I read this essay while I was still working in pure mathematics. I'm not sure whether I agreed with it then (I think I saw it more as a cheer for the home team than something that I analyzed critically). Skimming through it now, I am very skeptical of his main claim, which is that math is so interconnected that the very applied end of math benefits from the very pure end of math. His argument breaks down for at least four reasons:
(1) He gives examples of problem P1 in field F1 being related to problem P2 in field F2, then of problem P2' in field F2 being related to problem P3 in field F3, and concludes therefore that F1 and F3 are related. There is no reason why this should be true.
(2) Just because two problems P1 and P2 are distantly related to each other doesn't mean that the most efficient use of resources for solving problem P2 is to work on problem P1. The obvious counterargument is that the point is not to solve a specific problem, but to advance the field of mathematics as a whole. But one always has the choice to work on problems that are more or less centrally related to mathematics as a whole, and to the parts of mathematics that have any chance of actually being applied.
(3) Gowers' main example of a pure math problem tying in to applied mathematics is the relationship between partial differential equations and various problems in discrete mathematics. However the typical application here is that partial differential equations are used as a solution method to the discrete problem --- we turn the discrete problem into its continuous analog, which is much better understood, and then bound the difference between the continuous analog and the original discrete problem. Thus in his example it is actually partial differential equations, with their much more developed theory, being used to better understand the pure mathematical object; the theory of PDEs is not getting pushed forward at all.
(4) Gowers also gives the example of the relevance of the Kakeya problem to harmonic analysis, which I agree is actually a useful result. However, the conclusion to draw from this anecdote is that a randomly chosen problem has some non-zero probability of being relevant to at least one "practical" problem. We should expect to get "lucky" like this just as well if we focus on applications.
(Edited: removed reason (5) due to insufficient justification.)
From my above comments, you have probably gathered that I have moved to more applied fields than pure math. I did this for two reasons:
(1) To be able to make any claim about the practical value of math, one needs to have an understanding of how math is actually used.
(2) I realized that without any external measures of progress, the standards for whether a problem is worthwhile come down to essentially a weighted vote.
Reason (2) is tenuous but I think clear in some fields. However, I think reason (1) is a pretty solid reason that even the purest mathematicians should have some dialogue with applied researchers (or have done applied research themselves at some point).
This requires more justification than I am currently giving it, but it is easy to find examples of math problems that don't have even a tenuous connection to reality (I have also noticed that some pure mathematicians nevertheless argue that it does; their arguments are so weak that I can only conclude that they are trying to retroactively justify a decision they already made, and I am saying this as someone who has published papers in the field in question). The source of examples I am most familiar with is (a large portion of) enumerative combinatorics. It is possible that this is the only example, but I suspect that if I was more familiar with algebraic number theory then I could make a similar claim there.
For what it is worth, the last time here I tried to give an example of something in algebraic number theory not mattering to reality it turned out that it actually had some sort of practical purpose.
Upon further reflection, I don't think I can justify my claim that these sorts of problems have no connection to reality at all; perhaps a better claim is that these problems are a very inefficient way of making headway on problems that we care about, even if we extrapolate into the far future. But this would be a much subtler and difficult claim to justify, so for now I'm editing my above post to retract this statement. Since you quoted it in your response, people will still have access to it if they care.
I don't think I can justify my claim that these sorts of problems have no connection to reality at all; perhaps a better claim is that these problems are a very inefficient way of making headway on problems that we care about, even if we extrapolate into the far future.
Upvoted for correctly understanding the issue (even while taking a position opposite to mine).
For what it's worth, I was extremely surprised that you listed, of all things, enumerative combinatorics (i.e. counting things) as an example of a branch of mathematics with a "tenuous" connection to "reality".
I understand the argument Gowers is making, and believed it until recently. The disagreement boils down to a factual claim about the world, which is going to have to be resolved by actually looking out at the world.
For concreteness, here is how I would suggest trying to bring in information from the territory. Find some development which has been important in human history, and then working backwards argue that broader and broader theoretical contributions were valuable insofar as they facilitated this development. If any of these theoretical contributions were needed before there was evidence of their importance, then this provides some evidence that working on apparently useless problems is valuable.
If no examples of this form can be produced (I concede that the actual steps in such an argument might be difficult to verify, but I have seen very few plausible candidates), then it seems to offer compelling evidence that belief in the usefulness of interesting problems is, minimally, unfounded.
