May 30, 2022

In this conversation, Semon Rezchikov and I talk about what other disciplines can learn from mathematics, creating and cultivating collaborations, working at different levels of abstraction, and a lot more!

Semon is currently a postdoc in mathematics at Harvard where he specializes in symplectic geometry. He has an amazing ability to go up and down the ladder of abstraction — doing extremely hardcore math while at the same time paying attention to *how* he’s doing that work and the broader institutional structures that it fits into. Semon is worth listening to both because he has great ideas and also because in many ways, academic mathematics feels like it stands apart from other disciplines. Not just because of the subject matter, but because it has managed to buck many of the trend that other fields experienced over the course of the 20th century.

**Links**

**Transcript**

[00:00:35]

Welcome back to idea machines. Before we get started, I'm going to do two quick pieces of housekeeping. I realized that my updates have been a little bit erratic. My excuse is that I've been working on my own idea machine. That being said, I've gotten enough feedback that people do get something out of the podcast and I have enough fun doing it that I am going to try to commit to a once a month cadence probably releasing on the pressure second [00:01:35] day of.

Second thing is that I want to start doing more experiments with the podcast. I don't hear enough experiments in podcasting and I'm in this sort of unique position where I don't really care about revenue or listener numbers. I don't actually look at them. And, and I don't make any revenue. So with that in mind, I, I want to try some stuff.

The podcast will continue to be a long form conversation that that won't change. But I do want to figure out if there are ways to. Maybe something like fake commercials for lesser known scientific concepts, micro interviews. If you have ideas, send them to me in an email or on Twitter. So that's, that's the housekeeping.

This conversation, Simon Rezchikov and I talk about what other disciplines can learn from mathematics, creating and cultivating collaborations, working at different levels of abstraction. is currently a post-doc in mathematics at Harvard, where he specializes in symplectic geometry. He has an amazing ability to go up, go up and down the ladder of [00:02:35] abstraction, doing extremely hardcore math while at the same time, paying attention to how he's doing the work and the broader institutional structures that affect.

He's worth listening to both because he has great ideas. And also because in many ways, academic mathematics feels like it stands apart from other disciplines, not just because of the subject matter, but because it has managed to buck many of the trends that other fields experience of the course of the 20th century.

So it's worth sort of poking at why that happened and perhaps. How other fields might be able to replicate some of the healthier parts of mathematics. So without further ado, here's our conversation.

[00:03:16] **Ben:**

I want to start with the notion that I think most people have that the way that mathematicians go about a working on things and be thinking about how to work on things like what to work on is that you like go in a room and you maybe read some papers and you think really hard, and then [00:03:35] you find some problem.

And then. You like spend some number of years on a Blackboard and then you come up with a solution. But apparently that's not that that's not how it actually works.

[00:03:49] **Semon:** Okay. I don't think that's a
complete description. So definitely people spend time in front of
blackboards. I think the length of a typical length of a project
can definitely.

Vary between disciplines I think yeah, within mathematics. So I think, but also on the other hand, it's also hard to define what is a single project. As you know, a single, there might be kind of a single intellectual art through which several papers are produced, where you don't even quite know the end of the project when you start.

But, and so, you know, two, a two years on a single project is probably kind of a significant project for many people. Because that's just a lot of time, but it's true that, you know, even a graduate student might spend several years working on at least a single kind of larger set of ideas because the community does have enough [00:04:35] sort of stability to allow for that.

But it's not entirely true that people work alone. I think these days mathematics is pretty collaborative people. Yeah. If you're mad, you know, in the end, you're kind of, you probably are making a lot of stuff up and sort of doing self consistency checks through this sort of formal algebra or this sort of, kind of technique of proof.

It makes you make sure helps you stay sane. But when other people kind of can think about the same objects from a different perspective, usually things go faster and at the very least it helps you kind of decide which parts of the mathematical ideas are really. So often, you know, people work with collaborators or there might be a community of people who were kind of talking about some set of ideas and they may be, there may be misunderstanding one another, a little bit.

And then they're kind of biting off pieces of a sort of, kind of collective and collectively imagined [00:05:35] mathematical construct to kind of make real on their own or with smaller groups of people. So all of those

[00:05:40] **Ben:** happen. And how did these
collaborations. Like come about and

[00:05:44] **Semon:** how do you structure them?
That's great.

That's a great question. So I think this is probably several different models. I can tell you some that I've run across. So during, so sometimes there are conferences and then people might start. So recently I was at a conference and I went out to dinner with a few people, and then after dinner, we were.

We were talking about like some of our recent work and trying to understand like where it might go up. And somebody, you know, I was like, oh, you know, I didn't get to ask you any questions. You know, here's something I've always wanted to know from you. And they were like, oh yes, this is how this should work.

But here's something I don't know. And then somehow we realized that you know, there was some reasonable kind of very reasonable guests as to what the answer is. Something that needed to be known would be so I guess now we're writing a paper together, [00:06:35] hopefully that guess works. So that's one way to start a collaboration.

You go out to a fancy dinner and afterwards you're like, Hey, I guess we maybe solved the problem. There is other ways sometimes people just to two people might realize they're confused about the same thing. So. Collaboration like that kind of from somewhat different types of technical backgrounds, we both realized we're confused about a related set of ideas.

We were like, okay, well I guess maybe we can try to get unconfused together.

[00:07:00] **Ben:** Can I, can I interject, like, I
think it's actually realizing that you are confused about the same
problem as someone who's coming at it from a different direction is
actually hard in and of itself. Yes. Yes. How, how does, like, what
is actually the process of realizing that the problem that both of
you have is in fact the same problem?

Well,

[00:07:28] **Semon:** you probably have to understand
a little bit about the other person's work and you probably have to
in some [00:07:35] way, have some basal
amount of rapport with the other person first, because. You know,
you're not going to get yourself to like, engage with this
different foreign language, unless you kind of like liked them to
some degree.

