"You and Your Research"

分享一篇文章。它表面上为从事科学研究的人而写，但其实适用性广泛。这是一篇关于如何做出卓越工作的老派文章。
阅读时间估算：25min，可以中午吃饭时看。

Richard Hamming 理查德·汉明

“You and Your Research”
《你与你的研究》

Transcription of the 转录自
Bell Communications Research Colloquium Seminar
贝尔通信研究研讨会 研讨会
7 March 1986 1986 年 3 月 7 日

At a seminar in the Bell Communications Research Colloquia Series, Dr. Richard W. Hamming, a Professor at the Naval Postgraduate School in Monterey, California and a retired Bell Labs scientist, gave a very interesting and stimulating talk, You and Your Research’ to an overflow audience of some 200 Bellcore staff members and visitors at the Morris Research and Engineering Center on March 7, 1986. This talk centered on Hamming’s observations and research on the question “Why do so few scientists make significant contributions and so many are forgotten in the long run?” From his more than forty years of experience, thirty of which were at Bell Laboratories, he has made a number of direct observations, asked very pointed questions of scientists about what, how, and why they did things, studied the lives of great scientists and great contributions, and has done introspection and studied theories of creativity. The talk is about what he has learned in terms of the properties of the individual scientists, their abilities, traits, working habits, attitudes, and philosophy.
在贝尔通信研究系列研讨会的一次讲座中，美国海军研究生院教授、已退休的贝尔实验室科学家理查德·W·汉明博士，于 1986 年 3 月 7 日在莫里斯研究与工程中心，向约 200 名贝尔核心员工及访客发表了题为“你与你的研究”的演讲。此次演讲聚焦于汉明对 “为何如此少的科学家能做出重大贡献，而多数人在长远看来被遗忘？” 这一问题的观察与研究。凭借他超过四十年的经验（其中三十年在贝尔实验室），他进行了大量第一视角观察，向科学家们提出了关于他们做什么、如何做及为何做的尖锐问题，研究了伟大科学家及其重大贡献的生平，并进行了关于内省及创造力理论的研究。演讲内容涵盖了他所学到的关于科学家个人特质、能力、性格、工作习惯、态度及哲学观等方面的见解。

%%已省略转录者的解释和主持人的长篇大论%%

THE TALK: “You and Your Research” by Dr. Richard W. Hamming
演讲：《你与你的研究》——理查德·W·汉明博士

It’s a pleasure to be here. I doubt if I can live up to the Introduction. The title of my talk is, “You and Your Research.” It is not about managing research, it is about how you individually do your research. I could give a talk on the other subject - but it’s not, it’s about you. I’m not talking about ordinary run-of-the-mill research; I’m talking about great research. And for the sake of describing great research I’ll occasionally say Nobel-Prize type of work. It doesn’t have to gain the Nobel Prize, but I mean those kinds of things which we perceive are significant things. Relativity, if you want, Shannon’s information theory, any number of outstanding theories - that’s the kind of thing I’m talking about.
很高兴来到这里。我怀疑自己能否不负引荐之词。我的演讲题目是《你与你的研究》。这并非关于研究管理，而是关乎你个人如何进行自己的研究。我本可以就另一主题展开讨论——但并非如此，它关乎的是你。我谈论的不是普通寻常的研究，而是伟大的研究。为了描述伟大的研究，我偶尔会提及诺贝尔奖级别的工作。它不必非得获得诺贝尔奖，但我指的是那些我们认为意义重大的成就。比如相对论，香农的信息论，以及众多杰出的理论——那正是我所谈论的这类事物。

Now, how did I come to do this study? At Los Alamos I was brought in to run the computing machines which other people had got going, so those scientists and physicists could get back to business. 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 wanted to know why they were so different from me. I saw Feynman up close. I saw Fermi and Teller. I saw Oppenheimer. I saw Hans Bethe: he was my boss. I saw quite a few very capable people. I became very interested in the difference between those who do and those who might have done.
那么，我是如何开始这项研究的呢？在洛斯阿拉莫斯，我被安排去操作别人已经启动的计算机，以便那些科学家和物理学家能回归他们的工作。我意识到自己只是个配角。我明白，尽管身体上我们相同，他们却与众不同。直白地说，我嫉妒了。我想知道他们为何与我如此不同。我近距离观察过费曼，见过费米和泰勒，见过奥本海默，还有我的上司汉斯·贝特。我见识了不少能力非凡的人物。我对实干者与潜在实干者之间的差异产生了浓厚兴趣。

When I came to Bell Labs, I came into a very productive department. Bode was the department head at the time; Shannon was there, and there were other people. 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.
当我来到贝尔实验室时，我进入了一个成果丰硕的部门。当时博德是部门主管；香农也在那里，还有其他一些人。我继续探究这些问题：“为什么？”以及“区别在哪里？”随后我通过阅读传记、自传，向人们提问：“你是如何开始做这件事的？”来持续探索。我试图找出其中的差异。这就是本次演讲要探讨的内容。

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, however you define significant? I’m not going to define it - you know what I mean. I will talk mainly about science because that is what I have studied. But so far as I know, and I’ve been told by others, much of what I say applies to many fields. Outstanding work is characterized very much the same way in most fields, but I will confine myself to science.
那么，为什么这次演讲很重要呢？我认为其重要性在于，据我所知，在座的各位都只有一次生命。即便你相信轮回转世，这对你的今生来世也毫无助益！为何不在这一生中做些有意义的事呢？无论你如何定义“有意义”——我不会去定义它，你们都懂我的意思。我将主要谈论科学，因为这是我研究的领域。但据我所知，并且他人也告诉我，我所讲的许多内容适用于多个领域。在大多数领域，杰出工作的特征极为相似，不过我将仅限于讨论科学范畴。

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. Well, that’s a kind of dumb thing to say. I say, why shouldn’t you set out to do something significant. You don’t have to tell other people, but shouldn’t you say to yourself,
Yes, I would like to do something significant.”
为了与你们每个人对话，我必须用第一人称来说话。我需要你们放下谦逊，对自己说：“是的，我想做出一流的工作。” 我们的社会不鼓励那些立志做出卓越成就的人。你们被认为不该如此；运气应当降临于你，让你偶然间成就伟业。嗯，这种说法有点愚蠢。我认为，为何你们不能立志去做些有意义的事呢？你不必告诉他人，但难道不应该对自己说：“是的，我想做些有意义的事。”

In order to get to the second stage, I have to drop modesty and talk in the first person about what I’ve seen, what I’ve done, and what I’ve heard. I’m going to talk about people, some of whom you know, and I trust that when we leave, you won’t quote me as saying some of the things I said.
为了进入第二阶段，我不得不放下谦逊，以第一人称谈谈我的所见、所为与所闻。我将提及一些人，其中有些你们认识，并且我相信在我们离开后，你们不会到处引用我所说的某些话。

Let me start not logically, but psychologically. 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? Wasn’t it a little too repetitive? Consider Shannon. He didn’t do just information theory. Several years before, he did some other good things and some which are still locked up in the security of cryptography. He did many good things.
让我从心理层面而非逻辑层面开始。我发现主要的反对意见在于人们认为伟大的科学成就是靠运气实现的——一切都归结于运气。那么，想想爱因斯坦吧。注意他做出了多少不同的杰出贡献。这难道全是运气吗？是不是有点过于重复了？再想想香农。他不仅创立了信息论，几年前他还完成了其他一些卓越的工作，其中部分成果至今仍因密码学的保密性而未公开。他成就斐然。

You see again and again, that it is more than one thing from a good person. Once in a while a person does only one thing in his whole life, and we’ll talk about that later, but a lot of times there is repetition. I claim that luck will not cover everything. And I will cite Pasteur who said, “Luck favors the prepared mind.” And I think that says it the way I believe it. There is indeed an element of luck, and no, there isn’t. 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.
你一次又一次地看到，一个优秀的人所成就的远不止一件事。偶尔有人一生只做成一件事，我们稍后会谈到，但多数时候是重复的行为。我断言运气无法涵盖一切。我将引用巴斯德的话：“机遇偏爱有准备的头脑。”我认为这恰如其分地表达了我的信念。确实存在运气的成分，但又不尽然。有准备的头脑迟早会发现重要之事并付诸行动。所以，是的，这是运气。你所做的具体事情是运气使然，但你能有所作为并非偶然。

For example, when I came to Bell Labs, I shared an office for a while with Shannon. At the same time he was doing information theory, I was doing coding theory. It is suspicious that the two of us did it at the same place and at the same time - it was in the atmosphere. And you can say, “Yes, it was luck.” On the other hand you can say, “But why of all the people in Bell Labs then were those the two who did it?” Yes, it is partly luck, and partly it is the prepared mind; but ‘partly’ is the other thing I’m going to talk about. So, although I’ll come back several more times to luck, 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. And I will quote, finally, Newton on the matter. Newton said, “If others would think as hard as I did, then they would get similar results.”
例如，当我来到贝尔实验室时，曾与香农共用一间办公室。他在研究信息论的同时，我正在钻研编码理论。我们两人在同一时间、同一地点完成这些工作确实令人起疑——这就像是弥漫在空气中的灵感。你或许会说：“没错，这全靠运气。”但反过来说：“可当时贝尔实验室那么多人，为什么偏偏是我们两个取得了突破？”确实，部分靠运气，部分靠有准备的头脑；但这个“部分”正是我要探讨的另一个重点。因此，虽然我还会多次提及运气因素，但我想先澄清：运气并非决定能否做出伟大工作的唯一标准。我认为你对此有一定掌控力，但并非完全掌控。最后，我要引用牛顿对此的看法。牛顿曾说：“如果他人能像我这般刻苦思考，他们也能获得类似的成果。”