I should also say that my standards for usefulness may be lower than some mainstream critics of science (although they still reject a great deal of modern mathematics). For example, I would contend that trying to understand any physical phenomena which occur at low energies is obviously useful, and that understanding any completely mysterious phenomena at any energy is plausibly useful.
Find some development which has been important in human history, and then working backwards argue that broader and broader theoretical contributions were valuable insofar as they facilitated this development.
Your previous comments indicate that you have a ready-made formula for rejecting any such example, which is to deny that the theoretical contributions were "necessary". That is, you will argue that the important development "could have" happened without them. For instance, you addressed the classic example of non-Euclidean geometry paving the way for general relativity by saying that Einstein could have just invented non-Euclidean geometry on his own (!) when he needed it.
Such an argument is difficult to take seriously and seems to me only to indicate that, whatever your past history, you simply have, at the moment, a strong distaste for abstract mathematics. (Or, alternatively, perhaps you're playing an intense game of Devil's Advocate with yourself.) That's fine, tastes differ. But again, that's hardly enough reason to jump to the conclusion that nobody should be doing things like inventing non-Euclidean geometry.
You've characterized my position as motivated cognition in defense of the status quo, but in my view that is both wrong and unfair. It's wrong, first of all, because I don't necessarily think the status quo is optimal -- in fact I think mathematical research could probably be done a lot more efficiently. I just don't happen to favor changes in the particular direction that you advocate (basically the adoption of a concreteness heuristic for deciding what's "useful"). But even more importantly perhaps, it's unfair: even if my ideal mathematical world looks more like the current one than yours does, the fact remains that we are living in an exceptional period in human history. Most societies have not conducted extensive amounts of "theoretical research", but instead have occupied themselves almost exclusively with what they found to be "practical" and "relevant" within their local world; your position, rather than mine, is closer to the human default. In my view, the last few centuries of Western civilization are an exceptional instance of people finally beginning to almost start getting things right with respect to this question.
I don't actually think the issue here is exclusively empirical; I can sense important disagreements that may be better characterized as value differences (conceivably, these may ultimately also reduce to empirical disagreements, but if so it would be at several more inferential steps' remove). But I will concede that there is a substantial empirical component. On my analysis, what it boils down to is that you think you have a good way of predicting the long-term impact of mathematical work, whereas I don't think you do, because I don't think the heuristics you're using are any more powerful than (or even particularly different from) the most common human default.
you addressed the classic example of non-Euclidean geometry paving the way for general relativity by saying that Einstein could have just invented non-Euclidean geometry on his own (!) when he needed it.
My claim was that Einstein explicitly considered gravity as curvature of space before being aware of any formal developments in non-Euclidean geometry. I inferred that, if Einstein had lived before any formal developments in non-Euclidean geometry occurred, then non-Euclidean geometry would have become an object of study not because it was interesting but because it was important. If you really want to have this argument, then you should describe where you think things would have broken down if non-Euclidean geometry had not already been developed. Would general relativity never have occurred to Einstein? Would the community have scoffed at the idea more than they did? Would the theory have stagnated before the math could catch up?
But lets count this as a point for the home team. Lets suppose that general relativity had been set back a hundred years, and that we had never considered the possibility of gravitational time dilation until we discovered the empirical formula for the time dilation experienced by satellites. I agree that this is worse than what really happened, but its not bad enough to convince me that I should support work on interesting problems. I would be interested in additional examples, even if they were much less compelling.
You've characterized my position as motivated cognition in defense of the status quo, but in my view that is both wrong and unfair
I don't really care whether your position is motivated cognition. I realized my own beliefs were motivated cognition, and now I would like to replace them with beliefs that better reflect reality.
you think you have a good way of predicting the long-term impact of mathematical work,
We are both trying to predict the long-term impact of human activities. You don't get to abstain from having beliefs. My claim is that concretely motivated problems are a significantly better use of the smartest researchers' time than interesting abstract problems; your claim is that they aren't. I came to my belief by observing the historical record, noting that important advances have at least been proximately due to smart people working on concrete problems, and suspecting that the causal connections drawn to more abstract problems are highly tenuous. If you think this reasoning is the explanation for the rate of human progress prior to the 17th century, then you should say so and I can describe at length why I believe you are almost certainly wrong.