So that's actually a crucial thing. It's like the personal aspect of it. Then you know it because maybe you'll you kind of like this person's work and maybe you like the way they go about it. That's interesting to you. Then you can try to, you know, talk about what you've recently been thinking about.

And then, you know, the same mathematical object might pop up. And then that, that sort of, that might be you know, I'm not any kind of truly any mathematical object worth studying, usually has incarnations and different formal languages, which are related to one another through kind of highly non-obvious transformation.

So for example, everyone knows about a circle, but a circle. Could you could think of that as like the set of points of distance one, you could think of it as some sort of close, not right. You can, you can sort of, there are many different concrete [00:08:35] intuitions through which you can grapple with this sort of object.

And usually if that's true, that sort of tells you that it's an interesting object. If a mathematical object only exists because of a technicality, it maybe isn't so interesting. So that's why it's maybe possible to notice that the same object occurs in two different peoples. Misunderstandings.

[00:08:53] **Ben:** Yeah. But I think the cruxy thing
for me is that it is at the end of the day, it's like a really
human process. There's not a way of sort of colliding what both of,
you know, without hanging out.

[00:09:11] **Semon:** So people. And people can try
to communicate what they know through texts. So people write
reviews on.

I gave a few talks recently in a number of people have asked me to write like a review of this subject. There's no subject, just to be clear. I kind of gave a talk with the kind of impression that there is a subject to be worked on, but nobody's really done any work on it that you're [00:09:35] meeting this subject into existence.

That's definitely part of your job as an academic. But you know, then that's one way of explaining, I think that, that can be a little bit less, like one-on-one less personal. People also write these a different version of that is people write kind of problems. People write problem statements.

Like I think these are interesting problems and then our goal. So there's all these famous, like lists of conjectures, which you know, in any given discipline. Usually when people decide, oh, there's an interesting mathematical area to be developed. At some point they have a conference and somebody writes down like a list of problems and the, the conditions for these problems are that they should kind of matter.

They should help you understand like the larger structure of this area and that they should, the problems to solve should be precise enough that you don't need some very complex motivation to be able to engage with them. So that's part of, I think the, the trick in mathematics. You know, different people have very different like internal understandings of something, but you reduce the statements or [00:10:35] the problems or the theorems, ideally down to something that you don't need a huge superstructure in order to engage with, because then people will different, like techniques or perspective can engage with the same thing.

So that can makes it that depersonalizes it. Yeah. That's true. Kind of a deliberate, I think tactic.

And

[00:10:51] **Ben:** do you think that mathematics is.
Unique in its ability to sort of have those both like clean problem
statements. And, and I think like I get the sense that it's, it's
almost like it's higher status in mathematics to just declare
problems.

Whereas it feels like in other discipline, One, there are, the problems are much more implicit. Like anybody in, in some specialization has, has an idea of what they are, but they're very rarely made lightly explicit. And then to pointing out [00:11:35] problems is fairly low status, unless you simultaneously point out the problem and then solve it.

Do you think there's like a cultural difference?

[00:11:45] **Semon:** Potentially. So I think, yeah,
anyone can make conjectures in that, but usually if you make a
conjecture, it's either wrong or on. Interesting. It's a true for
resulting proof is boring. So to get anyone to listen to you, when
you make problem, you state problems, you need to, you need to have
a certain amount of kind of controllers.

Simultaneously, you know, maybe if you have a cell while you're in, it's clear. Okay. You don't understand the salary. You don't understand what's in it. It's a blob that does magic. Okay. The problem is understand the magic Nath and you don't, you can't see the thing. Right? So in some sense, defining problems as part of.

That's very similar to somebody showing somebody look, here's a protein. Oh, interesting. That's a very [00:12:35] similar process. And I do think that pointing out, like, look, here's a protein that we don't understand. And you didn't know about the existence of this protein. That can be a fairly high status work say in biology.

So that might be a better analogy. Yeah.

[00:12:46] **Ben:** Yeah, no, I like that a lot that
math does not have, you could almost say like the substrate, that
the context of reality.

[00:12:56] **Semon:** I mean it's there, right? It's
just that you have to know what to look for in order to see it. So,
right. Like, you know, number theorists, love examples like this,
you know, like, oh, everybody knows about the natural numbers, but
you know, they just love pointing out.

Like, here's this crazy pattern. You would never think of this pattern because you don't have this kind of overarching perspective on it that they have developed over a few thousand years.

[00:13:22] **Ben:** It's not my thing really been
around for a few thousand years. It's

pretty

[00:13:25] **Semon:** old. Yeah.

[00:13:27] **Ben:** W w what would you,

[00:13:30] **Semon:** this is just curiosity.

What, what would

[00:13:32] **Ben:** you call the first [00:13:35] instance of number theory in
history?

[00:13:38] **Semon:** I'm not really sure. I don't
think I'm not a historian in that sense. I mean, certainly, you
know, the Bell's equation is related to like all kinds of problems
in. Like I think grease or something. I don't exactly know when the
Chinese, when the Chinese remainder theorem is from, like, I I'm,
I'm just not history.

Unfortunately, I'm just curious. But I do think the basic server very old, I mean, you know, it was squared of two is a very old thing. Right. That's the sort of irrationality, the skirt of two is really ancient. So it must predate that by quite a bit. Cause that's a very sophisticated question.

[00:14:13] **Ben:** Okay. Yeah. So then going, going
back to collaborations I think it's a surprising thing that you've
told me about in the past is that collaborations in mathematics are
like, people have different specializations in the sense that the
collaborations are not just completely flat of like everybody just
sort of [00:14:35] stabbing at a place.

And that you you've actually had pretty interesting collaborations structures.

