The correct response to Hamming’s question is “Because I have a comparative advantage in working on the problem I am working on”. There are many, many important problems in the world of greater and lesser degrees of importance. There are many, many people working on them, even within one field. It does not make sense for everyone to attack the same most important problem, if indeed such a single problem could even be identified. There is a point of diminishing returns. 100 chemists working on the most important problem in chemistry are not going to advance chemistry as much as 10 chemists working on the most important problem, and 90 working on a variety of other, lesser problems.
This point was first made to me by Richard Stallman who told me quite clearly that free software was not the most important problem in the world—I think he cited overpopulation as an example of a more serious problem—but software freedom was the problem he was uniquely well situated to address.
There are seven billion people in the world. I know of no problem that actually needs 7 billion minds to solve it. We are pretty much all well advised to find the biggest problem we have a comparative advantage at, and work on solving that problem. We don’t all have to, indeed we shouldn’t, all work on the same thing.
I’m torn regarding this argument. Aaron Swartz wrote a very nice piece which I can’t find (his personal site now appears to be down) about how working entirely on things that are your current comparative advantage is fixed mindset, and what you could be doing instead is changing what your comparative advantage is. I’m glad that Aaron Swartz did this, and I worry that focusing on comparative advantage gives me an excuse not to branch out. (My current comparative advantage is in mathematics but I’m not convinced that means I should only be spending my life working on mathematics.)
To make my argument clearer, I will use you as an example; please forgive me.
If you have a comparative advantage in maths, and decide to change your comparative advantage to medical, computer, or social science, as soon as you have caught up on the fundamentals of the field necessary to make an informed opinion you will already have a comparative advantage because of your background.
Your proficiency in maths lent you a comparative advantage in maths; your comparative advantage in maths lends you a comparative advantage in [economics]; your comparative advantage in maths and [economics] lends you a comparative advantage in [biochemistry], etcetera.
I think this makes sense. We need to distinguish between something like “obvious current comparative advantage” and “less obvious potential comparative advantage.” In practice, the heuristic “stick to your comparative advantage” may optimize excessively for the former at the expense of the latter.
So in that case, the question is in some ways addressed by narrowing the meaning of “field”.
If a physicist interprets Hamming’s question as “what is the most important problem in your field?” as “what is the most important problem in physics?” then obviously not everyone should be answering it. If, instead, the physicist interprets it as “what is the most important problem in quantum cryptography?”, that being his/her more specific field, then it becomes more reasonable (and more vital!) that the physicist is indeed working on the most important problem in their field.
Although, upon reflection, if I decide to become the world’s expert in lit-match juggling, and the most important problem is lighting the third one before the first two burn down, that is obviously not necessarily an important problem on a larger scale. But I think my point above still has value even if it’s missing something that permits this counterexample.
And a response that brings up another important point is simply that everyday language is said without precision. When someone claims that their problem isn’t important, they don’t mean that it has zero importance, and when they say it’s not going to lead to something important, they aren’t really claiming that it has a zero chance of leading to anything important. Indeed, they aren’t even claiming aht the expected value of it is low—imagine they are working on something which, by contributing to general knowledge, increases the odds of solving each of 2000 problems by 0.1% each, Nobody in their right mind would claim that that is an important problem, yet it increases the expected number of important problems that are solved by more than 1.
The correct response to Hamming’s question is “Because I have a comparative advantage in working on the problem I am working on”. There are many, many important problems in the world of greater and lesser degrees of importance. There are many, many people working on them, even within one field. It does not make sense for everyone to attack the same most important problem, if indeed such a single problem could even be identified. There is a point of diminishing returns. 100 chemists working on the most important problem in chemistry are not going to advance chemistry as much as 10 chemists working on the most important problem, and 90 working on a variety of other, lesser problems.
This point was first made to me by Richard Stallman who told me quite clearly that free software was not the most important problem in the world—I think he cited overpopulation as an example of a more serious problem—but software freedom was the problem he was uniquely well situated to address.
There are seven billion people in the world. I know of no problem that actually needs 7 billion minds to solve it. We are pretty much all well advised to find the biggest problem we have a comparative advantage at, and work on solving that problem. We don’t all have to, indeed we shouldn’t, all work on the same thing.
I’m torn regarding this argument. Aaron Swartz wrote a very nice piece which I can’t find (his personal site now appears to be down) about how working entirely on things that are your current comparative advantage is fixed mindset, and what you could be doing instead is changing what your comparative advantage is. I’m glad that Aaron Swartz did this, and I worry that focusing on comparative advantage gives me an excuse not to branch out. (My current comparative advantage is in mathematics but I’m not convinced that means I should only be spending my life working on mathematics.)
To make my argument clearer, I will use you as an example; please forgive me.
If you have a comparative advantage in maths, and decide to change your comparative advantage to medical, computer, or social science, as soon as you have caught up on the fundamentals of the field necessary to make an informed opinion you will already have a comparative advantage because of your background.
Your proficiency in maths lent you a comparative advantage in maths; your comparative advantage in maths lends you a comparative advantage in [economics]; your comparative advantage in maths and [economics] lends you a comparative advantage in [biochemistry], etcetera.
I think this makes sense. We need to distinguish between something like “obvious current comparative advantage” and “less obvious potential comparative advantage.” In practice, the heuristic “stick to your comparative advantage” may optimize excessively for the former at the expense of the latter.
So in that case, the question is in some ways addressed by narrowing the meaning of “field”.
If a physicist interprets Hamming’s question as “what is the most important problem in your field?” as “what is the most important problem in physics?” then obviously not everyone should be answering it. If, instead, the physicist interprets it as “what is the most important problem in quantum cryptography?”, that being his/her more specific field, then it becomes more reasonable (and more vital!) that the physicist is indeed working on the most important problem in their field.
Although, upon reflection, if I decide to become the world’s expert in lit-match juggling, and the most important problem is lighting the third one before the first two burn down, that is obviously not necessarily an important problem on a larger scale. But I think my point above still has value even if it’s missing something that permits this counterexample.
And a response that brings up another important point is simply that everyday language is said without precision. When someone claims that their problem isn’t important, they don’t mean that it has zero importance, and when they say it’s not going to lead to something important, they aren’t really claiming that it has a zero chance of leading to anything important. Indeed, they aren’t even claiming aht the expected value of it is low—imagine they are working on something which, by contributing to general knowledge, increases the odds of solving each of 2000 problems by 0.1% each, Nobody in their right mind would claim that that is an important problem, yet it increases the expected number of important problems that are solved by more than 1.
I would