Youand Your
Research—
A talk byRichard W. Hamming—
Bellcore,
7 March
1986

4

You
and Your
Research—
A talk byRichard W. Hamming—
Bellcore,
7 March
1986

5

6

“You and Your Research” is one of Richard Hamming’s many lectures.
In 1996, he published a write-up of his graduate course lectures inengineering at the U.S. Naval Postgraduate School in a book called The
Art of Doing Science and Engineering; Learning to Learn. In Hamming’s
words, “the course centers around how to look at and think aboutknowledge,” and is an extension of the wisdom of “You and Your
Research.” The book was republished this year, with a foreword fromBret Victor, by Stripe Press.

7—You and Your Research­[START]

I have given a talk with this title many times, and it turns out from discussions after the talk I could have just as well have called it “You and YourEngineering Career,” or even “You and Your Career.” But I left the word“research” in the title because that is what I have most studied.
From the previous chapters you have an adequate background for how I
made the study, and I need not mention again the names of the famous
people I have studied closely. The earlier chapters are, in a sense, just agreat expansion, with much more detail, of the original talk. This chapter
is, in a sense, a summary of the previous 29 chapters.

8

Why do I believe this talk is important? It is important because as far as I
know each of you has but one life to lead, and it seems to me it is better todo significant things than to just get along through life to its end.
Certainly near the end it is nice to look back at a life of accomplishments
rather than a life where you have merely survived and amused yourself.
Thus in a real sense I am preaching the messages that (1) it is worth
trying to accomplish the goals you set yourself and (2) it is worth setting
yourself high goals.
Again, to be convincing to you I will talk mainly about my own
experience, but there are equivalent stories I could use involving others. I
want to get you to the state where you will say to yourself, “Yes, I would
like to do first-class work. If Hamming could, then why not me?” Oursociety frowns on those who say this too loudly, but I only ask you say it
to yourself! What you consider first-class work is up to you; you must pickyour goals, but make them high!
I will start psychologically rather than logically. The major objection
cited by people against striving to do great things is the belief that it is alla matter of luck. I have repeatedly cited Pasteur’s remark, “Luck favors the
prepared mind.” It both admits there is an element of luck and yet claims
to a great extent it is up to you. You prepare yourself to succeed or not, as
you choose, from moment to moment by the way you live your life.
As an example related to the “luck” aspect, when I first came to Bell Telephone Laboratories I shared an office with Claude Shannon. At about thesame time, he created information theory and I created coding theory. They
were “in the air,” you can say, and you are right. Yet why did we do it andthe others who were also there not do it? Luck? Some, perhaps, but also9

because we were what we were and the others were what they were. The
differences were we were more prepared to find, work on, and create thecorresponding theories.
If it were mainly luck, then great things should not tend to be done repeatedly by the same people. Shannon did a lot of important things besides information theory—his master’s thesis was applying Boolean algebra to switching circuits! Einstein did many great things, not just one or
two. For example, when he was around 12–14 years old, he asked himself
what light would look like if he went at the velocity of light. He would,
apparently, see a local peak, yet the corresponding mathematical equations would not support a stationary extreme! An obvious contradiction!
Is it surprising he later discovered special relativity, which was in the air
and which many people were working on at that time? He had preparedhimself long ago, by that early question, to understand better than theothers what was going on and how to approach it.

