# What is Good Mathematics?

> An annotated edition of this paper on Fermat's Library, where scientists and readers explain its ideas, equations and history in the margins. Annotated edition: https://fermatslibrary.com/s/what-is-good-mathematics-

- **Authors:** Terence Tao
- **Published:** 2007
- **Topic:** Mathematics
- **Original:** https://s3-us-west-1.amazonaws.com/fermatslibrary/uploads%2F1642448195922-y1fbx19l5a-88d3b59c632567f26a8e5616800a7735%2F0702396.pdf
- **Pages:** 12
- **Annotations:** 4 comments in 4 threads
- **Featured:** Fermat's Library Journal Club
- **Annotated edition:** https://fermatslibrary.com/s/what-is-good-mathematics-

## Annotations

### Annotation 1 (page 1)

Beside the passage: “WHAT IS GOOD MATHEMATICS?”

**Annotation** by Tymor Hamamsy (2024-04-15):

> >> "We tend to think of mathematics as purely logical, but the teaching of math, its values, its usefulness and its workings are packed with nuance. So what is “good” mathematics? In 2007, the mathematician Terence Tao wrote this 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 one of the most honored and prolific mathematicians alive. In this episode, he joins our host and fellow mathematician Steven Strogratz to revisit the makings of good mathematics."
>
> Source: https://www.quantamagazine.org/what-makes-for-good-mathematics-20240201/

### Annotation 2 (page 1)

Beside the passage: “TERENCE TAO”

**Annotation** by Tymor Hamamsy (2024-04-15):

> Terence Chi-Shen Tao is an Australian mathematician, and a professor of mathematics at UCLA. His research areas cover harmonic analysis, PDEs, algebraic/arithmetic/geometric combinatorics, probability theory, analytics number theory and more. Needless to say, his research spans many topics…
>
> British mathematician and Fields medalist Timothy Gowers made this quote about Tao's breadth of mathematical knowledge:
>
> >>Tao's mathematical knowledge has an extraordinary combination of breadth and depth: he can write confidently and authoritatively on topics as diverse as partial differential equations, analytic number theory, the geometry of 3-manifolds, nonstandard analysis, group theory, model theory, quantum mechanics, probability, ergodic theory, combinatorics, harmonic analysis, image processing, functional analysis, and many others. Some of these are areas to which he has made fundamental contributions. Others are areas that he appears to understand at the deep intuitive level of an expert despite officially not working in those areas. How he does all this, as well as writing papers and books at a prodigious rate, is a complete mystery. It has been said that David Hilbert was the last person to know all of mathematics, but it is not easy to find gaps in Tao's knowledge, and if you do then you may well find that the gaps have been filled a year later.
>
> Source: https://en.wikipedia.org/wiki/Terence_Tao

### Annotation 3 (page 1)

Beside the passage: “Abstract. Some personal thoughts and opinions on what “good quality mathematics” is, and whether one should try to deﬁne this term rigorously. As a case study, the story of Szemer´edi’s theorem is presented.”

**Annotation** by Tymor Hamamsy (2024-04-15):

> Some thoughts from Terence Tao about why he wrote this article in 2007:
>
> >> "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 greybeards 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 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 were areas of mathematics — for example, Riemannian 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 [what] mathematicians find intellectually interesting end up being physically important. But even within mathematics, subjects that mathematicians find elegant also happen to provide deep insight."
>
>
> Source: https://www.quantamagazine.org/what-makes-for-good-mathematics-20240201/

### Annotation 4 (page 4)

Beside the passage: “2. Case study: Szemer ´ edi’s theorem”

**Annotation** by Tymor Hamamsy (2024-04-15):

> Szemeredi’s theorem: In arithmetic combinatorics, Szemerédi's theorem is a result concerning arithmetic progressions in subsets of the integers.
>
> Here is a great lecture titled: "The afterlife of Szemerédi's theorem" from Timothy Gowers.
>
> Source: https://www.youtube.com/watch?v=8W_YDHNNeBU

## Full text

Extracted from the PDF. [Annotation N] marks where each annotation above sits.

#### Page 1

arXiv:math/0702396v1 [math.HO] 13 Feb 2007

WHAT IS GOOD MATHEMATICS? [Annotation 1]

TERENCE TAO [Annotation 2]

Abstract. Some personal thoughts and opinions on what “good quality mathematics” is, and whether one should try to deﬁne this term rigorously. As a case study, the [Annotation 3] story of Szemer´edi’s theorem is presented.

