你和你的研究
理查德 · 卫斯理 · 汉明（Richard Wesley Hamming）[1]是美国数学家，图灵奖得主，其贡献包括汉明码、汉明距离和汉明谱窗以及数值方法。他曾做过一场演讲《You and your research》[2]，这篇文章算是浓缩版，其中关于人生和做研究的建议，看完惭愧不已却又大受鼓舞。简单总结的话——等等，为什么要简单总结呢，这么好的文章值得花上半小时慢慢品味！
原文、翻译（DeepL + 个人校对）和一些批注如下。
A stroke of genius: striving for greatness in all you do
天才之举：在你所做的一切中争取伟大
Little has been written on managing your own research (and very little on avoiding other people managing your research); however, your research is much more under your control than you may realize.
关于如何管理自己的研究的文章很少（关于避免其他人管理你的研究的文章也很少）；不管怎样，你的研究比你可能意识到的更受你控制。
We are concerned with great research here. Work that will get wide recognition, perhaps even win a Nobel Prize. As most people realize, the average published paper is read by the author, the referee, and perhaps one other person. Classic papers are read by thousands. We are concerned with research that will matter in the long run and become more than a footnote in history.
我们在这里关注的是伟大的研究。有些会获得广泛认可，甚至获得诺贝尔奖。众所周知，论文一般会被作者、评委，或许还有另一个人读到。经典论文则有成千上万人阅读。我们所关心的（应该）是那些长远来看将起到重要作用的，而不仅仅是历史上的一个脚注的研究。
想起在哪儿看过的一句话：「有一天我们可能会因此成为一本书的脚注。」
If you are to do important work then you must work on the right problem at the right time and in the right way. Without any one of the three, you may do good work but you will almost certainly miss real greatness.
如果你要做重要的工作，那么你必须在正确的时间，以正确的方式，解决正确的问题。如果没有这三者中的任何一个，你可能会做得很好，但你几乎肯定会错过真正的伟大。
Greatness is a matter of style. For example, after learning the elements of painting, you study under a master. While studying you pay attention to what the master says in discussing your work, but you know that if you are to achieve greatness then you must find your own style. Furthermore, a successful style in one age is not necessarily appropriate for another age. Cubism would not have gone over big during the realism period.
伟大是一种风格。例如，在学习了绘画的要素之后，你在大师手下学习。学习时，你会留意大师在讨论你的作品时所说的话，但是你知道，如果你想成就伟大，那么你必须找到自己的风格。此外，一个时代的成功风格并不一定适合另一个时代。在现实主义时期，立体主义不会走得太远。
就时尚风格而言，中世纪欧洲贵族男士的装扮风格（高跟鞋、丝袜、假发）放在今天会被当成神经病。而卡尔 · 拉格斐说，风格就是从打破常规、击碎已被接受的现实开始。
Similarly, there is no simple formula for doing great science or engineering, I can only talk around the topic. The topic is important because, so far as we have any solid evidence, you have but one life to live. Under these circumstances it seems better to live a life in which you do important things (important in your eyes, of course) than to merely live out your life. No sense frittering away your life on things that will not even appear in the footnotes.
同样，做伟大的科学或工程也没有简单的公式，我只能围绕这个话题来谈。这个话题很重要，因为，到目前为止，我们所知道的是，人只有一次生命。在这种情况下，过一种做重要事情的生活（当然是在你看来很重要的）似乎比仅仅过你自己的生活要好。没有必要把生命浪费在那些甚至不会出现在脚注中的东西上。
图源：notion.so
choosing the problem
选择问题
I begin with the choice of problem. Most scientists spend almost all of their time working on problems that even they admit are neither great or are likely to lead to great work; hence, almost surely, they will not do important work. Note that importance of the results of a solution does not make the problem important. In all the 30 years I spent at Bell Telephone Laboratories (before it was broken up) no one to my knowledge worked on time travel, teleportation, or anti-gravity. Why? Because they had no attack on the problem. Thus an important aspect of any problem is that you have a good attack, a good starting place, some reasonable idea of how to begin.
