这篇摘抄来源于对 理查德·卫斯理·汉明（Richard Wesley Hamming） 在 1986 年 3 月 7 日 的名为 You and Your Research 演讲的转录。

Hamming，1968 年图灵机获得者，信息论中 Hamming Distance 理论主要贡献者

该演讲主要聚焦在 Hamming 对 “为什么只有极少数的科学家做出了伟大的贡献，而绝大部分科学家却在时间的长流中被遗忘” 这一问题的观察和研究。

以下内容是对演讲转录的摘抄，完整的演讲内容见 You and Your Research

摘抄的内容并非逐字的对原文进行翻译，为保证阅读流畅，可能会更改/增删一些表达，但尽可能的保证表达的含义相同。

以下摘抄中为 Hamming 的第一人称。

#The Talk

I saw I was a stooge. I saw that although physically I was the same, they were different. And to put the thing bluntly, I was envious.
…
I continued examining the questions, Why? and What is the difference?‘’ I continued subsequently by reading biographies, autobiographies, asking people questions such as: ``How did you come to do this?‘’ I tried to find out what are the differences. And that’s what this talk is about.

我在刚加入贝尔实验室时，面对费曼，香农，汉斯等科学家时，深感到自己与他们的差异，并对他们的能力和高效感到羡慕。为了探索出他们与自己不同的原因，我阅读了传记，自传以及对他们进行了采访。这些探索过程和结果便是这个演讲的内容。

Now, why is this talk important? I think it is important because, 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
…
I will talk mainly about science because that is what I have studied.
…
Outstanding work is characterized very much the same way in most fields, but I will confine myself to science.

为什么这个话题很重要，因为人只会活一次，即便你相信来世，也没关系，为何不在今生就做一些伟大的事呢？

我将会主要通过科学领域的观察来回答这个话题，但这个话题同样适用于其他的领域。

I have to get you to 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.

#关于运气

In order to get at you individually, I must talk in the first person. I have to get you to 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.

你应该放弃谦逊，并对自己说 “是的，我想做一流的工作”。我们的社会风气并不赞赏那些努力去做伟大事业的人，它期望的是某人做出了伟大的工作，是因为这个人踩了狗屎运。

I find that the major objection is that people think great science is done by luck. It’s all a matter of luck. Well, consider Einstein. Note how many different things he did that were good. Was it all luck?

我发现科学研究最大的阻碍在于人们认为伟大的科学是靠运气完成的，认为所有科学研究都是运气问题。但你想下爱因斯坦，想下他做了多少伟大的工作，难道所有这些伟大工作都是因为爱因斯坦运气好吗？

You see again and again, that it is more than one thing from a good person
…
I claim that luck will not cover everything. And I will cite Pasteur who said, ``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.

你会一次又一次看到，一个优秀的人并不是仅仅有一个成就。Pasteur 说 “好运偏爱有准备的人”，那些有准备的人或早或晚都会发现一个重要的事情并去完成它。

I want to dispose of this matter of luck as being the sole criterion whether you do great work or not. I claim you have some, but not total, control over it.
…
Newton said, ``If others would think as hard as I did, then they would get similar results.‘’

我反对的是将运气作为你是否能做伟大工作的唯一标准。针对于“运气”，你对它是存在一些控制权的，就像牛顿所言“如果其他人像我一样思考，他们就会得到和我相似结果。”

#关于勇气

Bill Pfann, the fellow who did zone melting, came into my office one day. He had this idea dimly in his mind about what he wanted and he had some equations. … but ultimately he has collected all the prizes in the field. Once he got well started, his shyness, his awkwardness, his inarticulateness, fell away and he became much more productive in many other ways. Certainly he became much more articulate.

A fellow named Clogston…I didn’t think he had much…Well I would have fired the fellow…Clogston finally did the Clogston cable. After that there was a steady stream of good ideas. One success brought him confidence and courage.

Bill Pfann 一开始在他们部门的认可微乎其微，但他最后获得了他领域的所有奖项。他开始获奖后，他的害羞，他的尴尬，他的口吃都消失了。他在许多领域都变得更加高效，他也变得更加善于表达。

我的一个叫做 Clogston 的同事，我觉得他并没有太多的才华，甚至于我曾想要开除他。但他最终做出了以他命名的电缆，一次的成功给他带来了自信和勇气。

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

成功科学家的一大品质就是拥有勇气，一旦你鼓起勇气并相信你能解决重要的问题，那你就能成功。而如果你认为自己做不到，那大概率你确实无法做到。

伟大科学家的勇气，让他们即使在几乎不可能的情况下，仍然能思考，仍然能继续思考。

#关于年龄

Age is another factor which the physicists particularly worry about. They always are saying that you have got to do it when you are young or you will never do it. Einstein did things very early, and all the quantum mechanic fellows were disgustingly young when they did their best work. 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. I don’t know how whatever field you are in fits this scale, but age has some effect.

年龄是物理学家常常担心的问题。物理学家总是说，伟大的成就要么在你年轻时得到，要么就永远得不到。爱因斯坦在他非常年轻的时候取得了成就，所有的量子力学研究员也都在他们非常年轻的时候完成了我们认为最好的工作。大多数数学家，理论物理学家，天体物理学家也是这样，这并不是说他们在晚年没有做好工作，而是大家觉得最有价值的往往是他们年轻时的工作。但另一方面，音乐，政治，文学方面的人，我们认为他们最好的作品却往往在他们晚年时产出。总之年龄确实会有一些影响。

But let me say why age seems to have the effect it does. 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.
The third one, Brattain, practically with tears in his eyes, said, I know about this Nobel-Prize effect and I am not going to let it affect me; I am going to remain good old Walter Brattain.‘’ Well I said to myself, That is nice.‘’ But in a few weeks I saw it was affecting him. Now he could only work on great problems.
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. So that is another reason why you find that when you get early recognition it seems to sterilize you.