One of the characteristics you see, and many people have it including great scientists, is that usually when they were young they had independent thoughts and had the courage to pursue them. For example, 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?” Now he knew that electromagnetic theory says you cannot have a stationary local maximum. But if he moved along with the velocity of light, he would see a local maximum. He could see a contradiction at the age of 12, 14, or somewhere around there, that everything was not right and that the velocity of light had something peculiar. Is it luck that he finally created special relativity? Early on, he had laid down some of the pieces by thinking of the fragments. Now that’s the necessary but not sufficient condition. All of these items I will talk about are both luck and not luck.
你所见到的特质之一，许多人都具备，包括伟大的科学家们，那就是他们年轻时通常拥有独立思考的勇气并勇于追寻。例如，爱因斯坦大约在十二三岁时自问：“如果我以光速前进，去看一束光波，它会是什么样子？”他当时知道电磁理论指出不可能存在静止的局部最大值。但若他以光速移动，便能看见一个局部最大值。他在那个年纪——大约十二三岁——就察觉到了矛盾，意识到事情并非全然正确，光速有着某种奇特之处。他最终创立了狭义相对论，这是运气吗？早在那时，他已通过思考片段奠定了一些基础。这虽是必要条件，却非充分条件。我将谈及的所有这些事例，既是运气，也非运气。

How about having lots of ‘brains?’ It sounds good. Most of you in this room probably have more than enough brains to do first-class work. But great work is something else than mere brains. Brains are measured in various ways. In mathematics, theoretical physics, astrophysics, typically brains correlates to a great extent with the ability to manipulate symbols. And so the typical IQ test is apt to score them fairly high. On the other hand, in other fields it is something different. For example, 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. It was pretty clear to me that this man didn’t know much mathematics and he wasn’t really articulate. His problem seemed interesting so I took it home and did a little work. I finally showed him how to run computers so he could compute his own answers. I gave him the power to compute. He went ahead, with negligible recognition from his own department, 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.
拥有许多聪明的“头脑”怎么样？听起来不错。在座的各位大多拥有足够进行一流工作的头脑。但伟大的工作远不止于此。头脑的衡量方式多种多样。在数学、理论物理、天体物理学领域，头脑往往与符号操作能力高度相关。因此，典型的智商测试倾向于给这些领域的人打出高分。然而在其他领域，情况则有所不同。例如，区域熔炼技术的发明者比尔·普凡某日来到我的办公室。他对自己想要实现的想法只有模糊概念，手里拿着几个公式。我很清楚这个人数学懂得不多，表达也不够流畅。但他的问题很有意思，我便带回家做了些研究，最终教会他使用计算机来自己计算结果——我赋予了他计算的能力。尽管起初未获本部门重视，他仍坚持前行，最终囊括了该领域所有重要奖项。 一旦他顺利开始，他的羞怯、笨拙和言语不清便消失了，他在许多其他方面变得更加多产。当然，他也变得更加善于表达了。

And I can cite another person in the same way. I trust he isn’t in the audience, i.e. a fellow named Clogston. I met him when I was working on a problem with John Pierce’s group and I didn’t think he had much. I asked my friends who had been with him at school, “Was he like that in graduate school?” “Yes,” they replied. Well I would have fired the fellow, but J. R. Pierce was smart and kept him on. Clogston finally did the Clogston cable. After that there was a steady stream of good ideas. One success brought him confidence and courage.
我还可以举出另一个类似的人。但愿他不在听众之中，即一个名叫克洛格斯顿的家伙。我在与约翰·皮尔斯的小组一起研究一个问题时遇见了他，当时我并不认为他有什么过人之处。我问那些在学校里就认识他的朋友：“他在研究生院时也是这样吗？”他们回答：“是的。”嗯，我可能会解雇这个人，但 J.R.皮尔斯很聪明，留下了他。克洛格斯顿最终发明了克洛格斯顿电缆。此后，好点子源源不断。一次成功带给了他信心和勇气。

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. Courage is one of the things that Shannon had supremely. You have only to think of his major theorem. He 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? That is the characteristic of great scientists; they have courage. They will go forward under incredible circumstances; they think and continue to think.
成功科学家的特质之一便是拥有勇气。一旦你鼓起勇气，相信自己能够解决重要问题，那么你就能做到。如果你认为自己不行，几乎可以肯定你不会成功。 勇气是香农所极度具备的品质之一。只需想想他的主要定理：他想要创建一种编码方法，却不知从何入手，于是便构造了一个随机码。随后他陷入了困境，接着他提出了一个看似不可能的问题：“平均随机码会如何表现？”他继而证明了平均码可以任意地好，因此必然存在至少一个好的编码。若非拥有无限勇气之人，谁敢有如此大胆的想法？这正是伟大科学家的特质；他们拥有勇气。他们会在难以置信的环境中勇往直前；他们思考并持续思考。

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.
年龄是物理学家们尤为担忧的另一个因素。他们总说，你得趁年轻时有所作为，否则将一事无成。爱因斯坦很早就取得了成就，而所有量子力学领域的佼佼者在做出最杰出工作时都年轻得令人咋舌。大多数数学家、理论物理学家和天体物理学家在我们看来其巅峰之作都诞生于青年时期。并非他们晚年没有优秀作品，而是我们最珍视的往往是其早期成果。反观音乐、政治和文学领域，我们通常认为他们的最佳作品多诞生于晚年。不知你所处领域是否符合这一规律，但年龄确实具有某种影响力。

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. You may find yourself as I saw Brattain when he got a Nobel Prize. The day the prize was announced we all assembled in Arnold Auditorium; all three winners got up and made speeches. 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.
但让我解释为何年龄似乎会产生这样的影响。首先，如果你做出了一些出色的工作，你会发现自己被各种委员会缠身，无法再继续工作。你可能会像我看到布拉顿获得诺贝尔奖时那样。获奖消息公布那天，我们齐聚阿诺德礼堂；三位获奖者都起身发表了讲话。第三位，布拉顿，几乎是眼含泪水地说：“我知道诺贝尔奖的影响，我不会让它改变我；我会继续做那个朴实的老沃尔特·布拉顿。”我心想：“这很好。”但几周后，我发现这已经影响到了他。那时他只能着手解决重大的问题了。

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. In fact I will give you my favorite quotation of many years. The Institute for Advanced Study in Princeton, in my opinion, has ruined more good scientists than any institution has created, judged by what they did before they came and judged by what they did after. Not that they weren’t good afterwards, but they were superb before they got there and were only good afterwards.
当你成名后，就很难再专注于小问题。这正是香农所遭遇的困境。在信息论之后，你还能拿出什么更精彩的作品呢？伟大的科学家们常犯此错误。他们未能持续播下那些能长成参天大树的微小橡果，而是试图一蹴而就。但事情往往不会如此发展。因此，这也是为何早期获得认可似乎会让人失去创造力。实际上，我想分享多年来我最喜欢的一句话。在我看来，普林斯顿高等研究院毁掉的好科学家比任何机构培养的都要多——这既基于他们去那里之前的成就，也基于之后的作为。并非他们之后不够优秀，而是他们在到达之前卓越非凡，之后却只是优秀而已。

This brings up the subject, out of order perhaps, of working conditions. 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. One of the better times of the Cambridge Physical Laboratories was when they had practically shacks - they did some of the best physics ever.
这或许有些不合时宜地引出了工作条件的话题。大多数人认为的最佳工作条件，其实并非如此。很明显不是，因为人们往往在条件恶劣时效率最高。剑桥物理实验室最辉煌的时期之一，就是当他们几乎在棚屋里工作时——他们完成了史上最杰出的物理学研究。

I give you a story from my own private life. Early on it became evident to me that Bell Laboratories was not going to give me the conventional acre of programming people to program computing machines in absolute binary. It was clear they weren’t going to. But that was the way everybody did it. I could go to the West Coast and get a job with the airplane companies without any trouble, but the exciting people were at Bell Labs and the fellows out there in the airplane companies were not. I thought for a long while about, “Did I want to go or not?” and I wondered how I could get the best of two possible worlds. I finally said to myself, “Hamming, you think the machines can do practically everything. Why can’t you make them write programs?” What appeared at first to me as a defect forced me into automatic programming very early. What appears to be a fault, often, by a change of viewpoint, turns out to be one of the greatest assets you can have. But you are not likely to think that when you first look the thing and say, “Gee, I’m never going to get enough programmers, so how can I ever do any great programming?”
我讲述一段个人经历。很早我就意识到，贝尔实验室不会给我配备成批的程序员来用绝对二进制为计算机编程。显然他们不打算这么做，但这却是当时通行的做法。我本可以毫不费力地去西海岸的航空公司谋职，但真正令人振奋的人才在贝尔实验室，而航空公司的同行们并非如此。我长时间思考：“我究竟该不该去？”并思索如何能在两个世界中取得最佳平衡。最终我对自己说：“汉明，你认为机器几乎无所不能，为什么不能让它们编写程序呢？”最初看似缺陷的情况，促使我很早就投身于自动编程领域。许多看似缺点的事物，只要转换视角，往往会成为你最宝贵的财富。但当你初次面对时，很可能会想：“天啊，我永远不会有足够的程序员，那还怎么完成伟大的编程工作呢？”

And there are many other stories of the same kind; Grace Hopper has similar ones. 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.
而且还有许多类似的故事；格蕾丝·霍珀也有相似的经历。我认为，如果你仔细观察，会发现伟大的科学家们常常通过稍微转换问题的角度，将缺陷转化为优势。例如，许多科学家在发现自己无法解决某个问题时，最终开始研究为何不能。他们随后转换思路，说道：“但这当然就是它的本质”，并因此获得了重要的成果。所以理想的工作条件非常奇特，你想要的未必对你最有益。

Now for the matter of drive. 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!
现在来谈谈驱动力的问题。你注意到大多数伟大的科学家都拥有非凡的驱动力。我在贝尔实验室与约翰·图基共事十年，他就具备这种强大的驱动力。入职大约三四年后，某天我发现约翰·图基竟比我还年轻些。约翰是个天才，而我显然不是。于是我气冲冲闯进博德的办公室质问：“我这个年纪的人怎么可能像约翰·图基懂得那么多？”他仰靠在椅背上，双手枕着后脑，微微咧嘴笑道：“汉明，如果你像他那样坚持努力多年，你会惊讶于自己所能掌握的学识。”我当即灰溜溜地退出了办公室！