1. The many aspects of mathematical quality

We all agree that mathematicians should strive to produce good mathematics. But how does one deﬁne “good mathematics”, and should one even dare to try at all? Let us ﬁrst consider the former question. Almost immediately one realises that there are many diﬀerent types of mathematics which could be designated “good”. For instance, “good mathematics” could refer (in no particular order) to

(i) Good mathematical problem-solving (e.g. a major breakthrough on an impor-

tant mathematical problem); (ii) Good mathematical technique (e.g. a masterful use of existing methods, or the

development of new tools); (iii) Good mathematical theory (e.g. a conceptual framework or choice of notation

which systematically uniﬁes and generalises an existing body of results); (iv) Good mathematical insight (e.g. a major conceptual simpliﬁcation, or the

realisation of a unifying principle, heuristic, analogy, or theme); (v) Good mathematical discov ery (e.g. the revelation of an unexpected and in-

triguing new mathematical phenomenon, connection, or counterexample); (vi) Good mathematical application (e.g. to important problems in physics, engi-

neering, computer science, statistics, etc., or from one ﬁeld of mathematics to another); (vii) Good mathematical exposition (e.g. a detailed and informative survey on a

timely mathematical topic, or a clear and well-motivated argument); (viii) Good mathematical pedagogy (e.g. a lecture or writing style which enables

others to learn and do mathematics more eﬀectively, or contributions to mathematical education); (ix) Good mathematical vi s i on (e.g. a long- range and fruitful program or set of

conjectures); (x) Good mathematical taste (e.g. a research goal which is inherently interesting

and impacts important topics, themes, or questions); (xi) Good mathematical public relations (e.g. an eﬀective showcasing of a mathe-

matical achievement to non- mathematicians, o r from one ﬁeld of mathematics to another); (xii) Good meta-mathematics (e.g. advances in the foundations, philosophy, history,

scholarship, or practice of mathematics); (xiii) Rigorous mathematics (with all details correctly and carefully given in full);

1

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2 TERENCE TAO

(xiv) Beautiful mathematics (e.g. the amazing identities of Ramanujan; r esults which

are easy (and pretty) to state but not to prove); (xv) Elegant mathematics (e.g. Paul Erd˝os’ concept of “proofs from the Book”;

achieving a diﬃcult result with a minimum of eﬀort); (xvi) Creative mathematics (e.g. a radically new and original technique, viewpoint,

or species of result); (xvii) Useful mathematics (e.g. a lemma or method which will be used repeatedly in

future work on the subject); (xviii) Strong mathematics (e.g. a sharp result that matches the known counterex-

amples, or a result which deduces a n unexpectedly strong conclusion from a seemingly weak hypothesis); (xix) Deep mathematics (e.g. a result which is manifestly non-tr ivial, for instance by

capturing a subtle phenomenon beyond the reach of more elementary tools); (xx) Intuitive mathematics (e.g. an arg ument which is natural and easily visualis-

able); (xxi) Deﬁnitive mathematics (e.g. a classiﬁcation of all objects of a certain type; the

ﬁnal word on a mathematical topic); (xxii) etc., etc. 1

As the above list demonstrates, the concept of mathematical quality is a highdimensional one, and lacks an obvious canonical total ordering 2 . I believe this is because mathematics is itself complex and high-dimensional, and evolves in unexpected and adaptive ways; each o f the above qualities represents a diﬀerent way in which we as a community improve our understanding and usage of the subject. There does not appear to be universal agreement as to the relative importance or weight of each of the above qualities. This is partly due to tactical considerations: a ﬁeld of mathematics at a given stage of development may be more receptive to one approach to mathematics than another. It is also partly due to cultural considerations: any given ﬁeld or school of mathematics tends to attract like-minded mathematicians who prefer similar approaches to a subject. It also reﬂects the diversity of mathematical ability; diﬀerent mathematicians tend to excel in diﬀerent mathematical styles, and are thus well suited for diﬀerent types of mathematical challenges. (See also [12] for some related discussion.)