但我要解释下为何在科学领域，看起来伟大工作都发生在年轻时。这是因为，一旦你做了一些好的工作，你就会发现自己身处各种委员会中，你也就不再能做任何伟大工作了。

Brattain 在诺贝尔奖项宣布的那天，说他不会让诺贝尔奖影响它，但几周后，我看到了诺贝尔奖给他带来的影响，现在他只能解决 大 问题了。

当你有名后，你很难解决 小 的问题。伟大的科学家经常犯这样的错误，他们不再种植可能会长成大橡树的 小橡子，，他们试图直接获取大橡树，但事情的发展并不是这样的。这也是为什么你会发现，当你获得了早期认可，你就被“绝育”了。

#关于工作条件

I think that if you look carefully you will see that often the great scientists, by turning the problem around a bit, changed a defect to an asset. For example, 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. So ideal working conditions are very strange. The ones you want aren’t always the best ones for you.

如果你仔细观察，你会发现伟大的科学家经常会将缺陷变为资产。比如，许多科学奖当发现他们无法解决一个问题时，他们会开始思考 为什么，并最终以此得到了一个重要的解决方式。所以理想的工作条件很奇怪。你想要的并不总是最适合你的。

#关于驱动力

You observe that most great scientists have tremendous drive. I worked for ten years with John Tukey at Bell Labs. He had tremendous drive. One day about three or four years after I joined, 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!

大多数伟大的科学家都有巨大的动力。我在贝尔实验室与 John Tukey 一起工作了十年，在我加入贝尔的大约三四年后的一天，我发现约翰·图基甚至比我还年轻一点。约翰是个天才，而我显然不是。有一天我冲进 Bode 的办公室说，“像我这个年纪的人，怎样才能像 John Tukey 一样知道那么多呢？” Bode 靠在椅子上，双手放在脑后，微微一笑，说：“Hamming，如果你像他一样努力工作并坚持多年的话，你就会对你自己的知识积累而感到惊讶。”

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 - it is very much like compound interest. I don’t want to give you a rate, but it is a very high rate. 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. I took Bode’s remark to heart; I spent a good deal more of my time for some years trying to work a bit harder and I found, in fact, I could get more work done. 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.

Bode 说的是：“知识和生产力就像复利。假设两个能力大致相同的人，一个人比另一个人多工作 10%，后者的产量将超过前者的两倍以上。”

你知道的越多，你学到的就越多，你学得越多，你能做的就越多，你能做的越多，机会就越多——这很像复利。

我把 Bode 的话记在心里：几年来，我花了很多时间试图更加努力地工作，事实上，我发现我可以完成更多的工作。我不喜欢在我妻子面前说出来，但有时我确实有点忽视她。我需要学习。如果你打算完成你想要做的事情，你必须忽略一些东西，这没有办法。

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.

但误用的驱动力，不会带你走向任何的成功。我经常想，为什么我在贝尔实验室的那么多好朋友，他们和我一样努力或比我更加的努力工作，却没有那么多东西可以展示。滥用努力是一个非常严重的问题。仅仅努力工作是不够的，你必须在正确的方向上努力。

#关于接受模棱两可

There’s another trait on the side which I want to talk about; that trait is ambiguity. It took me a while to discover its importance.。 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. 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.

另一个我花了很长时间才意识到的重要特质是接受模棱两可。大多数人喜欢相信一件事是真的或是假的，但伟大的科学家能忍受模棱两可。一方面他们足够的相信一个理论，这样他们才能继续研究这个理论。另一方面他们又对这个理论存在足够的怀疑，以至于他们能注意到理论的错误，并发展出新的替代性理论。如果你太相信，那么你永远不会注意到缺陷，但如果你怀疑的太多，你就不会出发。相信和怀疑之间需要一个可爱的平衡。

大多数伟大的科学家都很清楚为什么他们的理论是正确的，同时他们也很清楚理论中存在的一些无法说通的点，科学家们也不会忘记这些点。

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.

达尔文在他的自传中写道，他发现有必要写下每一个看起来与他的理论不相符合的证据，否则它们就会从他的脑海中消失。当你发现明显的缺陷时，你必须保持敏感并跟踪这些事情，并思考如何解释它们或如何改变理论以适应它们，这些往往会造就伟大的贡献。

#关于潜意识

Everybody who has studied creativity is driven finally to saying, ``creativity comes out of your subconscious.‘’ Somehow, suddenly, there it is. It just appears. Well, we know very little about the subconscious; but one thing you are pretty well aware of is that your dreams also come out of your subconscious. And you’re aware your dreams are, to a fair extent, a reworking of the experiences of the day. 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.

每一个研究过创造力的人最终都会说，“创造力来自你的潜意识。不知何故，突然间，它就在那里。它只是出现”。虽然我对潜意识研究甚少，但我知道宛如日有所思夜有所梦一般，如果你日复一日地深深地沉浸在一个话题上，你的潜意识除了解决你的问题之外别无他法。因此，当你遇到一个真正重要的问题时，你不要让其他任何事情成为你关注的焦点——你专注在这个问题上，让你的潜意识保持饥饿，这样它就必须解决你的问题。这样的话，你就可以安然入睡，并在某一个早上免费得到答案。

#关于目标

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 them…The average scientist, so far as I can make out, 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.

