对这篇文章最深的感受，是结束的时候提到的一点，追求卓越最大的收获，不在于"赢"——"而在于改变自己、与自己搏斗的过程中，你成为了怎样的人。"我们和我们的人生，我们和AI之间都是一个彼此驯养和HARNESS的过程，如果幸运，我们一起进化，一起带着一些五彩的泡泡隐入历史的尘埃。以及他最后的，「我已经相当详细地告诉你该如何成功，因此你没有理由做得不如我。祝你好运。」

所以带着这个祝福与期许，开始不时的审视下自己的人生和人生中大大小小的选择，如同香农下棋时经常会大胆地把皇后直接冲进战场。然后笑着说：“I ain’t scared of nothing.”“我什么都不怕。”他说，每当我陷入困境时，我也会对自己重复这句话：“我什么都不怕。”--所以不妨从这里开始，别害怕，往前走，或者会有灵光一闪的奇迹。

以上，谢谢你阅读到最后一个字。

附-中英文原文对照全文：

You and Your Research /你与你的研究

A talk by Richard W. Hamming — Bellcore, 7 March 1986

理查德·W·汉明 演讲—— 贝尔通信研究院，1986 年3 月7 日

中英对照版· 译注：本文为汉明经典演讲《You and Your Research》全文，后由Stripe Press 收录于《The Art of Doing Science and Engineering: Learning to Learn》一书。

出版说明/ Publisher's Note

"You and Your Research" is one of Richard Hamming's many lectures. In 1996, he published a write-up of his graduate course lectures in engineering at the U.S. Naval Postgraduate School in a book called The Art of Doing Science and Engineering; Learning to Learn. In Hamming's words, "the course centers around how to look at and think about knowledge," and is an extension of the wisdom of "You and Your Research." The book was republished this year, with a foreword from Bret Victor, by Stripe Press.

《你与你的研究》是理查德·汉明众多演讲中的一篇。1996年，他将自己在美国海军研究生院讲授的工程学研究生课程整理成书，名为《做科学与工程的艺术：学会学习》。用汉明本人的话说，"这门课围绕着如何看待和思考知识展开"，是《你与你的研究》中智慧的延伸。今年，这本书由Stripe Press 重新出版，并由布雷特·维克托（Bret Victor）作序。

正文/ The Talk

[START /开始]

I have given a talk with this title many times, and it turns out from discussions after the talk I could have just as well have called it "You and Your Engineering Career," or even "You and Your Career." But I left the word "research" in the title because that is what I have most studied.

这个题目的演讲我做过很多次。从演讲后的讨论看，我其实完全可以把它叫做"你与你的工程生涯"，甚至"你与你的职业生涯"。但我还是在标题里保留了"研究"这个词，因为这是我钻研最深的领域。

From the previous chapters you have an adequate background for how I made the study, and I need not mention again the names of the famous people I have studied closely. The earlier chapters are, in a sense, just a great expansion, with much more detail, of the original talk. This chapter is, in a sense, a summary of the previous 29 chapters.

从前面的章节中，你已经充分了解了我是如何做这项研究的，我不必再次提及那些我曾近距离观察过的著名人物的名字。从某种意义上说，前面的章节只是对这场原始演讲的极大扩展和更详尽的展开。而本章，从某种意义上说，是对前面29 章的总结。

Why do I believe this talk is important? It is important because as far as I know each of you has but one life to lead, and it seems to me it is better to do significant things than to just get along through life to its end. Certainly near the end it is nice to look back at a life of accomplishments rather than a life where you have merely survived and amused yourself. Thus in a real sense I am preaching the messages that (1) it is worth trying to accomplish the goals you set yourself and (2) it is worth setting yourself high goals.

我为什么认为这场演讲重要？它之所以重要，是因为据我所知，你们每个人都只有一次人生可以度过，而在我看来，做一些有意义的事，胜过浑浑噩噩地把日子过到头。临近终点时，回望一生满是成就，总好过回望一生只是苟活和自娱自乐。所以从真正的意义上说，我在宣讲两条信念：（1）努力去实现你为自己设定的目标，是值得的；（2）为自己设定远大的目标，是值得的。

Again, to be convincing to you I will talk mainly about my own experience, but there are equivalent stories I could use involving others. I want to get you to the state where you will say to yourself, "Yes, I would like to do first-class work. If Hamming could, then why not me?" Our society frowns on those who say this too loudly, but I only ask you say it to yourself! What you consider first-class work is up to you; you must pick your goals, but make them high!

同样，为了让你信服，我主要会谈我自己的经历，不过我也有许多关于他人的类似故事可讲。我想把你带到这样一种状态：你会对自己说，"是的，我想做第一流的工作。如果汉明能做到，为什么我不能？"我们的社会不喜欢那些把这话说得太大声的人，但我只要求你对自己说！什么算第一流的工作由你自己定；你必须挑选你的目标，但要把目标定得高远！

I will start psychologically rather than logically. The major objection cited by people against striving to do great things is the belief that it is all a matter of luck. I have repeatedly cited Pasteur's remark, "Luck favors the prepared mind." It both admits there is an element of luck and yet claims to a great extent it is up to you. You prepare yourself to succeed or not, as you choose, from moment to moment by the way you live your life.

我会从心理层面而非逻辑层面切入。人们反对去追求伟大成就时，最常援引的理由，是认为这一切全凭运气。我反复引用巴斯德的那句话："机遇偏爱有准备的头脑。"这句话既承认运气有其作用，又主张这在很大程度上取决于你自己。你是否为成功做好准备，全在你的选择——你以何种方式度过生活，时时刻刻都在做这个准备。

As an example related to the "luck" aspect, when I first came to Bell Telephone Laboratories I shared an office with Claude Shannon. At about the same time, he created information theory and I created coding theory. They were "in the air," you can say, and you are right. Yet why did we do it and the others who were also there not do it? Luck? Some, perhaps, but also because we were what we were and the others were what they were. The differences were we were more prepared to find, work on, and create the corresponding theories.

举一个与"运气"有关的例子：我初到贝尔电话实验室时，和克劳德·香农共用一间办公室。差不多在同一时期，他创立了信息论，我创立了编码理论。你可以说，这些思想当时"已在空气中弥漫"，你说得没错。可是，为什么是我们做成了，而同样身处其中的其他人没有？运气吗？或许有一些，但更因为我们之所以是我们，他人之所以是他人。区别在于：我们更有准备去发现、去钻研、去创造相应的理论。

If it were mainly luck, then great things should not tend to be done repeatedly by the same people. Shannon did a lot of important things besides information theory—his master's thesis was applying Boolean algebra to switching circuits! Einstein did many great things, not just one or two. For example, when he was around 12–14 years old, he asked himself what light would look like if he went at the velocity of light. He would, apparently, see a local peak, yet the corresponding mathematical equations would not support a stationary extreme! An obvious contradiction! Is it surprising he later discovered special relativity, which was in the air and which many people were working on at that time? He had prepared himself long ago, by that early question, to understand better than the others what was going on and how to approach it.