我从问题的选择开始。大多数科学家几乎把所有的时间，都花在研究那些他们自己都承认并不伟大又不可能引向伟大工作的问题上；因此，几乎可以肯定，他们不会做重要的工作。请注意，解决方案结果的重要性并不使问题变得重要。我在贝尔电话实验室的 30 年里（在它被拆分之前） ，据我所知，没有人从事过时间旅行、心灵传输或反重力方面的工作。为什么？因为他们没有着手攻克那些问题。因此，任何问题的一个重要方面是你有一个好的攻克，一个好的起点，一些关于如何开始的合理想法。
用「攻克」始终少了些味道。
To illustrate, consider my experience at BTL. For the first few years, I ate lunch with the mathematicians. I soon found that they were more interested in fun and games than in serious work, so I shifted to eating with the physics table. There I stayed for a number of years until the Nobel Prize, promotions, and offers from other companies, removed most of the interesting people. So I shifted to the corresponding chemistry table where I had a friend.
拿我在 BTL 的经历来说。最初几年里，我都是和数学家们共进午餐的。我很快发现，比起正经工作，他们对娱乐和游戏的兴趣更大，于是我转去和物理学家们用餐。在诺贝尔奖、晋升机会和其他公司的 offer 把大多数有趣的人都带走之前，我在那里呆了好几年。于是，我又转去和化学家们一起用餐，那里我有一个朋友。
At first I asked what were the important problems in chemistry, then what important problems they were working on, or problems that might lead to important results. One day I asked, "if what they were working on was not important, and was not likely to lead to important things, they why were they working on them?" After that I had to eat with the engineers!
起初，我问他们化学中最重要的问题是什么，然后他们正在研究什么重要的或者可能带来重要结果的问题。有一天我问，「如果他们正在做的事情不重要，也不太可能引向重要的事情，他们为什么要做这些事情呢？」之后我不得不和工程师们一起吃饭！
早年读过《别独自用餐》一书，大意是说你应该多和同事们用餐以促进、维持关系。年纪越长，越发觉得这个观点很对，但我加上了一个条件——只要他们是有趣的人。后来，我越来越独自用餐，但也更为舒畅，至少少了一大堆尬聊时刻吧。独处和思考也很重要！
About four months later, my friend stopped me in the hall and remarked that my question had bothered him. He had spent the summer thinking about the important problems in his area, and while had had not changed his research he thought it was well worth the effort. I thanked him and kept walking. A few weeks later I noticed that he was made head of the department. Many years later he became a member of the National Academy of Engineering. The one person who could hear the question went on to do important things and all the others -- so far as I know -- did not do anything worth public attention.
大约四个月后，我的朋友在大厅里拦住我，说我的问题困扰着他。他整个夏天都在思考他所在领域的重要问题，尽管他没有改变他的研究（他认为值得努力）。我向他道谢，然后继续往前走。几个星期后，我注意到他被任命为系主任。许多年后，他成为了国家工程学院的一员。能听进去这个问题的人继续做着重要的事，而其他人，据我所知，却没做什么值得一提的事。
There are many right problems, but very few people search carefully for them. Rather they simply drift along doing what comes to them, following the easiest path to tomorrow. Great scientists all spend a lot of time and effort in examining the important problems in their field. Many have a list of 10 to 20 problems that might be important if they had a decent attack. As a result, when they notice something new that they had not known but seems to be relevant, then they are prepared to turn to the corresponding problem, work on it, and get there first.
世上有许多正确的问题，但很少有人仔细地寻找它们。相反，他们只是随波逐流，沿着最简单的道路过日子。伟大的科学家都会花费大量的时间和精力来研究他们所在领域的重要问题。有些人会有一个列着 10 到 20 个 问题的清单，如果他们正经攻克，这些问题可能是重要的。因此，当他们注意到一些他们以前不知道但似乎相关的新问题时，那么他们就会准备转向相应的问题，努力解决，并首先完成。
Some people work with their doors open in clear view of those who pass by, while others carefully protect themselves from interruptions. Those with the door open get less work done each day, but those with their door closed tend not know what to work on, nor are they apt to hear the clues to the missing piece to one of their "list" problems. I cannot prove that the open door produces the open mind, or the other way around. I only can observe the correlation. I suspect that each reinforces the other, that an open door will more likely lead you and important problems than will a closed door.