如果你不为一个重要的问题工作，你基本不可能做出伟大的成就，这是显而易见的。

我看到的普通科学家，几乎把所有的时间都花在了他们认为不重要的问题上，他也不相信这些问题会引领他们走向别的重要的问题。

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.

普通的科学家，几乎一直在做例行的舒适区内的工作，所以他们不会有巨大的产出，就这么简单。如果你想要做伟大工作，你显然必须在重要的问题上工作，而且你应该有一个想法知道什么是重要的问题。

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.

大多数科学家知道许多重要的问题，他们会关注着大约 10 到 20 个重要的问题。当他们有一个新想法或看到一个新契机，他们脑海中会出现一个声音“嗯，这个与问题 A 有关”。然后他们就会抛下其他一切，全力投入这个问题。

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…One of the chief tricks is to live a long time!

当机会出现时，伟大的科学家们会抓住它并追求它。他们会放弃了其他所有的东西。他们之所以能抛弃其他的一切，而专注于抓住这个机遇，是因为他们已经有过了深刻的思考。他们的思维已经准备好了，只要他们一看到了他们一直等待的机会，他们就会续追逐它。

另外等待机遇的一个窍门就是活得长。

#关于开放

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.

如果你工作时把门关上，你在今天和明天可以更好的完成工作，且你会比大多数人更高效。但 10 年后你或许并不知道什么问题才是真正需要被解决的，所有你认真完成的工作可能与重要性并不相关。

把门打开工作的人，或许会收到各种干扰，但他也会时不时的得到“当前世界什么事情最重要”的线索。

#关于抽象工作

In the same way, when using the machine up in the attic in the early days, I was solving one problem after another after another; a fair number were successful and there were a few failures. I went home one Friday after finishing a problem, and curiously enough I wasn’t happy; I was depressed. I could see life being a long sequence of one problem after another after another. After quite a while of thinking I decided, ``No, 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.‘’

早年间我攻克一个又一个难题，成功的多，失败的少。在一个周五，当我解决完一个问题回家时，我并没有感到快乐，相反我感到沮丧。我感觉的人生就是一个问题接着一个问题，再接着一个问题。在一段时间的思考后，我决定“我应该关心明年所有的问题，而不仅仅是我面前的问题。”

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. By changing a problem slightly you can often do great work rather than merely good work. Instead of attacking isolated problems, I made the resolution that I would never again solve an isolated problem except as characteristic of a class.

你应该以“别人可以在我工作的基础上建立其他工作”的方式做的你的工作。科学的本质是积累，所以我下定决心不再解决孤立的问题。

Now if you are much of a mathematician you know that the effort to generalize often means that the solution is simple. Often by stopping and saying, ``This is the problem he wants but this is characteristic of so and so. Yes, I can attack the whole class with a far superior method than the particular one because I was earlier embedded in needless detail.‘’ The business of abstraction frequently makes things simple. Furthermore, I filed away the methods and prepared for the future problems.

如果你是一个数学家，你就知道泛化的解决方案往往意味着解决方案是简单的。在数学的工作中，你可能常常会停下工作并意识到“这就是要解决的问题，但这有个特殊点 blablabla。我其实可以以一种更简单的方式完整的解决这类型的所有问题，但因为我过早的陷入了不必要的细节，所以我只做出了一个解决特定问题的复杂答案。”抽象的过程常常让事物变得简单，此外，抽象意味着将方法进行了归档，并为之后的问题做准备。

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!

你选择以“别人可以在我的基础上再接再厉”的方式去工作，也可以以“别人基本上需要再次复制我所做的”的方式去工作，这两者会产生巨大的生产力差异。这不仅仅是你工作的方式，也包含你写报告的方式，写论文的方式。做一个广泛的，通用的解决方案通常比做一个特化问题的解决方案更简单，也通常更令人满意和有帮助。

#关于推销自己

it is not sufficient to do a job, you have to sell it. Selling to a scientist is an awkward thing to do. It’s very ugly; you shouldn’t have to do 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.‘’

只完成工作是不够的，你还需要推销它。“推销” 对科学家而言是一个尴尬的事，它很烦，你不应该需要做它。当你做出了一些伟大的事情事，这个世界应该立刻欢迎它。但事实上，每个人都因为自己的工作而忙碌，所以只有你推销了你的工作，其他人才会将他们的工作放在一边，并看看你做了什么，然后说“嗯，不错”。

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. We had a lot of so-called back room scientists. In a conference, they would keep quiet. Three weeks later after a decision was made they filed a report saying why you should do so and so. Well, it was too late. 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.

