I'm a second year mathematics major at a pretty good school. Ever since I became a math major I have been most interested in set theory and logic, which I guess can be lumped into the category of foundations of mathematics. Reading about Kurt Gödel and the story of Hilbert's programme really inspired me. My plans now are to find a mathematical logic program to go into foundational research, but I saw a post on a forum that really discouraged and shocked me.

It can be found here.

Similar posts in the thread also offer a bleak outlook.

Is it true? Is it mostly a dead field filled with quacks and not much going on?

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    $\begingroup$ related $\endgroup$ – t.b. Apr 13 '12 at 15:03
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    $\begingroup$ Do you plan on studying logic or set theory or model theory? All three are different and related to foundations. I don't know about logic, but the other two have quite active research nowadays. $\endgroup$ – Asaf Karagila Apr 13 '12 at 15:04
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    $\begingroup$ Imho, if you are young, it's generally a bad career move to decide you want to enter a field but only use classical methods. Rightfully so, few agencies are going to support such a research program. There's nothing wrong with being captivated by "classical" mathematics (if that's the right word for Godel's work), but that should motivate you to be interested in discovering in what ways mathematicians have reinterpreted the probelms being studied using more recently discovered knowledge. So as general advice, if you become passionate about something, study it ... but with an open mind. $\endgroup$ – Michael Joyce Apr 13 '12 at 15:17
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    $\begingroup$ @Asaf: the interesting thing about that request is that, outside of a few fields, I doubt that many mathematicians would be any more comfortable with toposes than with axioms for set theory. For example consider someone studying numerical methods for PDEs. Everyone finds their familiar theories to be the most natural. $\endgroup$ – Carl Mummert Apr 13 '12 at 15:56
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    $\begingroup$ In my experience it is certainly not a dead field, and I find foundational questions fascinating. However, the question of how easy it is to get a job in this area is a notable question. At all the departments I've been associated with, the logic group has been very small compared with other research groups in the department. I'm not saying this is justified, but it is something to keep in mind. $\endgroup$ – Cheerful Parsnip Apr 14 '12 at 23:49

There are two meanings of "foundational research".

If you just mean mathematical logic (containing computability, set theory, model theory, and proof theory), there is a lot of ongoing research in those fields. Of course the cutting-edge results are usually technical, but the same can be said for every other well-developed area of mathematics. Nobody would read a paper by Galois and think that it is reflective of cutting edge work in algebra, or read work by Cauchy and think that is it reflective of current research in analysis. Similarly, it's a mistake to read papers in mathematical logic from the first half of the 20th century and think that they are reflective of current research in the field. If you want to see current work, you could look at the Journal of Symbolic Logic or the Journal of Mathematical Logic, both of which are well-regarded research journals in the field.

Sometimes "foundational research" is used in a different sense, to mean work that is supposed to provide some sort of philosophical foundation for mathematics. For better or worse this is not the direct aim of most researchers in mathematical logic, although they are happy if their work does help provide insight into foundational issues. The idea that there is some "universal foundation" on which all of mathematics is built is much more difficult to defend in light of what we currently know, compared to what people knew in 1900 or 1930.

One recent example of the interplay between technical research and foundational insight is in algorithmic randomness. This field was initiated in the 1960s, but in the 2000s there was an explosion of new work, much of which is documented in the recent 855-page book Algorithmic Randomness and Complexity by Downey and Hirschfeldt. While many of the results appear technical to outsiders, they do provide a much clearer foundational picture of randomness than anyone had in 1995. They do this in the modern style, by deeply exploring and comparing the mathematics of multiple notions of effective randomness.


Is foundational research dead? I certainly hope not, but the answer you receive will depend on who you ask.

There is a lot of research in set theory which one could consider foundational, since it concerns new axioms and the justification thereof. For example, large cardinals, inner model theory and Woodin's $\Omega$-conjecture all have a foundational flavour. Joel David Hamkins has written an excellent overview of current issues in set theory on this very site.

