# Opinion 1: Doron Zeilberger is a great mathematician and prophet of the computer-aided future, but he is still blinded by the idea that intrinsic value in mathematics comes from interestingness

I have had the pleasure of reading over the years a great many of Doron Zeilberger’s notorious Opinions, and I have a great appreciation for his devotion to experimental mathematics! I agree in particular with his opinions that much of mathematics is empty symbol pushing, leading to nothing but expanding the egos of its authors. However, Dr. Z identifies the reason behind this to be the embrace of infinity in mainstream mathematics. This I believe is preposterous. It is entirely possible to do absolutely useless mathematics while staying firmly in the realm of the finite!

For instance, in What is Mathematics and What Should it Be, Zeilberger holds up Ramanujan’s identity

\frac{1}{\pi} = 2\sqrt{2} \sum_{k=0}^{\infty} \frac{(1103+26390k)(1/4)_k(1/2)_k(3/4)_k}{k!^3}\cdot \frac{1}{99^{4k+2}}

where (a)_k=a(a+1)\ldots(a+k-1) as “in the eyes of God”, much prettier than Euler’s formula

e^{i\pi}+1=0

In defense of this, he says that Ramanujan’s formula enables a very fast computation of \pi to billions of decimals. However, NASA uses only 15 digits of pi even in computations which need to be astronomically precise! Computing billions of digits of \pi is an utter waste of time, useful only to provide entertainment to GPU clusters or give children practice on how to memorize numbers!

On the other hand, while Euler’s formula is an embarrassing triviality, the theory behind it is a beautiful connection between complex arithmetic and planar geometry, as Tristam Needham’s excellent book Visual Complex Analysis explains. I use this connection in Semagrams to avoid having to remember any names for rotating, translating, scaling in 2d – I just use complex numbers! Although it is not a traditional criterion of beauty, I see saving the working programmer keystrokes as a noble end.

Dr. Z’s criterion in “What is Mathematics and What Should it Be” for what is good mathematics is the following.

Every statement that has a proof from the book, is ipso facto, trivial, at least, a posteriori, since all deep statements have long proofs. In my eyes the most beautiful theorems are those with succinct statements for which the shortest known (and hopefully any) proof is very long.

However, it is precisely this criterion that leads to all of the ridiculous ego-driven symbol pushing in mathematics. People want to find these “chestnuts”, these simple statements with tricky solutions, to show off how smart they are. This criterion implies that a proof in mathematics is only worthwhile if I can come up with it, but you can’t. Any mathematics that naturally follows from easily understandable principles is “trivial” and hence worthless!

With this in mind, where does Zeilberger see the future of mathematics?

Mathematics should become a science, and its main raison-d’etre should be the discovery of mathematical truth (broadly defined!).

I disagree! I think that the goal of mathematics is not to become a science, but rather to serve the sciences, to provide scaffolding and rigor so that the scientist may rest her feet upon solid ground as she reaches towards the stars, and have “abstract molds” at hand in which she can pour concrete structures into. The most useful mathematics for the scientist may have “trivial” proofs, which do not serve the purpose of aggrandizing the ego of the mathematician who discovers them. But that is not the point of mathematics; mathematicians should be happy to be forgotten so long as their theories drive the creations of wonders for the eons ahead.

And it is by this criterion that I also warn against a dogmatic rejection of infinity. I suspect that I agree with Dr. Z that the ultimate test of a mathematical theory is whether it can be implemented on a computer. In this case, I would claim that there is plenty of “infinity-based mathematics” that is perfectly applicable to computation! A large part of mathematical physics, which depends on infinities for the continuum and for randomness, falls into this category. If it is convenient to work with infinity, and the results end up being useful to computation, who is to say something wrong has happened? It is often easier to work with things “in the limit”, with the finite-approximation case analyzed afterwards, as finite approximation brings its own complications that can clutter the intuition.