在推销自己时，必须要做好三件事：

  • 学会清晰的写作，这样人们才会愿意阅读
  • 学会正式的演讲
  • 学会非正式环境的谈话

我们有很多所谓的“幕后科学家”。在会议上，他们会保持沉默。当会议结束的三周后，他们会提交一份报告，说明为什么要这样做。但这样就太晚了，没人会关注到他们。他们不会在激烈的会议中间站起来说 “出于这些原因，我们应该 blablabla”。你必须要需要掌握这种沟通形式以及准备好随时演讲。

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. 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. Then a larger number of people will say, Yes, Joe has done that,‘’ or Mary has done that; I really see where it is; yes, Mary really gave a good talk; I understand what Mary has done.‘’

技术人员通常想要做一个非常聚焦，专精的技术演讲，而大多数时候，听众则想要一个广泛的一般性演讲，并且想要更多的调查数据和问题背景。所以，大多数的技术演讲是无效的，演讲者说出一个话题，然后突然进入了细节，听众很难跟上演讲者的思路。你应该给出一个大框架，说明为什么这个问题很重要，然后慢慢勾勒出所作的内容。这样大部分的听众会给出 “是的，Joy 做了一个重要的事”，“Mary 做了一个很好的演讲，我能明白 Mary 做了什么” 这样的评价。

#关于聚焦方向

I committed 10% of my time trying to understand the bigger problems in the field, i.e. what was and what was not important. 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. So I changed something I did and I marched in the direction I thought was important. It’s that easy.

我把 10% 的时间用来理解领域中更 大 的问题，也就是什么是重要的，什么不重要。我发现在早期，我相信了 A 是重要的，但我却花了一周的时间在 B 问题上。这有点蠢。如果我真的相信我应该在 A 方向行动，为什么我还要朝着 B 方向前进？我要么改变我的目标，要么改变我所做的事情。所以我改变了我所做的事情，我朝着我认为重要的方向前进。就这么简单。

Now you might tell me you haven’t got control over what you have to work on. Well, when you first begin, you may not. But once you’re moderately successful, there are more people asking for results than you can deliver and you have some power of choice, but not completely.

你可能会告诉我，你没有权力控制你所要做的事情。好吧，当你刚开始工作时，你可能确实没有。但一旦你有了一定的成功，就会有更多的人需要你的结果，而你却无法满足所有人的需求，这时你就有了一些选择的权力，但不是完全的。

I am telling you how you can get what you want in spite of top management. You have to sell your ideas there also.

你可以在不受高层管理的影响下，得到你想要的东西，但你必须在管理层推销你的想法。

#关于动力

Is the effort to be a great scientist worth it?‘’ To answer this, you must ask people. When you get beyond their modesty, most people will say, Yes, doing really first-class work, and knowing it, is as good as wine, women and song put together,‘’ or if it’s a woman she says, It is as good as wine, men and song put together.‘’ And if you look at the bosses, they tend to come back or ask for reports, trying to participate in those moments of discovery. They’re always in the way. So evidently those who have done it, want to do it again. But it is a limited survey. I have never dared to go out and ask those who didn’t do great work how they felt about the matter. It’s a biased sample, but I still think it is worth the struggle. 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.

“成为一位伟大的科学家的努力是否值得？”为了回答这个问题，你需要去询问人们。当你让他们抛下顾虑时，大多数人会说，“是的，做真正一流的工作，并理解它，就像把美酒、女人和歌曲结合在一起那样好。” 或者如果你问的是一个女人，她会说：“这就像把美酒、男人和歌曲结合在一起一样美好。” 当你观察那些老板时，他们似乎总是会来参与进一流的工作或要求给出一流工作的报告，他们总是试图参与那些重要的发现时刻，虽然这一定程度上会会妨碍我们的工作。所以显然，那些曾经做过一流工作的人，都会想再次去做一流的工作。但这是一个有限的调查。我从未敢问那些没有做出伟大工作的人他们对此事的感受。虽然这是一个有偏差的样本，但我仍然认为努力去做一流的工作绝对是值得的，因为事实上，价值更多地在于挣扎本身，而不是结果。努力让自己变得更好似乎本身就是有价值的。在我看来，成功和名声只是一种额外收益。

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 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. They don’t have the deep commitment that is apparently necessary for really first-class work. They turn out lots of good work, but we were talking, remember, about first-class work. There is a difference. Good people, very talented people, almost always turn out good work. We’re talking about the outstanding work, the type of work that gets the Nobel Prize and gets recognition.

那些能力较弱但致力于实现伟大成就的人，比那些有着非凡技能、却只是粗略的使用技能的人完成更多工作。那些有着非凡技能的人白天工作，晚上回家做其他事情，然后第二天回来继续工作，他们没有显现出真正做一流工作所必需的深入投入。他们的成果很多，但请记住，我们谈论的是一流的工作。这两者之间存在差异。表现出色的人，非常有才华的人几乎总是能完成好的工作。但我们讨论的是杰出的工作，那种能获得诺贝尔奖并得到认可的工作。

#关于穿着

I came from Los Alamos and in the early days I was using a machine in New York at 590 Madison Avenue where we merely rented time. I was still dressing in western clothes, big slash pockets, a bolo and all those things. I vaguely noticed that I was not getting as good service as other people. So I set out to measure. You came in and you waited for your turn; I felt I was not getting a fair deal. I said to myself, ``Why? No Vice President at IBM said, Give Hamming a bad time It is the secretaries at the bottom who are doing this. When a slot appears, they’ll rush to find someone to slip in, but they go out and find somebody else. Now, why? I haven’t mistreated them.‘’ Answer, I wasn’t dressing the way they felt somebody in that situation should. It came down to just that - I wasn’t dressing properly. 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.