10

Newton observed that if others would think as hard as he did, then theywould be able to do the same things. Edison said genius was 99%
perspiration and 1% inspiration. It is hard work, applied for long years,
which leads to the creative act, and it is rarely just handed to you without
any serious effort on your part. Yes, sometimes it just happens, and then it
is pure luck. It seems to me to be folly for you to depend solely on luck forthe outcome of this one life you have to lead.
One of the characteristics you see is that great people when young weregenerally active—though Newton did not seem exceptional until well into
his undergraduate days at Cambridge, Einstein was not a great student,
and many other great people were not at the top of their class.
Brains are nice to have, but many people who seem not to have great IQs
have done great things. At Bell Telephone Laboratories Bill Pfann walked
into my office one day with a problem in zone melting. He did not seem tome, then, to know much mathematics, to be articulate, or to have a lot ofclever brains, but I had already learned brains come in many forms andflavors, and to beware of ignoring any chance I got to work with a goodman. I first did a little analytical work on his equations, and soon realized
what he needed was computing. I checked up on him by asking around in
his department, and I found they had a low opinion of him and his idea forzone melting. But that is not the first time a person has not been appreciatedlocally, and I was not about to lose my chance of working with a greatidea—which is what zone melting seemed to me, though not to his own
department! There is an old saying: “A prophet is without honor in his
own country.” Mohammed fled from his own city to a nearby one, andthere got his first real recognition!
So I helped Bill Pfann, taught him how to use the computer, how to getnumerical solutions to his problems, and let him have all the machine time
he needed. It turned out zone melting was just what we needed to purify
materials for transistors, for example, and it has proved to be essential inmany areas of work. He ended up with all the prizes in the field, much
more articulate as his confidence grew, and the other day I found his old
lab is now a part of a national monument! Ability comes in many forms,
and on the surface the variety is great; below the surface there are many
common elements.
Having disposed of the psychological objections of luck and the lack ofhigh-IQ-type brains, let us go on to how to do great things. Among theimportant properties to have is the belief you can do important things. If
you do not work on important problems, how can you expect to do important work? Yet direct observation and direct questioning of people show
most scientists spend most of their time working on things they believe are
not important and are not likely to lead to important things.
As an example, after I had been eating for some years with the physics
table at the Bell Telephone Laboratories restaurant, fame, promotion, andhiring by other companies ruined the average quality of the people, so I
shifted to the chemistry table in another corner of the restaurant. I began
by asking what the important problems were in chemistry, then later what
important problems they were working on, and finally one day said, “Ifwhat you are working on is not important and not likely to lead toimportant things, then why are you working on it?” After that I was not
welcome and had to shift to eating with the engineers! That was in thespring, and in the fall one of the chemists stopped me in the hall and said,“What you said caused me to think for the whole summer about what theimportant problems are in my field, and while I have not changed myresearch it was well worth the effort.” I thanked him and went on—and
noticed in a few months he was made head of the group. About ten years
ago I saw he became a member of the National Academy of Engineering.
No other person at the table did I ever hear of, and no other person wascapable of responding to the question I had asked: “Why are you notworking on and thinking about the important problems in your area?” If
you do not work on important problems, then it is obvious you have little
chance of doing important things.
Confidence in yourself, then, is an essential property. Or, if you want to,
you can call it “courage.” Shannon had courage. Who else but a man withalmost infinite courage would ever think of averaging over all random
codes and expect the average code would be good? He knew what he wasdoing was important and pursued it intensely. Courage, or confidence, is aproperty to develop in yourself. Look at your successes, and pay lessattention to failures than you are usually advised to do in the expression,“Learn from your mistakes.” While playing chess Shannon would often
advance his queen boldly into the fray and say, “I ain’t scared of nothing.” I

11learned to repeat it to myself when stuck, and at times it has enabled me to
go on to a success. I deliberately copied a part of the style of a great scientist.
The courage to continue is essential, since great research often has long
periods with no success and many discouragements.
The desire for excellence is an essential feature for doing great work.
Without such a goal you will tend to wander like a drunken sailor. The
sailor takes one step in one direction and the next in some independent
direction. As a result the steps tend to cancel each other out, and the
expected distance from the starting point is proportional to the square rootof the number of steps taken. With a vision of excellence, and with the goalof doing significant work, there is a tendency for the steps to go in the same
direction and thus go a distance proportional to the number of steps taken,
which in a lifetime is a large number indeed. As noted before, Chapter 1,
the difference between having a vision and not having a vision is almost
everything, and doing excellent work provides a goal which is steady in thisworld of constant change.