倘若主要靠运气，那么伟大的成就就不该总是由同一批人反复完成。香农除了信息论，还做了许多重要的工作——他的硕士论文就是把布尔代数应用到开关电路上！爱因斯坦做的伟大工作也不止一两件。比如，他大约12 到14 岁时，曾问自己：如果以光速前进，光看上去会是什么样？看上去他会看到一个局部的波峰，然而对应的数学方程却不支持这样一个静止的极值！这显然是个矛盾！那么，他后来发现了狭义相对论——那同样是当时"弥漫在空气中"、许多人都在研究的课题——这还令人惊讶吗？早在那时，他就通过那个早年的发问，让自己比别人更深刻地理解了其中究竟发生了什么、该如何着手。

Newton observed that if others would think as hard as he did, then they would be able to do the same things. Edison said genius was 99% perspiration and 1% inspiration. It is hard work, applied for long years, which leads to the creative act, and it is rarely just handed to you without any serious effort on your part. Yes, sometimes it just happens, and then it is pure luck. It seems to me to be folly for you to depend solely on luck for the outcome of this one life you have to lead.

牛顿曾说，如果别人能像他那样努力思考，他们也能做出同样的成就。爱迪生说，天才是99% 的汗水加1% 的灵感。是常年累月投入的艰苦努力，才催生了那创造性的一刻；它很少在你不付出任何认真努力的情况下凭空降临。是的，有时它确实会自己发生，那便是纯粹的运气。可在我看来，对你这仅有一次的人生，把结果全然寄托于运气，是一种愚蠢。

One of the characteristics you see is that great people when young were generally active—though Newton did not seem exceptional until well into his undergraduate days at Cambridge, Einstein was not a great student, and many other great people were not at the top of their class.

你会观察到的一个特点是：伟大的人物年轻时通常都很活跃——尽管牛顿直到剑桥本科阶段相当靠后才显出过人之处，爱因斯坦也算不上优等生，还有许多其他伟人当年并不是班上的尖子。

Brains are nice to have, but many people who seem not to have great IQs have done great things. At Bell Telephone Laboratories Bill Pfann walked into my office one day with a problem in zone melting. He did not seem to me, then, to know much mathematics, to be articulate, or to have a lot of clever brains, but I had already learned brains come in many forms and flavors, and to beware of ignoring any chance I got to work with a good man. I first did a little analytical work on his equations, and soon realized what he needed was computing. I checked up on him by asking around in his department, and I found they had a low opinion of him and his idea for zone melting. But that is not the first time a person has not been appreciated locally, and I was not about to lose my chance of working with a great idea—which is what zone melting seemed to me, though not to his own department! There is an old saying: "A prophet is without honor in his own country." Mohammed fled from his own city to a nearby one, and there got his first real recognition!

聪明的头脑固然好，但许多看上去智商并不出众的人，却做出了伟大的成就。在贝尔电话实验室，有一天比尔·普凡（Bill Pfann）带着一个区域熔炼（zone melting）的问题走进我的办公室。当时在我看来，他似乎不太懂数学、口才不佳、也没有特别机敏的头脑；但我早已懂得，才智有多种形式和风味，要警惕错过任何与优秀之人合作的机会。我先对他的方程做了一点分析工作，很快意识到他真正需要的是计算。我向他所在部门的人打听，发现他们对他和他的区域熔炼想法评价不高。但这并不是头一回有人在本地不被赏识，而我可不打算错过和一个伟大想法共事的机会——在我看来，区域熔炼正是这样一个伟大想法，尽管他自己部门并不这么认为！有句老话说："先知在本乡无人尊敬。"穆罕默德从自己的城市逃到邻近的城市，才在那里获得了第一份真正的认可！

So I helped Bill Pfann, taught him how to use the computer, how to get the numerical solutions to his problems, and let him have all the machine time he needed. It turned out zone melting was just what we needed to purify materials for transistors, for example, and it has proved to be essential in many areas of work. He ended up with all the prizes in the field, much more articulate as his confidence grew, and the other day I found his old lab is now a part of a national monument! Ability comes in many forms, and on the surface the variety is great; below the surface there are many common elements.

于是我帮助了比尔·普凡，教他如何使用计算机、如何得到问题的数值解，并把他所需的全部机时都让给他。结果证明，区域熔炼恰恰正是我们提纯晶体管材料等所急需的，它后来在许多工作领域都被证明不可或缺。他最终拿下了该领域所有的奖项，随着信心增长，他的表达也越来越流畅；前几天我还发现，他当年的旧实验室如今已成为一处国家级纪念遗址的一部分！能力以多种形式呈现，表面上千差万别；但在表象之下，却有许多共通的要素。

Having disposed of the psychological objections of luck and the lack of high-IQ-type brains, let us go on to how to do great things. Among the important properties to have is the belief you can do important things. If you do not work on important problems, how can you expect to do important work? Yet direct observation and direct questioning of people show most scientists spend most of their time working on things they believe are not important and are not likely to lead to important things.

处理完关于"运气"和"缺乏高智商头脑"这两条心理上的反对意见，让我们继续谈如何成就大事。其中一项重要的品质，是相信自己能做重要的事。如果你不去研究重要的问题，又怎么能指望做出重要的工作？然而，直接的观察和对人们的直接询问表明，大多数科学家把大部分时间花在他们自己都认为不重要、也不太可能通向重要成果的事情上。

As an example, after I had been eating for some years with the physics table at the Bell Telephone Laboratories restaurant, fame, promotion, and hiring by other companies ruined the average quality of the people, so I shifted to the chemistry table in another corner of the restaurant. I began by asking what the important problems were in chemistry, then later what important problems they were working on, and finally one day said, "If what you are working on is not important and not likely to lead to important things, then why are you working on it?" After that I was not welcome and had to shift to eating with the engineers!

举个例子：我在贝尔电话实验室的餐厅里和物理学家那桌一起吃了好些年饭，后来名望、升迁以及被其他公司挖走，拉低了这群人的平均水准，于是我转到餐厅另一角的化学家那桌。我先是问化学里有哪些重要问题，后来又问他们正在研究哪些重要问题，终于有一天我说："如果你做的事情既不重要、又不太可能通向重要的成果，那你为什么还在做它？"从那以后我就不受欢迎了，只好转去和工程师们一起吃饭！

That was in the spring, and in the fall one of the chemists stopped me in the hall and said, "What you said caused me to think for the whole summer about what the important problems are in my field, and while I have not changed my research it was well worth the effort." I thanked him and went on—and noticed in a few months he was made head of the group. About ten years ago I saw he became a member of the National Academy of Engineering. No other person at the table did I ever hear of, and no other person was capable of responding to the question I had asked: "Why are you not working on and thinking about the important problems in your area?" If you do not work on important problems, then it is obvious you have little chance of doing important things.