A very different sort of foundational work is undertaken in reverse mathematics. This programme, initiated by Harvey Friedman, attempts to discover the weakest systems capable of proving theorems from ordinary mathematics, by proving equivalences between those systems and theorems over a weak base theory. This has proved a very fruitful area of research.

If you're prepared to look into the more philosophical end of things, there is a small but thriving community investigating neo-logicism and various forms of abstraction principles inspired by Frege's work.

Hopefully other people can fill out this response a bit, as I probably won't have any more time to improve it until after the weekend.

  • $\begingroup$ One possibility is to look for applications to other fields that seem to have a lot of "low hanging fruit" for those versed in the newest methods. General topology was an example in the mid 1960s to mid 1970s, but I think now virtually all the low hanging fruit there has been picked. A more recent example is "set theoretic real analysis", although I think the low-hanging fruit is quickly being picked. Another example is Nabutovsky/Weinberger's work, which I heard about in 1999 but don't know anything about (google "computability theory and differential geometry"). $\endgroup$ – Dave L. Renfro Apr 13 '12 at 15:55
  • $\begingroup$ For an example of something I think might presently be "low hanging fruit" for someone with the appropriate background, see my comment at math.stackexchange.com/questions/131738 in which "low hanging fruit" appears. $\endgroup$ – Dave L. Renfro Apr 20 '12 at 14:40

I wouldn't recommend you the response there as particularly closed to reality. Unfortunately, that might be a consensus on a large part of the academia.

The problem is that non logicians tend to look logic as a rather bizarre and esoteric subject. But it is not. A great example are large cardinal axioms. I guess that people outside the adherence of {set theorists} think what the poster in that forum message said, large cardinals axioms are things set theorists invent to pass the time. But the reality is another. Measurable cardinals where basically proposed as an axiom that could settle a lot of undecidable but "expected" results that are independent from ZF (or ZFC or ZFC+CH).

What are some kind of these results: One of those is that for a certain 2-player game, involving a set of reals that is not very complicated (in a specific way, called analytic), one of the players must have a winning strategy. Why is this result expected? To find a game such that neither player has a winning strategy, one need to invoke the axiom of choice, which usually means a really complicated set is involved. In turn, this has further applications in other areas, as "natural" and "intuitive" sets are usually analytic or similar.

Then you get other areas of logic, which I cannot say so much (I'm a graduate student in set theory). I do know that model theory has a lot of ongoing research related with "more popular" parts of math such as algebraic geometry. Also, lambda calculus + set theory + computer science. Or recursion theory+randomness. There are quite a lot of labs in good universities working in logic, and there's no reason for it to be thought as a dead subject.

  • $\begingroup$ I think that a better motivation for measurable cardinals is not decidability of games but rather the fact the existence of a measurable cardinal implies CH holds for co-analytic sets (at least if I recall correctly). $\endgroup$ – Asaf Karagila Apr 14 '12 at 23:32
  • $\begingroup$ @Asaf: the perfect set property (which in turn implies CH) is just one of the things that follows from determinacy for a given pointclass. $\endgroup$ – Carl Mummert Apr 14 '12 at 23:40
  • $\begingroup$ @Carl: I know. However determinacy, while important and quite a strong property, is less motivational than the perfect set property and CH. $\endgroup$ – Asaf Karagila Apr 14 '12 at 23:43
  • $\begingroup$ @Asaf: That is certaily right, but I think it's clearer why co-analytic sets are expected to be determined, vs. they are expected not to be a counterexample for CH. After all, (I think that) for must mathematicians AC is more grounded than CH. But definitely, to complete my post, determinacy for "definable" sets is important as it works to show what one expects them to satisfy, and that in turn is important since these are not arbitrary sets that no mathematician works with, but usually "natural" examples. $\endgroup$ – Rafa Apr 15 '12 at 16:51

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