Finally, I would like to defend my own area of study, category theory, from an imagined dismissal on grounds that all of the theorems are trivial. I got into category theory, and through category theory, the rest of mathematics, via getting into the programming language Haskell in highschool. Category theory is an incredibly powerful tool for organizing computation, and I continue to use it daily in my work in AlgebraicJulia to serve the scientist. I would encourage Dr. Z to reevaluate what he finds important in mathematics, and to encourage his students to use their skills not just to prove impressive theorems in order to get tenure, but to look outwards and see how their clever minds can be put to work on the problems of humanity.

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I agree with you that mathematical results should not be valued in proportion to the difficulty of their proofs. There are probably many things that make for a good result. But I especially like results that illuminate the world - that help us see things more clearly - and often these become more illuminating as we make their proofs simpler, because the illumination comes not just from knowing that the result is true, but why. So I am always trying to make everything simpler.

On another note, it would be good to see some examples of what you call “ridiculous ego-driven symbol pushing” in mathematics. Of course it is socially risky to name and shame, for several reasons! But I am a bit curious about what exactly you mean. Different people have quite different opinions about which mathematics is worthwhile and which is more symbol pushing. I find that as I learn more math, my opinion sometimes changes. So maybe we could chat about this offline sometime.

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Part of that was just channeling the style of Dr. Z for the bit of this post. But more generally, I don’t think I’m in a position to be sure that different parts of math are worthless, because math can have surprising consequences down the line. Time and time again, parts of math which seem worthless on the outside have some hidden gem inside.

That being said, I do believe that much math is not pursued in the spirit of service to the scientist and engineer; it is pursued out of an intrinsic love for patterns. And the danger there is in the absence of “objective” criteria for what patterns are “interesting”, there is a tendency to equate interestingness with “sport-like” cleverness.

But it’s complicated, because often the most useful results are discovered only through “play”, using only “what seems interesting” as a guide!

With all that out of the way, I will be brave enough to name in public some parts of math that are valued within mainstream academia but not in my estimation.

1. Computing homotopy groups of the sphere.
2. Classifying finite groups.
3. The twin prime conjecture.
4. The general approach to mathematical statistical mechanics that I encountered in my master’s program, where there was a lot of attention paid to computing difficult partition functions by hand and phase transition, and not a lot of attention paid to fundamental issues like “what is an open system.” I’d prefer a “Zeilberger”-style treatment, where you just numerically investigate phase transition of different models, because this scales to more complex real-world situations where clever tricks don’t apply.
5. Anything to do with large cardinals.

There are other things that I have a suspicion aren’t that useful, but it could just be that I don’t know enough about them yet.

But of course, always happy to chat offline as well.

At the end of your list you say you suspect items 1-5 aren’t useful. Of course ‘useful’ always begs the question: “useful for what?”. But somehow you changed the issue from “worthwhile” to “useful”. I don’t think math needs to be “useful” to be worthwhile.

For example, we probably know enough homotopy groups of spheres to do everything we currently need to do in math and physics. \pi_3(S^2)= \mathbb{Z} is important for skyrmions (topological solitons used to model baryons) . \pi_3(S^3) = \mathbb{Z} is important for instantons in SU(2) gauge theory (which cause detectable effects in the Standard Model). I’d say these are actually useful.

Very few people work on simply grinding out more higher homotopy groups of spheres. Most people who think about them are interested in they relate to other topics.

To category theorists, higher homotopy groups of spheres are interesting because they automatically arise when we repeatedly categorify the notion of “integer”. Joyal said “the sphere spectrum is the true integers”, and I explained that in week102 of This Week’s Finds. It’s really quite amazing!

There are also lots of shocking connections between homotopy groups of spheres and other subjects. Most famously, \lim_{n \to \infty} \pi_{n+3}(S^n) = \mathbb{Z}/24 has important connections to the huge network of ideas surrounding the number 24 which I overviewed in my recent lecture. It’s connected to how the double cover of the rotational symmetry group of the tetrahedron has 24 elements, the fact that bosonic string theory only works in 24+2-dimensional spacetime, the fact that superstring theory involves a 24-component field on the string worldsheet, the Riemann zeta function having \zeta(-1) = -1/12, the fact that at most 24 balls can touch a single ball of the same radius, the appearance of the number 24 in the formula for the discriminant of elliptic curves, and more.

