The Joy of Why - What Makes for ‘Good’ Math?

Episode Date: February 1, 2024

We tend to think of mathematics as purely logical, but the teaching of math, its usefulness and its workings are packed with nuance. So what is “good” mathematics? In 2007, the mathematician Terence Tao wrote an essay for the “Bulletin of the American Mathematical Society” that sought to answer this question. Today, as the recipient of a Fields Medal, a Breakthrough Prize in Mathematics and a MacArthur Fellowship, Tao is among the most prolific mathematicians alive. In this episode, he joins Steven Strogatz to revisit the makings of good mathematics.

Hello, I'm Brian Cox. I'm Robin Ince, and this is the Infinite Monkey Cage trailer for our brand new series. We've got mummies, we've got magic, we've got asteroids. Mummies, magic and asteroids. What's the link? That it was an asteroid that magically went over the world that led to Imhotep the mummy coming back to life? That's correct. I thought it would be weird, scientific as ever. But the most important thing to know is that we are going to deal with the biggest scientific question we finally ask.

What is better, cats or dogs? Listen wherever you get your podcasts. Back in October 2007, way back when the first generation iPhone was still a hot commodity and the stock market was at an all-time high before the Great Recession, Terence Tao, a professor of math at UCLA, was determined to answer a question that had long been debated among mathematicians. What exactly is good mathematics. Is it about rigor, elegance, real-world utility? Terry wrote a very thoughtful and generous, I would even say open-hearted essay

about all the ways that math could be good. But now, more than 15 years later, do we need to rethink what good mathematics is? I'm Steve Strogatz, and this is The Joy of Why, a podcast from Quantum Magazine, where my co-host, Jana Levin, and I take turns exploring some of the biggest unanswered questions in math and science today. Here today to revisit the eternal question of what makes math good is Terry Tao himself. Professor Tao has authored more than 300 research papers on an amazingly wide swath of mathematics including harmonic analysis, partial differential equations,

combinatorics, number theory, data science, random matrices, and much more. He's been referred to as the Mozart of mathematics. And as the winner of a Fields Medal, a Breakthrough Prize in mathematics, a MacArthur Fellowship, and many other awards, that moniker is certainly well deserved. Terry, welcome to The Joy of Why. Terry Wilson I'm glad to be here. Peter Robinson I'm very excited to be able to talk to you about this question of what it is that makes some types of mathematical research good. I can remember pretty vividly flipping through the bulletin of American Math Society

back in 2007 and coming across your essay about this issue that you posed for us. It's something that all mathematicians think about. But for people out there who may not be so familiar, could you tell us how did you land on this question? How did you define good math back at the time? Right. Yes, it was actually a solicitation. So the editor of the bulletin at the time had asked me to contribute an article. I think I had a very naive idea of what mathematics was as a student. I kind of had this idea that there was some sort of council of greybeard that would hand out problems for people to work on. And it was kind of a shock to me as a graduate student,

realizing that there wasn't actually this central authority to hand out problems. And people did self-directed research. I kept going to talks and listening to how other mathematicians talked about what they find exciting and what makes them excited about math. And the fact that each mathematician has a different way of approaching mathematics, like some would pursue by applications, some by sort of aesthetic beauty, some by just problem solving. They wanted to solve a problem and they would focus on sort of the most difficult, the most challenging tasks. Some would focus on technique, some would try to make things as elegant as possible. But what struck me when sort of listening

to so many of these different mathematicians talk about what they find valuable in mathematics is that even though we all had sort of different ideals as to what good mathematics

should look like, they all kind of tend to converge to the same thing. If a piece of mathematics is really good, people who pursue beauty will eventually happen across it. People who pursue, who value, you know, technical power or applications will eventually

land upon it. Eugene Wigner had a very famous essay on the unreasonable effectiveness of mathematics in the physical sciences almost a century ago, where he just observed that there are areas of mathematics, for example, Romanian geometry, the study of curved space, that was initially just a purely theoretical exercise to mathematicians, you know, trying to prove the parallel postulate and so forth, turning out to be precisely what Einstein and Poincaré and Hilbert needed to describe the mathematics of general relativity. And that's just a phenomenon that occurs. So it's not just that mathematics that mathematicians find intellectually interesting end up being physically important, but even within mathematics, you know, subjects that mathematicians find intellectually interesting end up being physically important.

