费曼在1965年因为量子电动力学方面的贡献与施温格、朝永振一郎分享了诺贝尔物理学奖之后，收到了来自世界各地的大量来信。他之前的一个博士生，Koichi Mano，也发信来祝贺。Koichi Mano曾经也是朝永振一郎的学生，于1955年获得博士学位，是费曼在加州理工学院（1951-1988）最早的一批博士生之一。
费曼回信问了Koichi Mano现在在做什么，得到如下答复：“研究相干理论及其在电磁波通过湍流大气传播中的一些应用…一个卑微的、偏实际类型的问题（a humble and down-to-earth type of problem）。”
费曼于1966年2月3日给Koichi Mano回复了以下这封著名的信件：
亲爱的Koichi：
我很高兴收到你的回信，同时也很高兴得知你在一家研究实验室有这样一个职位。
可惜你的信也让我有些不快，因为你看上去很伤感。似乎你老师的影响，让你对什么是有价值的问题产生了错误的观念。有价值的问题是那些你能够真正解决、或者有助于解决的问题，是那些你能够真正做出贡献的问题。如果有一个问题摆在我们面前尚未解决，而我们能找到一些方法往前推进一点，那么它就是科学方面的重大问题（grand in science）。我倒是想建议你，在找到可以真正轻松解决的大问题前，先找一些更简单的，或者如你所说的，更卑微（humbler）的问题来做，不管多么无足轻重（trivial）。这样你会尝到成功的喜悦，并从帮助你的同事中获得快乐，哪怕只是回答了一个能力不如你的同事所思考的问题。千万不要因为大问题才有价值的错误观念剥夺了自己的这些快乐。
你在我职业生涯的巅峰时期遇见了我，当时在你看来，似乎我关心的问题都是很高大上的（close to the gods）。但同一时期，我还有另一个博士生Albert Hibbs在研究风是如何吹在海洋中的水面上形成波浪的。我接收了他当学生是因为他带着想要解决的问题来找我。我对你犯了一个错误，我直接给你指定了题目，而不是让你去找到自己想要解决的问题，并让你对什么是有趣的、令人愉快的、或是重要的工作（也就是那些你认为你或许能做点贡献的工作），留下了错误的印象。抱歉，请你原谅。我希望这封信能补救一点点。
我研究过很多你称之为卑微（humble）的问题，但是我很享受这些问题，并且感觉非常好，因为有时我可以取得部分的成功。比如，我对高度抛光表面上的摩擦系数进行过实验，以尝试了解摩擦是如何运作的（结果失败了）；研究过晶体的弹性性质如何依赖于晶体中的原子间作用力、如何使电镀金属粘附到塑料物体（如收音机旋钮）上、中子如何从铀中扩散出来、镀膜玻璃表面的电磁波反射、爆炸中冲击波的形成、中子计数器的设计、为什么有些元素从L轨道而不是K轨道捕获电子、如何折叠纸张来制作某种类型的儿童玩具（称为柔性玩具）的一般理论、轻核的能级、湍流理论（我已经研究好几年了都没有成功）、再加上量子理论的所有“更重大”（“grander”）的问题。
只要我们能对一个问题真正做点贡献，就没有什么问题是太小或太无足轻重的。
你说你只是一个无名之辈。但对于你的妻子和孩子来说，你并不是。对于你的亲密同事来说，如果你能解答他们来你办公室提的那些简单问题，你就不是。对于我来说，你也不是。不要总认为自己是无名之辈，那样太悲哀了。知道自己在世上的定位，公正地评价自己，而不是按照自己年轻时的稚嫩理想，也不是按照你误以为的你老师的理想来评价。
祝你好运和幸福。
真挚的，
理查德·P·费曼
原文如下（收录在《Perfectly Reasonable Deviations from the Beaten Track —— The letters of Richard P. Feynman》一书中）：
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. Know 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.