I believe that this diverse and multifaceted nature o f “good mathematics” is very healthy for mathematics as a whole, as it it allows us to pursue many diﬀerent approaches to the subject, and exploit many diﬀerent types of mathematical talent, towards our common goal of greater mathematical prog ress and understanding. While each one of the above attributes is generally accepted to be a desirable trait to have in mathematics, it can become detrimental to a ﬁeld to pursue only one or two of them at the expense of all the others. Consider for instance the f ollowing hypothetical (and somewhat exaggerated) scenarios:

1 The above list is not meant to be exhaustive. In particular, it focuses primarily on the type of mathematics found in mathematical research papers, as opposed to classrooms, textbooks, or papers in disciplines close to mathematics, such as the natural sciences.

2 In particular, it is worth pointing out that mathematical rigour, while highly important, is only one component of what determines a quality piece of mathematics.

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WHAT IS GOOD MATHEMATICS? 3

• A ﬁeld which becomes increasingly ornate and baroque, in which individual

results ar e generalised and reﬁned for their own sake, but the subject as a whole drifts aimlessly without any deﬁnite direction or sense of progress; • A ﬁeld which becomes ﬁlled with many astounding conjectures, but with no

hope of r ig orous progress on any of them; • A ﬁeld which now consists primarily of using ad hoc methods to solve a collection

of unrelated problems, which have no unifying theme, connections, or purpose; • A ﬁeld which has become overly dry and theoretical, continually recasting and

unifying previous results in increasingly technical formal frameworks, but not generating any exciting new breakthroughs as a consequence; or • A ﬁeld which reveres classical results, and continually presents shorter, simpler,

and more elegant proofs o f these results, but which does not generate any truly original and new results beyond the classical literature. In each of these cases, the ﬁeld of mathematics exhibits much activity and progress in the short term, but risks a decline of relevance and a failure to attract younger mathematicians to the subject in the longer term. For t unately, it is hard for a ﬁeld to stagnate in this manner when it is constantly being challenged and revitalised by its connections to other ﬁelds of mathematics (or to r elated sciences), and by exposure to (and respect for) multiple cultures of “good mathematics”. These self-correcting mechanisms help to keep mathematics balanced, uniﬁed, productive, and vibrant.

Let us turn now to the other question posed above, namely whether we should tr y to pin down a deﬁnition of “good mathematics” at all. In doing so, we run the risk of arrogance and hubris; in particular, we might fail to recognise exotic examples of genuine mathematical progress because they fall outside mainstream deﬁnitions 3 of “good mathematics”. On the other hand, there is a risk also in the opposite position - that all approaches to mathematics a r e equally suitable and deserving of equal resources 4 for any given mathematical ﬁeld of study, or that all contributions t o mathematics are equally important; such positions may be admirable fo r their idealism, but they sap mathematics of its sense of direction and purpose, and can also lead to a sub-optimal allocation of mathematical resources 5 . The true situation lies somewhere in between; for each area of mathematics, t he existing body of results, folklore, intuition and experience (or lack thereof) will indicate which types of approaches are likely to be fruitful and thus deserve the majority of r esources, and which ones are more speculative and which might warrant inspection by only a handful of independently minded mathematicians, just to cover all bases. For example, in mature and well-developed ﬁelds, it may make sense to pursue systematic programs and develop general theories in a rigoro us manner, conservatively following tried-a nd- tr ue methods and established intuition, whereas in newer and less settled ﬁelds, a greater emphasis might be placed on making and solving conjectures, experimenting with diﬀerent approaches, and relying to some extent on non-rig orous heuristics and analogies. It thus makes sense fro m a tactical point of

3 A related diﬃculty is that, with the notable exception of mathematical rigour, most of the above qualities are somewhat subjective, and contain some inherent imprecision or uncertainty. We thank Gil Kalai for emphasising this point.

4 Examples of scarce resources include money, time, attention, talent, and pages in top journals. 5 Another solution to this problem is to exploit the fact that mathematical resources are also highdimensional, for instance one can award prizes for exposition, for creativity, etc., or have diﬀerent journals devoted to diﬀerent types of achievement. We thank Gil Kalai for this observation.