我来自 Los Alamos，早期我在纽约的 590 麦迪逊大街使用一台机器，那时我们只能租用设备一段时间使用。那时我仍然穿着西部服装，大口袋，蝴蝶结等。我隐约注意到我得到服务并不如其他人。所以我开始衡量，当排队等待轮到我的时候，我觉得我没有得到公平的待遇。我问自己，为什么？IBM 的副总裁肯定没有说过要给 Hamming 难堪之类的话。当有机器有一个空闲时段出现时，工作人员会急忙去找某人去使用，但他们总会选择其他人。为什么？我并没有虐待那些工作人员。最后我发现答案是，我没有穿工作人员认为的那个场合应该穿的衣服。归根结底就是这个原因——我穿着不得体。

因此我必须做一个决定——我是要坚持我自己的风格，让它不断地削弱我在专业上的付出，还是我要表现得更为顺从？我决定竭力表现得更为合宜。当我这么做时，我得到了更好的服务。现在，作为一个有趣的老人，我得到的服务比其他人更好。

You should dress according to the expectations of the audience spoken to. If I am going to give an address at the MIT computer center, I dress with a bolo and an old corduroy jacket or something else. I know enough not to let my clothes, my appearance, my manners get in the way of what I care about. 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.

你应该根据你面对的观众的期望来着装。如果我要在麻省理工学院计算机中心发表演讲，我会穿一条蝴蝶领带和一件旧灯芯绒夹克之类的衣服。我知道不能让我的衣着、外表和礼仪妨碍我关心的事情。有许多科学家认为他们必须坚持自己的风格，用自己的方式做事。但他们必须改变自己来符合观众的期望，否则，他们会持续付出代价。

John Tukey almost always dressed very casually. He would go into an important office and it would take a long time before the other fellow realized that this is a first-class man and he had better listen. For a long time John has had to overcome this kind of hostility. It’s wasted effort! 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.

John Tukey 几乎总是穿着非常休闲的衣服。当他会走进一个重要的办公室，过很长时间，对方才会意识到这是一个一流的人，他最好要认真倾听。很长一段时间以来，John 一直不得不克服这种敌意。这是浪费力气！我并没有说你应该完全顺从，我说的是“看起来顺从会带给你很大的便利。”如果你选择以许多不同的方式来坚持你的自我，“我要用我的方式去做”，那么在整个职业生涯中，你会持续付出一些小的代价。而这在一生中累计起来，会导致大量不必要的麻烦。

And I think John Tukey paid a terrible price needlessly. He was a genius anyhow, but I think it would have been far better, and far simpler, had he been willing to conform a little bit instead of ego asserting. He is going to dress the way he wants all of the time. It applies not only to dress but to a thousand other things; people will continue to fight the system. Not that you shouldn’t occasionally!

我认为 John Tukey 付出了可怕的，且不必要的代价。无论如何，他是个天才，但我认为，如果他愿意更对这个社会顺从一点而不是一味的自我主张，事情会好得多，也简单得多。他一直按照他想要的方式穿着，而且不仅仅是在着装领域，在其他上千件事情上 John 也这样。人们如果持续的与社会的要求做斗争，会付出不少的代价。当然了，在一些时刻，坚持自己也是应该的。

#关于制度

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. Now you are going to tell me that somebody has to change the system. I agree; somebody’s has to. Which do you want to be? The person who changes the system or the person who does first-class science? Which person is it that you want to be? 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. My advice is to let somebody else do it and you get on with becoming a first-class scientist. Very few of you have the ability to both reform the system and become a first-class scientist.

许多二流的人都会陷入对制度系统的一些缺陷的关注，并大张旗鼓的要改变它，于是他把精力消耗在了一个愚蠢的项目上。或许你会说 “必须有人改变系统”。我同意，有人必须这样做，但你想成为哪种人？一个改变制度的人还是做出一流科学成就的人？你必须清楚地知道，当你与系统作斗争并与之斗争时，你究竟在做什么，你是不是在趁机休息或娱乐，你在与系统作斗争时浪费了多少精力。我的建议是让别人去做，然后你就可以成为一流的科学家。很少有人有能力既改革体制又成为一流的科学家。

On the other hand, we can’t always give in. There are times when a certain amount of rebellion is sensible. I have observed 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. 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’m not against all ego assertion; I’m against some.

另一方面，我们不能总是屈服于制度。有时，一定程度的反抗是明智的。我观察到，几乎所有科学家都出于对制度系统的纯粹热爱而喜欢对系统进行一定程度的改进。归根结底是，如果你在某个领域没有原创性，那么在其他领域就不可能有原创性。原创就是与众不同。如果你无法在一个制度系统中发现待改进的点，你很难成为一名原创性的科学家。但许多科学家的一些自我主张，让他在获取自我满足外，付出了过高的代价，他们过度的关注了制度是否满足他们的需求。我并不反对所有的自我主张，我反对一些代价高昂的自我主张。

Another fault is anger. Often a scientist becomes angry, and this is no way to handle things. Amusement, yes, anger, no. Anger is misdirected. You should follow and cooperate rather than struggle against the system all the time.

另一个错误是愤怒。科学家常常会生气，但错误会让你没有办法处理事务。幽默是好的，但愤怒不是。愤怒是误导性的，你应该跟随和配合制度，而不是一直与制度作斗争。

#关于自我认知

I am an egotistical person; there is no doubt about it. I knew that most people who took a sabbatical to write a book, didn’t finish it on time. So before I left, I told all my friends that when I come back, that book was going to be done! Yes, I would have it done - I’d have been ashamed to come back without it! I used my ego to make myself behave the way I wanted to. I bragged about something so I’d have to perform. I found out many times, like a cornered rat in a real trap, I was surprisingly capable.