But even within mathematics, subjects that mathematicians find elegant also happen to provide deep insight. What I feel like is that there is some Platonic good mathematics out there, and all our different value systems are just different ways of accessing that objective good stuff. That's very interesting. Being a sort of person inclined to Platonic thinking myself, I'm tempted to agree, although I'm a little surprised to hear you say that, because I would have thought where you were going initially seemed to be like there are so many different points of view about this.

It is an interesting fact, though, kind of an empirical fact, that we do converge on agreeing about what is good or not good, even though, as you say, we come at it from so many different values. The convergence may take time. So there are definitely fields, for example, where they look a lot better as measured by one metric than others. Maybe they have a lot of applications, but their presentation is extremely disgusting. Or things that are very elegant but don't yet have many good applications in the real

world. But I do feel like eventually all converge. Well, let me ask you about this point of contact with the real world. It's an interesting tension in math. You know, as little kids, let's say, when we first learn about geometry, you might think at that point that triangles are real or circles or straight lines are real and that they can tell you about the rectangular shapes you see in buildings out in the world or that surveyors need to use geometry. And after all, the word comes from the measurement of the earth, right, geometry. And so there was a time when geometry was empirical. But what I wanted to ask you has to do with a comment that John von Neumann made.

So von Neumann, for anyone not familiar, was himself a great mathematician. And he made this comment in this essay, The Mathematician, about the relationship between math and the empirical world, the real world, where he says roughly that mathematical ideas originate in empirics, but that at some point, once you get the mathematical ideas, the subject starts to take on a life of its own. And then it's more like a creative piece of art. Aesthetic criteria become important. But he says that causes danger that when a subject starts to become too far removed from its empirical source, like especially in its second or third generation, he says that there's a chance the subject can suffer from too much abstract inbreeding and it's in danger of degeneration. Any thoughts about that? I mean, does math have to stay in contact with its empirical source? Yes, I think it does have to be grounded. When I say that empirically, all these different ways of doing mathematics do

converge, it's only because this only happens when the subject is healthy. So, you know, the good news is that usually it is. But, for example, mathematicians value short proofs over long ones, or things being equal. But one could imagine people going overboard and, like, on some field of mathematics, being obsessed with making proofs as short as possible and having these extremely opaque two-line proofs of deep theorems. And they make it kind of this contest,

and then it becomes this sort of abstruse game, and then you lose all the intuition, you lose maybe deeper understanding because you're just so obsessed with making all your proofs as short as possible. Now, this doesn't actually happen in practice, but this is kind of a theoretical example. And I think von Neum abstraction was making huge strides in simplifying and unifying a lot of mathematics that was previously very empirical, especially in algebra. People were realizing numbers and polynomials and many other objects that were previously treated separately. You could all think of them as members of the same algebraic class, in this case, a rig. And a lot of progress in mathematics was being made by finding the right abstraction, whether it was a topological space or a vector space, whatever, and proving things in great generality.

And this is sometimes what we call the Borbaki era in mathematics. And it did be a little bit too far from being grounded. We, of course, had the whole new math episode in the States where educators tried to teach math in the Borbaki style

and eventually realized that that was not the appropriate pedagogy at that level. But now the pendulum has swung back quite a bit. The subject has matured quite a bit and every field of mathematics, geometry, topology, whatever, we have kind of satisfactory formalizations and we kind of know what the right abstractions are. And now the field is again focusing on interconnections and applications. It's connecting much more to the real world now. I mean, not just sort of physics, which is a traditional connection, but computer science, life sciences, social sciences. With the rise of big data, pretty much almost any human discipline now can be

methodized to some extent. I'm very interested in the word that you just used a minute ago about interconnections, because that seems like a central point for us to discuss. It's something that you mentioned in your essay that along with these what you call local criteria about elegance or real-world applications or whatever, you mentioned this global aspect of good mathematics, that good mathematics connects to other good mathematics. That's almost key to what makes it good, that it's integrated with other parts. But it's interesting because it sounds almost like circular reasoning, that good math is the math that connects to other good math. But it's a really powerful idea,