[00:14:43] **Semon:** Yeah. So I think different
people are naturally drawn to different kinds of thinking. And so
they naturally develop different sort of thinking styles. So some
people, for example, are very interested in someone had there's
different kinds.

Parts of mathematics, like analysis or algebra or you know, technical questions and typology or whatnot. And some people just happen to know certain techniques better than others. That's one access that you could sort of classify people on a different access is about question about sort of tasting what they think is important.

So some people. Wants to have a very kind of rich, formal structure. Other people want to have a very concrete, intuitive structure, and those are very different, those lead to very different questions. Which, you know, that's sort of something I've had to navigate with recently where there's a group of people who are sort of mathematical physicists and they kind of like a very rich, formal structure.

And there's other [00:15:35] people who do geometric analysis. Kind of geometric objects defined by partial differential equations and they want something very concrete. And there are relations between questions about areas. So I've spent some time trying to think about how one can kind of profitably move from one to the other.

But did Nash there's that, that sort of forces you to navigate a certain kind of tension. So. Maybe you have different access is whether people like these are the here's one, there's the frogs and birds.com. And you know, this, this is a real, this is a very strong phenomenon and mathematics is this, this

[00:16:09] **Ben:** that was originally dice.

[00:16:11] **Semon:** And maybe I'm not sure, but
it's certainly a very helpful framework. I think some people really
want to take a single problem and like kind of stab at it. Other
people want to see the big picture and how everything fits. And
both of these types of work can be useful or useless depending on
sort of the flavor of the, sort of the way the person approached
it.

So, you know, often, you know, often collaborations have like one person who's obviously more kind of hot and kind [00:16:35] of more birdlike and more frog like, and that can be a very productive.

[00:16:40] **Ben:** And how do you make your, like
let's, let's let's date? Let's, let's frog that a little bit. And
so like, what are the situations.

W what, what are the, both like the success and failure modes of birds in the success and failure modes of

[00:16:54] **Semon:** frocks. Great, good. This is, I
feel like this is somehow like very clearly known. So the success
so-so what frogs fail at is they can get stuck on a technical
problem, which does not matter to the larger aspect of the larger
university.

Hmm. And so in the long run, they can spend a lot of work resolving technical issues which are then like, kind of, not really looked out there because in the end they, you know, maybe the, you know, they didn't matter for kind of like progress. Yeah. What they can do is they can discover something that is not obvious from any larger superstructure.

Right. So they can sort of by directly [00:17:35] engaging with kind of the lower level details of mathematical reality. So. They can show the birds something they could never see and simultaneously they often have a lot of technical capacity. And so they can, you know, there might be some hard problem, which you know, no one, a large perspective can help you solve.

You just have to actually understand that problem. And then they can remove the problem. So that can learn to lead opened kind of to a new new world. That's the frog. The birds have an opposite success and failure. Remember. The success mode is that they point out, oh, here's something that you could have done.

That was easier. Here's kind of a missing piece in the puzzle. And then it turns out that's the easy way to go. So you know, get mathematical physicists, have a history of kind of being birds in this way, where they kind of point out, well, you guys were studying this equation to kind of study the typology of format of holes instead of, and you should study, set a different equation, which is much easier.

And we'll tell you all this. And the reason for this as sort of like incomprehensible to mathematician, but the math has made it much easier to solve a lot of problems. That's kind of the [00:18:35] ultimate bird success. The failure mode is that you spend a lot of time piecing things together, but then you only work on problems, which are, which makes sense from this huge perspective.

And those problems ended up being uninteresting to everyone else. And you end up being trapped by this. Kind of elaborate complexity of your own perspective. So you start working on kind of like an abstruse kind of, you know, you're like computing some quantity, which is interesting only if you understand this vast picture and it doesn't really shed light on anything.

That's simple for people to understand. That's usually not good. If you develop a new formal world that sort of in, maybe it's fine to work on it on this. But it is in the, and partially validated by solving problems that other people could ask without any of this larger understanding. That's

[00:19:26] **Ben:** yeah.

Like you can actually be too,

[00:19:31] **Semon:** too general, almost. That's
very often a [00:19:35] problem. So so you
know, one thing that one bit of mathematics that is popular among
non mathematicians for interesting reasons is category. So I know a
lot of computer scientists are sort of familiar with category
theory because it's been applied to programming languages fairly
successfully.

Now category theory is extremely general. It is, you know, the, the mathematical kind of joke description of it is that it's abstract nonsense. So, so that's a technical term approved by abstract now.

this is a tech, there are a number of interesting technical terms like morally true, and the proof by abstract nonsense and so forth, which have, I think interesting connotation so approved by abstract nonsense is you have some concrete question where you realize, and you want to answer it and you realize that its answer follows from the categorical structure of the question.

Like if you fit this question into the [00:20:35] framework of categories, There's a very general theorem and category theory, which implies what you wanted, what that tells you in some sense of that. Your question was not interesting because it had no, you know, it really wasn't a question about the concrete objects you were looking at at all.

It was a question about like relations between relations, right? So, you know, the. S. So, you know, there's this other phrase that the purpose of category theory is to make the trivial trivially trivial. And this is very useful because it lets you skip over the boring stuff and the boring stuff could actually, you get to get stuck on it for a very long time and it can have a lot of content.

But so category theory in mathematics is on one hand, extremely useful. And on the other hand can be viewed with a certain amount of. Because people can start working on kind of these very upstream, categorical constructions some more complicated than the ones that appear in programming languages, which, you know, most mathematicians can't make heads or tails of what they're about.

And some of those [00:21:35] are kind of not necessarily developed in a way to be made relevant to the rest of mathematics and that there is a sort of natural tension that anyone is interested in. Category theory has to navigate. How far do you go into the land of abstract nonsense? So, you know, even as the mathematicians are kind of viewed as like the abstract nonsense people by most people, even within mathematics is hierarchy continues and is it's factal yeah.