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.
博德所言即是：“知识与生产力犹如复利。”假设两人能力相当，其中一人比另一人多付出百分之十的努力，那么后者的产出将远超前者两倍以上。你懂得越多，学得就越多；学得越多，能做的就越多；能做的越多，机会也就越多——这与复利的效应极为相似。我不想给出具体利率，但这确实是一个极高的比率。若两人能力完全相同，而其中一人坚持日复一日多花一小时思考，其一生中的产出将会有天壤之别。 我将博德的话铭记于心；多年间，我投入大量时间试图更努力地工作，并发现实际上我能完成更多工作。虽不愿在妻子面前提及，但我的确有时冷落了她；因为我需要学习。若想达成目标，就必须有所取舍。这一点毋庸置疑。

On this matter of drive Edison says, “Genius is 99% perspiration and 1% inspiration.” He may have been exaggerating, but the idea is that solid work, steadily applied, gets you surprisingly far. The steady application of effort with a little bit more work, intelligently applied is what does it. That’s the trouble; 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.
关于勤奋这件事，爱迪生曾说：“天才是 1%的灵感加上 99%的汗水。”他或许有所夸张，但其核心在于，扎实且持之以恒的努力能带来超乎想象的成就。真正起作用的，是持续付出努力，并在此基础上稍加努力，明智地运用这些努力。 问题在于：若勤奋用错了方向，便徒劳无功。我常思索，为何我在贝尔实验室的许多好友，他们付出的努力不亚于我甚至更多，却收获甚微。错误地投入精力是个极其严重的问题。仅靠埋头苦干远远不够——必须明智地运用努力。

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. 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. Those are often the great contributions. 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.
我想谈的另一个特质是模糊性。我花了一段时间才发现它的重要性。大多数人喜欢相信事物非真即假。而伟大的科学家却能很好地容忍模糊性。他们既相信理论足以推进研究，又对其持疑以察觉错误和缺陷，从而能够迈步向前，创立新的替代理论。若过于相信，便难以发现瑕疵；若过于怀疑，则无法起步。 这需要一种微妙的平衡。但大多数伟大的科学家都清楚自己的理论为何成立，同时也注意到那些不太吻合的细微之处，并且不会忘记它们。达尔文在自传中写道，他发现有必要记下每一个与他的信念相悖的证据，否则这些证据就会从脑海中消失。当你发现明显的缺陷时，必须保持敏感，追踪这些情况，并留意它们如何被解释，或理论如何调整以容纳它们。这些往往是伟大的贡献。伟大的贡献很少是通过增加小数点后的位数来实现的。 这归根结底是一种情感上的投入。大多数伟大的科学家都完全投入到他们的问题中。那些没有投入的人很少能做出杰出的一流工作。

Now again, emotional commitment is not enough. It is a necessary condition apparently. And I think I can tell you the reason why. 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. 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. 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.
现在再次强调，仅有情感投入是不够的，它显然是一个必要条件。我想我可以告诉你原因。所有研究创造力的人最终都会说：“创造力源于你的潜意识。”不知何故，它突然就出现了，就这么显现出来。我们对潜意识知之甚少；但有一点你很清楚，那就是你的梦也来自潜意识。而且你意识到，你的梦在很大程度上是对一天经历的重塑。如果你日复一日地深深沉浸并致力于某个主题，你的潜意识别无选择，只能专注于你的问题。于是，某天早晨或某个下午醒来时，答案就在那里了。对于那些不专注于当前问题的人，潜意识会在其他事情上闲逛，无法产生重大成果。因此，管理自己的方法是，当你面临真正重要的问题时，不要让任何其他事情占据注意力的中心——你要持续思考这个问题。 让你的潜意识保持饥饿，这样它就必须专注于你的问题，于是你便能安然入睡，在清晨免费获得答案。

Now Alan Chynoweth mentioned that I used to eat at the physics table. I had been eating with the mathematicians and I found out that I already knew a fair amount of mathematics; in fact, I wasn’t learning much. The physics table was, as he said, an exciting place, but I think he exaggerated on how much I contributed. It was very interesting to listen to Shockley, Brattain, Bardeen, J. B. Johnson, Ken McKay and other people, and I was learning a lot. But unfortunately a Nobel Prize came, and a promotion came, and what was left was the dregs. Nobody wanted what was left. Well, there was no use eating with them!
艾伦·柴诺维斯曾提到我过去常在物理学家餐桌用餐。之前我与数学家们共餐时，发现自己已掌握相当多的数学知识，实际上并未学到太多新东西。正如他所说，物理餐桌是个激动人心的地方，但我认为他夸大了我的贡献。倾听肖克利、布拉顿、巴丁、J·B·约翰逊、肯·麦凯等人的谈话非常有趣，我学到了很多。但不幸的是，诺贝尔奖降临，晋升也随之而来，剩下的只是些残羹冷炙。无人想要那些剩下的东西。唉，再与他们共餐已无意义！

Over on the other side of the dining hall was a chemistry table. I had worked with one of the fellows, Dave McCall; furthermore he was courting our secretary at the time. I went over and said, “Do you mind if I join you?” They can’t say no, so I started eating with them for a while. And I started asking, “What are the important problems of your field?” And after a week or so, ” What important problems are you working on?” And after some more time I came in one day and said, “If what you are doing is not important, and if you don’t think it is going to lead to something important, why are you at Bell Labs working on it?” I wasn’t welcomed after that; I had to find somebody else to eat with! That was in the spring.
食堂的另一边有一张化学研究桌。我曾与其中一位同事戴夫·麦考尔共事过；而且他当时正在追求我们的秘书。我走过去问：“介意我加入你们吗？”他们没法拒绝，于是我就和他们一起吃了段时间饭。我开始问：“你们领域的重要问题有哪些？”大约一周后，我又问：“你们正在研究哪些重要问题？”又过了一段时间，有一天我走进来说：“如果你们正在做的事情不重要，而且你们认为它不会带来重要的成果，那为什么还要在贝尔实验室做这个呢？”从那以后，我就不受欢迎了；我得找别人一起吃饭了！那是春天的事。

In the fall, 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. I haven’t changed my research,” he says, “but I think it was well worthwhile.” And I said, “Thank you Dave,” and went on. I noticed a couple of months later he was made the head of the department. I noticed the other day he was a Member of the National Academy of Engineering. I noticed he has succeeded. I have never heard the names of any of the other fellows at that table mentioned in science and scientific circles. They were unable to ask themselves, “What are the important problems in my field?”
秋天，戴夫·麦考尔在走廊里拦住我说：“汉明，你的那句话让我深受触动。我整个夏天都在思考，也就是我所在领域的重要问题是什么。”他说，“我并没有改变我的研究方向，但我认为这非常值得。”我回答：“谢谢你，戴夫。”然后继续前行。几个月后，我注意到他被任命为系主任。前几天，我发现他成为了国家工程院的成员。我注意到他取得了成功。而我从未在科学界听到过那张桌子上其他任何人的名字。他们未能自问：“我所在领域的重要问题是什么？”

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. Let me warn you, ‘important problem’ must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn’t work on (1) time travel, (2) teleportation, and (3) 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. That is what makes a problem important. When I say that most scientists don’t work on important problems, I mean it in that sense. 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.
如果你不致力于一个重要的问题，你就不太可能做出重要的工作。这一点显而易见。伟大的科学家们会仔细思考其领域内的一系列重要问题，并时刻关注如何攻克它们。 让我提醒你，“重要问题”必须谨慎定义。在某种意义上，我在贝尔实验室期间，物理学的三大杰出问题从未被触及。我所说的“重要”是指保证能获得诺贝尔奖以及任何你提及的巨额奖金。我们并未研究（1）时间旅行，（2）瞬间移动，以及（3）反重力。这些问题之所以不重要，是因为我们缺乏攻克它们的方法。不是问题的结果使其重要，而是你拥有合理的攻克之道。这才是问题重要的原因。当我说大多数科学家不研究重要问题时，我正是基于这个意义。据我观察，普通科学家几乎将所有时间花在他们认为既不重要，也不相信会引向重要问题的工作上。

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.
我之前提到过播种橡实以期橡树成长。你未必总能确切知道该身处何方，但可以活跃在可能孕育机遇的地方。即便你认为伟大的科学成就全靠运气，也该立于雷电交加的山巅，而非躲进安全的山谷。然而普通科学家几乎始终在做常规稳妥的工作，因此成果寥寥。道理很简单：若要成就伟业，必须致力于重要课题，并且怀揣创见。

Along those lines at some urging from John Tukey and others, I finally adopted what I called “Great Thoughts Time.” When I went to lunch Friday noon, I would only discuss great thoughts after that. By great thoughts I mean ones like: “What will be the role of computers in all of AT&T?”, “How will computers change science?” For example, I came up with the observation at that time that nine out of ten experiments were done in the lab and one in ten on the computer. I made a remark to the vice presidents one time, that it would be reversed, i.e. nine out of ten experiments would be done on the computer and one in ten in the lab. They knew I was a crazy mathematician and had no sense of reality. I knew they were wrong and they’ve been proved wrong while I have been proved right. They built laboratories when they didn’t need them. I saw that computers were transforming science because I spent a lot of time asking “What will be the impact of computers on science and how can I change it?” I asked myself, “How is it going to change Bell Labs?” I remarked one time, in the same address, that more than one-half of the people at Bell Labs will be interacting closely with computing machines before I leave. Well, you all have terminals now. I thought hard about where was my field going, where were the opportunities, and what were the important things to do. Let me go there so there is a chance I can do important things.
在约翰·图基等人的敦促下，我最终采纳了所谓的“伟大思想时刻”。每逢周五中午用餐时，我只在那之后探讨伟大思想。所谓伟大思想，指的是诸如“计算机在 AT&T 中将扮演什么角色？”、“计算机将如何改变科学？”这类问题。例如，我当时观察到，十次实验中有九次是在实验室完成的，只有一次使用计算机。我曾对几位副总裁说过，这种情况将会逆转，即十次实验中有九次将通过计算机完成，仅有一次在实验室进行。他们认为我是个不切实际的疯狂数学家。而我知道他们错了，事实证明我是对的，他们错了。他们在不需要的时候建造了实验室。我意识到计算机正在变革科学，因为我花了很多时间思考“计算机将对科学产生何种影响，我该如何推动这种变革？”我自问：“它将如何改变贝尔实验室？”我曾在那次演讲中提到，超过一半的贝尔实验室员工在我离职前将会与计算机紧密互动。如今，你们都已拥有终端设备。我深入思考过我的领域将走向何方，机遇何在，以及哪些是值得去做的重要事情。让我投身于此，方有可能成就重要之事。