12

Age is a factor physicists and mathematicians worry about. It is easily
observed that the greatest work of a theoretical physicist, mathematician,or astrophysicist is generally done very early. They may continue to dogood work all their lives, but what society ends up valuing most is almost
always their earliest great work. The exceptions are very, very few indeed.
But in literature, music composition, and politics, age seems to be an asset.
The best compositions of a composer are usually the late ones, as judged
by popular opinion. One reason for this is that fame in science is a curse
to quality productivity, though it tends to supply all the tools and freedom
you want to do great things. Another reason is that most famous people,
sooner or later, tend to think they can only work on important problems—
hence they fail to plant the little acorns which grow into the mighty oaktrees. I have seen it many times, from Brattain of transistor fame and aNobel Prize to Shannon and his information theory. Not that you should
merely work on random things, but on small things which seem to you tohave the possibility of future growth. In my opinion the Institute forAdvanced Study at Princeton has ruined more great scientists than any
other place has created—considering what they did before and what they
did after going there. A few, like von Neumann, escaped the closed
atmosphere of the place, with all its physical comforts and prestige, andcontinued to contribute to the advancement of science, but most remained
there and continued to work on the same problems which got them there
but which were generally no longer of great importance to society.
Thus what you consider to be good working conditions may not be goodfor you! There are many illustrations of this point. For example, working
with one’s door closed lets you get more work done per year than if you
had an open door, but I have observed repeatedly that later those withthe closed doors, while working just as hard as others, seem to work onslightly the wrong problems, while those who have let their door stay
open get less work done but tend to work on the right problems! I cannot
prove the cause-and-effect relationship; I can only observed the correlation. I suspect the open mind leads to the open door, and the open door
tends to lead to the open mind; they reinforce each other.
A similar story from my own experience. In the early days of programming
computers in absolute binary, the usual approach was usually through an“acre of programmers.” It was soon evident to me that Bell Telephone
Laboratories would never give me an acre of programmers. What to do? I
could go to a West Coast airframe manufacturer and get a job and have theproverbial acre, but Bell Telephone Laboratories had a fascinating collectionof great people from whom I could learn a lot, and the airframe
manufacturers had relatively fewer such people. After quite a few weeks ofwondering what to do I finally said to myself, “Hamming, you believemachines can do symbol manipulation. Why not get them to do the detailsof the programming?” Thus I was led directly to a frontier of computerscience by simply inverting the problem. What had seemed to be a defectnow became an asset and pushed me in the right direction! Grace Hopper
had a number of similar stories from computer science, and there are manyother stories with the same moral: When stuck, often inverting the problem
and realizing the new formulation is better represents a significant step
forward. I am not asserting all blockages can be so rearranged, but I am
asserting that many more than you might at first suspect can be so changed
from a more or less routine response to a great one.
This is related to another aspect of changing the problem. I was once solving
on a digital computer the first really large simulation of a system ofsimultaneous differential equations, which at that time were the naturalproblem for an analog computer—but they had not been able to do it, andI was doing it on an IBM 701. The method of integration was an adaptationof the classical Milne’s method, and it was ugly to say the least. I suddenly
realized that of course, being a military problem, I would have to file a reporton how it was done, and every analog installation would go over it trying to
object to what was actually being proved as against just getting the answers—I
was showing convincingly that on some large problems, the digital computer
could beat the analog computer on its own home ground. Realizing this, I
realized the method of solution should be cleaned up, so I developed a new
method of integration which had a nice theory, changed the method on themachine with a change of comparatively few instructions, and then computed
the rest of the trajectories using the new formula. I published the new
method and for some years it was in wide use and known as “Hamming’s
method.” I do not recommend the method now that further progress has
been made and the computers are different. To repeat the point I am making,
I changed the problem from just getting answers to the realization I wasdemonstrating clearly for the first time the superiority of digital computersover the current analog computers, thus making a significant contribution