For the past few days I've been pondering the question of how best to respond to paulfchristiano's recent posts and comments questioning the value of mathematical research. I don't think I can do it concisely, in a single post; bridging the inferential distance may require something more like a sequence of posts. I may end up writing such a sequence eventually, since it would involve ideas I've actually been wanting to write up for some time, and which are actually relevant to more than just the specific questions at issue here (whether society should sponsor mathematics, and given that it does, whether paulfchristiano or anyone else in the LW readership should pursue it).
However, as the preceding parenthetical hints at, I'm actually somewhat conflicted about whether I should even bother. Although I believe that mathematical research should be conducted by somebody, it's not at all clear to me that the discipline needs more people beyond those who already "get" its importance, and are out there doing it rather than writing skeptical posts like paulfchristiano's. It seems perfectly plausible to me that those who feel as paulfchristiano does should just leave the profession and do something else that feels more "important" to them. This is surely the best practical solution on an individual level for those who think they have a better idea than existing institutions of where the most promising research directions lie, at least until Hansonian prediction markets are (ever) implemented.
Nevertheless, for those interested in the society-level question of whether mathematics (as such) may be justifiably pursued by anyone, or any community of people, as a professional occupation (which is quite distinct from the question of whether e.g. paulfchristiano should personally pursue it), I recommend, at least as a start, grappling with the arguments put forward by the best mathematicians in their own words. I think this essay by Timothy Gowers (a Fields Medalist), titled "The Importance of Mathematics", is a good place to begin. I would particularly draw the attention of those like paulfchristiano, who think they have a good idea of which branches of mathematics are useful and which aren't, to the following passage, from pp.8-9 (unfortunately the illustrations are missing, but the point being made is pretty clear nonetheless):
So - mathematicians can tell their governments - if you cut funding to pure mathematical
research, you run the risk of losing out on unexpected benefits, which historically
have been by far the most important.
However, the miserly finance minister need not be convinced quite yet. It may be very
hard to identify positively the areas of mathematics likely to lead to practical benefits, but
that does not rule out the possibility of identifying negatively the areas that will quite
clearly be useless, or at least useless for the next two hundred years. In fact, the finance
minister does not even need to be certain that they will be useless. If a large area of
mathematics has only a one in ten thousand chance of producing economic benefit in the
next fifty years, then perhaps that at least could be cut.
You will not be surprised to hear me say that this policy would still be completely
misguided. A major reason, one that has been commented on many times and is implied
by the subtitle of this conference, "A Celebration of the Universality of Mathematical
Thought", is that mathematics is very interconnected, far more so than it appears on the
surface. The picture in the back of the finance minister's mind might be something like
Figure 4. According to this picture, mathematics is divided into several subdisciplines, of
varying degrees of practicality, and it is a simple matter to cut funding to the less practical
ones.A more realistic picture, though still outrageously simplified, is given in Figure 5.
(Just for the purposes of comparison, Figure 6 shows Figures 4 and 5 superimposed.) The
nodes of Figure 5 represent small areas of mathematical activity and the lines joining them
represent interrelationships between those areas. The small areas of activity form clusters
where there are more of these interrelationships, and these clusters can perhaps be thought
of as subdisciplines. However, the boundaries of these clusters are not precise, and many
of the interrelationships are between clusters rather than within them.
In particular, if mathematicians work on difficult practical problems, they do not do so
in isolation from the rest of mathematics. Rather, they bring to the problems several tools
- mathematical tricks, rules of thumb, theorems known to be useful (in the mathematical
sense), and so on. They do not know in advance which of these tools they will use, but they
hope that after they have thought hard about a problem they will realize what is needed to
solve it. If they are lucky, they can simply apply their existing expertise straightforwardly.
More often, they will have to adapt it to some extent(...)
Thus, a good way to think about mathematics as a whole is that it is a huge body of
knowledge, a bit like an encyclopaedia but with an enormous number of cross-references.
This knowledge is stored in books, papers, computers and the brains of thousands of
mathematicians round the world. It is not as convenient to look up a piece of mathematics
as it is to look up a word in an encyclopaedia, especially as it is not always easy to
specify exactly what it is that one wants to look up. Nevertheless, this "encyclopaedia" of
mathematics is an incredible resource. And just as, if one were to try to get rid of all the
entries in an encyclopaedia, or, to give a different comparison, all the books in a library,
that nobody ever looked up, the result would be a greatly impoverished encyclopaedia or
library, so, any attempt to purge mathematics of its less useful parts would almost certainly
be very damaging to the more useful parts as well.