The hierarchy is preserved for the same reasons.

[00:22:02] **Ben:** And actually that actually goes
back to I think you mentioned when you're, you're talking about the
failure mode of frogs, which is that they can end up working on
things that. Ultimately don't matter. And I want to like poke how
you think about what things matter and don't matter in mathematics
because sort of, I think about this a lot in the context of like
technologies, like people, people always think like technology
needs to be useful for, to like some, [00:22:35] but like some end consumer.

But then. You often need to do things to me. Like you need to do some useless things in order to eventually build a useful thing. And then, but then mathematics, like the concept of usefulness on the like like I'm going to use this for a thing in the world. Not, not the metric, like yeah. But there's still things that like matter and don't matter.

So

[00:23:01] **Semon:** how do you think about, so it's
definitely not true that people decide which mathematics matters
based on its applicability to real-world concerns. That might be
true and applied with medics actually, which has maybe in as much
as there's a distinction that it's sort of a distinction of value
and judgment.

But in mathematics, So I said that mathematical object is more real in some sense, when it can be viewed from many perspectives. So there are certain objects which therefore many different kinds of mathematicians can grapple with. And there are certain questions which kind of any mathematician can [00:23:35] understand.

And that is one of the ways in which people decide that mathematics is important. So for example you might ask a question. Okay. So this might be some, so here's a, here's a question which I would think is important. I'm just going to say something technical, but I can kind of explain what it means, you know, understand sort of statements about the representation theory of of the fundamental group of a surface.

Okay. So what that means is if you have any loop in a surface, then you can assign to that loop a matrix. Okay. And then if you kind of compose. And then the condition of that for this assignment is that if you compose the loops, but kind of going from one after the other, then you assign that composed loop the product of his two matrices.

Okay. And if you deformed the loop then the matrix you assign is preserved under the defamation. Okay. So that's the, that's the sort of question was, can you classify these things? Can you understand them? They turn out to be kind of relevant to differential equations, to partial, to of all different kinds to physics, to kind of typology.

Hasn't got a very bad. So, you know, progress on that is kind of [00:24:35] obviously important because it turns out to be connected to other questions and all of mathematics. So that's one perspective, kind of the, the, the simplest, like the questions that any mathematician would kind of find interesting.

Cause they can understand them and they're like, oh yeah, that's nice. Those are that's one way of measuring importance and a different one is about the. Sort of the narrative, you know, mathematics method, you just spend a lot of time tying making sure that kind of all the mathematics is kind of in practice connected with the rest of it.

And there are all these big narratives which tie it together. So those narratives often tell us a lot of things that are go far beyond what we can prove. So we know a lot more about numbers. Than we can prove. In some sense, we have much more evidence. So, you know, one, maybe one thing is the Remont hypothesis is important and we kind of have much more evidence for the Riemann hypothesis in some sense, then we have for [00:25:35] any physical belief about our world.

And it's not just important to, because it's kind of some basic question it's important because it's some Keystone in some much larger narrative about the statistics of many kinds of number, theoretic questions. So You know, there are other more questions which might sound abstruse and are not so simple to state, but because they kind of would clarify a piece of this larger conceptual understanding when all these conjectures and heuristics and so forth.

Yeah. You know, like making it heuristic rigorous can be very valuable and that heuristic might be to that statement might be extremely complex. But it means that this larger understanding of how you generate all the heuristics is correct or not correct. And that is important. There's also a surprise.

So people might have questions about which they expect the answer to be something. And then you show it's not that that's important. So if there are strong expectations, it's not that easy to form expectations in mathematics, but,

[00:26:30] **Ben:** but as you were saying that
there, there are these like narrative arcs. [00:26:35] Do something that is both like correct and
defies the narrative.

[00:26:39] **Semon:** That's an interesting, that
means there must be something there, or maybe not. Maybe it's only
because there was some technicality and like, you know, the
technicality is not kind of, it doesn't enlighten the rest of the
narrative. So that's some sort of balance which people argue about
and is determined in the end, I guess, socially, but also through
the production of, I don't know, results and theorems and expect
mathematical experiments and so forth.

[00:27:04] **Ben:** And to, to, so I'm gonna, I'm
going to yank us back to, to the, the, the collaborations. And just
like in the past, we've talked about like how you actually do like
program management around these collaborations. And it felt like I
got the impression that mathematics actually has like pretty good
standards for how this is.

What

[00:27:29] **Semon:** do you mean by program
management? Meaning

[00:27:31] **Ben:** like like you're like, like how,
like [00:27:35] how you were basically just
managing your collaborators, like you you're talking about like
how, what was it? It was like, you need to like wrangle people for,
for. I, or yeah, or like, yeah. So you've got like, just like how
to manage your collaborators.

[00:27:51] **Semon:** So I guess

[00:27:54] **Ben:** we were developing like a theory
on that.

[00:27:56] **Semon:** Yeah, I think a little bit. So
on one hand, I guess in mathematics and math, every, so in the
sciences, there's usually somebody with money and then they kind of
determined what has. Is

[00:28:08] **Ben:** this, is this a funder or is this
like

[00:28:10] **Semon:** a, I would think the guy pie is
huge.

So yeah, in the sciences, maybe the model is what like funding agencies, PI is and and lab members, right. And often the PIs are setting the direction. The grant people are kind of essentially putting constraints on what's possible. So they steer the direction some much larger way, but they kind of can't really see the ground to all right.

And [00:28:35] then a bunch of creative work happens at lowest level. But you know, you're very constrained by what's possible in your lab in mathematics. There aren't really labs, right. You know, there are certainly places where people know more. Other places about certain parts of mathematics. So it's hard to do certain kinds of mathematics without kind of people around you who know something because most of the mathematics isn't written down.

And

[00:28:58] **Ben:** that, that statement is shocking
in and of itself.