13

to the science behind the activity of computing answers.
All these stories show that the conditions you tend to want are seldom thebest ones for you—the interaction with harsh reality tends to push you
into significant discoveries which otherwise you would never have thought
about while doing pure research in a vacuum of your private interests.
Now to the matter of drive. Looking around, you can easily observe that
great people have a great deal of drive to do things. I had worked with John
Tukey for some years before I found he was essentially my age, so I went toour mutual boss and asked him, “How can anyone my age know as much
as John Tukey does?” He leaned back, grinned, and said, “You would be
surprised how much you would know if you had worked as hard as he hasfor as many years.” There was nothing for me to do but slink out of his
office, which I did. I thought about the remark for some weeks and decided
that while I could never work as hard as John did, I could do a lot better
than I had been doing.

14

In a sense my boss was saying intellectual investment is like compoundinterest: the more you do, the more you learn how to do, so the more you
can do, etc. 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. The steady application of a bit more
effort has a great total accumulation.
But be careful—the race is not to the one who works hardest! You need towork on the right problem at the right time and in the right way—what I
have been calling “style.” At the urging of others, for some years I set aside
Friday afternoons for “great thoughts.” Of course, I would answer the
telephone, sign a letter, and such trivia, but essentially, once lunch started,
I would only think great thoughts—what was the nature of computing,
how would it affect the development of science, what was the natural roleof computers in Bell Telephone Laboratories, what effect will computers
have on AT&T, on science generally? I found it was well worth the 10% of
my time to do this careful examination of where computing was heading
so I would know where we were going and hence could go in the right
direction. I was not the drunken sailor staggering around and cancelingmany of my steps by random other steps, but could progress in a more orless straight line. I could also keep a sharp eye on the important problems
and see that my major effort went to them.
I strongly recommend taking the time, on a regular basis, to ask the larger
questions, and not stay immersed in the sea of detail where almost
everyone stays almost all of the time. These chapters have regularly stressed
the bigger picture, and if you are to be a leader into the future, rather thana follower of others, I am now saying it seems to me to be necessary for you
to look at the bigger picture on a regular, frequent basis for many years.

There is another trait of great people I must talk about—and it took me along time to realize it. Great people can tolerate ambiguity; they can bothbelieve and disbelieve at the same time. You must be able to believe yourorganization and field of research is the best there is, but also that there ismuch room for improvement! You can sort of see why this is a necessary
trait. If you believe too much, you will not likely see the chances for
significant improvements; if you do not believe enough, you will be filledwith doubts and get very little done, chances are only the 2%, 5%, and
10% improvements. I have not the faintest idea of how to teach thetolerance of ambiguity, both belief and disbelief at the same time, but great
people do it all the time.
Most great people also have 10 to 20 problems they regard as basic and ofgreat importance, and which they currently do not know how to solve.
They keep them in their mind, hoping to get a clue as to how to solve
them. When a clue does appear they generally drop other things and get towork immediately on the important problem. Therefore they tend to comein first, and the others who come in later are soon forgotten. I must warn
you, however, that the importance of the result is not the measure of theimportance of the problem. The three problems in physics—anti-gravity,
teleportation, and time travel—are seldom worked on because we have so
few clues as to how to start. A problem is important partly because there isa possible attack on it and not just because of its inherent importance.
There have been a number of times in this book when I came close to thepoint of saying it is not so much what you do as how you do it. I just told
you about the changing of the problem of solving a given set of differential
equations on an analog machine to doing it on a digital computer,changing programming from an acre of programmers to letting themachine do much of the mechanical part, and there are many similar
stories. Doing the job with “style” is important. As the old song says, “It
ain’t what you do, it’s the way that you do it.” Look over what you havedone, and recast it in a proper form. I do not mean give it false importance,
nor propagandize for it, nor pretend it is not what it is, but I do say that bypresenting it in its basic, fundamental form, it may have a larger range ofapplication than was first thought possible.
Again, you should do your job in such a fashion that others can build on
top of it. Do not in the process try to make yourself indispensable; if you
do, then you cannot be promoted, because you will be the only one who
can do what you are now doing! I have seen a number of times where thisclinging to the exclusive rights to the idea has in the long run done much
harm to the individual and to the organization. If you are to get recognition then others must use your results, adopt, adapt, extend, and elaborate
them, and in the process give you credit for it. I have long held the attitudeof telling everyone freely of my ideas, and in my long career I have had
only one important idea “stolen” by another person. I have found people15