有些人工作时门是敞开着的，可以清楚地看到路过的人，而另一些人则小心翼翼地保护自己不受干扰。那些开着门的人每天完成的工作更少，但那些关着门的人往往不知道该做什么，他们也不倾向于听到他们的「清单」中的问题所缺失的那一部分的线索。我无法证明敞开的大门能产生开放的思想，或者反过来。我只能观察到相关性。我怀疑这两者相辅相成，一扇敞开的门比一扇关闭的门更有可能引导你解决重要的问题。
Hard work is a trait that most great scientists have. Edison said that genius was 99% perspiration and 1% inspiration. Newton said that if others would work as hard as he did then they would get similar results. Hard work is necessary but it is not sufficient. Most people do not work as hard as they easily could. However, many who do work hard -- work on the wrong problem, at the wrong time, in the wrong way, and have very little to show for it.
努力工作是大多数伟大科学家的特征。爱迪生说，天才是 99% 的汗水和 1% 的灵感。牛顿说，如果其他人也像他一样努力工作，那么他们也会得到类似的结果。努力工作是必要的，但还不够。大多数人不会像他们容易做到的那样努力工作。然而，许多努力工作的人——在错误的时间，以错误的方式，解决错误的问题，因此没有什么成果。
You are aware that frequently more than one person starts working on the same problem at about the same time. In biology, both Darwin and Wallace had the idea of evolution at about the same time. In the area of special relativity, many people besides Einstein were working on it, including Poincare. However, Einstein worked on the idea in the right way.
你知道，通常不止一个人在大约同一时间着手处理同一个问题。在生物学领域，达尔文和华莱士几乎在同一时间产生了进化论的想法。在狭义相对论地区，除了爱因斯坦，还有很多人在研究这个问题，包括庞加莱。然而，爱因斯坦以正确的方式实现了这个想法。
The first person to produce definitive results generally gets all the credit. Those who come in second are soon forgotten. Thus working on the problem at the right time is essential. Einstein tried to find a unified theory, spent most of his later life on it, and died in a hospital still working on it with no significant results. Apparently, he attacked the problem too early, or perhaps it was the wrong problem.
通常，第一个拿出明确结论的人会得到所有的赞誉，次之者则很快被遗忘。因此，正确的时间至关重要。爱因斯坦试图找到一个统一的理论，他晚年的大部分时间都在研究这个理论，最后在一家医院去世前仍没停下却也没有取得重大成果。显然，他过早攻克这个问题，或者也许那就是个错误的问题。
There are a pair of errors that are often made when working on what you think is the right problem at the right time. One is to give up too soon, and the other is to persist and never get any results. The second is quite common. Obviously, if you start on a wrong problem and refuse to give up, you are automatically condemned to waste the rest of your life (see Einstein above). Knowing when you persist is not easy -- if you are wrong then you are stubborn; but if you turn out to be right, then you are strong-willed.
当你在正确的时间处理你认为正确的问题时，经常会出现一对错误。一种是过早放弃，另一种是坚持到底却没有任何结果。第二种是相当普遍的。很明显，如果你从一个错误的问题开始并且拒绝放弃，你注定要浪费余生（正如前面提到的爱因斯坦）。知道何时坚持并不容易——如果你是错的，你就是固执；但如果你是对的，你就是意志坚强。
I now turn to the major excuse given for not working on important problems. People are always claiming that success is a matter of luck, but as Pasteur pointed out, "Luck favors the prepared mind."
我现在要谈谈那些不解决重要问题的主要借口。人们总是声称成功是运气的问题，但正如巴斯德所言，「运气偏爱有准备的头脑。」
A great deal of direct experience, vicarious experience through questioning others, and reading extensively, convinces me of the truth of his statement. Outstanding successes are too often done by the same people for it be a matter of random chance.
基于大量的直接经验、通过质疑他人所得的间接经验和广泛的阅读，我确信他说的对。杰出的成功往往是由同一个人完成的，这不是一个随机的运气问题。
For example, when I first met Feynman at Los Alamos during the WWII, I believed that he would get a Nobel Prize. His energy, his style, his abilities, all indicated that he was a person who would do many things, and probably at least one would be important. Einstein, around the age of 12 or 14, asked himself what a light wave would look like if he wants at the speed of light. He knew that Maxwell's theory did not support a local, stationary maximum, but was what he ought to see if the current theory was correct. So it is not surprising that he later developed the special theory of relativity - he had prepared his mind for it long before.