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view to have at least a pa rt ia l (but evolving) consensus within each ﬁeld as to what qualities of mathematical progress one should prize the most, so that one can develop and advance the ﬁeld as eﬀectively as possible at each stage of its development. For instance, one ﬁeld may be in great need of solutions to pressing problems; another ﬁeld may be crying out for a theoretical framework to org anise the clutter of existing results, or a grand program or series of conjectures to stimulate new results; other ﬁelds would greatly beneﬁt from new, simpler, and more conceptual proofs of key theorems; yet more ﬁelds may require g ood publicity, a nd lucid introductions to the subject, in order to attract more activity and interest. Thus the determination of what would constitute good mathematics for a ﬁeld can and should depend highly on the state of the ﬁeld itself. It should also be a determination which is continually up da ted and debated, both within a ﬁeld and by external observers to that ﬁeld; as mentioned earlier, it is quite possible for a consensus on how a ﬁeld should progress to lead to imbalances within that ﬁeld, if they are not detected and corrected in time.

It may seem fr om the above discussion that the problem of evaluating mathematical quality, while important, is a hopelessly complicated one, especially since many good mathematical achievements may score highly on some of the qualities listed ab ove but not on others; also, many of these qualities are subjective and diﬃcult to measure precisely except with hindsight. However, there is the remarkable phenomenon 6 that good mathematics in one of the above senses tends t o beget more good mathematics in many of the other senses as well, leading to the tentative conjecture that perhaps there is, after all, a universal notion of good quality mathematics, and all the speciﬁc metrics listed above represent diﬀerent routes to uncover new mathematics, or diﬀerent stages or aspects of the evolution of a mathematical story.

2. Case study: Szemer [Annotation 4] ´ edi’s theorem

Turning now from the general to t he speciﬁc, let us now illustrate the phenomenon mentioned in the preceding paragraph by considering the history and context of Szemer´edi’s theorem [32] - the beautiful and celebrated result that any subset of integers of positive (upper) density must necessarily contain ar bitrarily long arithmetic progressions. I will avoid all technical details here; the interested reader is referred to [33] and the references therein fo r further discussion.

There ar e several natura l places to start this story. I will b egin with Ramsey’s theorem [23]: that any ﬁnitely coloured, suﬃciently large complete graph will contain large monochromatic complete subgraphs. (For instance, given any six people, either three will know each other, or three will be strangers to each other, assuming of course that “knowing one another” is a well-deﬁned and symmetric relation.) This result, while simple to prove (relying on nothing more than an iterated pigeonhole principle), represented the discovery of a new phenomenon and created a new species of mathematical result: the Ramsey-type theorem, each one of which being a diﬀerent formalisation of the newly gained insight in mathematics that complete di s order is impossible.

One of the ﬁrst Ramsey-type theorems (which actually predates Ramsey’s theorem by a f ew years) was van der Waerden’s theore m [37]: given any ﬁnite colouring of the integers, one of the colour classes must contain arbitrarily long arithmetic progressions. Van der Waerden’s highly recursive proof was very elegant, but had the drawback that it

6 This phenomenon is also somewhat related to the “unreasonable eﬀectiveness of mathematics” observed by Wigner [38].

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WHAT IS GOOD MATHEMATICS? 5

oﬀered fantastically poor quantitative bounds for the appearance of the ﬁrst arithmetic progression of a given length; indeed, the bound involved a n Ackermann function of this length and the number o f colours. Erd˝os and Tur´an [4] had the good mathematical taste to pursue this quantitative question 7 further, being motiva ted a lso by the desire to make progress on the (then conjectural) problem of whether the primes contained arbitrarily long progressions. They then advanced a number of strong conjectures, one of which became Szemer´edi’s theorem; another was the beautiful but (still open) stronger statement that any set of positive integers whose reciprocals were not absolutely summable contained arbitrarily long arithmetic progressions.

The ﬁrst progress on these conjectures was a sequence of counterexamples, culminating in the elegant construction of Behrend [1] of a moderately sparse set (whose density in {1, . . . , N} was asymptotically greater t han N −ε for any ﬁxed ε) without arithmetic progressions of length three. This construction ruled out the most ambitious of the Erd˝os-Tur´an conjectures (in which po lynomially sparse sets were conjectured to have many progressions), and as a consequence also r uled out a signiﬁcant class of elementary approaches to these problems (e.g. those based on inequalities such as the Cauchy-Schwar z or H¨older inequalities). While these examples did not fully settle the problem, they did indicate that the Erd˝os-Tur´an conjectures, if true, would necessarily have a non-trivial (and thus presumably interesting) proof.

