You and Your Research
In March 1986, the famed mathematician and computer scientist Richard Hamming returned to his former employer, Bell Labs, to give a talk at the Bell Communications Research Colloquia Series. His talk was titled “You and Your Research,” and it’s goal was straightforward: to deliver lessons for serious researchers about how to do “Nobel-Prize type of work” (a topic familiar to Hamming given the large number of Nobels won by his colleagues during his Bell Labs tenure).
This talk is famous among applied mathematicians and computer scientists because of its relentlessly honest and detailed dissection of how stars in these fields become stars — a designation that certainly applies to Hamming, who not only won the Turing Prize for his work on coding theory, but ended up with an IEEE prize named after him: the Richard W Hamming Medal.
A problem with his talk, however, is it’s length and density. It’s easy to lose yourself in its transcript, nodding your head again and again in agreement, then coming out the other side unable to keep track of all the ideas Hamming outlined.
My goal in this blog post to help bring some order to this state of affairs. Below I’ve summarized what I find to be the major points from Hamming’s address. To identify the sections of the speech that correspond to each point I use the wording from this transcription.
I can’t claim that the following is comprehensive (among other things, I do not annotate the questions after the talk), but I’m confident that I capture most of what’s important in this seminal seminar.
Idea #1: Luck is not as important as people think.
[location: see the section that starts with the sentence “let me start not logically, but psychologically…”]
Hamming notes that luck is a common explanation for doing great research. He doubts this explanation by noting that great researchers — like Einstein — do multiple good things in their career.
As an alternate explanation, he cites the following Newton quote: “If others would think as hard as I did, then they would get similar results.”
Idea #2: Knowledge and productivity are like compound interest
[location: “Now for the matter of drive.”]
Hamming notes that “most great scientists have tremendous drive.” He emphasizes the value of working hard by noting that the benefits of extra effort compound over time like interest. If you’re reading a little bit more and thinking a little bit longer than your colleagues, over time the gap between you and them grows.
He then supplies, however, a crucial caveat: you have to apply this effort intelligently. “That’s the trouble,” he elaborates, “drive, misapplied, doesn’t get you anywhere.” He illustrates this axiom by discussing former colleagues who worked harder than he did but have nothing to show for it.
Idea #3: Become comfortable with ambiguity
[location: “there’s another trait on the side which I want to talk about…”]
Hamming notes that great scientists form an “emotional commitment” to the theories they pursue and are able to carry on despite doubts and identified flaws.
He adds, however, that they are still careful about tracking and later addressing these shortcomings that arise along the way.
Idea #4: Creativity requires focus
[location: “Now again, emotional commitment is not enough…”]
Hamming notes his belief in the theory that “creativity comes out of your subconscious.” To make a breakthrough, he believes, you must focus without distraction on the problem long enough for your subconscious to start working it over.
As he summarizes: “If you’re deeply immersed and committed to a topic, day after day after day, your subconscious has nothing to do but work on your problem.”
Idea #5: Important work comes from important problems
[location: “Now Alan Chynoweth mention that I used to eat…“]
After talking about his efforts to seek out big thinkers in the Bell Labs cafeteria, Hamming emphasizes: “If you do not work on an important problem, it’s unlikely you’ll do important work.” He notes that the “average scientist” does not work on important problems but instead plays it safe. He wanted to avoid such mediocrity in his interactions.
He clarifies that for a problem to be important, not only most its impact be clear, but you must also possess a “reasonable attack.” He estimates that most great scientists will keep 10 to 20 great problems in mind at any one time, and if they learn a technique that might apply to one of them, they’ll “drop all the other things and get after it.”
Hamming recalls that he blocked off his Friday afternoons as “Great Thoughts Time,” and spent them only discussing and thinking about “great thoughts.”
Idea #6: Keep your door open
[location: “Another trait, it took me a while…”]
Hamming notes that at Bell Labs the scientists who kept their doors shut got more done in the short term. By contrast, the scientists who kept their doors open were distracted more often but ultimately this increased exposure to other people, problems, and ideas led them to more important work in the long term.
Idea #7: Transform isolated problems into general problems
[location: “I want to talk on another topic…”]
Hamming notes that early on he used to work on isolated problems. This depressed him: “I could see life being a long sequence of one problem after another after another.”
This changed his approach to focus on bigger, more general ideas that others could build on. “By changing a problem slightly” he clarifies, “you can often do great work rather than merely good work.”
He goes on to add that you should never work on an isolated problem unless it is “characteristic of a class.”
Ideas #8: Sell you results
[location: “I have now come down to a topic which is…”]
Hamming notes that the idea of marketing your results is “distasteful” and “awkward” to discuss. He also notes, however, that it’s necessary because “the fact is everyone is busy with their own work,” and you cannot expect them to discover your work on their own.
He suggests three things you must do to bring you ideas to other peoples’ attention: (a) “learn to write clearly,” (b) “learn to give reasonably formal talks,” and (c) “learn to give informal talks” (and know which type of talk is appropriate and when.)
He emphasizes that when giving a talk, in most venues, “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.”