And all this stuff about the number 24 is just a special case - admittedly, the most exciting special case - of the amazing relation between homotopy groups of spheres, Bernoulli numbers, the Riemann zeta function, the algebraic K-groups of the integers, and many other things that you might at first think were unconnected. I talked about the next case here: we have \lim_{n \to \infty} \pi_{n+7}(S^n) = \mathbb{Z}/240, and this is connected to how you can get at most 240 balls to touch a single ball of the same radius in 8 dimensions!

I wouldn’t go so far as to say most of this stuff is “useful”, but to me it’s worthwhile in very much the same way as the music of Bach: intricately patterned, surprising, endlessly mysterious, yet somehow inevitable. Unlike the music of Bach, this stuff emerges inevitably out of the fabric of mathematics itself.

It think it’s dangerous to lose oneself in these things. There are too many practical problems that need our attention. But I think that’s quite different from saying these things are “worthless”. In fact, it’s their bewitching fascination that makes them dangerous!

The question of how much math is “ego-driven” is fascinating to me. Certainly I get some egotistical pleasure in parading my knowledge as I just did. I try to keep it under control and focus on sharing the joy rather than merely showing off. It’s an endless challenge.

But I don’t think math is particularly ego-driven. I think almost any career path favored by ambitious men has an element of ego in it - and law, politics, business, sports, and practical forms of science are probably more ego-driven than math, simply because more people will be watching when you triumph. Frankly, nobody gives a damn when you prove \pi_{22}(S^{3}) = \mathbb{Z}/132 \times \mathbb{Z}/2. To work out something like that, which is apparently very hard, you have to be into the solitary pleasure of it.

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I think that, similarly to generalized discussions about what counts as “applied” mathematics, trying to define what “worthwhile” mathematics is and attempting to distinguish it from “symbol pushing” is itself not a useful activity. Grossly oversimplifying, scientific fields are determined by the questions that are asked and the methods employed and the communities involved. I believe that virtually all of us work on things that we believe are worthwhile and useful. As you both point out, we often learn some of the deepest, most “useful” notions through playing or by investigating seemingly useless notions. I guess that what I’m trying to say is: as long as we all ask ourselves what “worthwhile” means to us personally (so that we can work towards something which we consider to have substance) then we should not spend any time trying to determine what “worthwhile” should mean more broadly (or to others).

Having said all that, I’d like to echo Owen by saying that any practice of hurtful intellectual machismo (which does indeed occur as an organizing force in many areas of mathematics) should be actively fought and changed. However this isn’t a question of which mathematics is or isn’t worthwhile, it is a question of organizing our culture around kindness and inclusivity while fostering a community where we meet each other’s ideas with curiosity, rather than judgement.

(Written on my phone, while waiting for a hurricane to hit, sipping on coffee…. Ciao!)

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OK, there is an important distinction to have between “worth” and “use” that I wasn’t thinking about!

And perhaps this lies at the heart of my disagreement with Dr. Z. Dr. Z thinks that the short statements with long proofs are worth the most, and I think that the long statements with the short proofs are the most useful. I think that these views are actually somewhat compatible, if we think about the “worth” as something like the “intrinsic reward from discovering the nature of the universe”. And I think that this is certainly worthy!

Then Dr. Z (and many other pure mathematicians) think that we should be doing math for its intrinsic worth, whereas I think that we should put a good amount of that on hold until we make it through the 21st century safely. So in response to “useful for what”, I might say “getting through the 21st century safely.”

And one thing that I didn’t put on my list of things I don’t find useful, but I could have… is string theory. But I think we are in agreement about that. I think “dangerous” is a good way of putting it; dangerous in the same way that high-paying and high-status jobs in making people click on ads or predicting fractional movements in stock prices are dangerous in that it sucks talent away from more pressing matters. But I do believe there’s a eternal, transcendent inevitability about string theory/homotopy theory/etc. that is not present in the stock market or google, that makes it worthwhile in a cosmic sense.