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. Now I can tell you a horror story that was told to me but I can’t vouch for the truth of it. I was sitting in an airport talking to a friend of mine from Los Alamos about how it was lucky that the fission experiment occurred over in Europe when it did because that got us working on the atomic bomb here in the US. He said “No; 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!
大多数伟大的科学家都了解许多重要问题。他们手头有大约 10 到 20 个关键难题，正寻找攻克之道。一旦发现新思路出现，便会听到他们说：“这正好能解决那个问题。”于是他们放下其他一切，立刻跟进。现在我要讲一个别人告诉我的惊悚故事，但我无法保证其真实性。当时我坐在机场，与来自洛斯阿拉莫斯的朋友聊天，说到幸好裂变实验恰好在欧洲发生时，促使我们在美国启动了原子弹研发。他却说：“不对；在伯克利时，我们已经收集了一批数据；因为忙于制造更多设备，没来得及分析这些数据，否则我们本应发现裂变。”他们曾手握关键线索却未深究，最终屈居第二！

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!
伟大的科学家在机遇降临时，会立刻抓住并执着追求。他们放下一切杂务，摒弃其他干扰，专注于一个想法，因为他们早已深思熟虑。他们的头脑时刻准备着；一旦发现机会，便全力以赴。当然，很多时候未必成功，但无需屡战屡胜，也能成就卓越科学。这其实颇为简单。其中一个关键诀窍就是活得足够长久！

Another trait, it took me a while to notice. I noticed the following facts about people who work with the door open or the door closed. 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. Now I cannot prove the cause and effect sequence because you might say, “The closed door is symbolic of a closed mind.” I don’t know. But I can say 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.
另一个特质，我花了些时间才注意到。我观察到关于那些开着门或关着门工作的人的一些事实。我发现，如果你关上办公室的门，今天和明天你会完成更多工作，比大多数人更有效率。但十年后，不知何故，你却不清楚哪些问题值得去解决；你所有的辛勤努力似乎都在重要性上有些偏离。那些开着门工作的人会遭遇各种干扰，但他们偶尔也能获得关于世界现状及何为重要事务的线索。我无法证明其中的因果关系，因为你可能会说：“关着的门象征着封闭的思维。”我不确定。但我可以说，在那些开着门工作的人与最终成就大事的人之间存在相当好的关联，尽管关着门工作的人往往更加努力。不知何故，他们似乎总是在处理稍微偏离重点的事情——偏差不大，但足以让他们与声望失之交臂。

I want to talk on another topic. It is based on the song which I think many of you know, “It ain’t what you do, it’s the way that you do it.” I’ll start with an example of my own. I was conned into doing on a digital computer, in the absolute binary days, a problem which the best analog computers couldn’t do. And I was getting an answer. When I thought carefully and said to myself, “You know, Hamming, you’re going to have to file a report on this military job; after you spend a lot of money you’re going to have to account for it and every analog installation is going to want the report to see if they can’t find flaws in it.” I was doing the required integration by a rather crummy method, to say the least, but I was getting the answer. And I realized that in truth the problem was not just to get the answer; it was to demonstrate for the first time, and beyond question, that I could beat the analog computer on its own ground with a digital machine. I reworked the method of solution, created a theory which was nice and elegant, and changed the way we computed the answer; the results were no different. The published report had an elegant method which was later known for years as “Hamming’s Method of Integrating Differential Equations.” It is somewhat obsolete now, but for a while it was a very good method. By changing the problem slightly, I did important work rather than trivial work.
我想换个话题。这源于一首歌，我想很多人都知道，“重要的不是你做什么，而是你做事的方式”。我先以自己的一个例子开始。在纯二进制时代，我被哄骗用数字计算机解决了一个连最好的模拟计算机都无法处理的问题，并且我得到了答案。当我仔细思考后对自己说：“汉明，你得为这项军事任务提交报告；花了大笔钱后你必须有个交代，每个模拟设备安装点都会想要这份报告，看看能否从中挑出毛病。”我用的积分方法相当简陋，但确实得出了结果。我意识到，实际上问题不仅仅是得到答案，而是要首次无可置疑地证明，我能在模拟计算机的主场上用数字机器超越它。于是我重新设计了解决方案，创立了一套优美而精致的理论，改变了我们计算答案的方式；结果却并无二致。 已发表的报告中提出了一种优雅的方法，后来多年间被称为“哈明微分方程积分法”。如今该方法虽略显过时，但在当时却是非常优秀的解法。通过略微调整问题，我完成了重要而非琐碎的工作。

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.” By changing the question I still got the same kind of results or better, but I changed things and did important work. I attacked the major problem - 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!
同样地，早期在阁楼上使用机器时，我解决了一个又一个问题；其中不少成功了，也有几次失败。一个周五，解决完一个问题后回家，奇怪的是我并不快乐；反而感到沮丧。我能预见生活就是一连串永无止境的问题。经过一段时间的思考，我决定：“不，我应该投身于多样化产品的大规模生产中。我应该关注所有明年的问题，而不仅仅是眼前这一个。”通过改变提问方式，我依然取得了相同甚至更好的成果，但我改变了做法，完成了重要的工作。我着手解决主要问题——如何在未知明年具体问题的情况下，征服机器并处理所有明年的挑战？我该如何为此做准备？如何解决当前问题以便能掌控全局？如何遵循牛顿的法则？他曾说：“如果我看得比别人更远，那是因为我站在了巨人的肩膀上。”如今，我们却站在彼此的脚上！

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.
你应该以这样的方式完成工作，使他人能够在此基础上继续发展，这样他们确实会说：“是的，我站在某某的肩膀上，看得更远。”科学的本质是累积性的。通过稍微改变问题，你往往能做出伟大的工作，而不仅仅是好的工作。我不再解决孤立的问题，而是下定决心，除非作为某一类问题的代表，否则不再处理单一问题。

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.
如果你是一位真正的数学家，你会知道，努力推广往往意味着解决方案变得简单。常常停下来思考：“这是他想要的问题，但这是某某类问题的典型特征。是的，我可以用一种比特定方法更优越的方式解决整个类别，因为我之前陷入了不必要的细节中。”抽象的过程常常使事情简化。此外，我将这些方法归档，为未来的问题做好准备。

To end this part, 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!
在结束这一部分时，我要提醒大家：“拙匠常怪工具差——优秀的人则会利用现有条件，着手工作，并尽力得出最佳答案。”我建议，通过改变问题、以不同视角看待事物，你可以在最终的生产力上产生巨大差异，因为你可以选择一种方式让人们能够真正在你所做的基础上继续建设，或者选择另一种方式让下一个人不得不几乎重复你的工作。 这不仅仅是工作本身的问题，还包括你撰写报告的方式、论文的方式，以及整个态度。做一个广泛而通用的工作与做一个非常特殊的案例同样容易，而且前者更令人满足和富有成就感！

I have now come down to a topic which is very distasteful; 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.” I suggest that 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 in the Physical Review, or wherever else you want it, 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.
现在我要谈一个令人不悦的话题：仅仅完成工作是不够的，你还得推销它。对科学家来说，“推销”是件难堪的事——这很煞风景，本不该由你来做。世人理当翘首以盼，当你取得重大成果时，他们该争先恐后地前来迎接。但现实是每个人都忙于自己的工作。你必须将成果展示得足够出色，让他们愿意放下手头事务，仔细研读你的工作，然后回应道：“确实出色。”我建议当你翻开期刊时，不妨思考为何会阅读某些文章而跳过其他。你最好这样撰写报告：当它在《物理评论》或其他目标期刊发表后，读者翻页时不会一掠而过，而是会驻足细读。若无人停留阅读，你的成果便难获认可。

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.
在销售中，有三件事必须做到：学会清晰流畅地书写以吸引读者，掌握适度正式的演讲技巧，同时也要擅长即兴交谈。我们曾有许多所谓的“幕后科学家”。会议上，他们沉默不语。三周后决策已定，他们才递交报告阐述为何应采取某些行动。可惜为时已晚。他们不愿在激烈的会议讨论中、在活动进行时挺身而出，直言：“基于这些理由，我们应当这样做。”你需要精通这种即时的沟通方式，正如掌握精心准备的演讲一样。

When I first started, I got practically physically ill while giving a speech, and I was very, very nervous. I realized I either had to learn to give speeches smoothly or I would essentially partially cripple my whole career. The first time IBM asked me to give a speech in New York one evening, I decided I was going to give a really good speech, a speech that was wanted, not a technical one but a broad one, and at the end if they liked it, I’d quietly say, “Any time you want one I’ll come in and give you one.” As a result, I got a great deal of practice giving speeches to a limited audience and I got over being afraid. Furthermore, I could also then study what methods were effective and what were ineffective.
刚开始演讲时，我几乎会紧张到身体不适。我意识到，要么学会流畅地演讲，要么我的职业生涯将因此受阻。当 IBM 首次邀请我在纽约的一个晚上发表演讲时，我决心要呈现一场真正精彩的演讲——不是技术性的，而是内容广泛的，如果听众喜欢，我会轻声说：“任何时候需要，我都愿意再来分享。”结果，我在有限听众面前获得了大量练习机会，逐渐克服了恐惧。此外，我还得以研究哪些方法有效，哪些无效。

While going to meetings I had already been studying why some papers are remembered and most are not. 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.” The tendency is to give a highly restricted, safe talk; this is usually ineffective. Furthermore, many talks are filled with far too much information. So I say this idea of selling is obvious.
在参加会议的同时，我早已开始研究为何有些论文被铭记而大多数则不然。技术人员倾向于做高度局限的技术报告，而多数时候听众期待的是更宽泛的概述性演讲，他们需要的综述和背景信息远超讲者愿意提供的。因此，许多演讲效果不佳。讲者提出一个主题，便突然深入他所解决的细节，听众中鲜有人能跟上。你应当先描绘整体图景，说明其重要性，再逐步勾勒所做工作的轮廓。这样，更多人会说：“是的，乔做到了那一点，”或“玛丽完成了那项工作；我确实明白了关键所在；没错，玛丽的演讲很棒；我理解了玛丽的成果。”人们往往倾向于做高度受限、稳妥的演讲，但这通常效果不佳。此外，许多演讲充斥着过多的信息。所以我认为，这种推销的理念显而易见。

