Why Not Games




Notes on "You And Your Research" by Richard Hamming

This is a talk by Richard Hamming about doing Nobel Prize worthy research. You can and should read the entire transcript of the talk here - https://www.cs.virginia.edu/~robins/YouAndYourResearch.html

Notes

  • The first step is to accept that you want to be great.
  • Luck favors the prepared mind. The prepared mind sooner or later finds something important & does it. The particular thing you do is luck, but that you do something is not.
  • Great Scientists had independent thoughts when they were young and the courage to pursue them. Successful scientists have courage.
  • The mistake that great scientists make is that once you get the Nobel, you feel like you can only work on great problems.
  • They fail to plant the little acorns from which oak trees grow.
  • Constraints force clever solutions and so are some of greatest assets you can have.
    • The working conditions you want aren't always the ones that are best for you.
  • All great scientists have tremendous drive.
    • An extra hour every day compounds.
    • Drive misapplied gets you nowhere.
  • Great Scientists tolerate ambiguity well. They believe the theory enough to go ahead and doubt it enough to notice the faults.
    • Darwin would note down every piece of evidence that contradicted his beliefs.
    • Great contributions come from finding the flaws.
    • It comes down to an emotional commitment.
    • Starve your subconscious so that it has to work on the problem.
  • What are the important problems in my field?
    • If you do not work on an important problem, it is unlikely that you'll do important work.
    • 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.
    • They never worked on time travel, teleportation or antigravity at Bell Labs though. They are not important problems because we do not have an attack.
    • It's not just the consequence that makes a problem important, it is that you have a reasonable attack.
    • You can't always know exactly where to be, but you can keep active in places where something might happen.
    • The average scientist does safe, routine work almost all the time and so doesn't produce much.
  • He adopted great thoughts time. When he went to lunch Friday noon, he would only discuss great thoughts after that.
    • Eg; "What will be the role of computers in all of AT&T?" and "How will computers change science."
    • He saw that 9/10 experiments were done in the lab and 1/10 on the computer and remarked to a vice president that it would be reversed in the future.
  • Most Great Scientists have between 10 and 20 important problems for which they are looking for an attack and when they see a new idea come up, they say "Well that bears on this problem." They drop all the other things and get after it.
  • If you work with the door closed, you're more productive in a day-to-day sense, but it is the people with open doors who find important problems and so do important work.
  • When Hamming did a problem on a digital computer that the analog ones couldn't do, he knew that it was a bit deal.
    • He realized that every analog installation was going to look through the file that he wrote to try to find flaws in it.
    • He saw that the required integration was done with a crummy method which worked but was inelegant.
    • So, he reworked the method of solution and created an elegant theory and changed the computation method.
    • By changing the problem slightly, he was able to do important work instead of trivial work.
    • Similarly, he said that instead of solving one problem after another, he saw that he should be concerned with the mass production of a variable product. He needed to be concerned with all of next year's problems, not just the ones in front of his face.
    • By changing the question, he still got the same kind of result, but also changed things and did important work.
    • You need to do your job in such a fashion that others can build on top of it.
    • He made the resolution to never again solve an isolated problem except as a characteristic of a class.
    • It isn't just a matter of the job, it's the way you write the report, the way you write the paper, the whole attitude. It's just as easy to do a broad, general job as one very special case and it's much more satisfying and rewarding.
  • It's insufficient to do the a job, you have to sell it.
    • It's ugly and it's not ideal but it's necessary to get people to see your work.
    • You have to learn to write clearly and well.
    • You have to learn to give reasonably formal talks.
    • You have to learn to give informal talks.
    • Technical people want to give highly limited technical talks but the audience typically wants more broad and general talks. This makes many talks ineffective.
    • The tendency is to give highly restricted, safe talks, but this is usually ineffective.
    • Furthermore, many talks are filled with far too much information.
  • It's worth the struggle to try and do first class work because the value is in the struggle more than it is in the result.
  • Good people almost always turn out good work, but outstanding work requires drive and commitment.
  • If you fight the system, you will go no farther than you can go single-handedly. If you work with the system, you can go as far as it will support you.
    • Who do you want to be, the person who changes the system or the person who does first-class work?
  • If you read all the time what other people have done you will think the way they thought. Get the problem reasonably clear and then refuse to look at any answers until you've thought the problem through carefully.
    • You need to read more to find out what the problems are than to find the solutions.
    • You read, but it is not the amount, it is the way you read that counts.
  • If you want to be a great researcher, you won't make it being president of the company.

Further Thinking For Me

  • Think about how constraints force clever solutions with graphics for your games.
  • What are the important problems in video games?
  • How do I set up time for discussing great thoughts? What does that entail?
  • My mistake with The Quiet Sleep may have been that I did it in a way that was not persuasive and so it ended up trivial instead of important.
  • What is the system here and how can I use it to support my work?

- @murthynikhil

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