Richard Hamming · You and Your Research
The Bell Labs cafeteria had tables. Richard Hamming used to sit at the physics table, listening to Shockley, Brattain and Bardeen, learning a great deal. Then a Nobel Prize arrived, and a promotion, and the good people left. “what was left was the dregs. Nobody wanted what was left.” So he carried his tray across the dining hall to the chemistry table and asked whether he could join them.
They couldn’t say no. So he started asking questions. For the first week: what are the important problems of your field? After a while: which important problem are you working on? And after some more time he sat down one day and said it — if what you are doing is not important, and you don’t think it will lead to anything important, why are you at Bell Labs working on it?
“I wasn’t welcomed after that; I had to find somebody else to eat with!”
On 7 March 1986, a 71-year-old Hamming told that story to about two hundred people. His conclusion was not “work hard.” It was something harder: if you don’t work on an important problem, you won’t do important work — and most scientists, on his forty years of watching and asking them to their faces, spend their careers on things they themselves don’t believe matter.
The sharpest part of the talk is that he refuses to let “important” stay vague. Antigravity, time travel, teleportation: the consequences are enormous, guaranteed Nobel Prize and any sum of money you care to name. But they are not important problems, because there is no attack. “It’s not the consequence that makes a problem important, it is that you have a reasonable attack.” So “important” is a technical judgement, not an ambition. Great scientists, he says, keep ten to twenty such problems in mind and drop everything the moment a clue appears. His own arrangement was to spend Friday afternoons on great thoughts only — ten percent of the week spent working out which direction was worth walking in.
The rest is equally concrete and mostly unflattering. Courage beats brains: he points at Shannon proving that the average random code is arbitrarily good, and therefore that at least one good code must exist, and asks “Who but a man of infinite courage could have dared to think those thoughts?” Fame is a curse: Brattain stood in Arnold Auditorium the day his prize was announced, nearly in tears, swearing the Nobel effect would not touch him, and within weeks Hamming watched him work only on great problems. Knowledge compounds like interest: same ability, ten percent more work, more than twice the output. Work with your door closed and you get more done this year and next, and ten years later you find you have been solving slightly the wrong problems. And doing it isn’t enough — you have to sell it: write clearly, give formal talks, and learn to stand up in the middle of a hot meeting. Those who fail, he argues, usually lose not to ability but to ego assertion, to waging war on the system, and to a thousand alibis. “You can tell other people all the alibis you want. I don’t mind. But to yourself try to be honest.”
Then: therefore, go forth and become great scientists.
The next forty years handed him a split report card. In 2016 a study of the full publication sequences of 2,887 physicists found that a scientist’s highest-impact paper falls at random within that sequence — while an individual ability parameter really does exist and stays stable across a career. That is almost a formal restatement of Hamming’s own line: “The particular thing you do is luck, but that you do something is not.” His claim about age, meanwhile, had already expired by the time he made it: the share of Nobel physics work done before 30 peaked in 1923 at 31% and fell steadily to near zero by 2000, and since 1985 physicists have been the oldest of the three science laureate groups at the time of their prize-winning work. As for “one extra hour a day doubles a lifetime’s output” — the single most-quoted line — it is the one claim with no evidence behind it, and the model above says explicitly that raising output alone will not buy you the peak.
First the physics table collapsed.
Hamming had been eating with the mathematicians until he realised he already knew a fair amount of mathematics and wasn’t learning much. So he moved to the physics table — Shockley, Brattain, Bardeen, J. B. Johnson, Ken McKay. “It was very interesting to listen to Shockley, Brattain, Bardeen, J. B. Johnson, Ken McKay and other people, and I was learning a lot.” Then, in his own words: “But unfortunately a Nobel Prize came, and a promotion came, and what was left was the dregs. Nobody wanted what was left. Well, there was no use eating with them!”
Across the dining hall sat the chemists. He knew one of them, Dave McCall — who was, at the time, courting their secretary. He walked over and asked: do you mind if I join you?