我无疑是一个自负的人。我知道大多数人会决定在休假的时候写一本书，但常常完不成。所以我会在去休假前，告知我所有的朋友“当我休假结束，这本书就基本写完了”。这样我就能完成这本书，因为我一想到我回来时这书没写完，我就会觉得在朋友面前会太丢脸。我利用了我的自尊来完成我想要做的事，我会向别人吹嘘一些我必须要做的事。很多时候，这会让我像一个落入陷阱的老鼠一样，表现出令人吃惊的能力.

Now self-delusion in humans is very, very common. There are enumerable ways of you changing a thing and kidding yourself and making it look some other way. When you ask, Why didn’t you do such and such,‘’ the person has a thousand alibis. If you look at the history of science, usually these days there are 10 people right there ready, and we pay off for the person who is there first. The other nine fellows say, Well, I had the idea but I didn’t do it and so on and so on.‘’ There are so many alibis. 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.

自我欺骗非常，非常的普遍。有许多的方式，你可以改变一件事然后欺骗自己，让它看起来有不一样的表现。当被问起 “你为什么不 blablabla” 时，人们有一千个理由。当你回顾科学发展的历史，你会发现在一个时间点，可能有 10 个科学家都已经有了做出伟大成就的准备，但只有一个人会首先迈出最终一步，然后剩下的九个人会说“我也有了这个想法，但我没去做他，因为 blablabla。” 人能给自己找的借口太多了，但为何你不是第一个人？为什么你没法把事情做对？不要尝试找借口，不要尝试欺骗自己，你可以告诉别人所有你想要的接口。这无所谓，但你不要骗自己就好。

#Discussion

#关于勇气

Question: The remarks about having courage, no one could argue with; but those of us who have gray hairs or who are well established don’t have to worry too much. But what I sense 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?

Hamming: I’ll quote Ed David more. Ed David was concerned about the general loss of nerve in our society. It does seem to me that we’ve gone through various periods. Coming out of the war, coming out of Los Alamos where we built the bomb, coming out of building the radars and so on, there came into the mathematics department, and the research area, a group of people with a lot of guts. They’ve just seen things done; they’ve just won a war which was fantastic. 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. It doesn’t seem to me they have the desire for greatness; they lack the courage to do it. But we had, because we were in a favorable circumstance to have it; we just came through a tremendously successful war. In the war we were looking very, very bad for a long while; it was a very desperate struggle as you well know. And our success, I think, gave us courage and self confidence; that’s why you see, beginning in the late forties through the fifties, a tremendous productivity at the labs which was stimulated from the earlier times. Because many of us were earlier forced to learn other things - we were forced to learn the things we didn’t want to learn, we were forced to have an open door - and then we could exploit those things we learned. It is true, and I can’t do anything about it; I cannot blame the present generation either. It’s just a fact.

问题：你关于勇气的部分的阐述毋庸置疑。但对于我们这些老人或者说一些已经成家立业的人而言，我们有了后盾，所以我们能鼓起勇气。但对于现在的年轻人，他们处在一个高度的竞争环境下，他们需要承担过高的风险以至于很难鼓起勇气。对于这个情况，你有什么建议或看法？

Hamming：在我看来，我们和现在的年轻人确实经历了不同的时期。我们是从战争时期中走出来的，我们在 Los Alamos 制造了炸弹，我们创造了雷达，在数学系和其他科学领域，有许多充满勇气的人。他们刚刚完成了所有的事，他们刚刚赢得了一场非常伟大的战争。因为战争，我们有必要有勇气，因此我们做了很多事情。但在这个时刻，我无法重新创造出战争那样的范围，我也不能责怪当代人没有这样的氛围，所以同意你的说法。在我看来，现在的年轻人并没有追求伟大的愿望，他们缺乏这样做的勇气。但我们有，是因为我们处于有利的环境中，我们刚刚经历了一场非常成功的战争。在战争中，我们有很长一段时间看起来非常非常糟糕。正如你所知，这是一场非常绝望的斗争。我认为，战争中的成功给了我们勇气和自信；这就是为什么你会看到，从四十年代末到五十年代，实验室在早期的刺激下取得了巨大的成果。因为我们中的许多人早些时候被迫学习其他东西 - 我们被迫学习我们不想学习的东西，我们被迫打开一扇门 - 然后我们可以利用我们学到的那些东西。这是事实，但我对此无能为力；我也不能责怪当代人。这只是事实。

#关于头脑风暴

Question: Is brainstorming a daily process?

Hamming: 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. I do go in to strictly talk to somebody and say, Look, I think there has to be something here. Here’s what I think I see …‘’ and then begin talking back and forth. But you want to pick capable people. To use another analogy, you know the idea called the critical mass. If you have enough stuff you have critical mass. There is also the idea I used to call sound absorbers .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?‘’ When you talk to other people, 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.

问题：你是否觉得头脑风暴应该成为一个日常过程？

Hamming: 头脑风暴曾经是一个非常流行的活动，但它似乎没有产生太多的收益。对我自己而言，我觉得与某些人交谈是值得的，但一个头脑风暴活动却很少会产生结果。我会找到特定的人，然后说 “我发现…我觉得…”，然后开始与他讨论。有一个概念叫 “临界质量”，当你有足够的知识后，你就有了与别人交流的 “临界质量” 了，这时候交流才是有价值的。我有个自己定义的概念叫 “吸音器”。当你交流的对象，大多是 “吸音器” 时，你能得到的回答就都是 “是的，是的，是的，嗯，嗯，嗯”。你要做的，就是保证参与的对象，都到了 “临界质量”，然后就能得到 “是的，这让我想起了 xxx”，“你有没有考虑过 xxxx”。当你决定和别人交谈时，你要摆脱那些只会说 “哦，好的” 的人，然后找到那些能刺激你的人。

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. Yes, I find it necessary to talk to people. I think people with closed doors fail to do this so they fail to get their ideas sharpened, such as ``Did you ever notice something over here?‘’ I never knew anything about it - I can go over and look. Somebody points the way. On my visit here, I have already found several books that I must read when I get home. I talk to people and ask questions when I think they can answer me and give me clues that I do not know about. I go out and look!

