Based on the other comments, I feel like it is worthwhile to point out that Hamming is talking about how to be a successful scientist, as measured by things like promotions, publications, and reputation.
He is not talking about the impact of the problems themselves. From the quoted section, emphasis mine:
It’s not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important. When I say that most scientists don’t work on important problems, I mean it in that sense.
So it looks like we’re trying to apply the question one entire step before where Hamming did. For example there weren’t—and if I read Hamming right, still aren’t—reasonable attacks to the alignment problem. The prospective consequences are just so great we had to consider what is reasonable in a relative sense, and try anyway.
It feels like rationality largely boils down to the search for a generative rule for reasonable attacks.
This doesn’t quite feel right to me. From another section:
Age is another factor which the physicists particularly worry about. They always are saying that you have got to do it when you are young or you will never do it. Einstein did things very early, and all the quantum mechanic fellows were disgustingly young when they did their best work. Most mathematicians, theoretical physicists, and astrophysicists do what we consider their best work when they are young. It is not that they don’t do good work in their old age but what we value most is often what they did early. On the other hand, in music, politics and literature, often what we consider their best work was done late. I don’t know how whatever field you are in fits this scale, but age has some effect.
But let me say why age seems to have the effect it does. In the first place if you do some good work you will find yourself on all kinds of committees and unable to do any more work. You may find yourself as I saw Brattain when he got a Nobel Prize. The day the prize was announced we all assembled in Arnold Auditorium; all three winners got up and made speeches. The third one, 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.” Well I said to myself, “That is nice.” But in a few weeks I saw it was affecting him. Now he could only work on great problems.
So this is clearly not about professional success, because he points to professional success as a thing that kills the kind of greatness he’s trying to cultivate in people.
My impression is that he was genuinely pointing at “important” meaning “things that will have an impact”, just that tractability matters as much as as importance-if-you-solve-the-problem, which is why “teleportation” isn’t a good project.
He points to thinking about the important problems as causing success. When people change what they are doing, then they don’t continue to have it:
In the first place if you do some good work you will find yourself on all kinds of committees and unable to do any more work.
Carrying on from the end of your section:
When you are famous it is hard to work on small problems. This is what did Shannon in. After information theory, what do you do for an encore? The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow. They try to get the big thing right off. And that isn’t the way things go. So that is another reason why you find that when you get early recognition it seems to sterilize you. In fact I will give you my favorite quotation of many years. The Institute for Advanced Study in Princeton, in my opinion, has ruined more good scientists than any institution has created, judged by what they did before they came and judged by what they did after. Not that they weren’t good afterwards, but they were superb before they got there and were only good afterwards.
The talk is about things that cause people to do great work. When those causal factors change, the work output also changes. He goes on to cover other things which are about professional success:
Working with an open office door, to talk to your coworkers
Changing routine work into more general and important work, which is more satisfying
The importance of self-promotion
Working on presentation skills
How to recruit your boss to fight with outside agencies
How to get your boss to give you more resources
Dressing for success, and getting punished for non-conformity
Lastly, he is pretty specific about his motivations (emphasis mine):
I think it is very definitely worth the struggle to try and do first-class work because the truth is, the value is in the struggle more than it is in the result. The struggle to make something of yourself seems to be worthwhile in itself. The success and fame are sort of dividends, in my opinion.
So he is specifically talking about professional success in science. But—things like the rationality project and EA are good candidates for other fields to which the advice could be applied, especially in light of how important science is to them.
I agree that Hamming is talking about how to be a successful scientist, but I think “as measured by things like promotions, publications, and reputation” gives the wrong impression: that Hamming’s talking about how to optimize for personal success as opposed to overall impact. But the “have a reasonable attack” criterion is necessary for optimizing impact on the world, too, and I don’t think Hamming would have changed his advice if he’d been convinced that (e.g.) the way to maximize promotions, publications, and reputation is to get better at self-promotion or to falsify your results or something.
I think that personal success is the correct impression:
I noticed a couple of months later he was made the head of the department. I noticed the other day he was a Member of the National Academy of Engineering. I noticed he has succeeded. I have never heard the names of any of the other fellows at that table mentioned in science and scientific circles.
