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Terence Chi-Shen Tao is an Australian mathematician, and a professo...
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Szemeredi’s theorem: In arithmetic combinatorics, Szemerédi's theor...
arXiv:math/0702396v1 [math.HO] 13 Feb 2007
WHAT IS GOOD MATHEMATICS?
TERENCE TAO
Abstract. Some personal thoughts and opinions on what “good quality mathemat-
ics” is, and whether one should try to define this term rigorously. As a case study, the
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 math-
ematical 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
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 high-
dimensional one, and lacks an obvious canonical total ordering
2
. I believe this is be-
cause 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 mathemat-
ics 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; differ-
ent 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 ap-
proaches to the subject, and exploit many different types of mathematical talent, to-
wards 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.
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 gen-
uine 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 solv-
ing 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 high-
dimensional, 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.
4 TERENCE TAO
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 it-
self. 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
´
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 Sze-
mer´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 progres-
sions. 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 theo-
rem [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), repre-
sented 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].
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, culmi-
nating 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 el-
ementary 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.
6 TERENCE TAO
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 quantita-
tive 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 par-
ticular 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 theo-
rems, 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 con-
trolled 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 var-
ious 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 shift-
invariant functions controls the limiting behaviour of simple averages of shifts.
WHAT IS GOOD MATHEMATICS? 7
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 actu-
ally 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 recur-
rence 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 mention-
ing 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
8 TERENCE TAO
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 sig-
nificantly 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 exam-
ple (closely related, in fact, to examples of Furstenberg and Weiss mentioned earlier)
showing that Fourier-based notions o f pseudorandomness were inadequate for control-
ling 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 be-
cause 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 anal-
ogous 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.
WHAT IS GOOD MATHEMATICS? 9
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 characteris-
tic 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 as-
serted, 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 direc-
tions. 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 con-
vergence 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.
10 TERENCE TAO
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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12 TERENCE TAO
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Department of Mathematics, UCLA, Los Angeles CA 90095 -1555, USA.
E-mail address: tao@math.ucla.edu
>> "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/
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
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
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/