那是在春天，到了秋天，其中一位化学家在走廊里拦住我说："你说的那番话，让我整个夏天都在思考我这个领域里什么才是重要问题；虽然我没有改变自己的研究方向，但这番思考非常值得。"我谢过他便走开了——几个月后我注意到，他被任命为该小组的负责人。大约十年前，我看到他当选为美国国家工程院院士。那张桌子上其他人我再没听说过，也没有别人能够回应我提出的那个问题："你为什么不去研究、不去思考你领域里那些重要的问题？"如果你不研究重要的问题，那么显然你几乎没有机会做出重要的成就。

Confidence in yourself, then, is an essential property. Or, if you want to, you can call it "courage." Shannon had courage. Who else but a man with almost infinite courage would ever think of averaging over all random codes and expect the average code would be good? He knew what he was doing was important and pursued it intensely. Courage, or confidence, is a property to develop in yourself. Look at your successes, and pay less attention to failures than you are usually advised to do in the expression, "Learn from your mistakes." While playing chess Shannon would often advance his queen boldly into the fray and say, "I ain't scared of nothing." I learned to repeat it to myself when stuck, and at times it has enabled me to go on to a success. I deliberately copied a part of the style of a great scientist. The courage to continue is essential, since great research often has long periods with no success and many discouragements.

因此，对自己的信心，是一项必备的品质。或者，如果你愿意，也可以称之为"勇气"。香农就有勇气。除了一个拥有近乎无穷勇气的人，还有谁会想到去对所有随机码取平均，并期待这个平均的码会是好的？他知道自己所做的事很重要，并全力以赴地去追求。勇气，或者说信心，是你应当在自己身上培养的品质。多看看你的成功，而不要像人们常劝告的那句"从错误中学习"那样，把太多注意力放在失败上。下棋时，香农常常大胆地把皇后推进战团，嘴里说着"我什么都不怕"。每当卡住时，我学着对自己重复这句话，有好几次它都让我得以继续走向成功。我有意模仿了这位伟大科学家的一部分风格。继续下去的勇气至关重要，因为伟大的研究往往有很长一段时间毫无成果、充满挫折。

The desire for excellence is an essential feature for doing great work. Without such a goal you will tend to wander like a drunken sailor. The sailor takes one step in one direction and the next in some independent direction. As a result the steps tend to cancel each other out, and the expected distance from the starting point is proportional to the square root of the number of steps taken. With a vision of excellence, and with the goal of doing significant work, there is a tendency for the steps to go in the same direction and thus go a distance proportional to the number of steps taken, which in a lifetime is a large number indeed. As noted before, Chapter 1, the difference between having a vision and not having a vision is almost everything, and doing excellent work provides a goal which is steady in this world of constant change.

追求卓越的渴望，是做出伟大工作的一项根本特质。没有这样的目标，你就会像个醉汉水手一样四处游荡。这水手朝一个方向迈一步，下一步又朝另一个不相干的方向迈出。结果这些步子相互抵消，他离起点的期望距离只与步数的平方根成正比。而怀着对卓越的愿景、以做出有意义工作为目标，步子就倾向于朝同一个方向迈进，于是走出的距离与步数本身成正比——而在一生之中，步数确实是一个庞大的数字。如第1 章所述，有没有愿景，几乎决定了一切；而做卓越的工作，能在这个变动不居的世界里，提供一个稳定的目标。

Age is a factor physicists and mathematicians worry about. It is easily observed that the greatest work of a theoretical physicist, mathematician, or astrophysicist is generally done very early. They may continue to do good work all their lives, but what society ends up valuing most is almost always their earliest great work. The exceptions are very, very few indeed. But in literature, music composition, and politics, age seems to be an asset.

年龄是物理学家和数学家担忧的一个因素。人们很容易观察到，一位理论物理学家、数学家或天体物理学家最伟大的工作，通常都完成得很早。他们也许一生都能持续做出优秀的工作，但社会最终最看重的，几乎总是他们最早期的那项伟大成就。例外极少极少。然而在文学、音乐创作和政治领域，年龄似乎反倒是一种资本。

The best compositions of a composer are usually the late ones, as judged by popular opinion. One reason for this is that fame in science is a curse to quality productivity, though it tends to supply all the tools and freedom you want to do great things. Another reason is that most famous people, sooner or later, tend to think they can only work on important problems—hence they fail to plant the little acorns which grow into the mighty oak trees. I have seen it many times, from Brattain of transistor fame and a Nobel Prize to Shannon and his information theory. Not that you should merely work on random things, but on small things which seem to you to have the possibility of future growth.

按大众的评判，一位作曲家最好的作品通常是他晚年的作品。其中一个原因是：在科学界，名望是高质量产出的诅咒——尽管它往往能为你提供做大事所需的一切工具和自由。另一个原因是：大多数成名的人，迟早会觉得自己只能去研究重要的问题——于是他们便不再去种下那些日后能长成参天橡树的小橡果。我见过很多这样的例子，从因晶体管和诺贝尔奖而成名的巴丁，到香农和他的信息论。这并不是说你该随便做些什么，而是说要去做那些在你看来具有未来成长可能性的小事。

In my opinion the Institute for Advanced Study at Princeton has ruined more great scientists than any other place has created—considering what they did before and what they did after going there. A few, like von Neumann, escaped the closed atmosphere of the place, with all its physical comforts and prestige, and continued to contribute to the advancement of science, but most remained there and continued to work on the same problems which got them there but which were generally no longer of great importance to society.

在我看来，普林斯顿高等研究院毁掉的伟大科学家，比任何其他地方造就的还要多——只要对比他们去那里之前和之后所做的工作就知道了。少数人，比如冯·诺依曼，逃脱了那个地方封闭的氛围（尽管它有种种物质上的舒适和声望），继续为科学的进步作出贡献；但大多数人留在那里，继续研究当初让他们成名的那些问题，而这些问题通常已不再对社会有重大意义了。

Thus what you consider to be good working conditions may not be good for you! There are many illustrations of this point. For example, working with one's door closed lets you get more work done per year than if you had an open door, but I have observed repeatedly that later those with the closed doors, while working just as hard as others, seem to work on slightly the wrong problems, while those who have let their door stay open get less work done but tend to work on the right problems! I cannot prove the cause-and-effect relationship; I can only observe the correlation. I suspect the open mind leads to the open door, and the open door tends to lead to the open mind; they reinforce each other.

因此，你自以为是的好工作条件，未必真的对你好！这一点有许多例证。比如，关着门工作，每年能比开着门完成更多的工作；但我反复观察到，那些关门工作的人，后来尽管和别人一样努力，却似乎总在研究略微"错误"的问题；而那些任由门敞开着的人，虽然完成的工作较少，却往往在研究"正确"的问题！我无法证明其中的因果关系，只能观察到这种相关性。我猜想，开放的头脑会带来敞开的门，而敞开的门又倾向于带来开放的头脑；二者相互强化。

A similar story from my own experience. In the early days of programming computers in absolute binary, the usual approach was usually through an "acre of programmers." It was soon evident to me that Bell Telephone Laboratories would never give me an acre of programmers. What to do? I could go to a West Coast airframe manufacturer and get a job and have the proverbial acre, but Bell Telephone Laboratories had a fascinating collection of great people from whom I could learn a lot, and the airframe manufacturers had relatively fewer such people. After quite a few weeks of wondering what to do I finally said to myself, "Hamming, you believe machines can do symbol manipulation. Why not get them to do the details of the programming?" Thus I was led directly to a frontier of computer science by simply inverting the problem. What had seemed to be a defect now became an asset and pushed me in the right direction!