I think that ego is the wrong description of the phenomenon I was trying to put a finger on, though. Even if every individual mathematician has very little ego compared to the average human, they are still heavily influenced by what is seen as valuable by their community. This is an extremely natural, and extremely good human tendency; we want to be valued and respected by our peers. If we didn’t have this, probably society wouldn’t work. Additionally, within the framework of things that are valued, we want to compete for glory. Again, this is an extremely healthy tendency; from competition comes great works. However, the combination of “following community values” and “competition” makes it easy to drift into a relatively isolated community, where the research goals are totally unanchored from even things that the early practitioners of the field would find worthwhile or useful. It seems to me that this happens in all domains of human endeavor, but particularly in academia because it is exceedingly hard to tell the difference between a line of research which will pay off in 40 years, and a line of research which only subsists on self-reference, and if we want to support the former we must put up with the latter.

In response to @Benjamin_Bumpus, I definitely agree that trying to show that other’s math is useless is in itself useless! However, I think that sometimes it is good to “air out” concerns. A lot of mathematics culture is transmitted by graduate students taking on faith from their advisers what sort of things are “worthwhile/useful”. Particularly with things like the twin prime conjecture or the homotopy groups of the spheres, graduate students pick up that if they were to make some new finding that related to these topics, it would be seen as valuable. I want to push back on these “cultural assumptions” and encourage people to think for themselves, develop their own Opinions. Because if you are to guide yourself, you cannot only like things, you also have to dislike things. And that doesn’t mean you should tear down people who do those things; you should maintain a healthy skepticism of your own intuition. But sometimes some open disagreement is good.

Returning to the subject of ego, I think that some amount of ego can help with some of these problems, because while ego can make you vulnerable to the opinions of others, ego can insulate from other’s opinions, giving you the confidence to go out on your own thread.

I can’t believe you really believe in your position. First of all, the proof of a statement can never be shorter than the statement itself, since it has to include the statement. So, “long statements with short proofs” has to be defined in some careful way. But there are lots of long statements with relatively short proof that are extremely boring - to me, at least.

Dr. Z’s position does have an inherent kind of logic to it, which reminds me a lot of bitcoin mining and “proof of work”. Having proved a short statement with a very long proof is valuable in that we can then use it as a lemma in other proofs, potentially shortening their proofs a lot. It’s like a form of stored work.

The problem with his position is that it doesn’t distinguish interesting statements from boring ones. In any sufficiently powerful axiom system like Peano arithmetic we know that given any computable function f \colon \mathbb{N} \to \mathbb{N} there are arbitrarily long theorems whose minimum proof length P has P \ge f(L) where L is the theorem statement’s length - at least if the axiom system is consistent. For Dr. Z these would be valuable gems if we take f to be the Ackermann function and L \ge 10000. But by any normal human standard most of these are useless trash.

(Maybe Dr. Z doesn’t work in any fixed axiom system; the way we quickly prove these fake gems exist is by working in a stronger axiom system! I’ve never read him write anything about logic.)

Anyway, my own concepts of “worthwhile” and “useful” are deeply contextual - they depend on what I’m doing, what I should be doing and what I enjoy doing. So I don’t try to reduce them to anything about proof length, and this comment is just for fun.

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I would like to push back on this a bit. Most math grad students learn from talking to their peers and mentors to avoid trying to prove the twin prime conjecture or compute homotopy groups of spheres, since these things take a lot of work and the chance of success is low. After Yitang Zhang proved that there are infinitely many pairs of primes of distance \le 70,000,000 from each other, and bunch of people jumped in and reduced that bound to 246. But before he proved this, he worked as an accountant, a delivery worker, at a motel in Kentucky and at a Subway sandwich shop. The lesson is clear: yes we’ll like you if you succeed, but until then… I’ll have a sub with meatballs.

Most math grad students work on projects their advisors recommend, which extend recent progress in an incremental fashion.

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By this I mean that there are a lot of statements in category theory that require a great deal of throat clearing definitions, but then end up being a trivial proof. Obviously not every long statement with short proof is worthwhile! I was just making a contrast.

Hmmm. This is true, but I guess my impression comes from the fact that people will tell me often that their work is on some incremental progress in a big theory, and I’ll ask why the big theory was cooked up, and they will say that it’s related to twin primes or homotopy groups of spheres.