and I'm just wondering if you could expand on it a little bit more. Yeah, so, I mean, what mathematics is about, one of the things that mathematics does is that it makes connections that are very basic and fundamental, but not obvious if you just look at it from the surface level. A very early example of this is Descartes' invention of Cartesian coordinates that made a fundamental connection between geometry, the study of points and lines and spatial objects, and numbers, algebra. So for example, a circle, you can think of as a geometric

object, but you can also think of it as an equation. X squared plus Y squared equals one is the equation of a circle. At the time, it was a very revolutionary connection. You know, the ancient Greeks viewed number theory and geometry as almost completely disjoint subjects. But with Descartes, there was this fundamental connection. And now it's internalized, you know, the way we teach mathematics, it's not surprising anymore that if you have a geometric problem, you attack it with numbers. Or if you have a problem with numbers, you may attack it with geometry. It's somewhat because both geometry and numbers are aspects of the same mathematical concept. We have an entire field called algebraic geometry, which is neither algebra nor geometry, but it's a unified subject studying objects that

you can either think of as geometric shapes, like lines and circles and so forth, or as equations. But really, it's a holistic union of the two that we study. And as the subject has deepened, we've realized that that is more fundamental somehow than either algebra or geometry separately in some way. So these connections are helping us discover sort of the real mathematics that initially somehow our empirical studies only give us a corner of a subject. There's this famous parable of the elephant. I forget where. There are four blind men and they discover an elephant and one of them feels the leg

of an elephant. And they think, oh, this is very rough. It must be like a tree or something. And one of them feels the leg of an elephant. And they think, oh, this is very rough. It must be like a tree or something. And one of them feels the trunk. And it's only a lot later that they see that there's a single elephant object that is explaining all their separate hypothesis. So we're all blind initially.

We're just watching the shadows on Plato's cave and only later realizing. You are very philosophical here. This is something I can't resist now. If you're going to start talking about the elephant and the blind people, this suggests that you think mathematics is out there, that it is something like the elephant and that we are the blind or, you know, we're trying to see something that exists independent of human beings.

Is that really what you believe? When you do good mathematics, like it's not just pushing symbols around. You do feel like there is some actual object that you're trying to understand. And all our equations we have are just sort of approximations of that, or shadows. You can debate the philosophical point of what is actually reality and so forth. I mean, these are things you can actually touch. And the more real things get mathematically, sometimes the less physical they seem. As you said, geometry initially, you know, was a very tangible thing about objects in physical space that you could, you know, you can actually build a circle and a square and so forth. But modern geometry, you know,

we work in high dimensions, we can talk about discrete geometries, all kinds of wacky topologies. And I mean, subjects still deserve to be called geometry, even though there is no earth being measured anymore. The ancient Greek etymology is very outdated, but there's definitely something there, whether how real you want to call it. But I guess the point is that for the purpose of actually doing mathematics, it helps to believe it's real. Yeah. Isn't that interesting? It does. It seems like that's something that goes very deep in the history of math. I was struck by an essay by Archimedes writing to his friend or at least colleague, Eratosthenes. We're talking now like 250 BC. And he makes the remark, he's discovered a way to find the area of what we would call the segment of a parabola. He's taking a parabola. He cuts across it with a line segment that's at an oblique angle to the axis of the parabola. And he figures out this area. It gets a very beautiful result. But he says something to Eratosthenes like, these results were inherent

in the figures all along. You know, like they're there. They're there. They're just waiting for him to find. It's not like he created them. It's not like poetry. I mean, it's interesting, actually, isn't it, that a lot of great artists, Michelangelo talked about releasing the statue from the stone, you know, as if it were in there to begin with. And it sounds like you and many other great mathematicians have, as you say, it's very useful to believe this idea that it's there waiting for us, waiting for the right minds to discover it. Right. Well, I think one manifestation of that is that ideas that are often very complicated

to explain when they're first discovered, and they get simplified. I mean, often the reason why something looks very deep or difficult at the beginning is you don't have the right notation. For example, we have decimal notation now to manipulate numbers, and it's very convenient. But in the past, we had like, you know we had Roman numerals and then there were even more primitive number systems that were just really, really difficult to work with if you wanted to do mathematics. Euclid's elements, some of the arguments in these ancient texts, like there's one theorem in Euclid's elements I think called the Bridge of Falls or something. It's like the statement that I think the same as like a sausage triangle, the two angle base angles are equal.