[00:29:01] **Semon:** The second is also similar with
the sciences, right? Like most things people know about the natural
world aren't really that well-documented that's why it pays to be
sometimes lower down the chain. You might find something that isn't
known.

Yeah. But so because of that, people kind of can work very independently and even misunderstand one another, which is good because that leads to like the misunderstanding can then lead to kind of creative, like developments where people through different tastes might find different aspects of the same problem.

Interesting. And the whole thing is then kind of better that way. And then

[00:29:34] **Ben:** [00:29:35] like resolving, resolving. The confusion in
a legible way,

[00:29:40] **Semon:** it sort of pushes the field. So
that's, but also because everyone kind of can work on their own,
you know, coordination involves, you know, a certain amount of
narrative alignment.

And so you have to understand like, oh, this person is naturally suited to this kind of question. This person is naturally suited to this kind of question. So what are questions where both people are. First of all, you would need both people to make progress on it. That gives you competitive advantage, which is important, extremely important in kind of any scientific landscape.

And secondly if you can find a question of overlap, then, you know, there's some natural division of labor or some natural way in which both people can enlighten the other in surprising ways. If you can do everything yourself and you have some other person, like write it up, that's sort of not that phonic club.

So yeah, so there's, and then there's like, kind of on a [00:30:35] larger, but that's like kind of one on a single project collaboration to do larger collaboration. You have to kind of, you know, give you have to assign essentially you have to assign social value to questions, right? Like math, unlike sort of the math is small enough that it can just barely survive.

It's credit assigning system almost entirely on the basis of the social network of mathematicians. Oh, interesting. Okay. It is certainly important to have papers refereed because like it's important for somebody to read a paper and check the details. So the journals do matter, but a lot happen. So, you know, it doesn't have the same scaling.

The biology or machine learning has in part, because it's a small,

[00:31:20] **Ben:** do you know, like roughly how
many mathematicians. I can, I can look this

[00:31:25] **Semon:** up. I mean, it depends on who
you count as a mathematician. So that's the technique I'm asking
you. The reason, the reason I'm asking [00:31:35] that is because of course there's the
American mathematical society and they publish, like, this is the
number of mathematicians.

And the thing is like, they count like quite a lot of people. So you actually have the decision actually dramatically changes your answer. I would say there are on the order of the. Tens of thousands of mathematicians. Like if you think about like the number of attendees of the ICM, the international Congress of mathematicians, like, and then, you know, the thing is a lot of people, so it depends on like pure mathematicians, how pure, you know, that's going to go up and down.

But that's sort of the right order of magnitude. Okay. Cause which is a very small given that

[00:32:12] **Ben:** a compared to, to most other
disciplines then, especially compared to even. Science as a whole
like research

[00:32:20] **Semon:** has a whole. Yeah. So yeah, I
think like if you look at like, you know, all the, if you say like,
well look at the Harvard Kennedy school of business, and then they
have an MBA program, which is my impression is it's serious.

[00:32:35] And then you also look at like all the math pieces. Graduates and like the top 15 kind of us schools are kind of like, you know, I think the MBAs are like several times lecture. Yes. So that's, maybe I was surprised to learn that

[00:32:50] **Ben:** that's also good. Instead
of

[00:32:51] **Semon:** like, you can look at the
output rate, the flow rate, that's a very easy way to decide.

Yeah. But yeah, so you have to, yeah. So kind of you, there's like kind of, depending on how, if you can let go.

There are certain you have to, if you want to work with people, you have to find you, there's not, you can't really be a PI in mathematics, but if you are good at talking to people, you can encourage people to work on certain questions. So that over time kind of a larger set of questions get answered, and you can also make public statements to the and which are in some ways, invitations, like.

If you guys do these [00:33:35] things, then it'll be better for you because they fit into a larger context. So therefore your work is more significant that you're actually doing them a service by explaining some larger context. And simultaneously by sort of pointing out that maybe some problem is easy or comparatively, easy to some people that you, you might not do.

So that helps you if then they solve the problem because you kind of made a correct prediction of like, there is good mathematic. Yeah. So this is some complicated social game that, you know, mathematicians are not like, you know, they're kind of strange socially, but they do kind of play this game and the way in which they play this game depends on their personal preferences and how social they are.

[00:34:13] **Ben:** And actually speaking of the
social nature of mathematics I get the impression that mathematics
sort of as a discipline is. It feels much closer to what one might
think of as like old academia then many other disciplines in the
sense that my, my impression is [00:34:35]
that your, your tenure isn't as much based on like how much grant
money you're getting in.

And It's, it's not quite as much like a paper mill up and out

[00:34:46] **Semon:** gay. Yeah. There's definitely
pressure to publish. There, the expected publishing rate definitely
depends on the area. So, you know, probability publishers more, in
some ways it's a little bit more like applied mathematics, which
has more of a kind of paper mill quality to it.

I don't want to overstate that. But so there is space for people to write just a few papers if they're good and have got a job. Yeah. And so it's definitely true as I think in the rest of the sciences, that kind of high quality trumps quantity. Right. Then, you know, but modular, the fact that you do have, you do have to produce a certain amount of work in order to stay in academia and You know, in the end, like where you end up is very much determined on the significance of your work.

Right. And if you're very productive, consistently, certainly helps with people are kind of not as [00:35:35] worried. But yeah, it's definitely not determined based on grant money because essentially there's not that much grant money to go around. So that makes it have more of this old-school flavor. And it's also true that it's still not, it's genuinely not strange for people to graduate with like just their thesis to graduate from a PhD program.

And they can do very well. So long as they, during grad school learn something that other people don't know and that matters. That seems that that's helpful, but so that allows for, yeah, this. You know, th this there's this weird trick that mathematicians play, where like proofs are kind of supposedly a universal language that everyone can read.