我自己也有一个类似的故事。在用绝对二进制为计算机编程的早期，常规做法通常是动用"一大片程序员"。我很快就明白，贝尔电话实验室绝不会给我"一大片程序员"。怎么办？我可以去西海岸一家飞机制造商那里谋个职位，拥有那传说中的"一大片"人手；但贝尔实验室汇集了一批迷人的杰出人才，我能从他们身上学到很多，而飞机制造商那里这样的人才相对要少得多。苦苦琢磨了好几个星期之后，我终于对自己说："汉明，你相信机器能做符号运算。那为什么不让它们来做编程中那些繁琐的细节呢？"就这样，仅仅通过把问题反转过来，我便被直接引向了计算机科学的一个前沿。原本看似是缺陷的东西，如今反而成了优势，并把我推向了正确的方向！

Grace Hopper had a number of similar stories from computer science, and there are many other stories with the same moral: When stuck, often inverting the problem and realizing the new formulation is better represents a significant step forward. I am not asserting all blockages can be so rearranged, but I am asserting that many more than you might at first suspect can be so changed from a more or less routine response to a great one.

格蕾丝·霍珀（Grace Hopper）在计算机科学中也有不少类似的故事，还有许多其他故事都蕴含着同样的道理：当陷入僵局时，不妨把问题反转过来，意识到新的表述方式更好，这往往代表着一次重大的进步。我并不是断言所有的障碍都能这样重新安排，但我要断言的是：能够这样从一个或多或少平庸的应对，转变为一个出色应对的情形，远比你最初设想的要多得多。

This is related to another aspect of changing the problem. I was once solving on a digital computer the first really large simulation of a system of simultaneous differential equations, which at that time were the natural problem for an analog computer—but they had not been able to do it, and I was doing it on an IBM 701. The method of integration was an adaptation of the classical Milne's method, and it was ugly to say the least. I suddenly realized that of course, being a military problem, I would have to file a report on how it was done, and every analog installation would go over it trying to object to what was actually being proved as against just getting the answers—I was showing convincingly that on some large problems, the digital computer could beat the analog computer on its own home ground.

这与"改变问题"的另一个侧面有关。我曾在一台数字计算机上求解第一个真正大型的联立微分方程组仿真——那在当时本是模拟计算机的天然问题，可它们没能做出来，而我用一台IBM 701 做出来了。所用的积分方法，是对经典米尔恩（Milne）方法的改造，说得客气点也实在算不上漂亮。我忽然意识到：当然了，由于这是个军方课题，我必须就具体做法写一份报告，而每一处装有模拟计算机的机构都会逐字研读它，竭力对所证明的内容（而非仅仅得到答案这件事）提出异议——我正在令人信服地表明：在某些大型问题上，数字计算机能在模拟计算机的主场把它击败。

Realizing this, I realized the method of solution should be cleaned up, so I developed a new method of integration which had a nice theory, changed the method on the machine with a change of comparatively few instructions, and then computed the rest of the trajectories using the new formula. I published the new method and for some years it was in wide use and known as "Hamming's method." I do not recommend the method now that further progress has been made and the computers are different. To repeat the point I am making, I changed the problem from just getting answers to the realization I was demonstrating clearly for the first time the superiority of digital computers over the current analog computers, thus making a significant contribution to the science behind the activity of computing answers.

意识到这一点后，我明白这套解法应当被打磨干净，于是我发展出一种具有优美理论的新积分方法，只改动了相对很少的几条指令就在机器上换上了新方法，然后用新公式算出了其余的轨迹。我把这种新方法发表出来，有好些年它都被广泛使用，被称为"汉明方法"。如今随着研究进一步推进、计算机也已不同，我不再推荐这种方法了。重申我想说的要点：我把问题从"仅仅得到答案"，转变为意识到自己是在首次清晰地证明数字计算机相对于当时模拟计算机的优越性——从而对"计算答案"这一活动背后的科学，作出了一项重要的贡献。

All these stories show that the conditions you tend to want are seldom the best ones for you—the interaction with harsh reality tends to push you into significant discoveries which otherwise you would never have thought about while doing pure research in a vacuum of your private interests.

所有这些故事都表明：你往往想要的那些条件，很少是对你最好的条件——与严酷现实的碰撞，往往会把你推向那些重大的发现，而若你只是在自己私人兴趣的真空里做纯研究，这些发现你根本不会想到。

Now to the matter of drive. Looking around, you can easily observe that great people have a great deal of drive to do things. I had worked with John Tukey for some years before I found he was essentially my age, so I went to our mutual boss and asked him, "How can anyone my age know as much as John Tukey does?" He leaned back, grinned, and said, "You would be surprised how much you would know if you had worked as hard as he has for as many years." There was nothing for me to do but slink out of his office, which I did. I thought about the remark for some weeks and decided that while I could never work as hard as John did, I could do a lot better than I had been doing.

现在来谈谈"内驱力"。环顾四周，你很容易就能观察到，伟大的人物都有强烈的做事的内驱力。我和约翰·图基（John Tukey）共事了好几年，才发现他基本上和我同龄，于是我去找我们共同的上司，问他："和我同龄的人，怎么可能懂得像约翰·图基那么多？"他往后一靠，咧嘴一笑，说："如果你像他那样辛勤地工作那么多年，你会惊讶于自己竟能懂得那么多。"我无话可说，只能灰溜溜地走出他的办公室，我也确实那么做了。我把这句话琢磨了好几个星期，最后得出结论：虽然我永远无法像约翰那样拼命，但我可以比过去做得好得多。

In a sense my boss was saying intellectual investment is like compound interest: the more you do, the more you learn how to do, so the more you can do, etc. I do not know what compound interest rate to assign, but it must be well over 6%—one extra hour per day over a lifetime will much more than double the total output. The steady application of a bit more effort has a great total accumulation.

从某种意义上说，我的上司是在讲：智力上的投入就像复利——你做得越多，就越懂得如何去做，于是你就能做得越多，如此循环。我不知道该给它定多高的复利率，但肯定远高于6%——一生中每天多投入一个小时，最终的总产出会远不止翻一番。稳定地多付出一点努力，长期累积下来会有巨大的总和。

But be careful—the race is not to the one who works hardest! You need to work on the right problem at the right time and in the right way—what I have been calling "style." At the urging of others, for some years I set aside Friday afternoons for "great thoughts." Of course, I would answer the telephone, sign a letter, and such trivia, but essentially, once lunch started, I would only think great thoughts—what was the nature of computing, how would it affect the development of science, what was the natural role of computers in Bell Telephone Laboratories, what effect will computers have on AT&T, on science generally?

但要小心——胜利并不属于最拼命的那个人！你需要在正确的时间、用正确的方式去研究正确的问题——也就是我一直所说的"风格"（style）。在别人的劝促下，有好几年我把周五下午留出来专门用于"伟大的思考"。当然，我还是会接电话、签个文件之类的琐事，但本质上，一旦午饭开始，我就只思考宏大的问题——计算的本质是什么？它将如何影响科学的发展？计算机在贝尔电话实验室里天然的角色是什么？计算机会给AT&T、乃至整个科学带来怎样的影响？

I found it was well worth the 10% of my time to do this careful examination of where computing was heading so I would know where we were going and hence could go in the right direction. I was not the drunken sailor staggering around and canceling many of my steps by random other steps, but could progress in a more or less straight line. I could also keep a sharp eye on the important problems and see that my major effort went to them.