Let me summarize. You’ve got to work on important problems. I deny that it is all luck, but I admit there is a fair element of luck. I subscribe to Pasteur’s “Luck favors the prepared mind.” I favor heavily what I did. Friday afternoons for years - great thoughts only - means that 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.
让我来总结一下。你必须致力于解决重要问题。我不否认其中有运气的成分，但我承认运气确实占了相当大的比重。我赞同巴斯德的那句“机遇偏爱有准备的头脑”。我极为推崇自己过去的做法——多年来的每个周五下午，只思考伟大的想法，这意味着我投入了 10%的时间去试图理解领域内更宏大的问题，也就是什么重要、什么不重要。早年我发现，自己虽然相信“这个”，却整个星期都在朝着“那个”方向前进。这有点愚蠢。如果我真心认为行动应该在那边，为什么我还要朝这个方向走呢？我要么改变目标，要么改变行动。于是我改变了行动，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. I’ll tell you a story about that, and it bears on the subject of educating your boss. I had a boss named Schelkunoff; he was, and still is, a very good friend of mine. Some military person came to me and demanded some answers by Friday. Well, I had already dedicated my computing resources to reducing data on the fly for a group of scientists; I was knee deep in short, small, important problems. This military person wanted me to solve his problem by the end of the day on Friday. I said, “No, I’ll give it to you Monday. I can work on it over the weekend. I’m not going to do it now.” He goes down to my boss, Schelkunoff, and Schelkunoff says, “You must run this for him; he’s got to have it by Friday.” I tell him, “Why do I?”; he says, “You have to.” I said, “Fine, Sergei, but you’re sitting in your office Friday afternoon catching the late bus home to watch as this fellow walks out that door.” I gave the military person the answers late Friday afternoon. I then went to Schelkunoff’s office and sat down; as the man goes out I say, “You see Schelkunoff, this fellow has nothing under his arm; but I gave him the answers.” On Monday morning Schelkunoff called him up and said, “Did you come in to work over the weekend?” I could hear, as it were, a pause as the fellow ran through his mind of what was going to happen; but he knew he would have had to sign in, and he’d better not say he had when he hadn’t, so he said he hadn’t. Ever after that Schelkunoff said, “You set your deadlines; you can change them.”
现在你可能会告诉我，你无法控制自己必须处理的工作内容。嗯，刚开始时或许确实如此。但一旦你取得了一定的成功，就会有更多的人向你索要成果，多到你无法全部满足，这时你就有了选择权，尽管不是完全的自由。我要讲一个相关的故事，这涉及到如何引导你的上司。我曾有位上司叫谢尔库诺夫；他过去是，现在依然是我的好友。某位军方人士来找我，要求周五前给出答案。可我已经将计算资源全用于为一组科学家实时处理数据了；我正忙于一系列紧迫而重要的小问题。这位军方人士希望我在周五下班前解决他的问题。我说：“不行，我周一给你。我可以周末做，但现在不行。”他去找了我的上司谢尔库诺夫，谢尔库诺夫说：“你必须为他运行这个；他周五前必须拿到。”我问他：“为什么我必须做？”；他说：“你必须做。”我说：“好吧，谢尔盖，但周五下午你坐在办公室里，赶末班车回家时，会看着那家伙走出那扇门。”我在周五傍晚把答案交给了那位军人。随后我去了谢尔库诺夫的办公室坐下；当那人出去时，我说：‘你看，谢尔库诺夫，这家伙腋下什么都没夹；但我已经把答案给他了。’（暗示这个任务根本不紧急）周一早上，谢尔库诺夫打电话问他：‘你周末来加班了吗？’我仿佛能听到电话那头停顿了一下，那人在脑海里快速盘算着接下来会发生什么；但他知道自己必须签到，最好别撒谎说来了其实没来，于是他说没有。从那以后，谢尔库诺夫对我说：‘你自己设定的截止日期，你有权更改它们。’”

One lesson was sufficient to educate my boss as to why I didn’t want to do big jobs that displaced exploratory research and why I was justified in not doing crash jobs which absorb all the research computing facilities. I wanted instead to use the facilities to compute a large number of small problems. Again, in the early days, I was limited in computing capacity and it was clear, in my area, that a “mathematician had no use for machines.” But I needed more machine capacity. Every time I had to tell some scientist in some other area, “No I can’t; I haven’t the machine capacity,” he complained. I said “Go tell your Vice President that Hamming needs more computing capacity.” After a while I could see what was happening up there at the top; many people said to my Vice President, “Your man needs more computing capacity.” I got it!
一次教训就足以让我的老板明白，为何我不愿接手那些挤占探索性研究的大型任务，以及为何我有理由拒绝那些会占用所有研究计算资源的紧急项目。我更希望利用这些设施来计算大量的小问题。同样，在早期，我的计算能力有限，且在我的领域里，显然“数学家对机器没有需求”。但我需要更强的计算能力。每当不得不告诉其他领域的科学家“不行，我做不到；我没有足够的计算能力”时，他们便会抱怨。我说：“去告诉你的副总裁，汉明需要更多的计算能力。”过了一段时间，我看到了高层的变化；许多人向我的副总裁反映：“你的人需要更多计算能力。”我如愿以偿！

I also did a second thing. When I loaned what little programming power we had to help in the early days of computing, I said, “We are not getting the recognition for our programmers that they deserve. When you publish a paper you will thank that programmer or you aren’t getting any more help from me. That programmer is going to be thanked by name; she’s worked hard.” I waited a couple of years. I then went through a year of BSTJ articles and counted what fraction thanked some programmer. I took it into the boss and said, ” That’s the central role computing is playing in Bell Labs; if the BSTJ is important, that’s how important computing is.” He had to give in. You can educate your bosses. It’s a hard job. In this talk I’m only viewing from the bottom up; I’m not viewing from the top down. But I am telling you how you can get what you want in spite of top management. You have to sell your ideas there also.
我还做了第二件事。在早期计算时代，我出借了我们仅有的一点编程能力来提供帮助时，我曾说过：“我们的程序员没有得到应有的认可。当你发表论文时，必须感谢那位程序员，否则我不会再提供任何帮助。那位程序员必须被点名感谢；她付出了辛勤劳动。”我等了几年，然后查阅了一整年的《贝尔系统技术期刊》文章，统计了有多少比例感谢了某位程序员。我把结果拿给老板看，并说：“这就是计算在贝尔实验室扮演的核心角色；如果《贝尔系统技术期刊》很重要，那么计算就有多重要。”他不得不让步。你可以教育你的上司，这并非易事。在这次演讲中，我只从下往上看问题，而非自上而下。但我要告诉你们，尽管有高层管理，你们仍能达成所愿。在那里，你也需要推销你的想法。

Well I now come down to the topic, “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.
那么现在我来谈谈这个话题：“成为伟大科学家的努力是否值得？”要回答这个问题，你必须去问那些过来人。当你突破他们的谦逊后，大多数人会说：“是的，做出真正一流的工作并深知其价值，这种感觉堪比美酒、佳人与音乐的总和。”若是女性则会说：“这好比美酒、才俊与音乐的结合。”而观察那些领导者，他们总会回来听取汇报或要求报告，试图参与那些发现的瞬间。他们总是碍手碍脚。由此可见，那些曾取得成就的人渴望再次体验。但这只是有限的调查——我从未敢去询问那些未做出伟大成就的人对此事的感受。样本虽存在偏差，但我依然认为这份奋斗是值得的。我坚信努力追求一流工作绝对有价值，因为真相是：价值更多存在于奋斗过程而非结果之中。努力实现自我价值这件事本身似乎就具有意义。 依我看来，成功与名声不过是附加的红利。

I’ve told you how to do it. It is so easy, so why do so many people, with all their talents, fail? For example, my opinion, to this day, is that 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. Some of them did produce more than I did; Shannon produced more than I did, and some others produced a lot, but I was highly productive against a lot of other fellows who were better equipped. Why is it so? What happened to them? Why do so many of the people who have great promise, fail?
我已经告诉过你怎么做了。这如此简单，为何那么多才华横溢的人却失败了呢？比如，我至今仍认为，贝尔实验室数学部门里有不少人比我更有能力、天赋更高，但他们的产出却不如我。他们中有些人确实比我产出更多；香农的成果就超过了我，还有一些人也成果丰硕，但相较于许多条件更优越的同事，我的产出却相当高。这是为什么呢？他们身上发生了什么？为何那么多大有前途的人最终未能成功？

Well, 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.
嗯，其中一个原因是驱动力和投入精神。那些能力稍逊但全情投入的人，比起那些技艺高超却浅尝辄止的人——那些白天工作、回家做别的事、第二天再回来工作的人——成就更多。他们显然缺乏真正一流工作所必需的深度投入。他们能产出大量优秀作品，但请记住，我们讨论的是一流之作。这其中有区别。优秀的人才，极具天赋的人，几乎总能创作出好的作品。我们谈论的是卓越之作，是那种能赢得诺贝尔奖、获得广泛认可的作品。

The second thing is, I think, the problem of personality defects. Now I’ll cite a fellow whom I met out in Irvine. He had been the head of a computing center and he was temporarily on assignment as a special assistant to the president of the university. It was obvious he had a job with a great future. He took me into his office one time and showed me his method of getting letters done and how he took care of his correspondence. He pointed out how inefficient the secretary was. He kept all his letters stacked around there; he knew where everything was. And he would, on his word processor, get the letter out. He was bragging how marvelous it was and how he could get so much more work done without the secretary’s interference. Well, behind his back, I talked to the secretary. The secretary said, “Of course I can’t help him; I don’t get his mail. He won’t give me the stuff to log in; I don’t know where he puts it on the floor. Of course I can’t help him.” So I went to him and said, “Look, if you adopt the present method and do what you can do single-handedly, you can go just that far and no farther than you can do single-handedly. If you will learn to work with the system, you can go as far as the system will support you.” And, he never went any further. He had his personality defect of wanting total control and was not willing to recognize that you need the support of the system.
另一个原因，我认为是性格缺陷的问题。现在我要举一个在尔湾遇到的同事为例。他曾是计算中心的负责人，暂时被指派为大学校长的特别助理。显然，他的工作前景一片光明。有一次，他带我进办公室，展示他处理信件的方法以及如何应对往来函件。他指出秘书的效率有多低。他把所有信件堆在周围，自己清楚每样东西的位置。然后，他会在文字处理器上完成信件。他自夸这套方法多么了不起，没有秘书的干扰，他能完成更多工作。然而，背地里，我和秘书谈了谈。秘书说：“我当然帮不了他；我收不到他的邮件。他不给我材料登记；我不知道他把东西放哪儿了。我当然帮不了他。”于是我去找他，说：“听着，如果你采用现在的方法，单凭一己之力做事，你只能走这么远，无法超越你独自能做到的范围。” 如果你学会与系统协作，你能走多远，系统就会支持你多远。”而他从未再前进一步。他个性上的缺陷是渴望完全掌控，不愿承认你需要系统的支持。