This is like a two line proof in modern geometric texts, you know, with right axioms. But you could have this horrendous way of doing it. And it was where many students of geometry in the classical era just completely gave up mathematics. True. But we now have a much better way of doing it. So often the complications we see in mathematics are artifacts of our own limitations. And so as we mature, things become simpler and it feels more real because of that.

We're not seeing the artifacts. We're seeing the essence. Well, so going back to your essay when you wrote it at the time, I mean, this was pretty early in your career, not the very beginning, but still. Why did you feel back then that it was important to try to define what good mathematics was? I think, so by that point, I was already starting to advise graduate students. Ah. And I was noticing that, you know, there was some misconceptions about sort of what is good and what is not.

And I was also talking to mathematicians in different fields, and what one field valued in mathematics seemed different from others, but yet somehow we were all studying the same subject. And sometimes someone would say something that sort of rubbed me the wrong way. Like, this mathematics has no applications, therefore it has no value. Or this proof is just too complicated, therefore it has no value, or something like that. Or conversely, this proof is too simple therefore it is not worth... There was some snobbery and so forth sometimes I would encounter. In my experience, the best mathematics came when I understood a different point of view,

a different way of thinking about mathematics from someone in a different field and applying it to a problem that I cared about. And so somehow my experience of how to use mathematics properly, how to wield it, was so different from the one true way of doing mathematics. I felt like this point had to be made somehow, that there's really a plural way of doing mathematics, but whereas mathematics is still united. That's very revealing, because I had wondered, you know, like in my introduction, I mentioned the many different branches of math that you have explored and I didn't even include some. Like I can remember just a few years ago your work about this mystery in fluid dynamics about whether

certain equations that we think do a good job of approximating the motions of water and air. I don't want to go into details too much but just to say here you are, people think of you doing number theory or harmonic analysis, and suddenly you're working on fluid dynamics questions. I mean, I realize it's partial differential equations, but still, your breadth of interest seems to be related to your breadth of accepting different insights, different valuable ideas from all the different ways of doing good math. I forget who said it, but there are two types of mathematicians. There's hedgehogs and foxes. A fox is someone who knows a little bit about everything. A hedgehog is a creature that knows one thing very, very well. And neither is better than the other. They complement each other. I mean, in mathematics, you need people who are

really deep domain experts in one subfield, and they know a subject inside out. And you need people who can see the connections between one field and another. So I definitely identify as a fox. But I work with a lot of hedgehogs. The work I'm most proud of is often a collaboration like that. Oh, yeah. Do they realize that they're hedgehogs? Well, okay.

The roles change over time. There are other collaborations where I'm the hedgehog and someone else is a fox. These are sort of not permanent. These are not in your DNA. Ah, good point. We can wear both cloaks. Well, what about, was there a response to the essay at the time? Did people say anything back to you?

I got a fairly positive response in general. I mean, the bulletin of the AMS is not a hugely widely circulated publication, I think. Also, I didn't really say anything too controversial. Also, this kind of predated social media. So I think maybe there's a few math blogs that picked it up, but there was no Twitter. There was nothing to make it go viral. Also, I think in general, mathematicians don't spend much of their time and intellectual capital on speculation. I mean, there's another mathematician called Min Yong Kim, who had this very nice metaphor that to mathematicians, credibility is like currency, like money. If you prove theorems and you demonstrate that you know the subject, you're accumulating some of this currency of

credibility in the bank. And once you have enough currency, you can afford to speculate a little bit by being a bit philosophical and saying what might be true rather than what you can actually prove. But we tend to be conservative and we don't want an overdraft in our bank account. You don't want most of your writing to be speculative and only like 1% to actually prove something. Fair enough. Okay, so lots of years have passed since then. What are we talking about? It's more than 15 years.