“They can’t say no,” Hamming said, “so I started eating with them for a while.”
Then he began asking. For the first week: what are the important problems of your field? After a week or so: what important problems are you working on? And after some more time, he came in one day and said it:
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?— Richard Hamming, You and Your Research, 1986
“I wasn’t welcomed after that; I had to find somebody else to eat with! That was in the spring.”
In the fall, Dave McCall stopped him in the hall. “Hamming, that remark of yours got underneath my skin. I thought about it all summer, i.e. what were the important problems in my field. I haven’t changed my research,” he said, “but I think it was well worthwhile.” A couple of months later Hamming noticed McCall had been made head of the department; years later, that he had become a member of the National Academy of Engineering. Of the other men at that table, Hamming says, he never heard a single name mentioned in scientific circles again.
Richard Wesley Hamming was born in Chicago in 1915. All three of his degrees were in mathematics. In 1945 he arrived at Los Alamos, where his job was to run the computing machines other people had got going so that the scientists could get back to business. He describes that period without any softening:
I saw I was a stooge. I saw that although physically I was the same, they were different. And to put the thing bluntly, I was envious.— Richard Hamming, You and Your Research, 1986
The objects of that envy were Feynman, Fermi, Teller, Oppenheimer, and his own boss Hans Bethe. Everything in this talk grows out of the question that envy turned into: what separates the people who did it from the people who might have?
He joined Bell Labs in 1946 and stayed thirty years, sharing an office for a while with Claude Shannon. In 1950 he published the paper that founded error-correcting codes — Hamming codes and Hamming distance both come from it. In 1968 he received the Turing Award, the third person ever to do so. In 1987 the IEEE created a medal in his name; in 1988 he became its first recipient. His colleagues’ memories were not all reverent: some described him as egotistical, saying he sometimes went off “half-cocked, after some half-baked idea.” Richard Franke of the Naval Postgraduate School wrote of him: “I’ll also long remember him for his red plaid sport coat and his bad jokes.”
Now the year. On 7 March 1986 he was 71, ten years out of Bell Labs, teaching at the Naval Postgraduate School in Monterey. His audience was roughly two hundred people — but not at Bell Labs. They were at Bell Communications Research (Bellcore) in Morristown, New Jersey, an organisation that existed because AT&T had been broken up on 1 January 1984 and the seven regional “Baby Bell” companies had jointly taken over part of its research capacity. In his introduction, Alan Chynoweth made a point of greeting “many of our former colleagues from Bell Labs who, I understand, are here to be with us today.”
In other words: a man who spent thirty years inside Bell Labs in its golden age, standing in front of a roomful of people who had been sliced off from it two years earlier, explaining how the place worked. Chynoweth gave away the mood himself during the questions, grumbling about the red tape the regulators required and quoting an exasperated vice-president: “UNIX was never a deliverable!”
He drew his boundary in the first minute. This is not a talk about running a research lab: “It is not about managing research, it is about how you individually do your research.” When someone later asked what management could do about any of this, his answer was one sentence — management can do very little.
He begins by saying that he is not discussing ordinary research but great research — for convenience, “Nobel-Prize type of work”: relativity, Shannon’s information theory, that class of thing. Then he gives his reason for the talk’s importance, which is almost the least scientific sentence in it: “as far as I know, each of you has one life to live. Even if you believe in reincarnation it doesn’t do you any good from one life to the next!”
He announces that he will start not logically but psychologically, because the main objection is the belief that great science is all luck. His rebuttal is frequency: Einstein did too many good things for it to be chance, the repetition is suspicious; Shannon did not do only information theory. He cites Pasteur’s “Luck favors the prepared mind,” then sharpens it into something more precise:
So yes, it is luck. The particular thing you do is luck, but that you do something is not.— Richard Hamming, You and Your Research, 1986
The evidence is his own office. He shared it with Shannon; Shannon was doing information theory and he was doing coding theory, at the same place and the same time. “It is suspicious that the two of us did it at the same place and at the same time — it was in the atmosphere.” You can call that luck, he says, and then turns the question around: but why, of all the people at Bell Labs, were those the two who did it?
