“You and Your research”(Richard Hamming)

第一部分是演讲总结，第二部分是提问环节的总结。总结形式是中文极简逻辑概括加原文。

第一部分，演讲总结

1. 演讲主题：如何从事伟大的研究，而非短平快的研究。

I'm not talking about ordinary run-of-the-mill research; I'm talking about great research.

2. 演讲背景：

（1）为什么要做伟大的研究？因为时间有限，人生只有一次。另外，在伟大研究课题中挣扎的过程是难得的历练，其成就和与之而来的名声只是股息。

why is this talk important? I think it is important because, as far as I know, each of you has one life to live. Why shouldn't you do significant things in this one life？

I think it is very definitely worth the struggle to try and do first-class work because the truth is, 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, in my opinion.

（2）贝尔实验室中那么多天才科学家，为何最终只有少数人获得伟大成就？

Why do so many of the people who have great promise, fail?

3. 如何从事伟大的研究，以及避免哪些错误

（1）运气。实现伟大成就不全部依靠运气，运气只偏爱有准备之人。

I claim that luck will not cover everything. And I will cite Pasteur who said, ``Luck favors the prepared mind.''

（2）勇气。敢想敢做、不畏艰难是科学家必备素质

One of the characteristics of successful scientists is having courage. 

That is the characteristic of great scientists; they have courage. They will go forward under incredible circumstances; they think and continue to think.

（3）年轻。并不是越年轻越容易做出伟大科研成果，这种误解来源于人们只记住了年轻天才科学家在年少成名时的第一个杰作而忽视了其后续的杰出成就。年龄对科学家的真正影响是获得杰出成就之后很难再有耐心从头开始从播种开始培育下一课参天大树。

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.

When you are famous it is hard to work on small problems.

（4）工作环境。科学家在恶劣环境中效率更高。

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.

often the great scientists, by turning the problem around a bit, changed a defect

to an asset.

So ideal working conditions are very strange. The ones you want aren't always the best ones for you.

（5）自驱力。自驱力是获得伟大成就的必备素质，同时要集中精力，舍弃它事。

You observe that most great scientists have tremendous drive.

What Bode was saying was this: “Knowledge and productivity are like compound interest.” 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. 

You have to neglect things if you intend to get what you want done. There's no question about this.

solid work, steadily applied, gets you surprisingly far.

The misapplication of effort is a very serious matter. Just hard work is not enough - it must be applied sensibly.

（6）避免二元论。正确看待不完美的理论，不可全信，不可不信，在缺憾中寻求新的突破。

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. But most _great scientists are well aware of why their theories are true and they are also well aware of some slight misfits which don't quite fit and they don't forget it.

（7）全身心投入。只有全身心投入，研究时遇到的困惑才会进入潜意识，你才可能在不经意间获得宝贵的灵感。

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. It comes down to an emotional commitment. Most great scientists are completely committed to their problem. Those who don't become committed seldom produce outstanding, first-class work.

The people who do great work with less ability but who are committed to it, get more done that 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.

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.

（8）时刻思考什么是本领域的核心问题，否则你永远不会做出伟大成就。

Let me warn you, `important problem' must be phrased carefully.

It's not the consequence that makes a problem important, it is that you have a reasonable attack.

I spoke earlier about planting acorns so that oaks will grow. You can't always know exactly where to be, but you can keep active in places where something might happen. And 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. But the average scientist does routine safe work almost all the time and so he (or she) doesn't produce much. It's that simple. If you want to do great work, you clearly must work on important problems, and you should have an idea.

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. Their minds are prepared; they see the opportunity and they go after it. 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. It's kind of easy. One of the chief tricks is to live a long time!

（9）不要闭门造车，多了解外面的世界有利于发现新的机会。

I notice that 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.

（10）反求诸己，适者生存，学会从多个角度看待问题，化逆境为顺境，让一切为我所用。

I'll remind you, ``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.'' And I suggest that by altering the problem, by looking at the thing differently, you can make a great deal of difference in your final productivity because you can either do it in such a fashion that people can indeed build on what you've done, or you can do it in such a fashion that the next person has to essentially duplicate again what you've done. 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!

If you will learn to work with the system, you can go as far as the system will support you.