Oh yeah, time flies. Has your opinion changed? Is there anything we need to revise? The culture of math is changing quite a bit. I already had a broad view of mathematics and now I have an even broader one. So one very concrete example is computer-assisted proofs were still controversial in 2007. There was a famous conjecture called the Kepler conjecture, which concerns the most

efficient way to pack unit balls in three-dimensional space. And there's a standard packing, I think it's called the cubic central packing or something, that Kepler conjecture would be the best possible. This was finally resolved, but the proof was very computer-assisted. It was quite complicated, and chaos eventually actually created a whole computer language to formally verify this particular proof. But it was not accepted as a real proof for many years. But it illustrated how controversial the concept of a proof that you needed computer assistance to verify was. In the years since, there's been many, many other examples of proofs where a human can

reduce a complicated problem to something which still requires a computer to verify. And then the computer goes ahead and verifies it. We've kind of developed practices about how to do this responsibly, you know, how to publish code and data and ways to check and you open source things and so forth. And now there's widespread acceptance of computer-assisted proofs. Now I think the next cultural shift will be whether AI-generated proofs will be accepted. Right now, AI tools are not at the level where they can generate proofs to really advance mathematical problems. Maybe undergraduate-level homework assignments they can kind of manage, but research mathematics, they're not at that level yet. But at some point, we're going to start seeing AI-assisted papers come out, and there will be a debate. we're going to start seeing AI-assisted papers come out, and there will be a debate.

The way our culture has changed in some ways, back in 2007, only a fraction of mathematicians made their preprints available for publishing. Authors would jealously guard their preprints until they had the notification of acceptance from the journal, and then they might share. But now everyone puts their papers on public servers like the Archive. There's a lot more openness to put videos and blog posts about where the ideas of a paper come from, because people realize that this is what makes work more influential and more impactful. If you try to not publicize your work and be very secretive about it, it doesn't make a splash. Math has become much more collaborative. You know, 50 years ago, I would say that the majority of papers in mathematics were single author.

Now, definitely the majority are two or three or four authors. And we're just beginning to see really big projects like we do in the sciences, you know, like tens, hundreds of people collaborate. That's still difficult for mathematicians to do, but I think we're going to get there. Concurrently to that, we're becoming much more interdisciplinary. We're working with other scientists a lot more. We're working between fields of mathematics. And because of the internet, we can collaborate with people across the world. So the way we do mathematics is definitely changing. I hope in the future,

we will be able to utilize the amateur math community more. There are other fields like astronomy, where astronomers make great use of the amateur astronomy community, like a lot of comets, for example, found by amateurs. But mathematicians, there's a few isolated areas of mathematics, such as like tiling, two-dimensional tiling, and maybe finding records in prime numbers. There's a very select field of mathematics where amateurs do contribute and they're welcomed, but there's a lot of barriers. In most areas of mathematics, you need so much training and internalized conventional wisdom that we can't crowdsource things. But this may change in the future. Maybe one impact of AI would be to allow amateur mathematicians to contribute meaningfully to mathematics.

That's very interesting. So the amateurs might, with the help of AIs, either ask new questions that are good or help with good explorations of existing questions, that sort of thing? Many different modalities, yeah. So for example, there are now projects to formalize proofs of big theorems in these things called formal proof assistants, which are like computer languages that can 100% verify that a theorem is true or not and is proven or not. This actually enables large-scale collaboration mathematics. So in the past, if you collaborate with 10 other people to prove a theorem and each one contributes a step, everyone has to verify everyone else's math.

Because the thing about math is that if one step has an error in it, the whole thing can fall apart. So you need trust. And so therefore, this really inhibits really large-scale collaborations in mathematics. But there have been successful examples of really large theorems being formalized where there's a huge community, they don't all know each other, they don't all trust each other, but they communicate through uploading to some Git repository or something, like individual proofs of individual steps in the argument. And the formal proof software verifies

everything, and so you don't need to worry about trust. So we are enabling new modes of collaboration, which we haven't seen really in the past. It's really interesting to hear your vision, Terry. It's a fascinating thought. You don't hear the phrase citizen mathematician. You hear of citizen science. But why not citizen math? But I'm just wondering, are there any trends that you are worried about? For example, with computer-assisted proofs or AI-generated proofs, will we know that certain results are true, but we won't understand why? So that is a problem. I mean, it's already a problem even before the advent of AI. So there are many fields where the papers in a subject are getting longer and longer, hundreds of pages. And I'm hopeful that AI can actually conversely help simplify and it can explain as well as prove. So there's already

