二〇二五 十二月
（费曼获诺贝尔物理学奖）一位曾做过费曼学生、也曾师从朝永振一郎（Shinichiro Tomonaga）的老学生来信致贺。费曼回信询问真野先生近来在做什么。对方回答：“研究相干理论，并将其应用于电磁波在湍流大气中的传播……一个卑微又朴实无华的问题。”
理查德·P·费曼致真野浩一（Koichi Mano），1966年，2月3日
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亲爱的浩一：
收到你的来信我很高兴，也为你在研究所里有这样一份工作而感到喜悦。
不幸的是，你的来信让我替你感到难过，因为你似乎真的很悲伤。看来你老师对你的影响，让你对什么才算值得做的问题，产生了错误的看法。所谓值得做的问题，是那些你确实能解决或帮助解决，你能真正有所贡献的问题。一个科学问题之所以宏大，是因为它作为未解之谜摆在我们面前，而我们能看到自己有办法把它向前推进一点点。我建议你选择更简单的，或者正如你所说，更“卑微”的问题，直到找出一些你确实能轻松解决的——不管它们看起来多么琐碎。你会从成功中获得快乐，也会因为帮助了他人而感到喜悦，哪怕只是解答一位能力不如你的人心中的一个问题。不要因为你心里对“什么值得做”抱有错误观念，就把这些乐趣从自己那里夺走。
你遇见我时，正逢我事业的巅峰，在你看来我所关心的是那些接近“神”的问题。但与此同时，我还有一位博士生（Albert Hibbs 阿尔伯特·希布斯），他论文研究的是海上的风如何在水面上掀起波浪。我之所以收他做学生，是因为他带着自己想解决的问题来找我。而对你，我犯了个错误：我交给了你问题，而不是让你自己去找；这让你对什么是有趣、愉悦或重要的研究对象（比如，那些你觉得自己能有所作为的问题）产生了错误的观念。对此我感到抱歉，请原谅我。希望这封信能稍稍纠正一下。
我研究过数不清的、在你看来会被称作“卑微”的问题，但我很享受也为之自豪，因为我有时候也能取得一些成果。比如，研究高度抛光表面的摩擦系数实验，想弄清楚摩擦究竟是如何运作的（失败了）。或者，研究晶体的弹性性质如何取决于原子间的作用力，或是如何让电镀层更好地黏附在塑料制品上（比如收音机旋钮）。或者，中子如何从铀中扩散的。或者，镀在玻璃上的薄膜对电磁波的反射。爆炸中激波的形成与发展。中子计数器的设计。为什么有些元素会从L层俘获电子，而不是从K层。关于如何折纸做出一种儿童玩具（叫作“flexagon”，可翻折多边形）的通用理论。轻核的能级。还有湍流理论（我在这上面花了好几年也没成功）。此外还有量子理论中的所有那些“更宏大”的问题。
没有任何问题太小或太微不足道，只要我们真能做点什么。
你说你是个无名之辈。对你的妻子和孩子来说，你不是。如果当同事走进你办公室时，你能回答他们的简单问题，在你身边的人眼里，你很快也不再是无名之辈。对我来说，你也不是无名之辈。不要在你自己心里做个无名之辈——那太令人悲哀了。认清你在世界中的位置，公正地评价自己，不要按照年少时那套天真的理想，也不要按照错误想象的老师想追求的理想，来衡量自己。
祝你好运，幸福安康。
诚挚的，
理查德·P·费曼
Dec 2025
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 application to the propagation of electromagnetic waves through turbulent atmosphere. . . a humble and down-to-the-earth type of problem.”
RICHARD P. FEYNMAN TO KOICHI MANO, FEBRUARY 3, 1966
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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 a little 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) whose thesis 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 help 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 depend 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 L-orbits, but not from K-orbits. General theory of how to fold paper to make a certain kind 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. Know your place in the world and evaluate yourself fairly, not in terms of the 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