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’.
你会发现这种情况一再发生；优秀的科学家会对抗系统，而不是学会与系统协作并利用系统提供的一切。系统有很多资源，只要你学会如何使用。这需要耐心，但你可以很好地学会使用系统，也能学会如何绕过它。毕竟，如果你想要一个’不’的决定，只需去找你的上司，很容易就能得到’不’。如果你想做某事，不要问，直接去做。给他一个既成事实。不要给他机会对你说’不’。但如果你想要’不’，得到’不’很容易。

Another personality defect is ego assertion and I’ll speak in this case of my own experience. 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.
另一个性格缺陷是坚持个性，这里我将分享我的亲身经历。我来自洛斯阿拉莫斯，早期在纽约麦迪逊大道 590 号使用一台机器时，我们只是租用时间。那时我仍穿着西部风格的服装——大斜插口袋、波洛领带等等。我隐约察觉到自己的服务待遇不如他人，于是开始留心观察。进门后需排队等候，我感觉自己受到了不公平对待。我自问：“为何如此？IBM 的副总裁并未下令‘为难汉明’。是底层的秘书们在操作这些。一旦有空缺，她们会急忙找人补上，却总是跳过我去找别人。那么原因何在？我并未亏待她们。”答案在于，我的穿着不符合她们眼中该场合应有的形象。归根结底——只是衣着不当。我必须做出抉择：是坚持个性，按个人喜好着装，任由此事持续消耗我的专业精力；还是调整外表以更好地融入环境？最终我决定努力让自己看起来更符合规范。 从那一刻起，我得到的服务就大大改善了。如今，作为一个阅历丰富的老者，我享受到的服务比他人更胜一筹。

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.
你应该根据听众的期待来着装。如果我要在麻省理工计算机中心发表演讲，我会系上波洛领带，穿上旧灯芯绒夹克或类似的衣服。我深知不能让我的衣着、外表或举止妨碍我所关心的事情。许多科学家觉得必须坚持自我，按自己的方式行事。他们非得这样做、那样做不可，为此持续付出代价。

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.
约翰·图基几乎总是穿着随意。他会走进一间重要的办公室，而对方要花很长时间才能意识到这是一位顶尖人物，最好认真倾听。长期以来，约翰不得不克服这种因外表带来的抵触情绪。这完全是白费力气！我并非要求你随波逐流；我是说“表面上的顺应能让你走得更远”。 如果你执意以各种方式彰显自我——“我就要按自己的方式行事”，那么你将在整个职业生涯中持续付出微小代价。而这一点，贯穿一生，将累积成巨大的不必要的麻烦。

By taking the trouble to tell jokes to the secretaries and being a little friendly, I got superb secretarial help. For instance, one time for some idiot reason all the reproducing services at Murray Hill were tied up. Don’t ask me how, but they were. I wanted something done. My secretary called up somebody at Holmdel, hopped the company car, made the hour-long trip down and got it reproduced, and then came back. It was a payoff for the times I had made an effort to cheer her up, tell her jokes and be friendly; it was that little extra work that later paid off for me. 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.
我费心给秘书们讲笑话，表现得友善一些，从而获得了极佳的秘书协助。例如，有一次因某种愚蠢的原因，默里山的所有复印服务都被占用了。别问我怎么回事，但确实如此。我需要办点事。我的秘书给霍姆德尔那边的人打了个电话，跳上公司的车，花了一个小时赶过去完成了复印，然后又回来了。这是我之前努力逗她开心、讲笑话和表示友好的回报；正是那一点额外的付出后来为我带来了好处。通过认识到必须利用系统并研究如何让系统为你工作，你学会了如何让系统适应你的需求。否则，你可以一直与之对抗，像一场未宣战的小型战争，贯穿你的一生。

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!
我认为约翰·图基付出了不必要的惨痛代价。他无论如何都是个天才，但我认为如果他愿意稍微顺从一点，而不是一味地坚持自我，情况会好得多，也简单得多。他总是想怎么穿就怎么穿。这不仅体现在穿着上，还体现在无数其他事情上；人们总会继续与体制抗争。当然，偶尔抗争一下也未尝不可！

When they moved the library from the middle of Murray Hill to the far end, a friend of mine put in a request for a bicycle. Well, the organization was not dumb. They waited awhile and sent back a map of the grounds saying, “Will you please indicate on this map what paths you are going to take so we can get an insurance policy covering you.” A few more weeks went by. They then asked, “Where are you going to store the bicycle and how will it be locked so we can do so and so.” He finally realized that of course he was going to be red-taped to death so he gave in. He rose to be the President of Bell Laboratories.
当他们把图书馆从默里山的中心搬到远端时，我的一位朋友申请了一辆自行车。嗯，组织并不傻。他们等了一段时间，然后寄回一张场地地图，说：“请在这张地图上标出您将要走的路线，以便我们为您购买保险。”又过了几周，他们又问：“您打算把自行车存放在哪里？如何上锁？这样我们才能办理相关手续。”他终于意识到自己肯定会被繁琐的手续拖垮，于是放弃了。后来他晋升为贝尔实验室的总裁。

Barney Oliver was a good man. He wrote a letter one time to the IEEE. At that time the official shelf space at Bell Labs was so much and the height of the IEEE Proceedings at that time was larger; and since you couldn’t change the size of the official shelf space he wrote this letter to the IEEE Publication person saying, “Since so many IEEE members were at Bell Labs and since the official space was so high the journal size should be changed.” He sent it for his boss’s signature. Back came a carbon with his signature, but he still doesn’t know whether the original was sent or not. I am not saying you shouldn’t make gestures of reform. I am saying that my study of able people is that they don’t get themselves committed to that kind of warfare. They play it a little bit and drop it and get on with their work.
巴尼·奥利弗是个好人。他曾有一次给 IEEE 写了一封信。那时贝尔实验室的官方书架空间是固定的，而 IEEE 会刊的高度较大；由于无法改变官方书架的大小，他便致信 IEEE 的出版负责人说：“鉴于许多 IEEE 成员都在贝尔实验室工作，且官方书架空间如此之高，期刊尺寸应当调整。”他将信件呈请上司签署。结果返回了一份带有签名的复写副本，但他至今仍不清楚原件是否寄出。我并非说改革之举不可为。我想说的是，据我对能人志士的观察，他们不会让自己深陷于那种争斗之中。他们稍作尝试便抽身而退，继续专注于自己的工作。

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.
许多二流之辈因对体制的小小不满而卷入其中，并将其升级为对抗。他们把精力耗费在愚蠢的计划上。现在你会告诉我，总得有人去改变这个体制。我同意；确实需要有人去做。你想成为哪一种人？是改变体制的人，还是做一流科学的人？你究竟想成为哪一种？要清楚，当你与体制斗争、与之抗争时，你在做什么，有多少是出于一时兴起，又有多少是在浪费精力与体制对抗。我的建议是让别人去做这件事，而你则专注于成为一流的科学家。你们中很少有人既有能力改革体制又能成为一流的科学家。

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，我们不能总是让步。有时候，一定程度的叛逆是明智的。我观察到几乎所有的科学家都喜欢稍微戏弄一下体制，纯粹是出于喜爱。归根结底，你不能在一个领域有独创性，而在其他领域没有。独创性就是与众不同。没有其他独创性特质，你不可能成为一位原创科学家。但许多科学家让他在其他方面的怪癖付出了远高于必要的代价，只为获得自我满足。我并不反对所有的自我主张；我反对的是某些。

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.
另一个缺点是愤怒。科学家常常会生气，但这绝不是处理事情的方式。娱乐可以，愤怒不行。愤怒是方向错了。你应该跟随并合作，而不是一直与体制抗争。

Another thing you should look for is the positive side of things instead of the negative. I have already given you several examples, and there are many, many more; how, given the situation, by changing the way I looked at it, I converted what was apparently a defect to an asset. I’ll give you another example. 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. I have found that it paid to say, “Oh yes, I’ll get the answer for you Tuesday,” not having any idea how to do it. By Sunday night I was really hard thinking on how I was going to deliver by Tuesday. I often put my pride on the line and sometimes I failed, but as I said, 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.
你应该寻找事物的积极面而非消极面。我已经举过几个例子，还有很多很多；在特定情境下，通过转变视角，我如何将看似缺陷之处转化为优势。再举个例子：我是个自负的人，这点毋庸置疑。我知道大多数休假写书的人都没能按时完成。所以出发前，我告诉所有朋友等我回来时那本书肯定完成了！没错，我必须完成——要是空手而归就太丢脸了！我利用自尊心驱动自己按期望的方式行动。 通过夸下海口迫使自己兑现承诺。多次实践证明，就像落入陷阱的老鼠，我总能爆发出惊人潜力。我发现承诺“周二一定给你答案”虽然当时毫无头绪，但周日晚我就会拼命思考如何兑现。经常拿自尊作赌注，虽然偶有失败，但正如所言，绝境中的我总能用出色表现让自己惊讶。我认为你需要学会驾驭自身潜能。 我认为你需要懂得如何将一种情境从一种视角转换到另一种，这会增加成功的几率。