I think Bitcoin is a great analogy here. Sometimes it does feel like academic math research is like Bitcoin mining: you get rewarded based on the hardness of the problems you solve, regardless of the why.

That is a fun fact though about proof lengths in Peano! I think that perhaps some of those statements would be interesting, or at least the machine for generating such statements would be. It wouldn’t be a terrible heuristic for an automatic mathematician to try and find lemmas with short statements and long proofs and offer them up to humans as possibly helpful.

One of my favorite class of results is results that show that a certain synthetic theory has analytic models. I.e. synthetic differential geometry, or the recent work of the liquid tensor project. This takes all the annoying analytic details and deals with them once and for all, allowing the user to then work freely within the synthetic system. So I definitely get the intuition here.

I guess my impression comes from the fact that people will tell me often that their work is on some incremental progress in a big theory, and I’ll ask why the big theory was cooked up, and they will say that it’s related to twin primes or homotopy groups of spheres.

That sounds like something a mathematician would tell a reporter. Maybe they don’t think you’ll understand what they’re really doing - or maybe they don’t understand the deeper motivations of their line of work. (This often happens with students.)

For example, number theorists talking to reporters often act like Fermat’s Last Theorem is a big deal. It’s easy to explain and it has a romantic story attached to it. But what really matters is the Modularity Theorem! This is much harder to explain but also less silly: it’s a general result connecting elliptic curves to modular forms. Wiles was able to prove Fermat’s Last Theorem just a portion of the Modularity Theorem, but the reason his work is so important is that it paved the way to a full proof of the Modularity Theorem.

I said a bit about why homotopy groups of spheres matter - that is, what deeper issues they are connected to. I don’t understand the twin prime conjecture nearly as well. But the general hope with easy-to-state, hard-to-prove number theory problems is that we can only solve them if we understand more about questions which are much more deeply interesting (because they’re connected to more different subjects).

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That is a fun fact though about proof lengths in Peano! I think that perhaps some of those statements would be interesting, or at least the machine for generating such statements would be.

This fact was proved by Gödel. You will be amused and maybe annoyed by his proof:

You see, this kind of thing worries me. I guess I had the experience in undergrad of trusting my professors when I was taking classes that all the stuff I was learning in the classes would end up being super powerful and useful. And sometimes it would, but I eventually learned that the priorities of a typical research mathematician were very different than mine, and I learned to stop taking on faith that I should find interesting what the people I look up to find interesting.

But I had a lot of privilege to have very strong foundations going back to highschool, a lot of exposure to different subjects, and summer research which went in different directions than what I was learning in classes. I’m also quite stubborn. I think if it wasn’t for these traits, I might have ended up doing what my mentors in category theory were doing: i.e. homotopy theory. Because I looked up to them, and they seemed to think it was important. And then three years into graduate school, I would have probably had some sort of existential crisis when I realized that K-theory and spectral sequences weren’t a particularly direct route to better systems theories.

I think it’s essential that students should trust their advisers on what is important to work on. But I also think that advisers have a responsibility to clearly state their motivations on why they find something important, in such a way that a student can evaluate whether their goals are aligned with that line of research before investing the requisite 3 years or however long it takes to actually understand that line of research.

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I agree that mentors should talk about why they’re working on what they’re working on - and students should ask them.

When I was an undergrad I spent a lot of time in the math department library browsing books in math and physics, trying to get an overview of different subjects. I was motivated mainly by fundamental physics: quantum field theory, general relativity, quantum gravity, the foundations of quantum mechanics, things like that. So, math that seemed helpful for those topics seemed “useful” to me. (At the time I was not worried about the usefulness of fundamental physics, and I didn’t know that progress in this subject was coming to a halt right around this time and would remain stalled for the rest of my life.) I was also interested in math for its own sake, but I worried a lot about whether it was endless labyrinth where you could spend a lifetime studying any of infinitely many topics. What was the meaning of it all?

By now I’ve spent a lot more time studying pure mathematics and have a much better sense of what I consider important and why I consider it important. I know why homotopy theory is important to me, and it’s not about computing things. But it’s not quick to explain.