我发现，花掉我10% 的时间来这样仔细审视计算技术的走向，是非常值得的——这样我就能知道我们要去往何方，从而朝正确的方向前进。我不再是那个踉踉跄跄、用随机的另一步抵消掉许多步子的醉汉水手，而是能够大致沿一条直线前进。我也得以始终敏锐地盯住那些重要的问题，确保把我的主要精力投向它们。

I strongly recommend taking the time, on a regular basis, to ask the larger questions, and not stay immersed in the sea of detail where almost everyone stays almost all of the time. These chapters have regularly stressed the bigger picture, and if you are to be a leader into the future, rather than a follower of others, I am now saying it seems to me to be necessary for you to look at the bigger picture on a regular, frequent basis for many years.

我强烈建议你定期抽出时间去追问那些更宏大的问题，而不要像几乎所有人几乎所有时候那样，沉溺于细节的汪洋大海之中。这些章节一再强调"大局"；而如果你想成为引领未来的领导者，而非他人的追随者，那么我现在要说：在我看来，你有必要在许多年里，定期且频繁地去审视大局。

There is another trait of great people I must talk about—and it took me a long time to realize it. Great people can tolerate ambiguity; they can both believe and disbelieve at the same time. You must be able to believe your organization and field of research is the best there is, but also that there is much room for improvement! You can sort of see why this is a necessary trait. If you believe too much, you will not likely see the chances for significant improvements; if you do not believe enough, you will be filled with doubts and get very little done, chances are only the 2%, 5%, and 10% improvements. I have not the faintest idea of how to teach the tolerance of ambiguity, both belief and disbelief at the same time, but great people do it all the time.

还有一项伟人的特质我必须谈谈——我花了很长时间才意识到它。伟大的人能够容忍矛盾（ambiguity）；他们能在同一时刻既相信又不相信。你必须既能相信你所在的机构和研究领域是世上最好的，又能相信它还有很大的改进空间！你大致能看出为什么这是一项必备的特质。如果你信得太过，就不太可能看到那些重大改进的机会；如果你信得不够，就会满腹疑虑、几乎一事无成，能做到的至多是2%、5%、10% 的小改进。我丝毫不知道该如何教人去容忍这种矛盾——同时相信又不相信——但伟大的人一直都在这么做。

Most great people also have 10 to 20 problems they regard as basic and of great importance, and which they currently do not know how to solve. They keep them in their mind, hoping to get a clue as to how to solve them. When a clue does appear they generally drop other things and get to work immediately on the important problem. Therefore they tend to come in first, and the others who come in later are soon forgotten. I must warn you, however, that the importance of the result is not the measure of the importance of the problem. The three problems in physics—anti-gravity, teleportation, and time travel—are seldom worked on because we have so few clues as to how to start. A problem is important partly because there is a possible attack on it and not just because of its inherent importance.

大多数伟大的人，心里还揣着10 到20 个他们视为根本而重要、却暂时还不知如何求解的问题。他们把这些问题记在心里，盼着能找到解决它们的线索。一旦线索出现，他们通常会放下其他事情，立刻动手攻克那个重要的问题。因此他们往往率先抵达终点，而那些后来才到的人，很快就被人遗忘了。不过我必须提醒你：结果的重要性，并不是衡量问题重要性的标准。物理学中的三大问题——反重力、瞬间传送和时间旅行——之所以很少有人研究，是因为我们对如何着手几乎毫无线索。一个问题之所以重要，部分是因为它存在可能的攻克路径，而不只是因为它本身固有的重要性。

There have been a number of times in this book when I came close to the point of saying it is not so much what you do as how you do it. I just told you about the changing of the problem of solving a given set of differential equations on an analog machine to doing it on a digital computer, changing programming from an acre of programmers to letting the machine do much of the mechanical part, and there are many similar stories. Doing the job with "style" is important. As the old song says, "It ain't what you do, it's the way that you do it." Look over what you have done, and recast it in a proper form. I do not mean give it false importance, nor propagandize for it, nor pretend it is not what it is, but I do say that by presenting it in its basic, fundamental form, it may have a larger range of application than was first thought possible.

在这本书里，有好几次我几乎要说出这样一句话：重要的与其说是你做了什么，不如说是你怎么做。我刚刚讲过：把"在模拟机器上求解一组给定微分方程"的问题，改造为"在数字计算机上求解"；把"动用一大片程序员"的编程方式，改造为"让机器去做大部分机械性的工作"——类似的故事还有很多。带着"风格"去做事很重要。正如那首老歌所唱："重要的不是你做什么，而是你做的方式。"回头审视你做过的工作，把它重新铸造成恰当的形式。我并不是说要赋予它虚假的重要性，也不是说要为它做宣传，更不是说要假装它不是其本来的样子；我要说的是：通过把它以其最基本、最根本的形式呈现出来，它的适用范围可能比最初设想的要大得多。

Again, you should do your job in such a fashion that others can build on top of it. Do not in the process try to make yourself indispensable; if you do, then you cannot be promoted, because you will be the only one who can do what you are now doing! I have seen a number of times where this clinging to the exclusive rights to the idea has in the long run done much harm to the individual and to the organization. If you are to get recognition then others must use your results, adopt, adapt, extend, and elaborate them, and in the process give you credit for it. I have long held the attitude of telling everyone freely of my ideas, and in my long career I have had only one important idea "stolen" by another person. I have found people are remarkably honest if you are in your turn.

同样，你做工作的方式，应当让别人能够在它之上继续构建。在这个过程中，不要试图让自己变得不可替代；如果你那样做，你就无法被提拔，因为你将成为唯一能做你现在所做之事的人！我见过好几次，这种死抱着想法独占权不放的做法，长远看来对个人和组织都造成了很大的伤害。如果你想获得认可，就必须让别人使用你的成果——采纳、调整、扩展、加以阐发——并在这个过程中把功劳归于你。长久以来，我一直秉持把自己的想法毫无保留地告诉所有人的态度；在我漫长的职业生涯中，只有一个重要的想法被别人"偷走"过。我发现，只要你自己坦诚，人们也会出奇地诚实。

It is a poor workman who blames his tools. I have always tried to adopt the philosophy that I will do the best I can in the given circumstances, and after it is all over maybe I will try to see to it that things are better next time. This school is not perfect, but for each class I try to do as well as I can and not spend my effort trying to reform every small blemish in the system. I did change Bell Telephone Laboratories significantly, but did not spend much effort on trivial details. I let others do that if they wanted to—but I got on with the main task as I saw it. Do you want to be a reformer of the trivia of your old organization or a creator of the new organization? Pick your choice, but be clear which path you are going down.