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.
如今，自我欺骗在人类中极为普遍。有无数种方式让你改变一件事并自欺欺人，使其看起来是另一番模样。当你问：“为什么你没有做这样那样的事？”那个人总有千百个借口。如果你回顾科学史，通常现在有十个人都准备好了，而我们奖励的是第一个到达的人。另外九个人会说：“嗯，我也有这个想法，但我没去做，如此等等。”借口何其多。为什么你不是第一个？为什么你没有做对？别找借口，别试图欺骗自己。你可以对别人说任何你想说的借口，我不介意。但对自己，要尽量诚实。

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.
如果你真想成为一流的科学家，你需要了解自己，包括你的弱点、优点以及不良习性，比如我的自负。如何将缺点转化为优势？如何在人手不足的情况下，依然朝着必须前进的方向迈进？我再次强调，通过研究历史，我观察到成功的科学家会转变视角，将原本的缺陷变为资产。

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; furthermore I’ve told you how to reform. Therefore, go forth and become great scientists!
总之，我认为许多人未能成就伟大，原因包括：他们没有致力于重要的问题，没有情感上的投入，没有尝试将困难转化为易于处理但仍具重要性的局面，并且总是为自己找借口，归咎于运气。我已经告诉你们这有多简单，也指导了如何改进。因此，行动起来，成为伟大的科学家吧！

(End of the formal part of the talk.)
（演讲正式部分结束。）

DISCUSSION - QUESTIONS AND ANSWERS
讨论 - 问答环节

A. G. Chynoweth: Well that was 50 minutes of concentrated wisdom and observations accumulated over a fantastic career; I lost track of all the observations that were striking home. Some of them are very very timely. One was the plea for more computer capacity; I was hearing nothing but that this morning from several people, over and over again. So that was right on the mark today even though here we are 20 - 30 years after when you were making similar remarks, Dick. I can think of all sorts of lessons that all of us can draw from your talk. And for one, as I walk around the halls in the future I hope I won’t see as many closed doors in Bellcore. That was one observation I thought was very intriguing.
A. G. 奇诺维斯： 这真是 50 分钟浓缩的智慧与一段卓越职业生涯中积累的洞见；我数不清有多少观点直击心灵。其中一些尤为及时。比如对增加计算机能力的呼吁；今早我就从好几个人那里反复听到同样的需求。所以这一点在今天依然切中要害，尽管距离迪克你提出类似看法已过去二三十年。我能想到无数我们所有人都能从你的讲话中汲取的经验。其一，今后当我漫步在走廊时，但愿不会在贝尔科看到那么多紧闭的门——这个观察我觉得非常耐人寻味。

Thank you very, very much indeed Dick; that was a wonderful recollection. I’ll now open it up for questions. I’m sure there are many people who would like to take up on some of the points that Dick was making.
真的非常感谢你，迪克；那是一次精彩的回忆分享。现在我将开放提问环节。相信有很多人想就迪克提出的若干观点进行深入探讨。

Hamming: First let me respond to Alan Chynoweth about computing. I had computing in research and for 10 years I kept telling my management, “Get that ! machine out of research. We are being forced to run problems all the time. We can’t do research because were too busy operating and running the computing machines.” Finally the message got through. They were going to move computing out of research to someplace else. I was persona non grata to say the least and I was surprised that people didn’t kick my shins because everybody was having their toy taken away from them. I went in to Ed David’s office and said, “Look Ed, you’ve got to give your researchers a machine. If you give them a great big machine, we’ll be back in the same trouble we were before, so busy keeping it going we can’t think. Give them the smallest machine you can because they are very able people. They will learn how to do things on a small machine instead of mass computing.” As far as I’m concerned, that’s how UNIX arose. We gave them a moderately small machine and they decided to make it do great things. They had to come up with a system to do it on. It is called UNIX!
汉明: 首先让我回应艾伦·奇诺维斯关于计算的看法。我在研究部门负责计算工作长达十年，期间不断向管理层呼吁：“把那台该死的机器搬出研究部门！我们总被迫处理各种问题，忙于操作和维护计算机，根本无暇进行研究。”最终意见被采纳，计算设备将从研究部门迁至他处。我至少成了不受欢迎的人，甚至惊讶于没人对我怀恨在心——毕竟大家心爱的玩具被夺走了。我走进埃德·戴维的办公室说：“听着埃德，你必须给研究人员配备计算机。但若给大型机，我们又会重蹈覆辙——光维护就占尽精力。给他们最小的机器，因为这些人能力出众，会学会在小型机上实现功能，而非依赖大规模计算。”就我看来，UNIX 正是由此诞生。我们提供了中型小型机，他们决心让其成就伟业，于是开发出了实现这一目标的系统——这就是 UNIX！

A. G. Chynoweth: I just have to pick up on that one. In our present environment, Dick, while we wrestle with some of the red tape attributed to, or required by, the regulators, there is one quote that one exasperated AVP came up with and I’ve used it over and over again. He growled that, “UNIX was never a deliverable!”
A. G. 奇诺维斯： 我必须就此说几句。在我们当前的环境中，迪克，当我们与那些归因于或由监管机构要求的繁文缛节作斗争时，有一位恼怒的助理副总裁曾说过一句话，我反复引用。他愤愤不平地说：“UNIX 从来就不是一个可交付的产品！”

Question: What about personal stress? Does that seem to make a difference?
问题： 那么个人压力呢？那似乎有影响吗？

Hamming: Yes, it does. If you don’t get emotionally involved, it doesn’t. I had incipient ulcers most of the years that I was at Bell Labs. I have since gone off to the Naval Postgraduate School and laid back somewhat, and now my health is much better. But 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.
汉明： 是的，确实有影响。如果你不投入情感，就不会。在贝尔实验室的多数年份里，我都有早期溃疡的症状。后来我去了海军研究生院，稍微放松了些，现在我的健康状况好多了。但如果你想成为一位伟大的科学家，你就得承受压力。你可以过安逸的生活；你可以做个好人，或者成为伟大的科学家。但正如利奥·杜罗彻所说，好人总是最后一名。如果你想拥有很多休闲娱乐的美好生活，你会过得不错。

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?
问题：关于勇气的言论，无人能反驳；但我们这些已有白发或事业有成的人不必过于担忧。然而，我察觉到当今年轻人对于在高度竞争环境中承担风险确实存在忧虑。对此，您有何高见？

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.
汉明: 我要多引用埃德·戴维的话。埃德·戴维曾担忧我们社会整体勇气的丧失。在我看来，我们确实经历了不同阶段。从战争中走出，从我们制造原子弹的洛斯阿拉莫斯走出，从建造雷达等任务中走出，数学界和研究领域迎来了一批充满胆识的人。他们见证了奇迹的诞生；他们刚赢得一场不可思议的战争。我们有理由怀揣勇气，因此成就斐然。我无法重现那种境况。我不能责备当代人缺乏这种品质，但我认同你的观点；我只是不忍归咎于此。在我看来，他们似乎缺少追求卓越的渴望；他们缺乏付诸行动的勇气。而我们曾拥有，因为我们处于有利环境；我们刚刚经历了一场极其成功的战争。在战争漫长岁月里，我们曾岌岌可危；如你所知，那是一场殊死搏斗。 我认为，我们的成功赋予了我们勇气和自信；正因如此，从四十年代末到整个五十年代，实验室里涌现出巨大的生产力，这是早期经历所激发的。因为我们许多人早期被迫学习了其他知识——被迫学习不愿接触的内容，被迫保持开放心态——而后我们得以充分利用这些所学。这是事实，我无法改变；我也不能责怪当代人。这仅仅是现实。

Question: Is there something management could or should do?
问题：管理层是否能够或应该采取某些措施？

Hamming: Management can do very little. If you want to talk about managing research, that’s a totally different talk. I’d take another hour doing that. This talk is about how the individual gets very successful research done in spite of anything the management does or in spite of any other opposition. And how do you do it? Just as I observe people doing it. It’s just that simple and that hard!
汉明：管理层能做的非常有限。如果你想讨论研究管理，那完全是另一个话题，我需要额外一小时来阐述。本次讨论关注的是个人如何在管理层的任何举措或其他阻力下，依然能取得卓越的研究成果。如何做到？正如我观察他人实践的那样——简单至极，却也艰难无比！

Question: Is brainstorming a daily process?
问题：头脑风暴是日常活动吗？

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.
汉明: 曾几何时，集体讨论风靡一时，但似乎并未带来预期成效。就我个人而言，与其他人交流确实很有必要；但头脑风暴会议却往往收效甚微。我确实会专门找人深入交谈，比如这样说：“你看，我觉得这里应该存在某种规律。这是我目前观察到的现象…” 继而展开双向讨论。但关键要选择有能力的人。用个比喻来说，就像”临界质量”这个概念——当物质积累到足够程度就会产生链式反应。我还曾提出”声音吸收器”的说法：当吸收器过多时，你提出想法只会得到”对对对”的敷衍回应。真正需要的是能形成思维碰撞的临界质量——对方会回应”这让我联想到某件事”，或是”你考虑过这个方向吗？“。与人交流时，要避开那些只会附和”确实如此”的声音吸收器（虽然他们都是好人），找到能激发你思维火花的对话者。

For example, you couldn’t talk to John Pierce without being stimulated very quickly. There were a group of other people I used to talk with. For example there was Ed Gilbert; I used to go down to his office regularly and ask him questions and listen and come back stimulated. 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!
例如，与约翰·皮尔斯交谈总能迅速激发我的灵感。还有一群我常与之交流的人，比如埃德·吉尔伯特，我常去他的办公室，提问、倾听，然后带着启发回来。我精心选择与之头脑风暴的对象，因为那些只会吸收想法而不贡献的人是一种诅咒。他们人很好，却占满了空间，除了吸收想法外毫无贡献，新点子就这样消逝而非回响。是的，我认为与人交谈是必要的。那些闭门造车的人往往做不到这一点，因此他们的想法无法得到磨砺，比如“你注意到那边的什么了吗？”我之前一无所知——我可以过去看看。有人指明了方向。这次来访，我已经找到了几本回家后必读的书。当我认为对方能解答我的疑问，提供我不了解的线索时，我会与他们交谈并提问。我会走出去，亲自探索！

Question: What kind of tradeoffs did you make in allocating your time for reading and writing and actually doing research?
问题：在分配时间进行阅读、写作和实际研究时，你做了哪些权衡？