Then he takes apart “brains.” His example is Bill Pfann, the man who did zone melting, who walked into his office one day with an idea dimly in mind and some equations. “It was pretty clear to me that this man didn’t know much mathematics and he wasn’t really articulate.” Hamming took the problem home, did a little work, and eventually taught Pfann to run the computers himself. Pfann proceeded “with negligible recognition from his own department” and ultimately collected all the prizes in the field — and once he was properly started, his shyness, awkwardness and inarticulateness fell away. A second example is a man named Clogston: “Well I would have fired the fellow, but J. R. Pierce was smart and kept him on.” Clogston went on to do the Clogston cable, and after that a steady stream of good ideas. One success brought confidence and courage.
Courage is the keyword of this stretch, and his exhibit is Shannon’s proof. Shannon wanted to create a method of coding, didn’t know what to do, so he made a random code — and got stuck. Then he asked the impossible question: what would the average random code do? He proved the average code is arbitrarily good, and therefore that at least one good code must exist.
Who but a man of infinite courage could have dared to think those thoughts?— Richard Hamming, You and Your Research, 1986
Next come age and fame, which he braids together. Physicists always say you have to do it young, and the quantum mechanics people were “disgustingly young” when they did their best work. But he cares more about what fame does. He describes a scene: the day Brattain’s prize was announced, all three winners spoke in Arnold Auditorium, and Brattain, practically with tears in his eyes, said “I know about this Nobel-Prize effect and I am not going to let it affect me; I am going to remain good old Walter Brattain.” Hamming thought that was nice. “But in a few weeks I saw it was affecting him. Now he could only work on great problems.” Famous people stop planting “the little acorns from which the mighty oak trees grow.” He then drops his favourite verdict of many years: the Institute for Advanced Study at Princeton “has ruined more good scientists than any institution has created”.
The section on working conditions is the most usefully counter-intuitive in the talk. He had seen early that Bell Labs was never going to give him the conventional “acre of programming people” to write absolute binary, which was how everybody did it. He could go to the West Coast airframe companies and get them, but the exciting people were at Bell Labs. After a long time wondering whether to leave, he said to himself: 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.”
Then drive. He had worked with John Tukey for years before discovering Tukey was slightly younger than he was, and stormed into Hendrik Bode’s office to ask how anybody his age could know as much as Tukey did.
You would be surprised Hamming, how much you would know if you worked as hard as he did that many years.— Hendrik Bode to Hamming, recounted in You and Your Research, 1986
“I simply slunk out of the office!” He read the remark as compound interest: given two people of roughly the same ability, the one who works ten percent more “will more than twice outproduce the former”; the one who gets in one more hour of thinking, day in and day out, will be enormously more productive over a lifetime. He acted on it, and he states the cost plainly: “I don’t like to say it in front of my wife, but I did sort of neglect her sometimes; I needed to study. You have to neglect things if you intend to get what you want done.” Then he pulls the handbrake: “Just hard work is not enough — it must be applied sensibly.” He had good friends at Bell Labs who worked as hard or harder than he did and had much less to show for it.
What follows is the most quoted and most misquoted passage in the talk: the criterion for an important problem. He warns that the phrase must be used carefully, and then notes that during all his years at Bell Labs, the three “outstanding” problems in physics were never worked on — time travel, teleportation, 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.— Richard Hamming, You and Your Research, 1986
That single sentence drags the whole talk back from inspiration into engineering. It also explains his own institutional invention: at the urging of Tukey and others he set aside Friday afternoons for “Great Thoughts Time,” discussing nothing but great thoughts after lunch — what will be the role of computers in all of AT&T? How will computers change science? During those afternoons he arrived at an observation: nine out of ten experiments were then being done in the lab and one in ten on the computer, and the ratio would reverse. He said so to the vice-presidents, who “knew I was a crazy mathematician and had no sense of reality.” He also predicted that more than half the people at Bell Labs would be interacting closely with computing machines before he left. On his account, all of this was borne out, and they built laboratories they didn’t need.
