Umarbek

As far as I know, each of you has one life to live. Even if you believe in reincarnation it doesn't do you any good from one life to the next. Why shouldn't you do significant things in this one life, however you define significant?

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 favors the prepared mind. The prepared mind sooner or later finds something important and does it. So yes, it is luck. The particular thing you do is luck, but that you do something is not.

Newton said, "If others would think as hard as I did, then they would get similar results."

Einstein, somewhere around 12 or 14, asked himself the question, "What would a light wave look like if I went with the velocity of light to look at it?" He could see a contradiction at the age of 12 that everything was not right and that the velocity of light had something peculiar.

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.

Shannon wants to create a method of coding, but he doesn't know what to do so he makes a random code. Then he is stuck. And then he asks the impossible question, "What would the average random code do?" He then proves that the average code is arbitrarily good, and that therefore there must be at least one good code. Who but a man of infinite courage could have dared to think those thoughts?

When you are famous it is hard to work on small problems. This is what did Shannon in. After information theory, what do you do for an encore?

The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow. They try to get the big thing right off. And that isn't the way things go.

What most people think are the best working conditions, are not. Very clearly they are not because people are often most productive when working conditions are bad.

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.

Many scientists when they found they couldn't do a problem finally began to study why not. They then turned it around the other way and said, "But of course, this is what it is" and got an important result.

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.

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.

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.

Great contributions are rarely done by adding another decimal place.

If you are deeply immersed and committed to a topic, day after day after day, your subconscious has nothing to do but work on your problem. And so you wake up one morning, or on some afternoon, and there's the answer. For those who don't get committed to their current problem, the subconscious goofs off on other things and doesn't produce the big result.

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.

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?

Dave McCall stopped me in the hall and said, "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." A couple of months later he was made the head of the department. The other day he was a Member of the National Academy of Engineering. 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?"

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

The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. We didn't work on time travel, teleportation, and antigravity. They are not important problems because we do not have an attack. It's not the consequence that makes a problem important, it is that you have a reasonable attack.

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.

Even if you believe that great science is a matter of luck, you can stand on a mountain top where lightning strikes; you don't have to hide in the valley where you're safe.

Most great scientists know many important problems. They have something between 10 and 20 important problems for which they are looking for an attack. And when they see a new idea come up, one hears them say "Well that bears on this problem." They drop all the other things and get after it.

At Berkeley we had gathered a bunch of data; we didn't get around to reducing it because we were building some more equipment, but if we had reduced that data we would have found fission. They had it in their hands and they didn't pursue it. They came in second.

Their minds are prepared; they see the opportunity and they go after it. You don't have to hit many of them to do some great science. It's kind of easy. One of the chief tricks is to live a long time.

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; all the hard work you do is sort of tangential in importance. 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.

I should be in the mass production of a variable product. I should be concerned with all of next year's problems, not just the one in front of my face.

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." The essence of science is cumulative.

Instead of attacking isolated problems, I made the resolution that I would never again solve an isolated problem except as characteristic of a class.

The effort to generalize often means that the solution is simple. The business of abstraction frequently makes things simple.

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.

It isn't just a matter of the job, it's the way you write the report, the way you write the paper, the whole attitude. It's just as easy to do a broad, general job as one very special case. And it's much more satisfying and rewarding.

It is not sufficient to do a job, you have to sell it. 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 had better write your report so when it is published, as the readers are turning the pages they won't just turn your pages but they will stop and read yours. If they don't stop and read it, you won't get credit. They would not 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.

The technical person wants to give a highly limited technical talk. Most of the time the audience wants a broad general talk and wants much more survey and background than the speaker is willing to give. You should paint a general picture to say why it's important, and then slowly give a sketch of what was done.

I deny that it is all luck, but I admit there is a fair element of luck.

I found in the early days I had believed 'this' and yet had spent all week marching in 'that' direction. It was kind of foolish. If I really believe the action is over there, why do I march in this direction? I either had to change my goal or change what I did.

Once you're moderately successful, there are more people asking for results than you can deliver and you have some power of choice. 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'. But if you want a 'No', it's easy to get a 'No'.

Doing really first-class work, and knowing it, is as good as wine, women and song put together.

The value is in the struggle more than it is in the result. The struggle to make something of yourself seems to be worthwhile in itself. The success and fame are sort of dividends.

There are in the mathematics department at Bell Labs quite a few people far more able and far better endowed than I, but they didn't produce as much. 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.

If you will learn to work with the system, you can go as far as the system will support you. Good scientists will fight the system rather than learn to work with the system and take advantage of all the system has to offer.

I wasn't dressing the way they felt somebody in that situation should. 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 know enough not to let my clothes, my appearance, my manners get in the way of what I care about. I didn't say you should conform; I said "The appearance of conforming gets you a long way." If you chose to assert your ego in any number of ways, "I am going to do it my way," you pay a small steady price throughout the whole of your professional career. And this, over a whole lifetime, adds up to an enormous amount of needless trouble. Many a second-rate fellow gets caught up in some little twitting of the system, and carries it through to warfare. He expends his energy in a foolish project. Which do you want to be? The person who changes the system or the person who does first-class science?

You can't be an original scientist without having some other original characteristics. 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. I am an egotistical person; there is no doubt about it. I used my ego to make myself behave the way I wanted to. Like a cornered rat in a real trap, I was surprisingly capable. I often put my pride on the line and sometimes I failed, but like a cornered rat I'm surprised how often I did a good job. 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.

You can tell other people all the alibis you want. I don't mind. But to yourself try to be honest. 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?

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.

When you get too many sound absorbers, you give out an idea and they merely say, "Yes, yes, yes." What you want to do is get that critical mass in action; "Yes, that reminds me of so and so," or, "Have you thought about that or this?" You want to get rid of those sound absorbers who are nice people but merely say, "Oh yes," and to find those who will stimulate you right back.

I believe that you should spend at least as much time in the polish and presentation as you did in the original research. Now at least 50% of the time must go for the presentation.

If you read all the time what other people have done you will think the way they thought. If you want to think new thoughts that are different, then do what a lot of creative people do - get the problem reasonably clear and then refuse to look at any answers until you've thought the problem through carefully. 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.

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.

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.

When error correcting codes were well launched, I said, "Hamming, you are going to quit reading papers in the field; you are going to ignore it completely; you are going to try and do something else other than coast on that." I deliberately refused to go on in that field. I wouldn't even read papers to try to force myself to have a chance to do something else.

Knowing many of my own faults, I manage myself. I have a lot of faults, so I've got a lot of problems, i.e. a lot of possibilities of management. 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.

I don't know the alternate branches. Until you can say that the other branches would not have been equally or more successful, I can't say.

When I met Feynman at Los Alamos, I knew he was going to get a Nobel Prize. I didn't know what for. But I knew darn well he was going to do great work. No matter what directions came up in the future, this man would do great work.

There are a whole pail full of opportunities, of which, if you're in this situation, you seize one and you're great over there instead of over here.

Luck changes the odds, but there is some definite control on the part of the individual.

I've told you how easy it is; furthermore I've told you how to reform. Therefore, go forth and become great scientists.