are remarkably honest if you are in your turn.
It is a poor workman who blames his tools. I have always tried to adopt
the philosophy that I will do the best I can in the given circumstances,
and after it is all over maybe I will try to see to it that things are better
next time. This school is not perfect, but for each class I try to do as wellas I can and not spend my effort trying to reform every small blemish in
the system. I did change Bell Telephone Laboratories significantly, but did
not spend much effort on trivial details. I let others do that if they wanted
to—but I got on with the main task as I saw it. Do you want to be a reformer of the trivia of your old organization or a creator of the new organization? Pick your choice, but be clear which path you are going down.
I must come to the topic of “selling” new ideas. You must master three
things to do this (Chapter 5):
1. Giving formal presentations,
2. Producing written reports, and
3. Mastering the art of informal presentations as they happen to occur.

16

All three are essential—you must learn to sell your ideas, not by propaganda,
but by force of clear presentation. I am sorry to have to point this out;
many scientists and others think good ideas will win out automatically andneed not be carefully presented. They are wrong; many a good idea has
had to be rediscovered because it was not well presented the first time,years before! New ideas are automatically resisted by the establishment,
and to some extent justly. The organization cannot be in a continual stateof ferment and change, but it should respond to significant changes.
Change does not mean progress, but progress requires change.
To master the presentation of ideas, while books on the topic may bepartly useful, I strongly suggest you adopt the habit of privately critiquing
all presentations you attend and also asking the opinions of others. Try
to find those parts which you think are effective and which also can beadapted to your style. And this includes the gentle art of telling jokes attimes. Certainly a good after-dinner speech requires three well-told jokes:
one at the beginning, one in the middle to wake them up again, and thebest one at the end so they will remember at least one thing you said!
You are likely to be saying to yourself you have not the freedom to work on
what you believe you should when you want to. I did not either for many
years—I had to establish the reputation on my own time that I could doimportant work, and only then was I given the time to do it. You do nothire a plumber to learn plumbing while trying to fix your trouble; you
expect he is already an expert. Similarly, only when you have developed
your abilities will you generally get the freedom to practice your expertise,whatever you choose to make it, including the expertise of “universality,”
as I did. I have already discussed the gentle art of educating your bosses,
so I will not go into it again. It is part of the job of those who are going torise to the top. Along the way you will generally have superiors who areless able than you are, so do not complain, since how else could it be if you
are going to end up at the top and they are not?
Finally, I must address the topic of whether the effort required for excellence
worth it. I believe it is—the chief gain is in the effort to change yourself, inthe struggle with yourself, and it is less in the winning than you might
expect. Yes, it is nice to end up where you wanted to be, but the person you
are when you get there is far more important. I believe a life in which you
do not try to extend yourself regularly is not worth living—but it is up to
you to pick the goals you believe are worth striving for. As Socrates (469–399 BC) said,
The unexamined life is not worth living.
In summary: as I claimed at the start, the essence of the book is “style,”
and there is no real content in the form of the topics like coding theory,
filter theory, or simulation that were used for examples. I repeat: the content of these chapters is “style” of thinking, which I have tried to exhibit
in many forms. It is your problem to pick out those parts you can adapt
to your life as you plan it to be. A plan for the future, I believe, is essential for success, otherwise you will drift like the drunken sailor throughlife and accomplish much less than you could otherwise have done.
In a sense, this has been a course a revivalist preacher might have given—
repent your idle ways, and in the future strive for greatness as you see it. I
claim it is generally easier to succeed than it at first seems! It seems to me atalmost all times there is a halo of opportunities about everyone from which
to select. It is your life you have to live, and I am only one of many possible
guides you have for selecting and creating the style of the one life you haveto live. Most of the things I have been saying were not said to me; I had to
discover them for myself. I have now told you in some detail how to succeed,
hence you have no excuse for not doing better than I did. Good luck!