例如，在二战期间，当我在洛斯阿拉莫斯第一次见到费曼时，我相信他将获得诺贝尔奖。他的精力，他的风格，他的能力，都表明他是一个会做很多事情的人，而且可能至少有一件是重要的。爱因斯坦，大约在 12 或 14 岁的时候，问自己如果以光速想光波会是什么样子。他知道麦克斯韦的理论并不支持一个局部的、静止的最大值，因为如果当前理论是正确的，他就会看到应该有的样子。因此，他后来提出了狭义相对论也就不足为奇了——他在很早以前就已经做好了思想准备。
耳边响起费曼先生的话：「I have to understand the world, you see.」
Many times a discussion with a person who has just done something important will produce a description of how they were led, almost step by step, to the result. It is usually based on things they had done, or intensely thought about, years ago. You succeed because you have prepared yourself with the necessary background long ago, without, of course, knowing then that it would prove to be a necessary step to success.
很多时候，与一个刚刚做了重要事情的人讨论就能知道她/他是如何一步一步地走向成果的：通常是基于他们多年前所做的事情，或者他们认真思考过的事情。你成功了，是因为你很久以前就开始铺路，当然，你并不知道那是通往成功的必经之路。
图源：ACM.org
Personal traits
个人特征
These traits are not all essential, but tend to be present in most doers of great things in science. First, successful people exhibit more activity, more energy, than most people do. They look more places, they work harder, they think longer than less successful people. Knowledge and ability are much like compound interest -- the more you do the more you can do, and the more the opportunities are open for you. Thus, among other things, it was Feynman's energy and his constantly trying new things that made one think he would succeed.
这些特质并非都是必要的，但往往存在于大多数科学上伟大事业的实干家身上。首先，成功人士比大多数人表现出更多的活力和精力。他们看得更广，他们工作更努力，他们思考的时间比那些不那么成功的人要长。知识和能力就像复利——你做的越多，你能做的就越多，机会也就越多。因此，除了其他事情之外，费曼的精力和他不断尝试的新事物让人相信他会成功。
This trait must be coupled with emotional commitment. Perhaps the ablest mathematician I have watched up close seldom, if ever, seemed to care deeply about the problem he was working on. He has done great deal of first-class work, but not of the highest quality. Deep emotional commitment seems to be necessary for success. The reason is obvious. The emotional commitment keeps you thinking about the problem morning, noon and night, and that tends to beat out mere ability.
这种特质必须与情感承诺结合起来。似乎，我近距离观察过的最有能力的数学家（如果有的话），很少非常关心他正在研究的问题。他做了大量一流的工作，但不是最高质量的。深刻的情感投入似乎是成功的必要条件。原因很明显。情感上的投入使你从早到晚都在思考这个问题，而这往往会胜过单纯的解题能力。
While I was at Los Alamos after the war, I got to thinking about the famous Buffon needle problem where you can calculate the probability of a needle tossed at random of crossing one of a series of equally spaced parallel lines. I asked myself if it was essential that the needle be a straight line segment (if I counted multiple crossing)? No. Need the parallel lines be straight? No. Need they be equally spaced or is it only the average density of the lines on the plane? Is it surprising that some years later at Bell Labs when I was asked by some metallurgists how to measure the amount of grain boundary on some microphotographs I simply said, "Count the crossings of a random line of fixed length on the picture?" I was led to it by the previous, careful thought about an interesting, and I thought important, result in probability. The result is not great, but illustrates the mechanisms of preparation and emotional involvement.
战后我在洛斯阿拉莫斯的时候，我开始思考著名的布冯针问题（计算随机抛出的针穿过一系列等距平行线之一的概率）。我问自己，针是否必须是一条直线段（如果我计算多次穿越）？不是。平行线必须是直线吗？不。它们是否必须是等距的，或者只是平面上的线的平均密度？几年后在贝尔实验室，当一些冶金学家问我如何测量一些微观照片上的晶界数量时，我只是说：「计算图片上一条固定长度的随机线的交叉点」，这是否令人惊讶？我是被之前对概率学中一个有趣的、我认为很重要的结果的仔细思考所引导的。结果不是很好，但说明了准备和情感参与的机制。
The above story also illustrates what I call the "extra mile." I did more than the minimum, I looked deeper into the nature of the problem. This constant effort to understand more than the surface feature of a situation obviously prepares you to see new and slightly different applications of your knowledge. You cannot do many problems such as the above needle problem before you stumble on an important application.