Great scientists, he says, keep between ten and twenty important problems in mind, waiting for an attack; when a clue appears, “They drop all the other things and get after it,” which is why they arrive first. As a counter-example he tells a story he explicitly says he cannot vouch for: that at Berkeley they had gathered data which, had they reduced it, would have shown them fission — but they were busy building more equipment. “They came in second!”
Then the most widely travelled image in the talk: the open door and the closed door. With your door closed you get more work done today and tomorrow, and you are more productive than most. “But 10 years later somehow you don’t know quite know what problems are worth working on; all the hard work you do is sort of tangential in importance.” The man with the open door gets interrupted constantly but occasionally gets clues about what the world is and what might matter. He is careful here: “Now I cannot prove the cause and effect sequence because you might say, ‘The closed door is symbolic of a closed mind.’ I don’t know.” All he claims is a fairly good correlation — and that the people behind closed doors often work harder.
After that comes the song he quotes: “It ain’t what you do, it’s the way that you do it.” He describes a military computing job he had already solved by “a rather crummy method,” until he realised he would have to file a report and every analog installation would comb it for flaws — and therefore that the real problem was not to get the answer but to demonstrate beyond question that a digital machine could beat the analog computer on its own ground. He reworked the solution, built an elegant theory, got identical results, and the published method was known for years as Hamming’s method of integrating differential equations. The same reasoning produced the largest methodological decision of his life: “I made the resolution that I would never again solve an isolated problem except as characteristic of a class.”
Finally he arrives at a topic he calls distasteful: it is not sufficient to do a job, you have to sell it. “‘Selling’ to a scientist is an awkward thing to do. It’s very ugly; you shouldn’t have to do it.” But everyone is busy with their own work. He demands three skills — clear writing, formal talks, and informal talks — and complains about the “back room scientists” at Bell Labs who kept quiet in conferences and filed a report three weeks after the decision was made. He himself got physically ill giving speeches at first, so he volunteered to give them to small audiences until the fear went. Asked in the discussion how he split his time, he gives a startling number: at least 50% must go to the presentation.
The closing section asks why so many talented people fail. His list: insufficient drive and commitment; personality defects (the man who insisted on handling all his own correspondence rather than working with the secretarial system — “he never went any further”); ego assertion, illustrated by his own western clothes at 590 Madison Avenue and his decision that “The appearance of conforming gets you a long way”; fighting the system (the friend whose bicycle request was red-taped to death, who rose to be President of Bell Laboratories); anger; and alibis. “You can tell other people all the alibis you want. I don’t mind. But to yourself try to be honest.”
Then: “Therefore, go forth and become great scientists!” The last line of the discussion is the same sentence in another key — “Go forth, then, and do great work!”
This talk has a longer twin, and the differences between it and the 1986 version are larger than most people assume.
After leaving Bell Labs in 1976, Hamming taught a capstone course at the Naval Postgraduate School, and in 1996–97 turned the lectures into a book: The Art of Doing Science and Engineering: Learning to Learn. Its final chapter is also called “You and Your Research,” and he states the relationship between the two at the top of it: the earlier chapters are “in a sense, just a great expansion, with much more detail, of the original talk. This chapter is, in a sense, a summary of the previous 29 chapters.” The famous eighteen pages are the abstract of a course, not the other way round.
The book contains a mathematical argument that the talk does not. Explaining why you need a goal of excellence, he reaches for a random walk: without one you wander like a drunken sailor, each step in an independent direction, the steps cancelling, so “the expected distance from the starting point is proportional to the square root of the number of steps taken.” With a vision, the steps tend to go the same way and you cover a distance “proportional to the number of steps taken, which in a lifetime is a large number indeed.” It is the one place where he turns his own advice into something you can compute, and it is absent from the stage in 1986.
