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.
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.
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 bu... (read more)