Notice he doesn’t talk about all the amazing things that were solved; he talks about lab positions and Nobel Prizes and getting equations named after himself.
I expect that Hamming would view having an impact on the world as being a good reason to choose going into science instead of law or finance, but once that choice is made being great at science is the reasonable thing to do.
To be clear, I don’t think he viewed reputations and promotions as the goal, I believe he viewed them as reasonable metrics that he was on the right track for doing great science.
Rereading the original text, I think he is talking about all three of (1) doing something that has a substantial impact on the world, (2) doing something that brings you major career success, and (3) doing something that turns you into a better scientist and a better person. (The last of those is mostly not very apparent in what he says, but there’s this: “I think it is very definitely worth the struggle to try and do first-class work because the truth is, the value is in the struggle more than it is in the result. The struggle to make something of yourself seems to be worthwhile in itself. The success and fame are sort of dividends, in my opinion.”)
Based on the other comments, I feel like it is worthwhile to point out that Hamming is talking about how to be a successful scientist, as measured by things like promotions, publications, and reputation.
He is not talking about the impact of the problems themselves. From the quoted section, emphasis mine:
So it looks like we’re trying to apply the question one entire step before where Hamming did. For example there weren’t—and if I read Hamming right, still aren’t—reasonable attacks to the alignment problem. The prospective consequences are just so great we had to consider what is reasonable in a relative sense, and try anyway.
It feels like rationality largely boils down to the search for a generative rule for reasonable attacks.
This doesn’t quite feel right to me. From another section:
So this is clearly not about professional success, because he points to professional success as a thing that kills the kind of greatness he’s trying to cultivate in people.
My impression is that he was genuinely pointing at “important” meaning “things that will have an impact”, just that tractability matters as much as as importance-if-you-solve-the-problem, which is why “teleportation” isn’t a good project.
I read this section completely differently.
He points to thinking about the important problems as causing success. When people change what they are doing, then they don’t continue to have it:
Carrying on from the end of your section:
The talk is about things that cause people to do great work. When those causal factors change, the work output also changes. He goes on to cover other things which are about professional success:
Working with an open office door, to talk to your coworkers
Changing routine work into more general and important work, which is more satisfying
The importance of self-promotion
Working on presentation skills
How to recruit your boss to fight with outside agencies
How to get your boss to give you more resources
Dressing for success, and getting punished for non-conformity
Lastly, he is pretty specific about his motivations (emphasis mine):
So he is specifically talking about professional success in science. But—things like the rationality project and EA are good candidates for other fields to which the advice could be applied, especially in light of how important science is to them.
I agree that Hamming is talking about how to be a successful scientist, but I think “as measured by things like promotions, publications, and reputation” gives the wrong impression: that Hamming’s talking about how to optimize for personal success as opposed to overall impact. But the “have a reasonable attack” criterion is necessary for optimizing impact on the world, too, and I don’t think Hamming would have changed his advice if he’d been convinced that (e.g.) the way to maximize promotions, publications, and reputation is to get better at self-promotion or to falsify your results or something.
I think that personal success is the correct impression:
Notice he doesn’t talk about all the amazing things that were solved; he talks about lab positions and Nobel Prizes and getting equations named after himself.
I expect that Hamming would view having an impact on the world as being a good reason to choose going into science instead of law or finance, but once that choice is made being great at science is the reasonable thing to do.
To be clear, I don’t think he viewed reputations and promotions as the goal, I believe he viewed them as reasonable metrics that he was on the right track for doing great science.
Rereading the original text, I think he is talking about all three of (1) doing something that has a substantial impact on the world, (2) doing something that brings you major career success, and (3) doing something that turns you into a better scientist and a better person. (The last of those is mostly not very apparent in what he says, but there’s this: “I think it is very definitely worth the struggle to try and do first-class work because the truth is, the value is in the struggle more than it is in the result. The struggle to make something of yourself seems to be worthwhile in itself. The success and fame are sort of dividends, in my opinion.”)