上面的故事也印证了我称之为「额外 1 英里」的东西。我做比最低限度更多的事情，我更深入研究问题的本质。这种不断了解表征之外的努力，显然让你更有所准备——将你的知识应用于新的和稍微不同的领域。在你偶然发现一个重要的应用之前，你无法研究很多像上面的针头问题那样的问题。
Courage is another attribute of those who do great things. Shannon is a good example. For some time he would come to work at about 10:00 am, play chess until about 2:00 pm and go home.
勇气是那些做伟大事情的人的另一个特质。香农就是一个很好的例子。有一段时间，他会在上午 10 点左右来上班，下棋下到下午 2 点左右，然后回家。
The important point is how he played chess. When attacked he seldom, if ever, defended his position, rather he attacked back. Such a method of playing soon produces a very interrelated board. He would then pause a bit, think and advance his queen saying, "I ain't afraid of nothin'." It took me a while to realize that of course that is why he was able to prove the existence of good coding methods. Who but Shannon would think to average overall random codes and expect to find that the average was close to ideal? I learned from him to say the same to myself when stuck, and on some occasions his approach enabled me to get significant results.
重点是他下棋的方式。被攻击时，他很少防御（如果有的话），而是反击。这样一种玩法很快就产生了一个非常相关的棋局。然后他会停顿一下，思考一下，推进他的女王说，「我什么都不怕。」我花了一段时间才意识到，这就是为什么自然是他才能够证明好的编码方法的存在。除了香农，还有谁会想到对所有随机编码平均化，然后期望发现平均值接近理想值？我从他那里学会了在遇到困难时对自己说同样的话，有时候，使我得到了重要的结果。
Without courage you are unlikely to attack important problems with any persistence, and hence not likely to do important things. Courage brings self-confidence, an essential feature of doing difficult things. However, it can border on over-confidence at time which is more of a hindrance than a help.
没有勇气，你就不可能坚持不懈地解决重要问题，也就不可能完成重要的事。勇气带来自信，而自信是完成困难事情的基础要素。然而，它也可能导致过度自信，那可是一个障碍而不是一个帮助。
There is another trait that took me many years to notice, and that is the ability to tolerate ambiguity. Most people want to believe what they learn is the truth: there are a few people who doubt everything. If you believe too much then you are not likely to find the essentially new view that transforms a field, and if you doubt too much you will not be able to do much at all. It is a fine balance between believing what you learn and at the same time doubting things. Great steps forward usually involve a change of viewpoint to outside the standard ones in the field.
还有一个我花了很多年才注意到的特质——容忍模棱两可的能力。大多数人愿意相信他们所学到的是真理，只有少数人怀疑一切。如果你轻易相信，就很难找到改变一个领域的本质上的新观点，如果过度怀疑，你什么都做不了。在相信和怀疑之间需要一个很好的平衡。伟大的进步通常涉及到对该领域的标准观点之外的改变。
While you are learning things you need to think about them and examine them from many sides. By connecting them in many ways with what you already know.... you can later retrieve them in unusual situations. It took me a long time to realize that each time I learned something I should put "hooks" on it. This is another face of the extra effort, the studying more deeply, the going the extra mile, that seems to be characteristic of great scientists.
当你学习的时候，你需要从多个角度去思考和审视它们。通过多种方式将他们与你已经知道的联系起来……以后，你就可以在不寻常的情况下回溯它们。我花了很长时间才意识到，每当我学到一些东西，我就应该在上面挂上「钩子」。这是额外努力的另一面，更深入研究，多走一步（上面提到的「额外 1 英里」，这似乎是伟大科学家的特征。
The evidence is overwhelming that steps that transform a field often come from outsiders. In archaeology, carbon dating came from physics. The first airplane was built by the Wright brothers who were bicycle experts.
