What Problems to Solve!

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.