The most-quoted number, meanwhile, does not match between the two versions. On stage he gives a ratio: “Given two people of approximately the same ability and one person who works ten percent more than the other, the latter will more than twice outproduce the former.” In the book he gives a rate: “I do not know what compound interest rate to assign, but it must be well over 6% — one extra hour per day over a lifetime will much more than double the total output.” Those are two different claims (an input–output elasticity versus an annual growth rate), and neither is measured anywhere. More to the point, the book’s very next sentence is a warning that never travels with the number: “But be careful — the race is not to the one who works hardest!”
What the book cuts is the entire etiquette half. The long section on ego assertion from the 1986 stage — the clothing experiment at 590 Madison Avenue, “The appearance of conforming gets you a long way,” the criticism of John Tukey’s casual dress (“I think John Tukey paid a terrible price needlessly”) — does not appear anywhere in the 1997 chapter. Nor does the answer about stress: “You can lead a nice life; you can be a nice guy or you can be a great scientist. But nice guys end last, is what Leo Durocher said.” Nor does “I don’t like to say it in front of my wife”. Eleven years on, writing it down for students, he kept the epistemology and deleted the manners.
That deletion is worth a second look, because the biographical afterword published with that chapter records that colleagues described Hamming as egotistical, given to going off “half-cocked, after some half-baked idea” — and that the first detail a colleague reached for in remembering him was a red plaid sport coat. The man who advised the appearance of conforming is remembered for a loud jacket.
One more detail exists only in the book, and it punctures the tidy stage version. Telling the Pfann story on stage, he says merely that he asked friends who had been with Pfann at school. In the book he writes: “I checked up on him by asking around in his department, and I found they had a low opinion of him and his idea for zone melting.” He got on board anyway, because, as he puts it, “I was not about to lose my chance of working with a great idea”. What zone melting turned out to be good for was purifying the materials for transistors.
Finally, the layer that most needs saying out loud: what kind of study this is. It is not research in any technical sense. The data are four decades of face-to-face questioning, biographies and autobiographies, and his own introspection. The sample is Feynman, Fermi, Teller, Oppenheimer, Bethe, Shannon, Tukey, Bode, Brattain, Bardeen, Pierce — the people who had already won, at two of the most brutally selected institutions in the history of science. This is textbook survivorship bias.
And the best thing about the talk is that Hamming says so himself, on stage. Asked whether the effort is worth it, he answers that the people who did it all say yes — and then dismantles his own answer:
But it is a limited survey. I have never dared to go out and ask those who didn't do great work how they felt about the matter. It's a biased sample, but I still think it is worth the struggle.— Richard Hamming, You and Your Research, 1986
He names the flaw in his own argument and keeps going. That is part of why the talk has outlived almost all comparable advice: it is hard to attack with a hole it did not concede first.
PARTLY HELD UP · as of 2026-09
“A problem is important when you have an attack on it” and “luck favours the prepared” were later restated by scientometrics with startling precision. But his claim about age had already expired the year he made it, his most popular line — a little more work doubles a lifetime’s output — still has no evidence behind it, and even the “stable individual ability” half has been reproduced by a model containing nothing but luck.
2007: the lunch-table sermon entered the peer-reviewed literature. Thomas Erren, Paul Cullen, Michael Erren and Philip Bourne published “Ten Simple Rules for Doing Your Best Research, According to Hamming” in PLoS Computational Biology, with a blunt motive: the 1986 talk “was never formally published, so that Dr. Hamming’s thoughts are not as widely known as they deserve to be.” Rule 3 is “Age Is Important.” Rule 10 is “Leave Your Door Open.” The authors also flag what they are handing over: the rules are “somewhat philosophical and behavioural rather than concrete suggestions for how to tackle a particular scientific professional activity.”