大量证据表明，一个领域的改变往往来自局外人。考古学的碳年代测定法来自物理学。第一架飞机是由莱特兄弟建造的，而他们是自行车专家。
准确地讲，是能成功飞行的飞机是他们创建的。毕竟，在莱特兄弟之前也有其他人在尝试，只是飞不起来。
Thus, as an expert in your field, you face a difficult problem. There is, apparently, an ocean of kooks with their crazy ideas; however, if there is a great step forward it probably will be made by one of them! If you listen too much to them then you will not get any of your own work done, but if you ignore them then you may miss your great chance. I have no simple answer except do not dismiss the outsider too abruptly as is generally done by in the insiders.
因此，作为你所在领域的专家，你面临着一个困难的问题。显然，这里有大量的怪人，他们有着疯狂的想法；然而，如果有一个伟大的进步，它可能是由他们中的一个人做出的！如果你太听他们的话，那么你将无法完成自己的工作。但如果你忽视他们，那么你可能会错过你的伟大机会。我没有简单的答案，只是不要像局内人，太突然地否定局外人。
"Brains" are nice to have, but often the top graduate students do not contribute as much as some lower rated ones. Brains come in all kinds of flavors. Experimental physicists do not think the same way as theoreticians do. Some experimentalists seem to think with their hands, i.e., playing with equipment lets them think more clearly. It took me a few years to realize that people who did not know a lot of mathematics still could contribute. Just because they could not solve a quadratic equation immediately in their head did not mean I should ignore them. When someone's flavor of brains does not match yours may be more reason for paying attention to them.
拥有「大脑」固然不错，但优秀的研究生往往贡献不如一些排名较低的研究生。大脑不尽相同。实验物理学家和理论家的思维方式不同。一些实验者似乎用手来思考，即玩弄设备可以让他们更清晰思考。我花了几年时间才意识到，那些不太懂数学的人仍然可以做出贡献。仅仅因为他们不能在脑海中立即解开一个一元二次方程，并不意味着我应该忽视他们。当某人的思考方式与你不同时，更应该关注人家。
珍惜那些看起来与你所想格格不入，却让人耳目一新的想法。
Vision
愿景
You need a vision of who you are and where your field is going. A suitable parable is that of the drunken sailor. He staggers one way and then the other with independent, random steps. In n steps he will be, on the average, about 3n steps away from where he started. but if there is a pretty girl in one direction he will get a distance proportional to n. The difference, over a life time of choices, between 3n and n is very large and represents the difference between having no vision and having a vision. The particular vision you have is less important than just having one - there are many paths to success. Therefore, it is wise to have a vision of what you may become, of where you want to go, as well as how to get there. No vision, not much chance of doing great work; with a vision you have a good chance.
你需要一个关于你是谁以及你的领域要去哪里的愿景。一个合适的比喻是醉酒的水手。他以独立的、随机的步子踉踉跄跄地走在路上，然后又走到另一边。但如果在一个方向有一个漂亮的女孩，他将得到与 n 成正比的距离。在一生的选择中，3n 和 n 之间的差异非常大，代表了没有愿景和有愿景之间的差异。你所拥有的特定愿景不如仅仅拥有一个愿景重要—有许多通往成功的道路。因此，对你可能成为什么，对你想去的地方，以及如何到达那里，有一个愿景是明智的。没有愿景，做伟大工作的机会就不多；有了愿景，你就有很大的机会。
Another topic I must discuss is that of age. Historically, the greatest contributions of mathematicians, theoretical physicists, and astrophysicists are done when they are very young. On the other hand, apparently in music composition, politics, and literature, the later works are most valued by society. Other areas seem to fall in between these extremes, and you need to realize that in some areas you had better get going promptly.
我必须讨论的另一个话题是年龄问题。历史上，数学家、理论物理学家和天体物理学家最伟大的贡献都是在他们非常年轻的时候完成的。另一方面，在音乐创作、政治和文学中，后期作品显然是最受社会重视的。其他领域似乎处于这两个极端之间，你需要意识到，在某些领域，你最好迅速行动起来。
People often complain about the working conditions they have to put up with, but it is easily observed that some of the greatest work was done under unfavorable conditions. What most people believe is the best working conditions for them is seldom, if ever, true. In my opinion the Institute for Advanced Study in Princeton has ruined more good people than it has helped. You have only to judge their work before they were appointed and afterwards to come to this conclusion. There are exceptions, to be sure, but on the average the supposed ideal working conditions seem to sterilize people.