The next major advance was by Roth [27], who applied the Hardy-Littlewood circle method 8 together with a new method (the density increment argument) in a beautifully elegant manner to establish Roth’s theorem: every set of integers of positive density contained inﬁnitely many progressions of length three. It was then natural to try to extend Roth’s methods to progressions of longer length. Roth and many others tried to do so for many years, but without full success; the reason for the obstruction here was not fully appreciated until the work of Gowers much la t er. It took the formidable genius of Endr´e Szemer´edi [31], [32], who returned to purely combinatorial methods (in particular, pushing the density increment argument to remarka ble new levels o f technical sophistication) to extend Roth’s theorem ﬁrst to progressions of length four 9 , and then to progressions of arbitrary length, thus establishing his famous theorem. Szemer´edi’s proof was a technical tour de force, and intro duced many new ideas and techniques, the most important of which was a new way to look at extremely large graphs, namely to approximate them by bounded complexity models. This result, the celebrated and very useful Szemer´edi regularity l emma, is notable on many levels. As mentioned above, it gave a radically new insight regarding the structure of large graphs (which in modern language is now regarded as a structure theore m as well as a compactness theore m for such graphs); it gave a new proo f method (the energy increment method) which will become crucial later in this story; and it also generated an incredibly large number of unexpected applications, fro m gra ph theory to property testing to

7 Erd˝os also pursued the question of quantitative bounds for the original theorem of Ramsey, leading among other things to the founding of the immensely important probabilistic method in combinatorics, but this is a whole story in itself which we have no space to discuss here.

8 Again, the history of the circle method is another great story which we cannot detail here. Suﬃce to say though that this method, in modern language, is part of the now standard insight that Fourier analysis is an important tool for tackling problems in additive combinatorics.

9 Shortly afterward, Roth [28] was able to combine some of Szemer´edi’s ideas with his own Fourier analytic method to create a hybrid proof of Szemer´edi’s theorem for progressions of length four.

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additive combinator ics; the full story of this regularity lemma is unfortunately too lengthy to be described here.

While Szemer´edi’s accomplishment is undoubtedly a highlight of this particular story, it wa s by no means the last word on the matter. Szemer´edi’s proof of his theorem, while elementary, was remarkably intricate, and not easily comprehended. It also did not fully resolve the original questions motivating Erd˝os a nd Tur´an, as the proof itself used van der Waerden’s theorem at two key junctures and so did not give any improved quantitative bound o n that theorem. Furstenberg then had the mathematical taste to seek out a radically diﬀerent (and highly non-elementary 10 ) proof, based on an insightful analogy between combinatorial number theory and ergodic theory which he soon formalised as the very useful Furstenberg corre s pondence principle. Fr om this principle 11 one readily concludes that Szemer´edi’s theorem is equivalent to a multiple recurrence theorem for measure-preserving systems. It then became natural t o prove this theorem (now known as the Furstenberg recurrence theorem) directly by methods from ergodic theory, in particular by exploiting the vario us classiﬁcations and structural decompositions (e.g. the ergodic decomposition) available for such systems. Indeed, Furstenberg soon established the Furstenberg structure theorem, which described any measure preserving system as a weakly mixing extension o f a tower of compact extensions of a trivial system, and based on this theorem and several additional arguments (including a variant of the van der Waerden argument) was able to establish t he multiple recurrence theorem, and thus give a new proof of Szemer´edi’s theorem. It is a lso worth mentioning that Furstenberg also produced an excellent book [6] on this and related topics, which systematically formalised the basic theory while also contributing greatly to the growth and further development of this area.

Furstenberg and his coauthors then realised that this new method was potentially very powerful, and could be used to establish many more types of recurrence theorems, which (via the correspondence principle) then would yield a number o f highly non-trivial combinatorial theorems. Pursuing this vision, Furstenberg, Katznelson, and others obtained many variants and generalisations of Szemer´edi’s t heorem, obtaining for instance variants in higher dimensions and even establishing a density version of the Hales-Jewett theorem [18] (a very powerful and abstract generalisation of the van der Waerden theorem). Many of the results obtained by these inﬁnitary ergodic theory techniques are not known, even today, to have any “element ary” proof, thus testifying to the power of this method. Furthermore, as a valuable byproduct of these eﬀorts, a much deeper understanding of the structural classiﬁcation of measure-preserving systems was obtained. In particular, it was realised that fo r many classes of recurrence problem, the asymptotic recurrence pro perties of an ar bitrar y system are almost completely controlled by a special factor of that system, known as the (minimal) ch aracteristic factor of that system 12 . Determining the precise nature of this characteristic factor for various types of r ecurrence then became a major focus of study, as it was realised that

10 For instance, some versions of Furstenberg’s argument rely heavily on the axiom of choice, though it is possible to also recast the argument in a choice-free manner.