拙劣的工匠才怪罪自己的工具。我一向努力奉行这样一种哲学：在给定的环境下尽我所能做到最好，等一切结束之后，也许我会设法让下一次做得更好。这所学校并不完美，但每上一门课，我都尽力做到最好，而不把精力花在试图修补系统里每一处微小的瑕疵上。我确实显著地改变了贝尔电话实验室，但并没有在琐碎的细节上花太多力气。那些事，如果别人想做，就让他们去做——而我自己则继续推进我所认定的主要任务。你想做你那旧机构里琐碎事务的改良者，还是想做新机构的创造者？随你选择，但要清楚自己正在走哪一条路。

I must come to the topic of "selling" new ideas. You must master three things to do this (Chapter 5): 1. Giving formal presentations, 2. Producing written reports, and 3. Mastering the art of informal presentations as they happen to occur. All three are essential—you must learn to sell your ideas, not by propaganda, but by force of clear presentation. I am sorry to have to point this out; many scientists and others think good ideas will win out automatically and need not be carefully presented. They are wrong; many a good idea has had to be rediscovered because it was not well presented the first time, years before!

我必须谈到"推销"新想法这个话题。要做到这一点，你必须掌握三件事（第5 章）：1. 作正式的演讲；2. 撰写书面报告；3. 掌握在偶发场合作非正式陈述的艺术。这三者缺一不可——你必须学会推销自己的想法，不是靠宣传鼓吹，而是靠清晰陈述的力量。我很遗憾不得不指出这一点；许多科学家和其他人都以为好想法会自动胜出、无需精心呈现。他们错了；多少好想法不得不被人重新发现，只因为它第一次提出时——也许在多年以前——没有被好好地呈现出来！

New ideas are automatically resisted by the establishment, and to some extent justly. The organization cannot be in a continual state of ferment and change, but it should respond to significant changes. Change does not mean progress, but progress requires change.

新想法天然会遭到既有体制的抵制，而这在某种程度上也合情合理。一个组织不可能永远处于动荡与变革之中，但它应当对重大的变化作出回应。变化并不等于进步，但进步必然要求变化。

To master the presentation of ideas, while books on the topic may be partly useful, I strongly suggest you adopt the habit of privately critiquing all presentations you attend and also asking the opinions of others. Try to find those parts which you think are effective and which also can be adapted to your style. And this includes the gentle art of telling jokes at times. Certainly a good after-dinner speech requires three well-told jokes: one at the beginning, one in the middle to wake them up again, and the best one at the end so they will remember at least one thing you said!

要精通想法的呈现，虽然相关的书籍也有一定用处，但我强烈建议你养成这样的习惯：私下里点评你所参加的每一场演讲，同时也征询别人的意见。试着找出其中你认为有效、并且也能融入你自身风格的部分。这其中也包括适时讲笑话这门温和的艺术。一场出色的餐后演讲，当然需要三个讲得漂亮的笑话：开场一个，中间一个把大家重新唤醒，最后留一个最妙的，好让他们至少记住你说过的一件事！

You are likely to be saying to yourself you have not the freedom to work on what you believe you should when you want to. I did not either for many years—I had to establish the reputation on my own time that I could do important work, and only then was I given the time to do it. You do not hire a plumber to learn plumbing while trying to fix your trouble; you expect he is already an expert. Similarly, only when you have developed your abilities will you generally get the freedom to practice your expertise, whatever you choose to make it, including the expertise of "universality," as I did.

你很可能正在对自己说：我没有那份自由，在我想做的时候去做我认为自己该做的事。我也曾有很多年没有这份自由——我不得不用自己的业余时间去建立起"我能做出重要工作"的声誉，只有到那时，别人才给了我去做这件事的时间。你雇水管工，不是让他一边学手艺一边修你家的故障；你指望他本就是个行家。同样，只有当你磨炼出了自己的能力，你才通常会获得施展专长的自由——无论你选择把专长发展成什么，包括像我那样发展出"通才性"（universality）的专长。

I have already discussed the gentle art of educating your bosses, so I will not go into it again. It is part of the job of those who are going to rise to the top. Along the way you will generally have superiors who are less able than you are, so do not complain, since how else could it be if you are going to end up at the top and they are not?

我已经讨论过"教育你的上司"这门温和的艺术，就不再赘述了。这是那些将要登顶的人份内之事的一部分。在攀登的途中，你通常会遇到能力不如你的上司，所以不要抱怨——否则，若你终将登顶而他们不会，又怎么可能不是这样呢？

Finally, I must address the topic of whether the effort required for excellence is worth it. I believe it is—the chief gain is in the effort to change yourself, in the struggle with yourself, and it is less in the winning than you might expect. Yes, it is nice to end up where you wanted to be, but the person you are when you get there is far more important. I believe a life in which you do not try to extend yourself regularly is not worth living—but it is up to you to pick the goals you believe are worth striving for. As Socrates (469–399 BC) said, The unexamined life is not worth living.

最后，我必须谈谈这个话题：为追求卓越所付出的努力，到底值不值得。我相信值得——最主要的收获在于改变自己的努力之中、在于与自己的搏斗之中，而真正在于"取胜"的部分，比你预想的要少。是的，最终抵达你想去的地方固然美好，但当你抵达时你成为了怎样的人，远比这重要得多。我相信，一个不去定期拓展自己的人生，是不值得过的——但选择哪些目标值得为之奋斗，取决于你自己。正如苏格拉底（公元前469–399 年）所说：未经省察的人生不值得过。

In summary: as I claimed at the start, the essence of the book is "style," and there is no real content in the form of the topics like coding theory, filter theory, or simulation that were used for examples. I repeat: the content of these chapters is "style" of thinking, which I have tried to exhibit in many forms. It is your problem to pick out those parts you can adapt to your life as you plan it to be. A plan for the future, I believe, is essential for success, otherwise you will drift like the drunken sailor through life and accomplish much less than you could otherwise have done.

总结一下：正如我在开头所宣称的，这本书的精髓是"风格"，而像编码理论、滤波理论或仿真这些被用作例子的主题本身，并不构成真正的内容。我再说一遍：这些章节的内容，是思考的"风格"，我已尝试以多种形式将它展现出来。挑出其中你能用于自己人生规划的那些部分，是你自己的课题。我相信，对未来的规划是成功的必要条件；否则你就会像那个醉汉水手一样，在人生中随波逐流，所成就的远少于你本可以成就的。

In a sense, this has been a course a revivalist preacher might have given—repent your idle ways, and in the future strive for greatness as you see it. I claim it is generally easier to succeed than it at first seems! It seems to me at almost all times there is a halo of opportunities about everyone from which to select. It is your life you have to live, and I am only one of many possible guides you have for selecting and creating the style of the one life you have to live. Most of the things I have been saying were not said to me; I had to discover them for myself. I have now told you in some detail how to succeed, hence you have no excuse for not doing better than I did. Good luck!

