You and Your Research


Dr. Richard W. Hamming was one of those famous guys at Bell Labs during its heyday. Throughout his later career he gave a talk titled You and Your Research which is available in various forms on the internet. I highly recommend setting aside half an hour and reading it because a lot of his advice comes in the form of anecdotes that are difficult to summarize.

Annotated Quotes

I'm not a fan of quotes of received wisdom which are usually cherry-picked to support whatever you wanted to believe in the first place. However, they concisely express ideas and Hamming liked them so let's go with it.


Luck favors the prepared mind. - Pasteur

This is one of the themes of the talk. I like how success is couched in terms of luck and preparation. Obviously, you do what you can to prepare but often success boils down to being at the right place at the right time.


Knowledge and productivity are like compound interest. - Bode

Hamming tells a story of a contemporary who was his age but prolific. Why? Because for a decade he squeezed more work out of each hour. The more you know, the faster you work, and the more you learn. It's just like interest!

What a simile! Take a moment to appreciate this idea -- it was new to me.

If I have seen further than others, it is because I've stood on the shoulders of giants. - Newton

In addition to understanding what your predecessors have done, present your work so others can build on it. Easy for Hamming to say (he's one of the giants).


Genius is 99% perspiration and 1% inspiration. - Edison

This classic quote and the 10,000 hours rule from Malcolm Gladwell are widely misunderstood. Hamming says your effort must be intelligently applied. I couldn't agree more, it's not enough to work hard!

Becoming a concert pianist requires engaged practice -- mindless practice doesn't count towards your 10,000 hours.

Annotated Paragraphs

The System

John Tukey almost always dressed very casually. He would go into an important office and it would take a long time before the other fellow realized that this is a first-class man and he had better listen. For a long time John has had to overcome this kind of hostility. It's wasted effort! I didn't say you should conform; I said "The appearance of conforming gets you a long way." If you chose to assert your ego in any number of ways, "I am going to do it my way," you pay a small steady price throughout the whole of your professional career. And this, over a whole lifetime, adds up to an enormous amount of needless trouble.


On the other hand, we can't always give in. There are times when a certain amount of rebellion is sensible. I have observed almost all scientists enjoy a certain amount of twitting the system for the sheer love of it. What it comes down to basically is that you cannot be original in one area without having originality in others. Originality is being different. You can't be an original scientist without having some other original characteristics. But many a scientist has let his quirks in other places make him pay a far higher price than is necessary for the ego satisfaction he or she gets. I'm not against all ego assertion; I'm against some.

If you're doing the same thing as everybody else you won't stand out. Do something different and original.

I like fighting "the system" (the next time someone tries to identify you with an ID number instead of your name say, "I'm a human being, not a number!") and this wasn't what I wanted to hear. I want to hear that I should keep fighting for what I believe is right and never give up. The reality is you have to work with the system and carefully pick your battles; don't be Don Quixote fighting windmills.

Make Lemonade

I give you a story from my own private life. Early on it became evident to me that Bell Laboratories was not going to give me the conventional acre of programming people to program computing machines in absolute binary. It was clear they weren't going to. But that was the way everybody did it. I could go to the West Coast and get a job with the airplane companies without any trouble, but the exciting people were at Bell Labs and the fellows out there in the airplane companies were not. I thought for a long while about, "Did I want to go or not?" and I wondered how I could get the best of two possible worlds. I finally said to myself, "Hamming, you think the machines can do practically everything. Why can't you make them write programs?" What appeared at first to me as a defect forced me into automatic programming very early. What appears to be a fault, often, by a change of viewpoint, turns out to be one of the greatest assets you can have. But you are not likely to think that when you first look the thing and say, "Gee, I'm never going to get enough programmers, so how can I ever do any great programming?"

And there are many other stories of the same kind; Grace Hopper has similar ones. I think that if you look carefully you will see that often the great scientists, by turning the problem around a bit, changed a defect to an asset. For example, many scientists when they found they couldn't do a problem finally began to study why not. They then turned it around the other way and said, "But of course, this is what it is" and got an important result. So ideal working conditions are very strange. The ones you want aren't always the best ones for you.