11 There is also a similar correspondence principle which identiﬁes van der Waerden’s theorem with a multiple recurrence theorem for topological dynamical systems. This leads to the fascinating story of topological dynamics, which we unfortunately have no space to describe here.

12 An early example of this is von Neumann’s mean ergodic theorem, in which the factor of shiftinvariant functions controls the limiting behaviour of simple averages of shifts.

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this would lead to more precise information o n the limiting behaviour (in particular, it would show that certain asymptotic expressions related to multiple recurrence actually converged to a limit, which was a question left open from Furstenberg’s original argument s). Counterexamples of Furstenberg and Weiss, as well as results of Conze and Lesigne, eventually led to the conclusion that these characteristic factors should be describable by a very special (and algebraic) type of measure-preserving system, namely a nilsystem associated with nilpotent groups; these conclusions culminated in precise and rigorous descriptions of these factors in a technically impressive paper of Ho st and Kra [20] (and subsequently also by Ziegler [39]), which among other things settled the question mentioned earlier concerning convergence of the asymptotic multiple recurrence averages. The central role of these characteristic f actors illustrated quite starkly the presence of a dichotomy between structure (as represented here by nilsystems), and randomness (which is captured by a certain technical type of “mixing” property), and to the insight t hat it is this dichotomy which in fact underlies and powers Szemer´edi’s theorem and its relatives. Another feature of the Ho st- K r a analysis wo rt h mentioning is the pro minent appearance of averages a ssociated to “cubes” or “parallelopipeds”, which turn out to be more tractable to analyse for a number of reasons than the multiple recurrence averages associated to a r ithmetic progressions.

In parallel to these ergodic theory developments, other mathematicians were seeking to understand, reprove, and improve upon Szemer´edi’s theorem in other ways. An important conceptual breakthrough was made by Ruzsa and Szemer´edi [29], who used the Szemer´edi regularity lemma mentioned earlier to establish a number of results in graph theory, including what is now known as the triangle rem o val lem ma, which roughly asserts that a graph which contains a small number triangles can have those triangles removed by deleting a surprisingly small number of edges. They then observed that the Behrend example mentioned earlier gave some limits as to the quantitative bo unds in this lemma, in particular ruling out many classes of elementary approaches to this lemma (as such approaches typically give polynomial type bounds); indeed to this day all known proofs of the removal lemma proceed via some variant of the regularity lemma. Applying this connection in the contrapositive, it was observed that in fact the triangle removal lemma implied Roth’s theorem on progressions of length three. This discovery opened up for the ﬁrst time the possibility that Szemer´edi type theorems could be proven by purely graph- theoretical techniques, discarding almost entirely the additive structure of the problem. (Note that the ergodic theory approach still retained this structure, in the guise of the action of the shift operator on the system; also, Szemer´edi’s original proof is o nly partly graph-theoretical, as it exploits the additive structure of progressions in many diﬀerent places.) It t ook some time though to realise that the graph theoretic method, like the Fourier-analytic method before it, was largely restricted to detecting “low complexity” patterns such as triangles or progressions of length three, and to detect progressions of longer length would require the substantially more diﬃcult theory of h ypergraphs. In particular this motivated the program (spearheaded by Frankl and R¨odl) for obtaining satisfactory analogue of the regularity lemma for hypergraphs, which would be strong enough to yield consequences such as Szemer´edi’s theorem (as well as a number of variants and generalisations). This turned out to be a surprisingly delicate

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task, in particular carefully arranging the hierarchy 13 of parameters involved in such a regularisation so that they dominated each o t her in the correct order. Indeed the ﬁnal versions of the regularity lemma, and the companion “counting lemmas” from which one could deduce Szemer´edi’s theorem, have only appeared rather recently ([22], [2 4], [25], [26], [14], . . .). It is also worth mentioning a very instructive counterexample [10] of Gowers, which shows that the quantitative bounds in the original regularity lemma must be at least tower-exponent ia l in nature, thus indicating again the non-trivial nature (and power) of this lemma.