从某种意义上说，这堂课更像一位福音派传道人会讲的布道——忏悔你那懒散的过往，从此按你自己所理解的方式去追求伟大。我断言：成功通常比它乍看上去要容易！在我看来，几乎在任何时候，每个人身边都环绕着一圈机会的光晕，供你从中挑选。这是你必须去过的人生，而我只是你众多可能的向导之一，帮助你去选择、去创造你这仅有一次人生的风格。我所讲的大部分东西，并没有人讲给我听；我必须自己去发现它们。如今我已相当详细地告诉你该如何成功，因此你没有理由做得不如我。祝你好运！

[END /结束]

人物传记/ Biography

Richard W. Hamming（理查德·W·汉明）· 1915 年2 月11 日– 1998 年1 月7 日

Richard Hamming was born in Chicago, Illinois, USA on February 11, 1915, the son of Richard J. Hamming and Mabel G. Redfield. He was brought up in Chicago where he attended school and realized that he was a more able mathematician than his teacher. He wanted to study engineering but the only offer of a scholarship came from the University of Chicago, which had no engineering department. He entered the University of Chicago receiving his B.S. in mathematics.

理查德·汉明于1915 年2 月11 日生于美国伊利诺伊州芝加哥，是理查德·J·汉明与梅布尔·G·雷德菲尔德之子。他在芝加哥长大、上学，并意识到自己是个比老师更出色的数学家。他本想学工程，但唯一一份奖学金邀约来自芝加哥大学，而该校并没有工程系。于是他进入芝加哥大学，获得了数学学士学位。

After his undergraduate studies he went to the University of Nebraska, where he was awarded an M.A. in 1939. He received a Ph.D. in mathematics in 1942 from the University of Illinois at Urbana-Champaign. His doctoral dissertation, Some Problems in the Boundary Value Theory of Linear Differential Equations, was supervised by Waldemar Trjitzinsky (1901-1973). Hamming, however, developed interests in ideas that were quite far removed from his study of differential equations when he discovered George Boole's An Investigation of the Laws of Thought. He found Boole's book interesting, relevant, and believable. The ideas in it would prove highly significant later in his life when he became interested in coding theory.

本科毕业后，他前往内布拉斯加大学，于1939 年获得文学硕士学位。1942 年，他在伊利诺伊大学厄巴纳—香槟分校获得数学博士学位。他的博士论文《线性微分方程边值理论中的若干问题》由瓦尔德马·特尔吉钦斯基（1901–1973）指导。然而，当汉明读到乔治·布尔的《思维规律的研究》时，他的兴趣转向了与微分方程研究相去甚远的思想。他觉得布尔这本书有趣、切题、可信。书中的思想，在他日后对编码理论产生兴趣时，被证明极其重要。

After earning his doctorate, Hamming married Wanda Little on September 5, 1942. He taught first at the University of Illinois, and then at the J.B. Speed Scientific School of the University of Louisville. In 1945, encouraged by a friend, he joined the Manhattan Project, a U.S. government research project to produce an atomic bomb at Los Alamos, New Mexico. A month after he arrived at Los Alamos he was joined by his wife, who was also employed on the Manhattan Project. Hamming was put in charge of the IBM calculating machines that played a vital role in the project. He came in contact with many leading scientists, including Richard Feynman, Enrico Fermi, Edward Teller and J. Robert Oppenheimer. The theoretical physicist Hans Bethe was his boss. Wanda Hamming began by doing computations with desk calculators, and later worked for Enrico Fermi and Edward Teller.

取得博士学位后，汉明于1942 年9 月5 日与万达·利特尔结婚。他先在伊利诺伊大学任教，随后到路易斯维尔大学的J.B. 斯皮德理工学院执教。1945 年，在一位朋友的鼓励下，他加入了曼哈顿计划——美国政府在新墨西哥州洛斯阿拉莫斯研制原子弹的研究项目。他抵达洛斯阿拉莫斯一个月后，同样受雇于曼哈顿计划的妻子也来与他会合。汉明负责管理在该项目中发挥关键作用的IBM 计算机器。他得以接触许多顶尖科学家，包括理查德·费曼、恩里科·费米、爱德华·泰勒和J. 罗伯特·奥本海默。理论物理学家汉斯·贝特是他的上司。万达·汉明起初用台式计算器做计算，后来为费米和泰勒工作。

After the Manhattan Project ended Hamming remained at Los Alamos for six months, writing up details of the calculations they had done. He felt that it was important to try to understand exactly what had been achieved, and why it had been so successful. It was at this time that he realized that he had done the right thing by not studying engineering; engineers did much of the routine work, but mathematicians like himself were more critical to the cutting edge innovations. He formed a view of mathematics, arising from his Los Alamos experience, that computation was of major importance, but it made him skeptical of the standard approach that emphasized formal abstract mathematical theories.

曼哈顿计划结束后，汉明又在洛斯阿拉莫斯留了六个月，整理他们所做计算的细节。他觉得，努力弄清楚究竟取得了什么成果、以及它为何如此成功，是很重要的。正是在这段时间，他意识到当年没去学工程是做对了：工程师承担了大量例行性工作，而像他这样的数学家，对前沿创新更为关键。源于洛斯阿拉莫斯的经历，他形成了一种数学观——计算具有重大意义；但这也使他对那种强调形式化、抽象数学理论的标准路径心存怀疑。

In 1946 he accepted a position in the mathematics department at the Bell Telephone Laboratories in New Jersey. However, he didn't entirely break his link with Los Alamos Scientific Laboratories, and made two week visits each summer as a consultant. At Bell Labs he was able to work with both Claude Shannon, with whom he shared an office, and John Tukey. Some other young mathematicians had joined the Mathematical Research Department at Bell Labs just prior to Hamming. These included Donald Percy Ling and Brockway McMillan, who had been at Los Alamos at the same time as Hamming. Shannon, Ling, McMillan and Hamming called themselves the Young Turks.

1946年，他接受了新泽西州贝尔电话实验室数学部的一个职位。不过，他并未完全切断与洛斯阿拉莫斯科学实验室的联系，每年夏天都以顾问身份去做两周的访问。在贝尔实验室，他得以同时与和他共用办公室的克劳德·香农，以及约翰·图基共事。在汉明之前不久，还有几位年轻数学家加入了贝尔实验室数学研究部，其中包括与汉明同期在洛斯阿拉莫斯工作过的唐纳德·珀西·林和布罗克韦·麦克米伦。香农、林、麦克米伦和汉明自称"青年土耳其党人"（Young Turks）。

Hamming often related how they had all been affected by growing up in the depression, and all learned new skills with their war work. It led them, he said, to do unconventional things in unconventional ways. Hamming, for example, lunched with the physics group rather than his mathematics group, and they were fascinated by his unorthodox ideas and views. Not all his colleagues were happy to tolerate his unconventional ways. Some have described him as egotistical, saying he sometimes went off "half-cocked, after some half-baked idea." Unconventional ideas sometimes produce flashes of brilliance, but they sometimes also lead to failures.

汉明常讲起，他们都受到在大萧条中成长这段经历的影响，又都在战时工作中学会了新技能。他说，这使他们倾向于用非常规的方式去做非常规的事。比如，汉明不和自己的数学组而是和物理组共进午餐，而物理学家们对他那些离经叛道的想法和见解着迷不已。并非所有同事都乐于容忍他这种不合常规的作风。有人形容他自负，说他有时会"准备不足就贸然行动，追逐某个不成熟的念头"。非常规的想法有时会迸发出天才的火花，但有时也会导向失败。

Before discussing Hamming's highly significant work on error-correcting codes, we first note the many and varied problems he worked on in Bell Labs. These include problems involving design of telephone systems, traveling wave tubes, the equalization of television transmission lines, the stability of complex communication systems, and the blocking of calls through a telephone central office. He continued to work for Bell Telephones until 1976, although he became increasingly interested in teaching, and held visiting or adjunct professorships at Stanford University, the City College of New York, the University of California at Irvine and Princeton University between 1960 and 1976. After retiring from Bell Labs in 1976, he became a professor of computer science at the Naval Postgraduate School at Monterey, California. At this point he gave up his research career and concentrated on teaching and writing books.