And that's not quite true, but it tries to approximate that ideal. But everyone has sort of allowed to go on their own little journey and the communities does spend a lot of work trying to defend that. What,

[00:36:25] **Ben:** what sort of, what, what does
that work

[00:36:27] **Semon:** actually look like? Well, I
think it's true that it is actually true that grad students are not
required to like publish a paper a year.

Yeah, [00:36:35] that's true. And that's great that people, I think, do defend that kind of position and they are willing to put their reputation on the line and the kind of larger hiring process to defend that SAC separately. It's true that, you know, You know, work that is not coming out of one of the top three people or something is can still be considered legitimate.

You know, because like total it's approved, it's approved. No one can disagree with it. So if some random person makes some progress, you know, it's actually very quickly. If, if people can understand it, it's very quickly kind of. And this allows communities to work without quite understanding one or other for awhile and maybe make progress that way, which can be

[00:37:18] **Ben:** helpful.

Yeah. And and most of the funding for math departments actually comes from teaching. Is that

[00:37:26] **Semon:** yeah, I think that a lot of it
comes from teaching. A certain chunk of it comes from grants. Like
basically people use grants to, in order to teach less. Yeah.
That's more or [00:37:35] less how it
works. You know, of course there's this, as in, you know,
mathematics has this kind of current phenomenon where, you know,
rich individuals like fund a department or something or they fund a
prize.

But by and large, it seems to be less dependent on these gigantic institutional handouts from say the NSF or the NIH, because that the expenses aren't quite yet. But it does also mean that like, it is sort of constrained and you know, it can't, you know, like big biology has like, kind of so much money, maybe not enough, not as much as it needs.

I mean, these grant acceptance rates are extremely low.

[00:38:13] **Ben:** If it's, for some reason, it's
every mathematician magically had say order of magnitude more
funding

[00:38:21] **Semon:** when it matters. Yeah. So it's
not clear that they would know what to do with that. There is, I
thought a lot about the question of, to what degree does the
mathematics is some kind of social enterprise and that's maybe true
of every research [00:38:35] program, but
it's particularly true in mathematics because it's sort of so
dependent on individual creativity.

So I've thought a lot about to what degree you could scale the social enterprise and in what directions it could scale because it's true that kind of producing mathematicians is essentially an expensive and ad hoc process. But at the same time, Plausibly true that people might be able to do research of a somewhat different kind just in terms of collaborations or in terms of like what they felt to do free to do research on if they had access to different kind of funding, like math itself is cheap, but the.

Kind of freedom to say, okay, well, these next two years, I'm going to do this kind of crazy different thing. And that does not have to fit with my existing research program that could, that you have to sort of fight for. And that's like a more basic stroke thing about the structure of kind of math academia.

I feel like

[00:39:27] **Ben:** that's, that's like structurally
baked into almost the entire world where there's just a ton of
it's, it's [00:39:35] very hard to do
something completely different than the things that you have done.
Right? People, people, boat, people. Our book more inclined to help
you do things like what you've done in the past.

And they are inclined to push against you doing different things. Yeah,

[00:39:50] **Semon:** that's true.

[00:39:50] **Ben:** And, and sort of speaking of, of
money in the past, you've also pointed out that math is terrible at
capturing the value that it creates in this.

[00:40:02] **Semon:** Well, yeah. You know, math is,
I mean, it may be hard to estimate kind of human capital value.

Like maybe all mathematicians should be doing something else. I don't really know how to reason about that, but it's definitely objectively very cheap. Just in the sense of like all the funding that goes into mathematics is very little and arguably the

[00:40:21] **Ben:** sort of downstream, like
basically every, every technical anything we have is to some extent
downstream.

Mathematics

[00:40:32] **Semon:** th there is an argument to be
made of that kind. You know, [00:40:35] I
don't think one should over I think, you know, there are extreme
versions of this argument, which I think are maybe not helpful for
thinking about the world. Like you shouldn't think like, ah, yes,
computer science is downstream of the program.

Like this turning thing. Like, I don't really know that it's fair to say that, but it is true that whenever mathematicians produce something that's kind of more pragmatically useful for other people, it tends to be. It tends to be easy to replicate and it tends to be very robust. So there are lots of other ideas of this kind and, you know, separately, even a bunch of the value of mathematics to the larger world seems to me to not even be about specific mathematical discoveries, but to be about like the existence of this larger language and culture.

So, you know, neural network people now, you know, they have all of these like echo variant neural networks. Yeah. You know, that's all very old mathematics. But it's very helpful to have kind of that stuff feel like totally, like you need to have those kinds of ideas be completely explored [00:41:35] before a totally different community can really engage with them.

And that kind of complete kind of that sort of underlying cultural substrate actually does allow for different kinds of things, because doing that exploration takes a few people a lot of time. So in that sense, then it's very hard to like you know, yeah. What you do well, most mathematicians do things which will have no relevance to the larger world.

Although it may be necessary for the progress of the sort of more useful basal things. Like the idea of a manifold came out of like studying elliptic functions historically and manifolds are very useful idea. And I looked at functions are or something. I mean, they're also useful, but they maybe less well known.

Certainly I think a typical scientist does not know about them. Yeah. It came out, but it did come out of like studying transformation laws for elliptic functions, which is a pretty abstruse sounding thing. So, but because of that, there's just, there's no S it's very hard to find a way for mathematicians to kind of like dip into the future.

And because like, you can have a startup. You know, like it's not going to be industrially useful, but it is [00:42:35] clearly on this sort of path in a way that you kind of, it's very hard to imagine removing a completely. Yeah.

[00:42:42] **Ben:** So, no, I like it also because
it's, again, it's, it's sort of this extreme example of some kind
of continuum where it's like, everybody knows that math is really
important, but then everybody also knows that it's not a.