Here's a modern example: I don't have powerful GPUs that everyone is using to do deep learning research. Instead, I realized that solving problems on my laptop is still useful because the solutions I come up with can be scaled up with traditional CPUs. A state-of-the art, computationally-intensive image deep learning model doesn't do Google any good if they can't deploy it at scale.

Important Problems

Over on the other side of the dining hall was a chemistry table. [...] I went over and said, "Do you mind if I join you?" They can't say no, so I started eating with them for a while. And I started asking, "What are the important problems of your field?" And after a week or so, "What important problems are you working on?" And after some more time I came in one day and said, "If what you are doing is not important, and if you don't think it is going to lead to something important, why are you at Bell Labs working on it?" I wasn't welcomed after that...


If you do not work on an important problem, it's unlikely you'll do important work. It's perfectly obvious. Great scientists have thought through, in a careful way, a number of important problems in their field, and they keep an eye on wondering how to attack them. Let me warn you, 'important problem' must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn't work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It's not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important. When I say that most scientists don't work on important problems, I mean it in that sense.

When I was a grad student at Northwestern I'd browse Physical Review Letters and read articles in Reviews of Modern Physics. It gave me a sense of the broader scientific community and what people were working on.

Here's my list of important problems in physics:

  1. High-energy physics. What are the limits of the standard model?
  2. Graphene
  3. Quantum computers, qubits
  4. Opto-mechanical cavity wave resonators
  5. Neutrino physics
  6. 3D super-resolution imaging (X-Rays, CT, etc)
  7. Super-conducting fluids (quantum mechanics + fluid dynamics = fun)
  8. What are dark matter and dark energy?
  9. Exo-planets. What are solar systems like? Is ours typical or not?

I purposely left String Theory and Multi-Universe theories out because there's no "attack", no means of getting real data to test these theories.

I also left out Gravitational Waves because I didn't think they'd be discovered with the current generation detector. I was wrong on that count!

Present Your Work well

While going to meetings I had already been studying why some papers are remembered and most are not. The technical person wants to give a highly limited technical talk. Most of the time the audience wants a broad general talk and wants much more survey and background than the speaker is willing to give. As a result, many talks are ineffective. The speaker names a topic and suddenly plunges into the details he's solved. Few people in the audience may follow. You should paint a general picture to say why it's important, and then slowly give a sketch of what was done. Then a larger number of people will say, "Yes, Joe has done that," or "Mary has done that; I really see where it is; yes, Mary really gave a good talk; I understand what Mary has done." The tendency is to give a highly restricted, safe talk; this is usually ineffective. Furthermore, many talks are filled with far too much information. So I say this idea of selling is obvious.

I've been to many talks by grad students and professors who name a topic and then launch into the latest problem they've solved. Who are they talking to? Their lab mates? Nobody else can follow.

I completely agree that talks are filled with too much information. It's better to pare down the information and focus on conveying, really conveying, what's important.

I think too many presenters try to convince the audience they're smart. Here's a secret: you've been thinking about your problem longer than anyone else and nobody understands it better than you -- you are the smartest person in the room. Your job is to help everyone else understand what you're doing and why.

My ideal of communication are road signs. They convey information clearly and effectively. In fact, road signs do such a good job we don't even notice how easy it is. That's what you want in a talk. You want people to follow you on your journey as you tell a story.


...Great scientists tolerate ambiguity very well. They believe the theory enough to go ahead; they doubt it enough to notice the errors and faults so they can step forward and create the new replacement theory. If you believe too much you'll never notice the flaws; if you doubt too much you won't get started. It requires a lovely balance.


The premise of Hamming's talk is you want to get the most out of your one life. He argues that a good goal to set for yourself is to do first-class work, Nobel prize work. I'm not so sure.

He talks about forming an emotional commitment to your work. People who don't do first-class work are "dregs". Underlying his essay is the idea that if you don't spend every waking minute thinking about solving important problems, why bother?

Tolerate ambiguity. Doing great work is a good goal but so is spending time with your family. Being kind and helping others is a good goal. Judging a person based how they are likely to get a Nobel Prize isn't fair, or even useful -- not everyone wants a Nobel Prize.

My quote of received wisdom is this:

If you work really hard, and are kind, amazing things will happen. - Conan O'Brien