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.
汉明： 我早年认为，你在润色和展示上花费的时间至少应与原始研究相当。现在，至少 50%的时间必须用于展示。这是一个非常、非常大的比例。

Question: How much effort should go into library work?
提问： 在查找文献工作上应该投入多少精力？

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.
汉明: 这取决于领域。关于这点我想说的是，贝尔实验室曾有位极其聪明的同事。他总泡在图书馆里，博览群书。若需参考文献，找他准能获得各种资料。但在构建理论的过程中，我悟出一个道理：长远来看，不会有以他命名的学术效应。如今他已从贝尔实验室退休，担任兼职教授。他极具价值——我并非质疑这点，他还在《物理评论》上发表过不少优秀论文。但正因阅读过量，最终没有留下以他命名的学术效应。若总沉浸于他人成果，思维便会受其局限。若要孕育全新见解，不妨效法许多创新者：先将问题梳理清晰，在深入独立思考解决方案前，刻意避免接触现有答案，甚至尝试微调问题本身以臻完善。因此，保持跟进是必要的——但重点在于通过阅读发现问题，而非寻找现成解法。 阅读对于了解现状和可能性是必要的。但为了获取解决方案而阅读似乎并非做出卓越研究的方式。因此，我将给你两个答案。你阅读，但重要的不是数量，而是你阅读的方式。

Question: How do you get your name attached to things?
问题：你是如何让自己的名字与事物联系起来的？

Hamming: By doing great work. I’ll tell you the hamming window one. I had given Tukey a hard time, quite a few times, and I got a phone call from him from Princeton to me at Murray Hill. I knew that he was writing up power spectra and he asked me if I would mind if he called a certain window a “Hamming window.” And I said to him, “Come on, John; you know perfectly well I did only a small part of the work but you also did a lot.” He said, “Yes, Hamming, but you contributed a lot of small things; you’re entitled to some credit.” So he called it the hamming window. Now, let me go on. I had twitted John frequently about true greatness. I said true greatness is when your name is like ampere, watt, and fourier - when it’s spelled with a lower case letter. That’s how the hamming window came about.
汉明：通过做出伟大的工作。我来告诉你汉明窗的故事。我曾多次让图基难堪，有一次他从普林斯顿打电话到我在默里山的办公室。我知道他正在撰写关于功率谱的文章，他问我是否介意他将某个窗函数称为“汉明窗”。我对他说：“得了吧，约翰；你很清楚我只做了一小部分工作，而你也做了很多。”他说：“是的，汉明，但你贡献了许多小的方面；你理应得到一些荣誉。”于是他就称它为汉明窗。现在，让我继续。我经常调侃约翰关于真正伟大的定义。我说，真正的伟大是当你的名字像安培、瓦特和傅里叶那样——当它以小写字母拼写时。这就是汉明窗的由来。

Question: Dick, would you care to comment on the relative effectiveness between giving talks, writing papers, and writing books?
问题：迪克，你能否谈谈演讲、撰写论文和写书这三者之间的相对效果？

Hamming: 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. Let me tell you what infinite knowledge is. Since from the time of Newton to now, we have come close to doubling knowledge every 17 years, more or less. And we cope with that, essentially, by specialization. In the next 340 years at that rate, there will be 20 doublings, i.e. a million, and there will be a million fields of specialty for every one field now. It isn’t going to happen. The present growth of knowledge will choke itself off until we get different tools. I believe that books which try to digest, coordinate, get rid of the duplication, get rid of the less fruitful methods and present the underlying ideas clearly of what we know now, will be the things the future generations will value. 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. I don’t want to know that much about penguins is the usual reply. You just want to know the essence.
汉明: 短期内，若想激励他人，论文至关重要。若追求长远认可，在我看来，著书立说贡献更大，因为我们大多需要方向指引。在这个知识近乎无限的时代，我们需要导向来寻找出路。让我解释何为无限知识。自牛顿时代至今，我们大约每 17 年知识就翻一番。我们主要通过专业化来应对这一趋势。若按此速度，未来 340 年将出现 20 次翻倍，即百万倍增长，届时每个现有领域都将衍生出百万个专业分支。这不可能发生。当前知识的增长将自我抑制，直至我们掌握新工具。我相信，那些致力于消化、整合知识，剔除重复与低效方法，清晰阐述现有知识核心思想的书籍，将是未来世代所珍视的。公开演讲不可或缺；私下交流必不可少；书面论文同样必要。 但我倾向于认为，从长远来看，那些省略非必要内容的书籍比那些事无巨细都告诉你的书籍更为重要，因为你并不想知道所有事情。通常的回答是：我不想知道那么多关于企鹅的事情。你只想知道精髓所在。

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?
问题： 您提到了诺贝尔奖的问题以及随后对某些职业生涯造成的不良影响。这难道不是名声带来的一个更广泛的问题吗？一个人能做什么呢？

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.
汉明: 你可以做的一些事情如下。大约每七年左右，在你的领域进行一次重大转变，即便不是彻底转型。因此，我周期性地从数值分析转向硬件，再到软件等等，因为你的想法总会枯竭。当你进入一个新领域时，你必须像婴儿一样重新开始。你不再是那个无所不能的大人物，你可以回到起点，开始播种那些将成为参天橡树的橡子。我相信香农毁了自己。事实上，当他离开贝尔实验室时，我说：“香农的科学生涯就此结束了。”我收到了朋友们的大量批评，他们说香农依然聪明如初。我说：“是的，他会一样聪明，但他的科学生涯结束了。”我真心相信事实如此。

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.
你必须改变。一段时间后你会感到疲惫；你在一个领域耗尽了创造力。你需要寻找附近的新事物。我并非指从音乐转向理论物理再到英国文学；我的意思是，在你的专业领域内，你应该转换方向，以免变得僵化。虽然不能强制每七年就改变一次，但如果可能，我会设定一个研究条件：你必须每七年更换研究领域，并给出合理的定义，或者十年期满时，管理层有权强制你转变。我坚持这一改变，因为我是认真的。老前辈们的问题在于，他们固守一种方法；持续沿用。他们曾朝着正确的方向前进，但世界在变。新的方向已然出现；而他们却仍在旧路上前行。

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.
你需要进入新领域以获取新视角，并在耗尽旧有资源之前行动。对此你可以有所作为，但这需要付出努力与精力。要有勇气说：“是的，我愿放弃我的显赫声誉。”例如，当纠错码领域发展成熟时，手握这些理论的我曾告诉自己：“汉明，你将停止阅读该领域的论文；你要完全忽略它；你要尝试做些别的事情，而非依赖旧有成就随波逐流。”我刻意拒绝继续深耕那一领域，甚至不再阅读相关论文，以此迫使自己有机会开拓新天地。我管理着自己——这正是我整场演讲所倡导的理念。深知自身诸多缺点，我进行自我管理。我的缺点很多，因此面临大量问题，亦即存在众多自我提升的可能。

Question: Would you compare research and management?
问题：你会比较研究与管理工作吗？

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.
汉明：若想成为杰出的研究者，便不能同时担任公司总裁。若志在成为总裁，则另当别论。我并非反对担任总裁，只是个人志不在此。我认为伊恩·罗斯担任贝尔实验室总裁做得很出色。我并非反对此职；但必须明确自己的追求。此外，年轻时或立志成为伟大科学家，但随着年岁增长，想法可能改变。例如，某日我曾问上司博德：“您为何要当部门主管？继续做优秀科学家不好吗？“他答道：“汉明，我对贝尔实验室的数学发展有宏图愿景。若想实现这个愿景，我必须亲力推动；我必须成为部门主管。“当你的理想抱负仅凭一己之力就能实现时，自当全力追求。当你的愿景——那些你认为必须完成的事业——超越个人能力范围时，就需要转向管理岗位。而愿景愈是宏大，在管理道路上就需走得愈远。 如果你对整个实验室或整个贝尔系统有愿景，就必须亲临其境去实现它。从底层做起很难轻易达成目标。这取决于你的目标和愿望是什么。随着生活中这些因素的变化，你必须准备好随之改变。我选择避开管理岗位，因为我更喜欢单枪匹马地做我能做的事。但这是我做出的选择，带有个人偏见。每个人都有权做出自己的选择。保持开放的心态。但当你选定一条道路时，务必清楚自己做了什么选择。不要试图兼顾两边。

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?
问题：个人的期望有多重要？或者身处一个对你寄予厚望的群体或人群中，这又有多重要？

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.
汉明：在贝尔实验室，每个人都期待我能做出优秀的工作——这对我帮助很大。当大家都期望你表现出色时，如果你有自尊心，你就会做到。我认为身边有一流的人才非常宝贵。我主动寻找最优秀的人。当物理组失去了顶尖人才时，我便离开了；当我发现化学组情况相同时，我也选择了离开。我努力与那些能力出众的人为伍，这样我可以向他们学习，并且他们也会对我寄予厚望。通过有意识地管理自己，我认为我比放任自流做得要好得多。

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.
提问：你在谈话开始时淡化了运气的作用，但似乎也轻描淡写了那些让你来到洛斯阿拉莫斯、芝加哥以及贝尔实验室的际遇。

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.
汉明：这其中确实有些运气成分。但另一方面，我并不了解其他可能的发展路径。除非你能证明其他道路不会同样或更加成功，否则我无法断言。你所做的特定事情是运气吗？比如，当我在洛斯阿拉莫斯遇见费曼时，我就知道他将会获得诺贝尔奖。虽然不清楚具体因何而得，但我深信他必将做出卓越成就。无论未来出现何种方向，这个人都会做出伟大工作。果然，他确实做到了。这并非意味着你只在特定情境下做出一点成就而那是运气使然，机会迟早会以多种形式出现。机会就像满满一桶，身处其中的人只要抓住一个，就能在彼处而非此处成就伟大。运气的因素存在，但又不尽然。机遇眷顾有准备的头脑；机遇青睐有准备的人。这并非绝对保证，我不能承诺成功是必然的。我认为运气会改变概率，但个人确实拥有一定的掌控力。

Go forth, then, and do great work!
接下来，前进吧，去做伟大的工作吧！

(End of the General Research Colloquium Talk.)
（通用研究研讨会谈话结束。）

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