Immediately

[00:43:02] **Semon:** applicable. Yeah. And there's
this question of, how do you kind of make the navigation that
continuum smoother and that has you know, that's like a cultural
issue and like an institutional issue to some degree, you know,
it's probably true that new managers do know lots of stuff,
empirically they get hired and then they get, they like, their
lives are fine.

So it seems that, you know, people recognize that but the, you know, various also in part too, because mathematicians try to kind of preserve this sort of space for [00:43:35] people to explore. There is a lot of resistance in the pure mathematics community for people to try to like try random stuff and collaborate with people.

And, you know, there is probably some niche for you know, Interactions between mathematically minded people and kind of things which are more relevant to the contemporary world or near contemporary world. And that niches one where it's navigation was a little bit obscure. It's not There aren't, there are some institutions around it, but it's, it doesn't seem to me to be like completely systematized.

And that's in part because of the resistance of the pure mathematics community. Like historically, I mean, you know, it's true that like statistics, departments kind of used to be part of pure mathematics departments and then they got kicked out, probably they left and they were like, we can make more money than you.

No, seriously. I don't know. I mean, there's like, I don't know the history of Berkeley stats department isn't famously one of the first ones that have this. I don't know the detailed history, but there was definitely some kind of conflict and it was a cultural conflict. Yeah. So these sorts of cultural [00:44:35] issues are things that I guess anyone has a saying, and I, I'm kind of very curious how they will evolve in the coming 50 years.

Yeah.

[00:44:42] **Ben:** To, to change the subject just a
bit again the, can you, can you dig into how. Do you call them
retreats? Like when, when the, the thing where you get a bunch of
mathematicians and you get them to all live in a place

[00:44:56] **Semon:** for like, so there's this
interesting well that's, there are things with a couple CS
there.

Of course they're there. That's maybe. So there are kind of research programs. So that's where some Institute has flies together. Post-docs maybe some grad students, maybe some sort of senior faculty and they all spend time in one area for a couple of months in order to maybe make progress on some kind of idea of a question.

So, yeah. That is something that there are kind of dedicated institutes to doing. In some sense, this is one of the places where like kind of external [00:45:35] funding has changed the structure of mathematics. Cause like the Institute of advanced study is basically one of these things. Yes. This Institute at Princeton where like basically a few old people, I mean, I'm kind of joking, but you know, there's a few kind of totemic people like people who have gone there because they sort of did something famous and they sit there.

And then what the Institute has done yesterday actually does in mathematics is it has these semester, longer year long programs. We're just house funding for a bunch of people to space. Been there spent a year there or half a year there, where to fly in there for a few weeks, a few times in the year. And that gets everyone together in one area and maybe by interacting, they can kind of figure out what's going on in some theoretical question, a different thing that people have done in much more short term is there's like a, kind of an interesting conference format, which is like, reminds me a little bit of like unconferences or whatnot, but it's actually kind of very serious where people choose you know, hot topic.

In a [00:46:35] kind of contemporary research and then they like rent out a giant house and then they have, I don't know, 20 people live in this house and maybe cook together and stuff. And then, you know, everyone there's like every learning center is like a week long learning seminar where there's some people who are like real experts in the area, a bunch of people who don't know that much, but would like to learn.

And then everyone has to give a talk on subjects that they don't know. And then there's serious people. The older people can go and point out where some, if there is a confusion and yeah, everyone. So there's like talks from nine to five and it's pretty exhausting. And then afterwards, you know, everyone goes on a hike or sits in the hot tub and talks about life and mathematics and that can be extremely productive and very fun.

And it's also extremely cheap because it's much cheaper to rent out a giant house than it is to rent out a bunch of hotels. So. If you're willing to do that, which most mathematicians are and a story,

[00:47:25] **Ben:** like, I don't know if I'm
misremembering this, but I remember you telling me a story where
like, there were, there were two people who like needed
[00:47:35] to figure something out together
and like they never would have done it except for the fact that
they just were like sitting at dinner together every night for, for
some number of nights.

[00:47:45] **Semon:** I. I mean, there are definitely
apocryphal stories of that kind where eventually people realize
that they're talking about the same thing. I can't think of an
example, right? I think I told you, you asked me, you know, is
there an example of like a research program where it's clear that
some major advance happened because two people were in the same
area.

And I gave an example, which was a very contemporary example, which is far outside of my area of expertise, but which is this. You know, Peter Schultz Lauren far kind of local geometric language and stuff where basically there was at one of these at this Institute in Berkeley. They had a program and these two people were there and Schultz was like a really technically visionary guy and Fargo talked very deeply about certain ideas.

And then they realized that basically like the sort of like fart, his dream could actually be made. And I think before that [00:48:35] people didn't quite realize like how far this would go. So that's kinda, I just gave you that as an example and that happens on a regular basis. That's maybe the reason why people have these programs and conferences, but it's hard to predict because so, you know, I don't really, like, I wish I could measure a rate.

Yes.

[00:48:50] **Ben:** You just need that marination.
It's actually like, okay. Oh, a weird thought that just occurred to
me. Yeah. That this sort of like just getting people to hang out
and talk is unique in mathematics because you do not need to do
cause like you can actually do real work by talking and writing on
a whiteboard.

And that like, if you wanna to replicate this in some other field, you would actually need that house to be like stocked with laboratory. Or something so that people could actually like, instead of just talking, they could actually like poke at whatever

the

[00:49:33] **Semon:** subject is. That would
[00:49:35] be ideal, but that would be hard
because experiments are slow.

The thing that you could imagine doing, or I could imagine doing is people are willing to like, share like very preliminary data, then they could kind of both look at something and figure out oh, I have something to say about your final. And I, that I don't know to what degree that really happens at say biology conferences, because there is a lot of competitive pressure to be very deliberate in the disclosure of data since it's sort of your biggest asset.

Yeah.

[00:50:05] **Ben:** And is it, how, how does
mathematics not fall into that trap?