2011: rule 3 fell over. Benjamin Jones and Bruce Weinberg, in PNAS, sorted all 525 Nobel Prizes awarded between 1901 and 2008 (182 in physics, 153 in chemistry, 190 in medicine) by the age at which the prize-winning work was done. The finding is that Hamming’s impression of the “disgustingly young” quantum mechanics generation was a snapshot of one cohort. In physics, the share of prize-winning work completed before age 30 peaked in 1923 at 31%; the share completed before 40 peaked in 1934 at 78% — the revolution itself. Before 1905, about two-thirds of laureates across the three fields did their prize work before 40 and about 20% before 30. By 2000, work before 30 “nearly never occurred” in any of the three fields, only 19% of physics work came before 40, and chemistry before 40 had also nearly vanished. Comparing pre-1905 with post-1985, the mean age of prize-winning work rose by 13.4 years in physics, 10.2 in chemistry and 7.4 in medicine. The 2014 review by Jones, Reedy and Weinberg adds two sharper points: variation within a field over time is about five times the variation across fields, and since 1985 physics laureates have been the oldest of the three fields at the moment of contribution, not the youngest. The piece of physics folklore Hamming repeated from the stage in 1986 had been inverted for at least a decade by then.
2016: his central sentence was confirmed almost word for word. Roberta Sinatra, Dashun Wang, Pierre Deville, Chaoming Song and Albert-László Barabási published “Quantifying the evolution of individual scientific impact” in Science, working from the complete publication sequences of 2,887 physicists plus more than ten thousand scientists across seven disciplines with careers of at least twenty years. Their headline result they call the random-impact rule: in the words of the abstract, impact “is distributed randomly within a scientist’s sequence of publications” — your most influential paper is as likely to be your first, your last, or anything in between. But they also extract a parameter Q, standing for how good a given scientist is at turning an idea into a discovery, which stays stable across a career; and the model implies that very high impact needs high Q plus a lucky project, and that raising productivity alone cannot substantially buy you a very high-impact result. Put the two halves together and you have a quantitative restatement of “The particular thing you do is luck, but that you do something is not.”
The same result cuts down his most popular line. “One extra hour a day doubles a lifetime’s output” is a pure productivity lever — precisely the lever the model says will not reach the peak. Hamming wrote “the race is not to the one who works hardest” in the book and said “Just hard work is not enough” on stage. The internet remembers the first half of the sentence.
2021: someone came for the good half of the report card too. M. V. Simkin argued in EPL (134, 48004) that Q may not require talent at all. Upgrade an old random citation-copying model — make the probability of copying a citation proportional to the logarithm of the total citations to all of that author’s papers — and the numerical simulations reproduce a picture similar to the empirical findings behind the Q factor. If he is right, then “stable individual ability” is luck as well, merely luck that has been compounding. The argument is unsettled, but it is enough reason not to read the 2016 paper as a verdict in Hamming’s favour.
As for the talk’s real afterlife: it did not become a hypothesis, it became a ritual. The question — what are the important problems in my field, and why am I not working on them — has been extracted and circulated on its own as a periodic self-examination in research groups, among graduate students, in rationalist communities; Paul Graham hosts the transcript on his own site. What almost nobody carries along is the other half: the ten percent of the week, the neglected wife, the deliberately correct clothes, and the biased sample he admitted to.
One last thing, which he said first. On stage he pronounced sentence on Shannon. “In fact when he left Bell Labs, I said, ‘That’s the end of Shannon’s scientific career.’” Friends objected that Shannon was as smart as ever, and he agreed — “Yes, he’ll be just as smart, but that’s the end of his scientific career,” he told them, “and I truly believe it was.” Shortly before retiring from the Naval Postgraduate School in 1997, he passed the same sentence on himself — he said that when he left Bell Labs he knew that was the end of his research career, and that the real end would come when he stopped teaching. He taught through December 1997. He died of a heart attack on 7 January 1998.