我会精心挑选那些我共事的人，我也会精心挑选我 不 一起进行头脑风暴的人，因为 “吸音器” 是诅咒。 他们是好人，但他们会充满整个空间但不提供任何的东西，他们只会吸收所有的想法，所有新的想法会直接消亡而不是在大家脑海中回荡。是的，与人交流是有必要的，我认为那些关起门工作的人没有机会磨砺自己的想法，他们听不到类似于 “你有没有意识到 xxxx” 这样的回复。如果别人提出了我从未想到过的想法，我就会去关注和学习下这想法，一些人就曾给过我这样的想法。在我来这访问的时候，我已经听到了一些当我回家后必须要读的书。我会与那些我觉得会给出我未曾想过的思路线索的人交谈和向他们提问题。

#关于阅读 / 写作 / 做研究 的时间平衡

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

Hamming: 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. Now at least 50% of the time must go for the presentation. It’s a big, big number.

问题： 你觉得在读书，写作和做研究间，时间该如何分配。

Hamming：在我早期工作时，我认为你应该至少花费与研究一样多的时间去润色和演示你的成果。而对于现在的我而言，至少需要 50 % 的时间需要用来展示成果，这是一个很大的占比。

#关于阅读的方式

Question: How much effort should go into library work?

Hamming: It depends upon the field. I will say this about it. There was a fellow at Bell Labs, a very, very, smart guy. He was always in the library; he read everything. If you wanted references, you went to him and he gave you all kinds of references. But in the middle of forming these theories, I formed a proposition: there would be no effect named after him in the long run. He is now retired from Bell Labs and is an Adjunct Professor. He was very valuable; I’m not questioning that. He wrote some very good Physical Review articles; but there’s no effect named after him because he read too much. 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.

问题：我应该将多少事件花费在图书馆进行阅读？

Hamming：这个答案和你研究的领域相关。我知道在贝尔实验室有个人，他非常非常聪明。他几乎每天都在图书馆，他读了所有的书籍。如果你需要参考资料，你就去找他，他会给你所有的参考资料。但在一系列理论产生的时期，我觉得不会有任何的理论会以他的名字来命名。他现在已经退休了，成为了一名兼职教授。他非常有价值，我不是在质疑这一点。他写了一些非常好的物理评论文章，但没有一个理论或效应以他的名字命名，因为他读的太多了。如果你一直在阅读别人的成果，你会以他们的方式去思考。如果你想要有不同的思考，那么你需要做一些创造性的事情，你需要清楚的定义问题，然后拒绝看任何答案，直到你真的仔细的思考过这个问题：你会如何做，你会如何稍微改变看问题的角度来使问题变得可以解决正确。所以是的，你需要保持阅读，你需要保持阅读来发现问题而不是找到答案。阅读是必要的，你需要靠阅读知道这个世界发生了什么，什么是可能的。但是通过阅读来找到答案，似乎不是做出伟大研究的方式。所以我答案是，你需要阅读，但要关注的不是阅读的量，而是阅读的方式。

#关于研究方向

Question: 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?

Hamming: 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. Shannon, I believe, ruined himself. In fact when he left Bell Labs, I said, That’s the end of Shannon’s scientific career.‘’ I received a lot of flak from my friends who said that Shannon was just as smart as ever. I said, Yes, he’ll be just as smart, but that’s the end of his scientific career,‘’ and I truly believe it was.

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.‘’ For example, when error correcting codes were well launched, having these theories, 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. I managed myself, which is what I’m preaching in this whole talk. 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.

问题：你提到了诺贝尔奖的问题，以及随后的名声对一些人事业的影响。这不是名声的一个更广泛的问题吗？一个人能做什么？

Hamming: 你可以做的一些事情是以下几点。大约每七年，在你的领域做一个重大的，如果不是完全的，转变。因此，我从数值分析转向硬件，再到软件，等等。你需要定期的转变，因为你会逐渐用完你的想法。当你进入一个新的领域时，你必须像一个婴儿一样重新开始。你不再是大人物，你可以从那里开始，你可以开始种植那些将成为巨大橡树的橡子。我相信香农毁了自己。事实上，当他离开贝尔实验室时，我说，“这是香农科学生涯的终结。”我的朋友们对此表示了很多的抱怨，他们说香农和以前一样聪明。我说，“是的，他还是一样聪明，但这是他科学生涯的终结”，我真的相信是这样的。

你必须改变。过了一段时间，你就会累了；你在一个领域里用完了你的独创性。你需要得到一些附近的东西。我不是说你应该从音乐转向理论物理学，再转向英国文学；我的意思是，在你的领域内，你应该转向其他领域，这样你就不会变得陈腐。你不需要强迫自己每七年改变一次，但如果你能，我会要求你在研究中改变你的领域，那些腐朽的人人们会发生什么事情呢？他们得到了一个技术，他们继续使用它，在当时那个时刻，这技术是在正确的方向上前进。但世界在变化，有了新的方向后，腐朽的人们仍然在他们以前的方向上前进。

你需要进入一个新的领域，以获得新的观点，而不是用完所有的旧观点。这需要努力和精力，你也需要勇气说，“是的，我会放弃我的伟大声誉。”例如，当纠错码被广泛应用时，我说，“Hamming，你要停止阅读这个领域的论文；你要完全忽略它；你要尝试做一些其他的事情，而不是在这个领域里继续。”我故意拒绝在这个领域继续前进。我甚至不会阅读论文，以便强迫自己有机会做其他的事情。我管理自己，这就是我在这次演讲中所宣扬的。了解我自己的许多缺点，然后管理自己。我有很多缺点，所以我有很多问题，也就有了很多管理的可能性。

#关于管理

Question: Would you compare research and management?