The Fourier analytic approach to Szemer´edi’s theorem, which had not progressed signiﬁcantly since the work of Roth, was ﬁnally revisited by Gowers [11], [13]. As with other approaches, the Fourier-ana lytic approach proceeded by establishing a dichotomy on sets of integers, that they were either structured or pseudora ndom in some sense. The relevant notio n o f structure here was worked out by Roth - structured sets should enjoy a density increment on medium-length arithmetic progressions - but the correct notion of pseudorandomness or “uniformity” was less clear. Gowers produced an example (closely related, in fact, to examples of Furstenberg and Weiss mentioned earlier) showing that Fourier-based notions o f pseudorandomness were inadequate for controlling progressions of length f our and higher, and then proceeded to introduce a diﬀerent notion of uniformity (very closely related to the cube averages of Host and Kra, and also to certain notions of hypergraph regularity) which suﬃced. The remaining task was to establish a quantitative and rigorous form of the dichotomy. This turned out to be surprisingly diﬃcult (mainly due to the limited utility of the Fourier transform in this setting), and in many ways analogous to the eﬀorts of Host-Kra and Ziegler to endow char acteristic factors with the algebraic structure of nilsystems. However, by combining Fo urier analytic tools with major results from additive combinatorics such as Freiman’s theorem and the Balo g-Szemer´edi theorem (the history of these being also an interesting story in its own right, see e.g. [35]), together with several new combinatorial and probabilistic methods, Gowers was able to achieve this in a remarkable tour de force, and in particular obtained remarkably strong quantitative bounds on Szemer´edi’s theorem and van der Waerden’s theorem 14 . To summarise so far, four parallel proofs of Szemer´edi’s theorem have been achieved; one by direct combinatorics, one by ergodic theory, one by hypergraph theory, a nd one by Fourier analysis and additive combinatorics. Even with so many proofs, there was still a sense that our understanding of this result was still incomplete; for instance, none of the approaches were powerful enough to detect progressions in the primes, mainly because of the sparsity of the prime sequence. (The Fourier method, or more precisely the Hardy-Littlewood-Vinogradov circle method, can be used however to establish inﬁnitely many progressions of length three in the primes [36], and with substantially more eﬀort can also partially address progressions of length four [19].) However, by using ideas from restriction theory in harmonic analysis (which is another fascinating story that we

13 This hierarchy seems related to the towers of extensions encountered by Furstenberg in his analogous quest to “regularise” a measure-preserving system, though the precise connection is still poorly understood at present.

14 It is worth noting also the brilliantly creative proof of van der Waerden’s theorem by Shelah [30], which held the previous record for the best constants for this theorem; the ideas of Shelah’s proof have not yet been successfully integrated into the rest of the subject, but I expect that this will happen in the future.

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will not discuss here), Green [15] was able to treat the primes “as if” they were dense, and in particular obtain an analogue of Roth’s theorem for dense subsets of primes. This opened up the intruiging possibility of a relative Szemer´edi theorem, a llowing one to detect ar ithmetic pro gressions in dense subsets of other sets than the integers, for instance dense subsets of primes. Indeed, a prototypical relative Roth theorem for dense subsets of quite sparse random sets had already appeared in the graph theory literature [21].

In j oint work 15 with Ben Green, we began the task of trying to relativise Gowers’ Fourier analytic and combinatorial arguments to such contexts as dense subsets of sparse random or “pseudorandom” sets. After much eﬀort (inspired in part by t he hypergraph theory, which was well adapted to count patterns in sparse sets, and also in part by an “arithmetic regularity lemma” of Green [16 ] that adapted the regularity lemma ideas from graph theory to additive contexts) we were eventually able (in an unpublished work) to detect progressions of length four in such sets. At this point we realised the analogies between the regularity lemma approach we were using, and the characteristic factor constructions in Host-Kra, and by substituting 16 in those constructions (in particular relying heavily on cube averages) we were able to establish a satisfactory relative Szemer´edi theorem, which relied on a certain transference p rinciple which asserted, roughly speaking, that dense subsets of sparse pseudorandom sets behaved “as if” they were dense in the original space. In order to apply this theorem to the primes, we needed t o enclose the primes in a suitably pseudorandom set (or more precisely a measure); but very fortuitiously for us, the recent breakthroughs 17 of Goldston and Yıldırım [8] on prime gaps 18 had constructed almost exactly what we needed for this purpose, allowing us to establish at last the old conjecture that the primes contained arbitrarily long arithmetic progressions.