[EN D]

17

—Richard W. Hamming
11 February, 1915 –7 January, 1998

18

BIO G R APH Y

Richard Hamming was born in Chicago, Illinois, USA on February 11,
1915, the son of Richard J. Hamming and Mabel G. Redfield. He wasbrought up in Chicago where he attended school and realized that he was amore able mathematician than his teacher. He wanted to study engineering
but the only offer of a scholarship came from the University of Chicago,
which had no engineering department. He entered the University of
Chicago receiving his B.S. in mathematics.
After his undergraduate studies he went to the University of Nebraska,
where he was awarded an M.A. in 1939. He received a Ph.D. in mathematics in 1942 from the University of Illinois at Urbana-Champaign. His doctoral dissertation, Some Problems in the Boundary Value Theory of Linear
Differential Equations, was supervised by Waldemar Trjitzinsky (19011973). Hamming, however, developed interests in ideas that were quite far
removed from his study of differential equations when he discovered George
Boole’s An Investigation of the Laws of Thought. He found Boole’s book interesting, relevant, and believable. The ideas in it would prove highly significant later in his life when he became interested in coding theory.
After earning his doctorate, Hamming married Wanda Little on
September 5, 1942. He taught first at the University of Illinois, and then at
the J.B. Speed Scientific School of the University of Louisville. In 1945,
encouraged by a friend, he joined the Manhattan Project, a U.S. government research project to produce an atomic bomb at Los Alamos, New
Mexico. A month after he arrived at Los Alamos he was joined by his wife,
who was also employed on the Manhattan Project. Hamming was put incharge of the IBM calculating machines that played a vital role in the project. He came in contact with many leading scientists, including Richard
Feynman, Enrico Fermi, Edward Teller and J. Robert Oppenheimer. The
theoretical physicist Hans Bethe was his boss. Wanda Hamming began by
doing computations with desk calculators, and later worked for Enrico
Fermi and Edward Teller.
After the Manhattan Project ended Hamming remained at Los Alamos for
six months, writing up details of the calculations they had done. He feltthat it was important to try to understand exactly what had been achieved,
and why it had been so successful. It was at this time that he realized that hehad done the right thing by not studying engineering; engineers did much of
the routine work, but mathematicians like himself were more critical to the
cutting edge innovations. He formed a view of mathematics, arising fromhis Los Alamos experience, that computation was of major importance, but

19

it made him skeptical of the standard approach that emphasized formal abstract mathematical theories.
In 1946 he accepted a position in the mathematics department at the Bell
Telephone Laboratories in New Jersey. However, he didn’t entirely breakhis link with Los Alamos Scientific Laboratories, and made two week visitseach summer as a consultant.

