费曼致学生真野光一
http://www.cnblogs.com/eshizhan/p/3848583.html
这是理查德·费曼回复学生真野光一的一封信，附英文原版。
费曼致学生真野光一（Koichi Mano）
真野是获诺贝尔奖的科学家费曼从前的学生，也曾经是朝永振一郎的学生。他写信来道贺。费曼回了信，问他近况如何。他回信说：“正在研究同调理论应用于电磁波在扰动的大气中的传播……是一个很卑微、末节的题目。”
亲爱的光一：
我非常高兴知道你的消息，也知道你在一家研究实验室里有个适当的职位。
不过你信中的语句看起来很哀伤，这令我有点忧心，好像你的老师给了你一个没有什么意思的想法，不太值得花和大的力气去研究。其实一个问题有没有价值，并不 在于问题本身的大小，而是看你好是不是能真正解决它，或有助于解决它。这样，你的辛苦就有真正的贡献，不是白费的。
在科学界，只要是出现在我们面前而还没有解决的问题，我们却有办法向答案推进一点，这就是伟大的问题。我倒是想建议你，先找一些更简单的，或者如你说的，更卑微的问题。让你可以轻易解决掉。不管问题有多么平凡都没关系，你会尝到成功的喜悦。而且要经常协助同事，就算回答那些能力不如你的人所提的问题，都是值得做的，都会累积自己的成就感。不要因为“什么问题没意思、什么问题才有价值”这种错误想法，而一直闷闷不乐，剥夺了自己对成功的喜悦。
我们相遇的时候，正是我生涯上的巅峰期。因此在你眼中，我对问题的解决能力，简直像神一样，好像什么都难不倒。但是我当时还带另外一位博士生希布斯 （Aibert Hibbs），他的博士论文只是研究风如何把海水吹出浪花。我接受他是因为他带着自己想解决的问题，跑来找我指导。我对你犯了一个错误，就是我指定了一个题目给你，而不是你自己找的题目。这让你误解了题目的意义，认为有些问题是有趣的、令人欣喜的或重要而值得的——也就是，你认为有些问题值得你花功夫去解决，有些则不然。
真抱歉，请原谅我的疏忽。希望这封信能稍微有点补救效果。
我自己研究过无数的题目，有很多都是你说的那种卑微的、末节的问题。但是我觉得很开心，而且做得很卖力。因为我有的时候会得到部分成果。我举一堆例子：
我研究过高度抛光表面的摩擦因数，想知道摩擦力是怎样运作的（结果失败了）；也研究过晶体的弹性与原子之间的作用力有怎样的关系；怎么把金属电镀到塑胶物 体上（如门把）；中子如何扩散出铀原子；电磁波如何从玻璃的薄镀膜反射；爆炸的时候，震波是怎样形成的，我也设计过中子计数器；计算轻原子核的能阶；探讨为何某些元素会捕获L层电子，却不会捕捉K层电子。我还研究了如何把纸折成某几种儿童玩具（用纸条折成的外形可变化的多边形）的一般理论；紊流理论（我在这上面花了好几年工夫，可惜没有结果）；当然还有量子理论的那些“比较伟大的”问题。
你说自己是个无足轻重的小人物。但我要说，你对你太太和孩子而言，可不是小人物。如何你的同事带着问题来，得到满意的答案而去，那你也不是小人物。你对我当然也不是小人物。不要妄自菲薄，认为自己是个无名氏，这样就令人伤感了。知道自己在这个世上的定位，努力扮演好自己的角色。不要用自己年轻时的幼稚想法来论断自己，也不要用别人的眼光和想法来评论自己。
祝你好运而愉快。
诚挚的祝福
理查德·费曼
1966年2月3日
What Problems to Solve – By Richard Feynman
A former student, who was also once a student of Tomonaga’s, wrote to extend his congratulations. Feynman responded, asking Mr. Mano what he was now doing. The response: “studying the Coherence theory with some applications to the propagation of electromagnetic waves through turbulent atmosphere… a humble and down-to-earth type of problem.”
Dear Koichi,
I was very happy to hear from you, and that you have such a position in the Research Laboratories. Unfortunately your letter made me unhappy for you seem to be truly sad. It seems that the influence of your teacher has been to give you a false idea of what are worthwhile problems. The worthwhile problems are the ones you can really solve or help solve, the ones you can really contribute something to. A problem is grand in science if it lies before us unsolved and we see some way for us to make some headway into it. I would advise you to take even simpler, or as you say, humbler, problems until you find some you can really solve easily, no matter how trivial. You will get the pleasure of success, and of helping your fellow man, even if it is only to answer a question in the mind of a colleague less able than you. You must not take away from yourself these pleasures because you have some erroneous idea of what is worthwhile.
You met me at the peak of my career when I seemed to you to be concerned with problems close to the gods. But at the same time I had another Ph.D. Student (Albert Hibbs) was on how it is that the winds build up waves blowing over water in the sea. I accepted him as a student because he came to me with the problem he wanted to solve. With you I made a mistake, I gave you the problem instead of letting you find your own; and left you with a wrong idea of what is interesting or pleasant or important to work on (namely those problems you see you may do something about). I am sorry, excuse me. I hope by this letter to correct it a little.
I have worked on innumerable problems that you would call humble, but which I enjoyed and felt very good about because I sometimes could partially succeed. For example, experiments on the coefficient of friction on highly polished surfaces, to try to learn something about how friction worked (failure). Or, how elastic properties of crystals depends on the forces between the atoms in them, or how to make electroplated metal stick to plastic objects (like radio knobs). Or, how neutrons diffuse out of Uranium. Or, the reflection of electromagnetic waves from films coating glass. The development of shock waves in explosions. The design of a neutron counter. Why some elements capture electrons from the L-orbits, but not the K-orbits. General theory of how to fold paper to make a certain type of child’s toy (called flexagons). The energy levels in the light nuclei. The theory of turbulence (I have spent several years on it without success). Plus all the “grander” problems of quantum theory.
No problem is too small or too trivial if we can really do something about it.
You say you are a nameless man. You are not to your wife and to your child. You will not long remain so to your immediate colleagues if you can answer their simple questions when they come into your office. You are not nameless to me. Do not remain nameless to yourself – it is too sad a way to be. now your place in the world and evaluate yourself fairly, not in terms of your naïve ideals of your own youth, nor in terms of what you erroneously imagine your teacher"s ideals are.
Best of luck and happiness.
Sincerely, Richard P. Feynman.