在讨论汉明在纠错码方面意义重大的工作之前，我们先看看他在贝尔实验室所研究过的众多而多样的问题。这些问题涉及电话系统的设计、行波管、电视传输线路的均衡、复杂通信系统的稳定性，以及电话中心局呼叫的阻塞。他一直为贝尔电话工作到1976年，尽管他对教学的兴趣与日俱增，并在1960 至1976 年间于斯坦福大学、纽约市立学院、加州大学欧文分校和普林斯顿大学担任客座或兼职教授。1976 年从贝尔实验室退休后，他成为加州蒙特雷海军研究生院的计算机科学教授。从这时起，他放下了研究生涯，专注于教学和著书。

He believed that the way mathematics was being taught was wrong, and that the only way to change it was to write textbooks with a new approach. Here are two examples of his views on mathematics teaching: "We live in an age of exponential growth in knowledge, and it is increasingly futile to teach only polished theorems and proofs. We must abandon the guided tour through the art gallery of mathematics, and instead teach how to create the mathematics we need. In my opinion, there is no long-term practical alternative." and "The way mathematics is currently taught it is exceedingly dull. In the calculus book we are currently using on my campus, I found no single problem whose answer I felt the student would care about! The problems in the text have the dignity of solving a crossword puzzle—hard to be sure, but the result is of no significance in life."

他认为当时数学的教授方式是错误的，而改变它的唯一办法，就是用全新的思路去编写教科书。以下是他关于数学教学的两段观点："我们生活在知识呈指数级增长的时代，只教那些打磨光滑的定理和证明，越来越是徒劳。我们必须放弃在数学艺术馆里的'导览式游览'，转而去教如何创造出我们所需要的数学。在我看来，从长远看别无切实可行的选择。"以及"如今数学的教法极其枯燥。在我们校园目前使用的微积分课本里，我找不到任何一道题，其答案是我觉得学生会真正在意的！课本里的题目，其'尊严'不过相当于解一道填字游戏——难度确有，但结果对人生毫无意义。"

His attempt to move to a new way of teaching calculus is exhibited in his 1985 book Methods of Mathematics Applied to Calculus, Probability, and Statistics. He said that the book is "very different from the standard texts and its success or failure will tell us something about the prospects for change and innovation." Other texts he wrote all attempted to change conventional approaches to the areas they studied.

他在1985 年的著作《应用于微积分、概率与统计的数学方法》中，展现了他改用全新方式教授微积分的尝试。他说，这本书"与标准教材大不相同，它的成败将告诉我们一些关于变革与创新前景的东西"。他所写的其他教材，也都试图改变各自研究领域的传统路径。

Richard Hamming is best known for his work at Bell Labs on error-detecting and error-correcting codes. His fundamental paper on this topic, "Error Detecting and Error Correcting Codes", appeared in April 1950 in the Bell System Technical Journal. This paper created an entirely new field within information theory. Hamming codes, Hamming distance and Hamming metric, standard terms used today in coding theory and other areas of mathematics, all originated in this classic paper and are of ongoing practical use in computer design.

理查德·汉明最为人所知的，是他在贝尔实验室关于检错码与纠错码的工作。他在这一主题上的奠基性论文《检错码与纠错码》于1950 年4 月发表在《贝尔系统技术期刊》上。这篇论文在信息论中开创了一个全新的领域。汉明码、汉明距离和汉明度量——如今编码理论及数学其他领域中的标准术语——全都源自这篇经典论文，并在计算机设计中持续发挥着实用价值。

In 1956 Hamming worked on the IBM 650, an early vacuum tube, drum memory, computer. His work led to the development of a rudimentary programming language. Hamming also worked on numerical analysis, especially integration of differential equations. The Hamming spectral window, still widely used in computation, is a special type of digital filter designed to pass certain frequencies and discriminate against closely related frequencies.

1956年，汉明在IBM 650 上工作——那是一台早期的、采用真空管和磁鼓存储器的计算机。他的工作促成了一种初级编程语言的开发。汉明也从事数值分析研究，尤其是微分方程的积分。至今仍在计算中广泛使用的"汉明窗"（Hamming spectral window），是一种特殊的数字滤波器，用于让某些频率通过、并抑制与之相近的频率。

In addition to the Turing Award, Hamming received many awards for his pioneering work. He was made a fellow of the Association for Computing Machinery in 1994. The Institute of Electrical and Electronics Engineers (IEEE) awarded him the Emanuel R Piore Award in 1979. The IEEE created "The Richard W. Hamming Medal" in his honor. He was the first recipient of this $10,000 prize medal in 1988. He was elected a member of the National Academy of Engineering in 1980, and received the Harold Pender Award from the University of Pennsylvania in 1981. In 1996, in Munich, Hamming received the prestigious $130,000 Eduard Rhein Award for Achievement in Technology for his work on error correcting codes.

除图灵奖外，汉明还因其开创性的工作获得了许多奖项。1994年，他当选为美国计算机协会（ACM）会士。1979 年，电气电子工程师学会（IEEE）授予他伊曼纽尔·R·皮奥雷奖。IEEE 还设立了"理查德·W·汉明奖章"以表彰他。1988 年，他成为这枚一万美元奖章的首位得主。1980 年，他当选美国国家工程院院士；1981 年获宾夕法尼亚大学颁发的哈罗德·彭德奖。1996 年，汉明在慕尼黑因其在纠错码方面的工作，荣获价值十三万美元、享有盛誉的爱德华·莱茵技术成就奖。

In 1997 Hamming retired from teaching at the Naval Postgraduate School and was made Distinguished Professor Emeritus. Shortly before he retired, he said that when he left Bell Labs, he knew that that was the end of his research career. It really would be the end, he said, when he retired from teaching. Indeed he was right, for having taught up to December 1997, he died of a heart attack in the following month. Richard Franke of the Naval Postgraduate School at Monterey wrote of Richard Hamming: "He will be long remembered for his keen insights into many facets of science and computation. I'll also long remember him for his red plaid sport coat and his bad jokes."

1997年，汉明从海军研究生院的教学岗位退休，并被授予杰出荣休教授称号。在退休前不久，他说：当他离开贝尔实验室时，他就知道那是自己研究生涯的终点。他说，等他从教学岗位退下来，那才真正是终点。他果然说对了：在一直教到1997 年12 月之后，次月他便因心脏病去世。蒙特雷海军研究生院的理查德·弗兰克这样写道："他将因对科学与计算诸多层面的敏锐洞见而被长久铭记。我也会长久记得他那件红格子运动外套，和他那些蹩脚的笑话。"