I disagree with this. I think it is a feature that all the low hanging fruit looks picked, until you pick another one.

Maybe our difference here is semantic, or we have different standards in mind for what constitutes "fruit." Googling you, I see that you seem to be in theoretical CS? My impression from talking with in the field people is that there is in fact a lot more low hanging fruit there.

Also I am not entirely sure if there is a divide between pure math and stuff pure mathematicians would consider "applied" (e.g. causal inference, theoretical economics, ?complexity theory? etc.) other than a cultural divide.

I strongly agree with this, which is one point that I'll be making later in my sequence.

But the cultural divide is significant, and it seems that in practice the most mathematically talented do skew heavily toward going into "pure math" so that more low hanging fruit has been plucked in the areas that mathematicians in math departments work in. I say this based on knowledge of apples-to-apples comparisons coming from people who work on math within and outside of "pure math." For example, Razborov's achievements in TCS have been hugely significant, but he's also worked in combinatorics and hasn't had similar success there. This isn't very much evidence – it could be that the combinatorics problems that he's worked on are really hard, or that he's only done it casually – but it's still evidence, and there are other examples.

And I think that anyone who makes even the slightest substantial contribution to homotopy type theory is doing interesting, original work.

I partially respond to this here.

I think the Low-Hanging Fruit Complaint is more often a result of not knowing where there's a hot, productive research frontier than of the universe actually lacking interesting new mathematics to uncover.

There's a lot of potential for semantic differences here, and risk of talking past each other. I'll try to be explicit. I believe that:

• There are very few people who have a nontrivial probability of discovering statements about the prime numbers that are both true, that people didn't already believe to be true, and that people find fascinating.
• The same is not far from being true for all areas of math that have been mainstream for 100+ years: algebraic topology, algebraic geometry, algebraic number theory, analytic number theory, partial differential equations, Lie Groups, functional analysis, etc.
• There is a lot of rich math to be discovered outside of the areas that pure mathematicians have focused on historically, and that people might find equally fascinating. In particular, I believe this to be true within the broad domain of machine learning.
• There are few historical examples of mathematicians discovering interesting new fields of math without being motivated by applications.

I am so confused as to why your standard seems to be so absurdly high to me.

The way in which I operationalize the originality / interest of research is "in 50 years, what will the best mathematicians think about it?" I think that this perspective is unusual amongst mathematicians as a group, but not among the greatest ones. I'd be interested in how it jibs with your own.

Anyway, I think that if one adopts this perspective and takes a careful look at current research using Bayesian reasoning, one is led to the conclusion that almost all of it will be considered to be irrelevant (confidence ~80%).

When I was in grad school, I observed people proving lots of theorems in low dimensional topology that were sort of interesting to me, but it's also my best guess that most of them will be viewed in hindsight as similar to how advanced Euclidean geometry theorems are today – along the lines of "that's sort of pretty, but not really worthy of serious attention."

Is it because I don't see how "superficially original" all of the work done in my field is? I lack perspective?

How old are you?

When I started grad school, I was blown away by how much the professors could do.

A few years out of grad school, I saw that a lot of the theorems were things that it was well known to experts that it was possible to prove by using certain techniques, and that proving them was in some sense a matter of the researchers dotting their i's and crossing their t's.

And in situations where something seemed strikingly original, the basic idea often turned out to be due to somebody other than the author of a paper (not to say that the author plagiarized – on the contrary, the author almost always acknowledged the source of the idea – but a lot of times people don't read the fine print well enough to notice).

For example, the Wikipedia page on Paul Vojta reads

In formulating a number of striking conjectures, he pointed out the possible existence of parallels between the Nevanlinna theory of complex analysis, and diophantine analysis. This was a novel contribution to the circle of ideas around the Mordell conjecture and abc conjecture, suggesting something of large importance to the integer solutions (affine space) aspect of diophantine equations. It has been taken up in his own work, and that of others.

I had the chance to speak with Vojta and ask how he discovered these things, and he said that his advisor Barry Mazur suggested that investigate possible parallels between Nevanlinna theory and diophantine analysis.

Similarly, even though Andrew Wiles' work on Fermat's Last Theorem does seem to be regarded by experts as highly original, the conceptual framework that he used had been developed by Barry Mazur, and I would guess (weakly – Idon't have an inside view – just extrapolating based on things that I've heard) that people with deep knowledge of the field would say that Mazur's contribution to the solution of Fermat's last theorem was more substantial than that of Wiles.

Your standards seem unusually high.

Yes, this is true. There are a number of reasons for this, but one is an encounter with Goro Shimura back in 2008 that left an impression on me – I thought about his words for many years.

I'll write more tomorrow.

I'd certainly defer to you in relation to subject matter knowledge (my knowledge of number theory really only extends through 1965 or so), but this is not the sense that I've gotten from speaking with the best number theorists.

When I met Shimura, he was extremely dismissive of contemporary number theory research, to a degree that seemed absurd to me (e.g. he characterized papers in the Annals of Mathematics as "very mediocre.") I would ordinarily be hesitant to write about a private conversation publicly, but he freely and eagerly expresses his views freely to everyone who he meets. Have you read The Map of My Life? He's very harsh and cranky and perhaps even paranoid, but that doesn't undercut his track record of being an extremely fertile mathematician. I reflected on his comments and learned more over the years (after meeting with him in 2008) his position came to seem progressively more sound (to my great surprise!).

A careful reading of Langlands' Reflexions on receiving the Shaw Prize hints that he thinks that the methods that Taylor and collaborators have been using to prove theorems such as the Sato-Tate conjecture won't have lasting value, though he's very guarded in how he expresses himself. I remember coming across a more recent essay where he was more explicit and forceful, but I forget where it is (somewhere on his website, sorry, I realize that this isn't so useful). It's not clear to me that Taylor would disagree – he may explicitly be more committed to solving problems in the near term than by creating work of lasting value.

One can speculate these views are driven by arrogance, but they're not even that exotic outside of the set of people who have unambiguously done great work. For example, the author of the Galois Representations blog, who you probably know of, wrote in response to Jordan Ellenberg:

That said, there is a secondary argument which portrays mathematics as a grand collective endeavour to which we can all contribute. I think that this is a little unrealistic. In my perspective, the actual number of people who are advancing mathematics in any genuine sense is very low. This is not to say that there aren’t quite a number of people doing interesting mathematics. But it’s not so clear the extent to which the discovery of conceptual breakthroughs is contingent on others first making incremental progress. This may sound like a depressing view of mathematics, but I don’t find it so. Merely to be an observer in the progress of number theory is enough for me — I know how to prove Fermat’s Last Theorem, how exciting is that?

apparently implicitly characterizing his own work as insignificant. And there aren't very many number theorists as capable as him.