20

At Bell Labs he was able to work with both Claude Shannon, with whom
he shared an office, and John Tukey. Some other young mathematicians
had joined the Mathematical Research Department at Bell Labs just priorto Hamming. These included Donald Percy Ling and Brockway
McMillan, who had been at Los Alamos at the same time as Hamming.
Shannon, Ling, McMillan and Hamming called themselves the Young
Turks. Hamming often related how they had all been affected by growing
up in the depression, and all learned new skills with their war work. It led
them, he said, to do unconventional things in unconventional ways.
Hamming, for example, lunched with the physics group rather than hismathematics group, and they were fascinated by his unorthodox ideas andviews. Not all his colleagues were happy to tolerate his unconventional
ways. Some have described him as egotistical, saying he sometimes went
off “half-cocked, after some half-baked idea.” Unconventional ideas sometimes produce flashes of brilliance, but they sometimes also lead to
failures.
Before discussing Hamming’s highly significant work on error-correcting
codes, we first note the many and varied problems he worked on in Bell
Labs. These include problems involving design of telephone systems, traveling wave tubes, the equalization of television transmission lines, the stability of complex communication systems, and the blocking of calls
through a telephone central office. He continued to work for Bell
Telephones until 1976, although he became increasingly interested inteaching, and held visiting or adjunct professorships at Stanford
University, the City College of New York, the University of California at
Irvine and Princeton University between 1960 and 1976. After retiringfrom Bell Labs in 1976, he became a professor of computer science at theNaval Postgraduate School at Monterey, California. At this point he gave
up his research career and concentrated on teaching and writing books.
He believed that the way mathematics was being taught was wrong, andthat the only way to change it was to write textbooks with a new approach. Here are two examples of his views on mathematics teaching:
We live in an age of exponential growth in knowledge, and it is increasingly futile to teach only polished theorems and proofs. We must abandon the guided tour through the art gallery of mathematics, and instead
teach how to create the mathematics we need. In my opinion, there is nolong-term practical alternative.

andThe way mathematics is currently taught it is exceedingly dull. In thecalculus book we are currently using on my campus, I found no single
problem whose answer I felt the student would care about! The problems
in the text have the dignity of solving a crossword puzzle—hard to be
sure, but the result is of no significance in life.
His attempt to move to a new way of teaching calculus is exhibited in his
1985 book Methods of Mathematics Applied to Calculus, Probability, andStatistics. He said that the book is “very different from the standard texts
and its success or failure will tell us something about the prospects forchange and innovation.” Other texts he wrote all attempted to change
conventional approaches to the areas they studied.
Richard Hamming is best known for his work at Bell Labs on error-detecting and error-correcting codes. His fundamental paper on this topic,“Error Detecting and Error Correcting Codes”, appeared in April 1950 in
the Bell System Technical Journal. This paper created an entirely new
field within information theory. Hamming codes, Hamming distanceand Hamming metric, standard terms used today in coding theory andother areas of mathematics, all originated in this classic paper and are ofongoing practical use in computer design.
In 1956 Hamming worked on the IBM 650, an early vacuum tube, drum
memory, computer. His work led to the development of a rudimentary
programming language. Hamming also worked on numerical analysis,
especially integration of differential equations. The Hamming spectral
window, still widely used in computation, is a special type of digital filter
designed to pass certain frequencies and discriminate against closely related frequencies.
In addition to the Turing Award, Hamming received many awards forhis pioneering work. He was made a fellow of the Association for
Computing Machinery in 1994. The Institute of Electrical andElectronics Engineers (IEEE) awarded him the Emanuel R Piore Awardin 1979.
The IEEE created “The Richard W. Hamming Medal” in his honor. He
was the first recipient of this $10,000 prize medal in 1988. He was elected a member of the National Academy of Engineering in 1980, and received the Harold Pender Award from the University of Pennsylvania in
1981. In 1996, in Munich, Hamming received the prestigious $130,000
Eduard Rheim Award for Achievement in Technology for his work on
error correcting codes.

21In 1997 Hamming retired from teaching at the Naval Postgraduate
School and was made Distinguished Professor Emeritus. Shortly before
he retired, he said that when he left Bell Labs, he knew that that was theend of his research career. It really would be the end, he said, when he retired from teaching. Indeed he was right, for having taught up to
December 1997, he died of a heart attack in the following month.
Richard Franke of the Naval Postgraduate School at Monterey wrote ofRichard Hamming:
He will be long remembered for his keen insights into many facets ofscience and computation. I’ ll also long remember him for his red
plaid sport coat and his bad jokes.

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