. Not all urgent tasks are really “urgent”; some are just artificial pressures. If you keep giving in to temporary tasks, you will never have time to do long-term important work. You can “educate” your boss through real-life examples to help them understand why some tasks should not take up your research time.
• Educating your boss. If you are limited on resource and administrator ignores your request, try to explain this to the people who asking for help, so that more people can help you to communicate with the administrator. If your group of contribution is been ignored, ask for deserved recognition before providing the help, and count and report your group of contributions.
• Worth it? “Is the effort to be a great scientist worth it?” A biased sample is see whether the people done it wants to do it again. Author thinks it is very definitely worth the struggle to try and do first-class work because the value is in the struggle more than it is in the result. The success and fame are sort of dividends, in the author’s opinion.

Why talents fail? What happened to them? Why do so many of the people who have great promise, fail?

• One of the reasons is drive and commitment. The people who do great work with less ability but who are committed to it, get more done than those who have great skill and dabble in it, who work during the day and go home and do other things and come back and work the next day. They don’t have the deep commitment that is apparently necessary for really first-class work.
• Second thing is personality defects. One example is somebody had his personality defect of wanting total control and was not willing to recognize that you need the support of the system. If he can learn to work with the system, he can go as far as the system would support him. Good scientists may not fight the system but should instead learn to work with the system and take advantage of all the system has to offer. You can learn how to use the system pretty well, and you can learn how to get around it. If you want to do something, don’t ask, do it. Present him with an accomplished fact. Don’t give him a chance to tell you “No”.
• Another personality defect is ego assertion. “I had to make the decision - was I going to assert my ego and dress the way I wanted to and have it steadily drain my effort from my professional life, or was I going to appear to conform better? I decided I would make an effort to appear to conform properly. The moment I did, I got much better service. And now, as an old colorful character, I get better service than other people.” You should dress according to the expectations of the audience spoken to. An enormous number of scientists feel they must assert their ego and do their thing their way. They have got to be able to do this, that, or the other thing, and they pay a steady price. “The appearance of conforming gets you a long way.”
• Relationship with system. By taking the trouble to tell jokes to the secretaries and being a little friendly, the author got superb secretarial help. By realizing you have to use the system and studying how to get the system to do your work, you learn how to adapt the system to your desires.
• Save the time from bureaucracy. You may finally realize that of course you are going to be red-taped to death so you should give in on small things. Able people don’t get themselves committed to that kind of warfare. Be clear, when you fight the system and struggle with it, what you are doing, how far to go out of amusement, and how much to waste your effort fighting the system. The advice is to let somebody else do it and you get on with becoming a first-class scientist.
• Not always give in on bureaucracy. Almost all scientists enjoy a certain amount of twitting the system for the sheer love of it. What it comes down to basically is that you cannot be original in one area without having originality in others. Originality is being different. But many a scientist has let his quirks in other places make him pay a far higher price than is necessary for the ego satisfaction he or she gets.
• Anger. Amusement, yes, anger, no. Anger is misdirected. You should follow and cooperate rather than struggle against the system all the time.
• Think positive. “I think you need to learn to use yourself. I think you need to know how to convert a situation from one view to another which would increase the chance of success.”
• Self-delusion. Self-delusion in humans is very, very common. “Why weren’t you first? Why didn’t you do it right? Don’t try an alibi. Don’t try and kid yourself. You can tell other people all the alibis you want. I don’t mind. But to yourself try to be honest.”
• Transfer your faults to asset. 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 in a direction when that’s exactly what you need to do? The successful scientist in history changed the viewpoint and what was a defect became an asset.

Question and Answer:

What about personal stress? Does that seem to make a difference?

• Yes, it does. If you don’t get emotionally involved, it doesn’t. If you want to be a great scientist you’re going to have to put up with stress. You can lead a nice life; you can be a nice guy or you can be a great scientist. But nice guys end last, is what Leo Durocher said. If you want to lead a nice happy life with a lot of recreation and everything else, you’ll lead a nice life.

The remarks about having courage. Among the young people these days is a real concern over the risk taking in a highly competitive environment. Do you have any words of wisdom on this?

• We had reasons for having courage and therefore we did a great deal. I can’t arrange that situation to do it again. I cannot blame the present generation for not having it, but I agree with what you say; I just cannot attach blame to it.

Is brainstorming a daily process?

• Once that was a very popular thing, but it seems not to have paid off. For myself I find it desirable to talk to other people; but a session of brainstorming is seldom worthwhile.

What kind of tradeoffs did you make in allocating your time for reading and writing and actually doing research?

• I believed, in my early days, that you should spend at least as much time in the polish and presentation as you did in the original research.

How much effort should go into library work?

• There may be no effect named after one because he read too much. If you read all the time what other people have done you will think the way they thought. The reading is necessary to know what is going on and what is possible. But reading to get the solutions does not seem to be the way to do great research.

Would you care to comment on the relative effectiveness between giving talks, writing papers, and writing books?

• In the short-haul, papers are very important if you want to stimulate someone tomorrow. If you want to get recognition long-haul, it seems to me writing books is more contribution because most of us need orientation. In this day of practically infinite knowledge, we need orientation to find our way. …Public talks are necessary; private talks are necessary; written papers are necessary. But I am inclined to believe that, in the long-haul, books which leave out what’s not essential are more important than books which tell you everything because you don’t want to know everything. …You just want to know the essence.

You mentioned the problem of the Nobel Prize and the subsequent notoriety of what was done to some of the careers. Isn’t that kind of a much more broad problem of fame? What can one do?

• Some things you could do are the following. Somewhere around every seven years make a significant, if not complete, shift in your field. Thus, I shifted from numerical analysis, to hardware, to software, and so on, periodically, because you tend to use up your ideas. When you go to a new field, you have to start over as a baby. You are no longer the big mukity muk and you can start back there and you can start planting those acorns which will become the giant oaks.
• You have to change. You get tired after a while; you use up your originality in one field. You need to get something nearby. I’m not saying that you shift from music to theoretical physics to English literature; I mean within your field you should shift areas so that you don’t go stale. You couldn’t get away with forcing a change every seven years, but if you could, I would require a condition for doing research, being that you will change your field of research every seven years with a reasonable definition of what it means, or at the end of 10 years, management has the right to compel you to change. I would insist on a change because I’m serious. What happens to the old fellows is that they get a technique going; they keep on using it. They were marching in that direction which was right then, but the world changes. There’s the new direction; but the old fellows are still marching in their former direction.
• You need to get into a new field to get new viewpoints, and before you use up all the old ones. You can do something about this, but it takes effort and energy. It takes courage to say, “Yes, I will give up my great reputation.”

Would you compare research and management?

• If you want to be a great researcher, you won’t make it being president of the company. If you want to be president of the company, that’s another thing. I’m not against being president of the company. I just don’t want to be. I’m not against it; but you have to be clear on what you want.
• When your vision of what you want to do is what you can do single-handedly, then you should pursue it. The day your vision, what you think needs to be done, is bigger than what you can do single-handedly, then you have to move toward management.
• I chose to avoid management because I preferred to do what I could do single-handedly. But that’s the choice that I made, and it is biased. Each person is entitled to their choice. Keep an open mind.

How important is one’s own expectation or how important is it to be in a group or surrounded by people who expect great work from you?

• At Bell Labs everyone expected good work from me - it was a big help. Everybody expects you to do a good job, so you do, if you’ve got pride. I think it’s very valuable to have first-class people around.
• I tried to go with people who had great ability so I could learn from them and who would expect great results out of me. By deliberately managing myself, I think I did much better than laissez-faire (Consciously manage yourself = proactively shape the growth environment).