Since we live in a world full of unhappiness and problems I feel a strong urge to work on things that will help, like epidemiology and (ultimately, I hope) ways of dealing with climate change and the Anthropocene. But since we live in a world of unhappiness and problems I also need the beauty, clarity and depth of pure mathematics and music to stay happy.

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One thing people talk about in software library design is “programmer happiness”. I.e., you might have an software library that has a lot of functionality, but is structured in such a way that it’s frustrating to use, it’s not consistent, it doesn’t spark joy.

I think we could evaluate homotopy groups of spheres in a similar light, making deep connections and integrating the world of mathematics sparks joy and wonder in the “mathematical user”, and that in and of itself is a “use”!

Anyways, thanks for engaging with me so much on these issues. One of my goals for localcharts is to develop of a philosophy of why we do what we do, and this has been clarifying for thinking about the range of positions one could take on this.

Every statement that has a proof from the book, is ipso facto, trivial, at least, a posteriori, since all deep statements have long proofs.

This is a bit like saying “it’s easy to factor the products of large primes, at least a posteriori”

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Let me elaborate a bit here - there’s a big, massively important difference between things that are trivial “a priori vs a posteriori” - proofs that are easy to find vs proofs that are easy to understand. One might say that, as long as the theorems are easy to understand, it’s not very important whether the proofs are easy to understand, since you can just understand the theorems (and a small set of specialists, or maybe just a computer, can check the proofs).

I don’t think this is really tenable, because to make advances we must expand the set of things that can be understood by humans, possibly aided by tools (to paraphrase Whitehead). In other words, to prove a theorem we must somehow reduce the complexity of the proof into something that we can find, which usually involves finding techniques that simplify existing proofs of moderately difficult theorems into trivialities. (I suppose this is essentially Grothendieck’s “rising sea”)

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It might seem rather narrow and pedantic to spend a lot of time calculating specific homotopy groups of spheres, but there is a really easy to understand reason why it’s interesting to study the homotopy groups of spheres in general: They lie at the very bones of logic, and it is completely insane and surprising that there should be anything to study at all.

First, what I mean by “they lie at the very bones of logic” is a very post-HoTT point of view: the homotopy groups of spheres have nothing intrinsically to do with homotopy or spheres, or anything topological or geometric. Rather, we ask the question: suppose we have a type of mathematical object defined by having a single instance with a single nontrivial self-identification. What can we understand about this type? Well, we can see it has many nontrivial self-identifications, since we can compose and invert the one we started with. And with a bit of cleverness, we can show that this exactly characterizes the type: it has a single object (up to identification), and the self identifications of that object form the group of integers.

Ok, to be expected: the integers are the free group on one generator, and we showed that they arise as the group of symmetries of an object which was assumed only to have a non-trivially symmetry. But let’s try another question. Suppose we have a type consisting of a mathematical object so that the reflexive self identification of that object has, itself, a non-trivial self identification. We can show that, as expected, this type has one object up to identification; that this one object has only its reflexive self identification (up to identification); and that this reflexive self-identitfication has the group of integers as its symmetry group of self-identifications (up to identification).

All is right in the world: we put one generator in, we get the group freely generated by a single generator out. But what if we ask the question: does the non-trivial self identification of the trivial self-identification of the object we started with have any non-trivial self-identifications? It turns out that it does! It has integer many of them. And it doesn’t stop there — you actually get non-trivial self-identifications of self-identifications arbitrarily deep. We don’t even know what they all are.

Why!? We put in only one generating self-identification and we get an apparently arbitrary complex algebra of self-identifications. It’s maddening.

Note that this is just the homotopy groups of the sphere, not of the spheres. It only gets worse as you go on (or, better, on a sphere-by-sphere basis, since the homotopy groups eventually have the same pattern to them — a pattern we also don’t fully understand).

On its face this is an affront to intuition: the homotopy groups of the spheres should be the integers at dimension n and nothing else — where could the rest possibly come from!? Turns out they come from all over math, in a sense: the geometry of rotations (O(n)), modular forms and/or elliptic curves, formal group laws in characteristic p, cobordism classes of manifolds, the K-theory of finite sets, and many many more examples.

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