experimental software where if you take a proof that has been formalized, you can actually convert it into an interactive human-readable document where you have the proof and you see the high level steps. And if there's a sentence you don't understand, you can double click on it and it will expand into smaller steps. Soon, I think you can also get an AI chatbot sitting next to you while you're going through the proof, and they can take questions, and they can explain each step as if they were the author. I think we're already very close to that. There are concerns. educate our students, particularly now that many of our traditional ways of assigning homework and so forth, we are almost at the point where these AI tools can just instantly answer many of our

standard exam questions. And so we need to teach our students new skills, like how to verify whether an AI-driven output is correct or not, and how to get a second opinion. And we may see the advent of a more experimental side to mathematics. So mathematics is almost entirely theoretical, whereas most sciences have both a theoretical and experimental component. We may eventually have results that are first only proven by computers. And as you say, we don't understand. But then once we have the data that the AI, the computer-generated proofs provide, we may be able to run experiments. There's a little bit of experimental mathematics now. People do study large data sets of various things, elliptic curves, say, but it could become

much bigger in the future. You have a very optimistic view, it sounds like to me. It's not like the golden ages in the past. If I'm hearing you right, you think that there's a lot of very exciting stuff ahead. Yeah, a lot of the new technological tools are very empowering. I mean, AI in general has many complex ups and downsides. And outside the sciences, there's a lot of possible disruption to the economy, intellectual property rights and so forth. But within math, I think the ratio of good to bad

is better than in many other areas. And, you know, the internet really has transformed the way we do mathematics. I collaborate with a lot of people in a lot of different fields. I could not do this without the internet. The fact that I can go on Wikipedia or whatever and get started learning a subject and I can email somebody and we can collaborate online. I've had to do things old school where I could only talk to people in my department and use physical mail for everything else. I could not do the math that I do now.

Wow. All right. I just have to underline what you just said, because I never thought in a million years I was going to hear this. Terry Tao reads Wikipedia to learn math? As a starting point. I mean, it's not always Wikipedia, but just to get the keywords, and then I will do a more specialized search of, say, MathSci.net or some other database. But yeah. It's not a criticism. I mean, I do the same thing. Wikipedia is actually, if there's any criticism of the math on Wikipedia, maybe it's that sometimes it's a little too advanced for the readers that it's intended for, I think. Not always. I mean, it depends.

It varies a lot from article to article. But that's just funny. I love hearing that. I mean, these tools, you have to be able to vet the output. you have to be able to vet the output. So, I mean, the reason why I can use Wikipedia to do mathematics is because I already know enough mathematics that I can smell if a piece of Wikipedia during mathematics is suspicious or not. It makes some sources, and one of them is going to be a better source than the other. And I know the authors. I have an idea of which reference is going to be better for me. If I use Wikipedia to learn about a subject that I had no experience in,

then I think it would be more of a random variable. Well, so we've been talking quite a bit about what it is that makes good mathematics, the possible future for new kinds of good mathematics, but maybe we should address the question why does this even matter? Why is it important for math to be good? Well, so first of all, I mean, why do we have mathematicians at all? Why does society value mathematicians and give us the resources to do what we do? It's because we do provide some value.

We can have applications to the real world, there's intellectual interest, and some of the theories we develop eventually end up providing insight into other phenomena. And not all mathematics is of equal value. I mean, you could compute more and more digits of pi, but at some point you don't learn anything. Any subject needs some sort of value judgment because you have to allocate resources. There's so much mathematics out there.

What advances do you want to highlight and publicize that other people know about? And which ones maybe I should just be sitting quietly on a journal somewhere. Even if you think of a subject as being completely objective and there's only true or false, we still have to make choices just because time is a limited resource, attention is a limited resource, money is a limited resource. These are always

important questions. Peter Van Doren Well, interesting that you mentioned about publicizing because it is something that I think is a distinctive feature of your work that you've also put in a lot of effort to make math publicly accessible through your blog, through various articles you've written. I remember discussing one that you wrote in American Scientist about universality and that idea. Why is it important to make math publicly accessible and understandable? I mean, what is it that you're trying to do?