The story still does not end here, but instead continues to develop in several directions. On one hand there are now a number of further applications of the tra nsference principle, for instance to obtain constellations in the Gaussian primes o r po lynomial progressions in the rat io na l primes. Another promising avenue of research is the convergence of the Fourier, hypergraph, and ergodic theory methods to each other, for instance in developing inﬁnitary versions of the graph and hypergraph theory (which have applications to o t her a reas of mathematics as well, such as property testing) or ﬁnitary versions of the ergodic theory. A third direction is to make the nilsystems that control recurrence in the ergodic theory setting, also control various ﬁnitary averages

15 Incidentally, I was initially attracted to these problems by their intersection with another great mathematical story, that of the Kakeya conjecture, which we again do not have space to discuss here. It is however related in a somewhat surprising fashion with the story of restriction theory mentioned earlier.

16 This was a little tricky for a number of reasons, most notably that the ergodic theory constructions were inﬁnitary in nature, whereas to deal with the primes it was necessary to work in a ﬁnitary context. Fortunately I had already attempted to ﬁnitise the ergodic approach to Szemer´edi’s theorem [34]; while that attempt was incomplete at the time, it turned out to have enough substance to be helpful for the application to the primes.

17 At the time of our paper, the construction we used was from a paper of Goldston and Yıldırım that was retracted for an unrelated error, which they eventually repaired with some clever new ideas from Pintz [9]. This supports a point made earlier, that it is not absolutely necessary for a piece of mathematics to be absolutely correct in every detail in order to be of value to future (rigorous) work.

18 Once again, the story of prime gaps is an interesting one which we will be unable to pursue here.

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relating to arithmetic progressions; in particular, G reen and I are actively working on computing correlations between primes and sequences generated by nilsystems (using methods dating back to Vinogradov) in order to establish more precise asymptotics on vario us patterns that can be found in the primes. Last, but not least, there is the original Erd˝os-Tur´an conjecture, which still remains open after all this progress, though there is now some very promising advances of Bourgain [2], [3] which should lead to further developments.

3. Conclusion

As we can see from the above case study, the very best examples of good mathematics do not merely fulﬁl one or more of the criteria of mathematical quality listed at the beginning of this article, but are more importantly part of a greater mathematical story, which then unfurls to generate many further pieces of good mathematics of many diﬀerent types. Indeed, one can view the history of entire ﬁelds of mathematics as being primarily generated by a handful of these great stories, their evolution thro ugh time, and their interaction with each other. I would thus conclude that good mathematics is not merely measured by one o r more of the “local” qualities listed previously (though these ar e certainly important, and worth pursuing and debating), but also depends on the more “global” question of how it ﬁts in with other pieces of good mathematics, either by building upon earlier achievements or encouraging the development of future breakthroughs. Of course, without the beneﬁt of hindsight it is diﬃcult to predict with certainty what types o f mathematics will have such a property. There does however seem to be some undeﬁnable sense that a certain piece of mathematics is “on to something”, that it is a piece of a larger puzzle waiting to be explored further. And it seems to me that it is the pursuit o f such intangible promises of f uture potential are least as important an aspect of mathematical progress than the more concrete and obvious aspects of mathematical quality listed previously. Thus I believe that good mathematics is more than simply the process of solving problems, building theories, and making arguments shorter, stronger, clearer, more elegant, or more rigorous, though these are of course all admirable goals; while achieving all of these tasks (and debating which ones should have higher priority within any given ﬁeld), we should also be aware of any possible larger context that one’s results could be placed in, as this may well lead to the greatest long-term beneﬁt for the result, for the ﬁeld, and for mathematics as a whole.

4. Acknowledgements

I thank Laura Kim for reading and commenting on an early draft of this manuscript, and Gil Kalai for many thoughtful comments and suggestions.

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(2007), 53-97. Department of Mathematics, UCLA, Los Angeles CA 90095 -1555, USA. E-mail address: tao@math.ucla.edu

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