[00:50:11] **Semon:** That is a great question. In
part there is. So I'm part, there are somewhat strong norms against
that, like, because the community is small enough. If it's everyone
finds out like, oh yeah, well this person just like scooped kind
of, yeah.

There's a very strong norm against scooping. That's lovely. It's okay. In certain contexts, like if, if, if it's clear for everyone, like somebody [00:50:35] could do this and somebody does the thing and it's because it was that it's sort of not really scooping. Sure. But if you, if there is really You know, word gets around, like who kind of had which ideas and when people behave in a way that seems particularly adversarial that has consequences for them.

So that's one way in which mathematics avoids that another way is that there's just like maybe it's, it's actually true that different people have kind of different skills. It is a little bit less competitive structurally because it isn't like everyone is working at the same kind of three problems.

And everyone has like all the money to go and like, just do the thing. And

[00:51:16] **Ben:** it's like small enough that
everybody can have a specialization such that there are people like
you, you can always do something that someone else
can't.

[00:51:24] **Semon:** Often there are people, I mean,
that, that might depend on who you are.

But yeah, often people with. It's more like it's large enough for that to be the case. Right? Like you [00:51:35] can develop some intuition about some area where yeah. Other people might be able to kind of prove what you're proving, but you might be much better at it than them. So people will be like, yeah, why don't you do it?

That's helpful. Yeah. It's that's useful. I mean, it certainly can happen that in the end, like, oh, there's some area on everyone has the same tools and then it does get competitive and people do start. Sorry. I think in some ways it has to do with like a diversity of tools. Like if, if every different lab kind of has a tool, which like the other labs don't have, then there's less reason to kind of compete.

You know, then you might as well kind of, but also that has to do with the norms, right? Like your, the pressure of being the person on the ground is that's a very harsh constraint. That's not. Premiere. I mean that my understand, I guess, that is largely imposed by the norms of the community itself in the sense that like a lot of like an NIH grants are actually kind of determined by scientific committees [00:52:35] or committees of scientists.

So,

[00:52:38] **Ben:** I mean, you could argue about
that, right? Because

[00:52:41] **Semon:** don't,

[00:52:42] **Ben:** is it, is it like, I mean, yes,
but then like, those committees are sort of mandated by the
structure of the funding agencies. Right. And so is it which, and
there's of course a feedback loop and they've been so intertwined
for decades that I'm clear which way that causality runs.

[00:53:02] **Semon:** Yeah. So I remember those are
my two guesses for how it's like one, there's just like a very
strong norm against this. And you don't, you just don't, you know,
if you're the person with the idea. And then you put the other
person on the paper because they like were helpful. You don't lose
that much. So it's just, you're not that disincentivized from doing
it.

Like in the end, people will kind of find out like, who did what work to some degree, even though officially credit is shared. And that means that, you know, everyone can kind of get. [00:53:35]

[00:53:35] **Ben:** It seems like a lot of this does
is depend on, on

[00:53:38] **Semon:** scale. Yeah. It's very scale
because you can actually find out. Right. And that's a trade-off
right.

Obviously. So, but maybe not as bad a trade off in mathematics, because it's not really clear what you would do with a lot more scale. On the other hand, you don't know, like, you know, if you look at, say a machine learning, this is a subject that's grown tremendously. And in part, you know, they have all these crazy research directions, which you, I think in the end kind of can only happen because they've had so many different kinds of people look at the same set of ideas.

So when you have a lot of people looking at something and they're like empowered to try it, it is often true that you kind of progress goes faster. I don't really know why that would be false in mathematics.

[00:54:23] **Ben:** Do you want to say anything about
choosing the right level of Metta newness?

Hmm.

[00:54:28] **Semon:** Yeah. You're thinking about, I
guess this is a, this is like a question [00:54:35] for, this is like a personal question for
everyone almost. I mean, everyone who has some freedom over what
they work on, which is actually not that many people you know, You
in any problem domain, whether that's like science, like science
research or whether that's like career or whatnot, or even, you
know, in a company there's this kind of the, the bird frog
dichotomy is replicated.

What Altitude's. Yeah. So for example, you know, in math, in mathematics, you could either be someone who. Puts together, lots of pieces and spend lots of time understanding how things fit together. Or you can be someone who looks at a single problem and makes hard progress at it. Similarly, maybe in biology, you can also mean maybe I have a friend who was trying to decide whether she should be in an individual contributor machine learning research company, or.

And that for her in part is Metta non-metro choice. So she [00:55:35] really likes doing kind of like explicit work on something, being down to the ground as a faculty, she would have to do more coordination based work. But that, like, let's see, you kind of have more scope. And also in many cases you are so in many areas, but not in all doing the.

Is a higher status thing, or maybe it's not higher status, but it's better compensated. So like on a larger scale, obviously we have like people who work in finance and may in some ways do kind of the most amount of work and they're compensated extremely well by society. And but you need people you need, you know, very kind of talented people to work with.

Yeah, problems down to the ground because otherwise nothing will happen. Like you can't actually progress by just rearranging incentive flows and having that kind of both sides of this be kind of the incentives be appropriately structured is a very, very challenging balancing act because you need both kinds of people.

But you know, you need a larger system in which they work and there's no reason for that [00:56:35] system. A B there's just no structural reason why the system would be compensating people appropriately, unless like, there are specific people who are really trying to arrange for that to be the case. And that's you know, that's very hard.

Yeah. So everyone kind of struggles with this. And I think because in sort of gets resolved based on personal preference. Yeah.

[00:56:54] **Ben:** I think, I think that's, yeah. I
liked that idea that the. Unless sort of by default, both like
status and compensation will flow to the more Metta people. But
then that ultimately will be disastrous if, if, if taken to its
logical conclusion.

And so it's like, we need to sort of stand up for the trend.

[00:57:35]