人们经常抱怨他们不得不忍受的工作条件，但很容易观察到，一些最伟大的工作是在不利的条件下完成的。大多数人认为对他们来说是最好的工作条件，如果有的话，也很少是真的。在我看来，普林斯顿高级研究所毁掉的人才比它帮助的要多。你只需判断他们在被任命前后的工作就可以得出这个结论。当然，也有例外，但平均而言，所谓的理想工作条件似乎使人「不育」。
Another obvious trait of great people is that they do their work in such a fashion that others can build on top of it. Newton said, "If I had seen farther than others it is because I stood on the shoulders of giants." Too many people seem to not want others to build on top of their work but rather they want to hoard it to themselves. Don't do things in such a fashion that next time it must be repeated by you, or by others, but rather in a fashion that represents a significant step forward.
伟大人物的另一个显而易见的特点是，他们以一种别人可以在其之上建立起来的方式，来完成他们的工作。牛顿说：「如果我比别人看得更远，那是因为我站在巨人的肩膀上。」太多的人似乎不希望别人建立在他们的工作之上，而是想把它囤积在自己身上。不要以这样的方式做事情，以至于下次必须由你或其他人重复，而是要以一种代表重大进步的方式。
开源的思想。
Selling
推销
I must now take up the unpleasant topic of selling your ideas. Too many scientists think that this is beneath them, that the world is waiting for their great results. In truth, the other researchers are busy with their own work. You must present your results so that they will stop their own work and listen to you. Presentation comes in three forms: published papers, prepared talks, and impromptu situations. You must master all three forms.
我现在必须开始讨论令人不快的话题——推销你的想法。太多的科学家认为这有失身份，认为世界正在等待他们的伟大成果。事实上，其他研究人员正忙于他们自己的工作。你必须展示你的成果，这样他们才会停下来听你讲。演讲有三种形式：发表论文、准备演讲和即兴情景。你必须掌握这三种形式。
Lots of good work has been lost because of poor presentation only to be rediscovered later by others. There is a real danger that you will not get credit for what you have done. I know of all too many times when the discoverer could not be bothered to present things clearly, and hence his or her work was of no importance to society.
很多好的研究都因为演示不到位而消失，后来才被别人重新发现。有一种真正的危险是，你所做的一切都不会得到认可。我知道有很多时候，发现者懒得把事情说清楚，导致他或她的工作对社会毫无意义。
Finally, I must at least address the question of whether greatness is worth the large effort it requires. Those who have done really great things generally report, privately, that it is better than wine, the opposite sex, and song put together. The realization that you have done it is overwhelming.
最后，我必须至少谈谈伟大是否值得付出巨大努力的问题。那些做过真正伟大事情的人一般都会私下报告说，那可比葡萄酒、异性和歌曲加起来还要好。意识到自己已经做到了，就会让人无法自拔。
Of course I have consulted only those who did do great things, and have no dared to ask those who did not. Perhaps they would reply differently. But, as is often said, it is in the struggle and not the success that the real gain appears. In striving to do great things, you change yourself into a better person, so they claim. The actual success is of less importance, so they say. And I tend to believe this theory.
当然，我只咨询了那些确实做了大事的人，没敢问那些没有做大事的人。也许他们会有不同的回答。但是，正如人们常说的，真正的收获是在奋斗中，而不是在成功中出现。在努力做伟大的事情时，你会把自己变成一个更好的人，他们是这么说的。实际的成功并不那么重要，他们是这么说的。而我倾向于相信这个理论。
No one ever told me the kinds of things I have just related to you; I had to find them out for myself. Since I have now told you how to succeed, you have no excuse for not trying and doing great work in your chosen field.
我刚刚告诉你的那些事情，从来没有人告诉过我；我必须自己去发现它们。既然我现在已经告诉你如何成功，你就没有理由不在你所选择的领域里努力并做出伟大的工作。
🔗 链接
[1] 理查德 · 卫斯理 · 汉明（Richard Wesley Hamming）: https://en.wikipedia.org/wiki/Richard_Hamming[2] 演讲版《You and your research》: https://www.youtube.com/watch?v=a1zDuOPkMSw