You find this happening again and again; good scientists will fight the system rather than learn to work with the system and take advantage of all the system has to offer. It has a lot, if you learn how to use it. It takes patience, but you can learn how to use the system pretty well, and you can learn how to get around it. After all, if you want a decision `No', you just go to your boss and get a `No' easy. 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'.

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. Or you can fight it steadily, as a small undeclared war, for the whole of your life.

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.

（11）杰出的成就不只需要埋头苦干，还需要向世界销售。

it is not sufficient to do a job, you have to sell it.

when you open a journal, as you turn the pages, you ask why you read some articles and not others.

There are three things you have to do in selling. 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.

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. As a result, many talks are ineffective. The speaker names a topic and suddenly plunges into the details he's solved. Few people in the audience may follow. You should paint a general picture to say why it's important, and then slowly give a sketch of what was done.

The tendency is to give a highly restricted, safe talk; this is usually ineffective. Furthermore, many talks are filled with far too much information.

You should dress according to the expectations of the audience spoken to.

（12）不断反思自己，认清自己的缺点和优点，持续保持警惕以避免自己的缺点发作起来，并充分利用自己的优势。

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.

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 into a direction when that's exactly what you need to do? I say again that I have seen, as I studied the history, the successful scientist changed the viewpoint and what was a defect became an asset.

In summary, I claim that some of the reasons why so many people who have greatness within their grasp don't succeed are: 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. They keep saying that it is a matter of luck. I've told you how easy it is; futhermore I've told you how to reform. Therefore, go forth and become great scientists!

第二部分，问答环节

1.

问：如何看待压力，压力有帮助吗？

答：有帮助。但如果是情绪化压力，则没有帮助。你要么活得轻松，要么获得伟大成就。

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

A: 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.

2.

问：头脑风暴是每日必需吗？

答：与谁交流非常重要，谨慎的选择朋友，拒绝那些只会迎合你想法的呆子。

Q：Is brainstorming a daily process?

A：I picked my people carefully with whom I did or whom I didn't brainstorm because the sound absorbers are a curse. They are just nice guys; they fill the whole space and they contribute nothing except they absorb ideas and the new ideas just die away instead of echoing on.

3.

问：渊博的知识对科学研究有多重要？

答：这取决于获取读书的思路，如果是为了记忆知识则会限制创新型思考，如果是了解前人解决问题的思路则有帮助。

Q：How much effort should go into library work?

A：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 how you would do it, how you could slightly change the problem to be the correct one. So yes, you need to keep up. You need to keep up more to find out what the problems are than to read to find the solutions. 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. So I'll give you two answers. You read; but it is not the amount, it is the way you read that counts.

4.

问：哪种形式对科学发展更有利，演讲，论文，还是著书。

答：短期看论文更能推动科研进步，长期看著作更有利于人们梳理科研发展脉络，找到真正重要的科学课题。

Q：Dick, would you care to comment on the relative effectiveness between giving talks, writing

_papers, and writing books?

A：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.

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.

5.

问：如何看待社会名声对科学家工作的影响，我们该如何做？

答：一个研究领域大约每7年一次飞跃，当你实现了杰出成就之后你必须有勇气寻求新的相关领域而非固守城池吃老本，否则将被时代抛弃。

Q：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?

A：Somewhere around every seven years make a significant, if not complete, shift in your field.

You have to change. You get tired after a while; you use up your originality in one field. You need to get something nearby.

You need to get into a new field to get new viewpoints, and 6before you use up all the old ones.

6.

问：如何看待成为研究员和成为管理者

答：二者无优劣之分，但不可兼得。明确你的理想并为之奋斗，切勿贪念兼得。如果你的理想可以由你一个人完成，那就不需要成为管理者；如果你的理想是改变一定范围的现状，那就需要成为那个范围的管理者。

Q: Would you compare research and management?

A: 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.

you have to be clear on what you want. Furthermore, when you're young, you may have picked wanting to be a great scientist, but as you live longer, you may change your mind.

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. And the bigger the vision is, the farther in management you have to go.

It depends upon what goals and what desires you have.

Keep an open mind. But when you do choose a path, for heaven's sake be aware of what you have done and the choice you have made. Don't try to do both sides.

7.

问：身处一个背负周围人期望的环境有多重要？

答：与一流人才共事使我受益匪浅。相比顺其自然，谨慎地约束自己更有利于自身成长。

Q: 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?

A: I think it's very valuable to have first-class people around. I sought out the best people.

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.

评论区索要演讲稿原文。