Hamming: 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 think Ian Ross does a good job as President of Bell Labs. I’m not against it; but 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. For instance, I went to my boss, Bode, one day and said, Why did you ever become department head? Why didn’t you just be a good scientist?‘’ He said, Hamming, I had a vision of what mathematics should be in Bell Laboratories. And I saw if that vision was going to be realized, I had to make it happen; I had to be department head.‘’ 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. If you have a vision of what the whole laboratory should be, or the whole Bell System, you have to get there to make it happen. You can’t make it happen from the bottom very easily. It depends upon what goals and what desires you have. And as they change in life, you have to be prepared to change. 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. 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.

问题：你能比较一下研究和管理的关系吗？

Hamming：如果你想成为一个伟大的研究者，你不会成为公司的总裁。如果你的目标是成为公司的总裁，那就完全是另一回事。我不反对成为公司的总裁，只不过我自己不想成为。我认为 Ian Ross 在贝尔实验室是一个很好的 Boss。我并不是反对人们去做管理，去做总裁，但你必须清楚你想要什么。此外，当你年轻的时候，你可能选择成为一个伟大的科学家，但随着你的年龄增长，你可能会改变主意。例如，有一天我去找我的老板 Bode，我问他：“你为什么要成为部门主管？你为什么不只是成为一个优秀的科学家？” 他说：“Hamming，我对贝尔实验室的数学有一个愿景。如果这个愿景有可能能够实现，那我就必须让它实现，所以我必须成为部门主管。”

当你对你想做的事情有一个愿景，而你可以独自完成，那么你应该去追求它。当你的愿景，你认为需要做的事情，比你一个人能做的事情更大的时候，你就必须向管理方向发展。愿景越大，你就必须走得越远。如果你有一个关于整个实验室或整个贝尔系统的愿景，你必须到管理层去实现它，你从一线员工的角度去实现它是非常困难的。所以管理和研究取决于你的目标和愿望。随着生活的变化，你必须做好准备去改变你的选择。我选择避免管理，因为我更喜欢独自做我能做的。

#关于别人的期许

Question: 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?

Hamming: 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 sought out the best people. The moment that physics table lost the best people, I left. The moment I saw that the same was true of the chemistry table, I left. 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.

问题：一个人的期望有多重要？或者说，被一个期望你能做出伟大工作的团队包围有多重要？

Hamming：在贝尔实验室，每个人都期望我能做出好的工作，这对我很有帮助。如果每个人都期望你能做出好的工作，你又有自尊心，那么你就会做出好的工作。我认为身边有一流的人是非常有价值的，所以我不断地在寻找最优秀的人。当物理学组失去最优秀的的人时，我离开了物理学组。当我看到化学组也是如此时，我也离开了。我试图和有很强能力的人在一起，这样我就可以向他们学习，他们也会期望我能做出伟大的成果。通过有意识地管理自己，我认为我做得比放任自流要好得多。

#关于运气

Question: You, at the outset of your talk, minimized or played down luck; but you seemed also to gloss over the circumstances that got you to Los Alamos, that got you to Chicago, that got you to Bell Laboratories.

Hamming: There was some luck. On the other hand 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. Is it luck the particular thing you do? For example, 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. And sure enough, he did do great work. It isn’t that you only do a little great work at this circumstance and that was luck, there are many opportunities sooner or later. 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. There is an element of luck, yes and no. Luck favors a prepared mind; luck favors a prepared person. It is not guaranteed; I don’t guarantee success as being absolutely certain. I’d say luck changes the odds, but there is some definite control on the part of the individual.

问题: 在你的演讲开始时，你淡化了运气的作用，你似乎也忽略了让你到 Log Alamos 的环境，让你到达 Chicago，让你到达贝尔实验室的环境。

Hamming：确实这些事有一些运气。但从另一方面，我也不知道如果这些事没发生，我会怎么样。除非我能说 “没这些事，我就不会同样成功或更成功”，不然我也没法将去这些地方定义为是 “好运” 的。例如，当我在 Los Alamos 遇到费曼时，我知道他将获得诺贝尔奖。我不知道具体是什么原因，但我就是很清楚地知道他会做出伟大的工作。无论未来出现什么样的方向，这个人都会做出伟大的工作，果然，他做出了伟大的工作。并不是说你只能在特定情况下做出伟大的工作，如果是那样的话，那确实是运气主导了一切。实际上你总会有很多机会。你会有一大堆机会。如果你处在某个情况下，你抓住了一个机会，你就会在那里取得伟大的成就。所以运气是有的，但它决定不了一切。运气青睐有准备的头脑，运气青睐有准备的人。当然我无法保证这一点，我不能保证成功是绝对的。我只能说运气改变了胜算，但个人也有一定的控制权。

#Reference

You and Your Research (virginia.edu)