It kind of happened organically. Early in my career, the World Wide Web was still very new, and mathematicians started having web pages with various content, but there wasn't much of a central directory. Before Google and so forth, it was actually hard to find individual resources. So I started sort of making little directories on my web page. And I would also make web pages for my own papers and make some commentary. Initially it was more for my own benefit, just as an organizational tool, just to help me find things. As a byproduct, it was available to the public, but I was kind of the primary consumer, or at least so I thought, of my own web pages.

But I remember very distinctly, there was one time when I wrote a paper and I put it on my web page and had a little sub page called what's new and I just said here's a paper there's a question in it that I still couldn't answer and I don't know how to solve it and I just made this comment and then like two days later I got an email saying oh I was just checking your home page I know the answer to this there's a paper which will solve your problem and it made me realize first of all that people were actually visiting my web page which I didn't really know, but that interaction with the community could really,

well, it could help me directly solve my questions. There's this law called Metcalfe's Law in networking, that if you have N people and they all talk to each other, there's about N squared connections between them. And so the larger the audience and the larger the forum where everyone can talk to everybody else, the more potential connections you can make and the more good things can happen. I mean, in my career, so much of the discoveries I've made or the connections I've made is because of an unexpected connection.

My whole career experience has been more connections equals just better stuff happening. Beautiful example of what you're just referring to, but I'd love to hear you talk about it, is the connections that you made with people in data science who were interested in questions having to do with medical resonance imaging, MRI. Right. Could you tell us a little about that story? So this was about 2006, 2005, I think. So there was an interdisciplinary program here on campus at UCLA on, I think, multi-scale geometric analysis or something like that, where they were bringing together pure mathematicians who were interested

in sort of multi-scale type geometry in its own right, and then people who had very concrete data type problems. And I had just started working on some problems in random matrix theory. So I was sort of known as someone who could manipulate matrices. And I met someone who I already knew, Emmanuel Candez, because at the time he worked right next who could manipulate matrices. And I met someone who I already knew, Emmanuel Candez, because at the time he worked right next door in Caltech. And he and another collaborator, Justin Bromberg, they had discovered this unusual phenomenon. So they were looking at MRI images, but they're very slow.

To collect enough really high-resolution image of a human body, enough to maybe catch a tumor or whatever medically important feature you want to find, it often takes several minutes because they have to scan all these different angles and then synthesize the data. And this was a problem, actually, because little kids, for example, just sit still for three minutes in the MRI machine was quite problematic.

So they were experimenting with a different way using some linear algebra. They were hoping to get a 10%, 20% better performance improvement, a slightly sharper image by tweaking the standard algorithm a little bit. So the standard algorithm is called least squares approximation, and they were doing something else

called total variation minimization. But then when they ran the computer software, they got like almost perfect reconstruction of their test image. Massive, massive improvement. And they couldn't explain this, but Emmanuel was at this program and we were chatting at tea or something,

and he just mentioned this. And actually my first thought was that you must have made a mistake in your calculation that what you're saying is not actually possible and I remember going back home that night and trying to write down an actual proof that what they were seeing could not actually happen and then halfway through I realized I had made an assumption which wasn't true and then I realized that actually it could work and then I figured out what might be the explanation and then we worked together and we actually found a good explanation and we published that and once we did that people realized that there were many other situations where you had to take a measurement which normally you required lots and lots of data

and in some cases you can take a much smaller amount of data and still get a really high resolution measurement. So now modern MRI machines, for example, a scan that used to take three minutes can now take 30 seconds. Because this software, this algorithm is hardwired, hard-coded into the machines now. It's a beautiful story. It's such a great story. I mean, talk about important mathematics that is changing lives literally in this context of medical imaging. I love the serendipity of it and your open-mindedness, you know, to hear this idea and then think, well, this is impossible. I can prove it and then realizing, no, actually, it's fantastic to see math making such an impact. Well, okay. I think I better let you

go, Terry. It's been a real pleasure discussing the essence of good mathematics with you. Thanks so much for joining us today. Yeah, no, it's been a pleasure. The Joy of Why is a podcast from Quantum Magazine, an editorially independent publication supported by the Simons Foundation. Funding decisions by the Simons Foundation have no influence on the selection of topics, guests, or other editorial decisions in this podcast or in Quanta Magazine. The Joy of Why is produced by PRX Productions. The production team is Caitlin Falds, Livia Brock, Genevieve Sponsler, and

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