Hamming on important problems
📚SOURCE
💎PERMANENT NOTES
🧵SYNTHESIS
Hamming spent decades at a famous laboratory watching who did work that lasted and who did not, and the lecture is his report. The scientists were about equally clever. The difference he saw was in what they chose to work on, and in a handful of habits around that choice.
The centre of it is a story about a lunch table. He sat with a group from another field and asked them, over some weeks, what the important problems in their field were, then who was working on them, and finally why they themselves were not. He was not welcome at that table for long. One of them, he says, went away and thought about it, and did well afterwards.
His definition of important is narrower than it sounds. A problem is not important because the consequences would be large. It is important if the consequences are large and you have a reasonable attack. So the working scientist keeps a short list of big problems with no way in yet, and drops everything when a way in appears.
Around that: effort compounds like interest, luck favours whoever is prepared, and doubt and commitment have to be held together.
✨KEY IDEAS
Ask what the important problems in your field are, and why you are not working on one.
Importance needs an attack as well as a payoff.
People who work with the door open are interrupted more and, years on, are working on better things.
Knowledge and output grow like compound interest, so a little more effort early ends far ahead.
Doing the work is half. You also have to present it so that others stop and read.
Keep an afternoon a week for thinking about where the field is going.
📝READING NOTES
Paraphrase, not quotation. The 1995 recording of a talk he had been giving, in versions, for a decade. Watched across Friday night and Saturday morning, 26 and 27 September, the case having gone in at 16:10 on the Friday.
An admission about order
📝 Issue 47 - Who chose your important problem went out on the 25th, two days before I watched this. I knew the lunch-table question secondhand, as most people do, and wrote the issue from that. Then I watched the lecture to see whether I had been fair to it. Mostly. The permanent note was written after.
What the full lecture adds to the famous question
- It is about selection, with the effort taken as given. He assumes you work hard. The lecture is about aim.
- Conditions are an excuse. He says the people who wait for ideal conditions do not produce, and that constraints often make the work.
- Convert the obstacle. When he was refused the programmers he wanted, he asked what the refusal implied, and ended up working on getting machines to write programs. I have a Marcus note that says the same in fewer words.
- Emotional commitment matters. The ones who care are the ones whose minds keep at the problem at night.
Turning it on my own roadmap
Honest inventory for the case I had just submitted: most of what I have shipped in five years began as someone else's priority that I then made mine. Good priorities, mostly. But the case reads as a list of things done well, and Hamming would ask who picked them. 📂 Promotion case for Group Product Manager is, underneath, a claim that I can choose.
Where I resist
- He describes a laboratory with patient funding and a culture of choosing one's own problem. Most of us are assigned. The honest version of his question at a company is narrower: of what I could argue for, what matters most?
- The compound-interest passage is true and is also how people talk themselves out of evenings. He says plainly that he neglected his wife. I note that, and 📖 Burkeman on finitude, and keep my shutdown.
- The open door. I think he is right, and I am keeping the two closed mornings anyway.
Became 💎 Important problems are chosen and not assigned. Compare 📖 Drucker on managing oneself: Drucker asks where I belong, Hamming asks what I am for.
Reading record
- Favourite: yes, one of the few I would hand to someone else
🗣️IN SHORT
- In : You and Your Research, lecture, 1995 recording
- Hamming argues that : lasting work comes from deliberately choosing important problems and arranging one's habits around them
- by stating that : able people mostly differ in what they aim at, that a problem is important only if it has both a large payoff and a possible attack, and that effort, openness and presentation compound over a career