Interview with Research Fellow Terence Tao
From an early age, you clearly possessed a gift for mathematics. What stimulated your interest in the subject, and when did you discover your talent for mathematical research? Which persons influenced you the most?
Ever since I can remember, I have enjoyed mathematics; I recall being fascinated by numbers even at age three, and viewed their manipulation as a kind of game. It was only much later, in high school, that I started to realize that mathematics is not just about symbolic manipulation, but has useful things to say about the real world; then, of course, I enjoyed it even more, though at a different level.
My parents were the ones who noticed my mathematical ability, and sought the advice of several teachers, professors, and education experts; I myself didn't feel anything out of the ordinary in what I was doing. I didn't really have any other experience to compare it to, so it felt natural to me. I was fortunate enough to have several good mentors during my high-school and college years who were willing to spend time with me just to discuss mathematics at a leisurely pace. For instance, there was a retired mathematics professor, Basil Rennie (who sadly died a few years ago), who I would visit each weekend and talk about recreational mathematics over tea and cakes. At the local university, Garth Gaudry also spent a lot of time with me and eventually became my masters thesis advisor; he was also the one who got me working in analysis, where I still primarily do most of my mathematics, and who encouraged me to study in the US. Once in graduate school, I of course benefitted from interaction with many other mathematicians, such as my advisor Eli Stein. But the same would be true of any other graduate student in mathematics.
You left Australia in 1992 to study mathematics at Princeton University. What inspired your decision to go there?
This was mostly at the urging of my masters thesis advisor Garth Gaudry. He felt that regardless of where I ended up eventually, in Australia, the US, or elsewhere, it would be good to get some international experience at the graduate level. There are of course several good universities in Australia also, but they unfortunately suffer somewhat from geographic isolation. I recall applying to a dozen places, and ending up with acceptance offers from both Princeton and MIT. I guess in the end I chose Princeton for its strength in harmonic analysis (in particular because of Eli Stein - I was already learning harmonic analysis in Australia out of his textbooks!)
After I completed my dissertation at Princeton, I was torn between continuing to work in the US and returning to Australia. Eventually I settled on a compromise in which I spent half the time in each; but now that I have settled down in Los Angeles with my work and family, I will probably stay in the US permanently.
What is the primary focus of your research today? Can you comment on the results of which you are most fond?
I work in a number of areas, but I don't view them as being disconnected. I tend to view mathematics as a unified subject and am particularly happy when I get the opportunity to work on a project that involves several fields at once. Perhaps the largest "connected component" of my research ranges from arithmetic and geometric combinatorics at one end (the study of arrangements of geometric objects such as lines and circles, including one of my favorite conjectures, the Kakeya conjecture, or the combinatorics of addition, subtraction and multiplication of sets), through harmonic analysis (especially the study of oscillatory integrals, maximal functions, and solutions to the linear wave and Schrödinger equations), and ends up in nonlinear PDE (especially nonlinear wave and dispersive equations).
Currently my focus is more at the nonlinear PDE end of this range, especially with regard to the global and asymptotic behavior of such evolution equations, and also with the hope of combining the analytical tools of nonlinear PDE with the more algebraic tools of completely integrable systems at some point. In addition, I work in a number of areas adjacent to one of the above fields; for instance I have begun to be interested in arithmetic progressions and connections with number theory, as well as with other aspects of harmonic analysis such as multilinear integrals, and other aspects of PDE, such as the spectral theory of Schrödinger operators with potentials or integrable systems.
Finally, with Allen Knutson, I have a rather different line of research: the algebraic combinatorics of several related problems, including the sum of Hermitian matrices problem, the tensor product muliplicities of representations, and intersections of Schubert varieties. Though we only have a few papers in this field, I still count this as one of my favorite areas to work in. This is because of all the unexpected structure and algebraic "miracles" which occur in these problems, and also because it is so technically and conceptually challenging. Of course, I also enjoy my work in analysis, but for a different reason. There are fewer miracles, but instead there is lots of intuition coming from physics and from geometry. The challenge is to quantify and exploit as much of this intuition as possible.
In analysis, many research programs do not conclude in a definitive paper, but rather in a progression of steadily improving partial results. Much of my work has been of this type (especially with regards to the Kakeya problem and its relatives, still one of my primary foci of research). But I do have two or three results of a more conclusive nature of which I feel particularly satisfied. The first is my original paper with Allen Knutson, in which we characterize the eigenvalues of a sum of two Hermitian matrices, first by reducing it to a purely geometric combinatorial question (that of understanding a certain geometric configuration called a "honeycomb"), and then by solving that question by a combinatorial argument. (There have since been a number of other proofs and conceptual clarifications, although the exact role of honeycombs remains partly mysterious). The second is my paper on the small energy global regularity of wave maps to the sphere in two dimensions, in which I introduce a new "microlocal" renormalization in order to turn this rather nonlinear problem into a more manageable semilinear evolution. While the result in itself is not yet definitive (the equation of general target manifolds other than the sphere was done afterwards, and the large energy case remains open, and very interesting), it did remove a psychological stumbling block by showing that these critical wave equations were not intractable. As a result there has been a resurgence of interest in these equations. Finally, I have had a very productive and enjoyable collaboration with Jim Colliander, Markus Keel, Gigliola Staffilani, and Hideo Takaoka, culminating this year in the establishment of global regularity and scattering for a critical nonlinear Schrödinger equation (for large energy data); this appears to be the first unconditional global existence result for this type of critical dispersive equation. The result required assembling and then refining several recent techniques developed in this field, including an induction-on-energy approach pioneered by Bourgain, and a certain interaction Morawetz inequality we had discovered a few years earlier. The result seems to reveal some new insights into the dynamics of such equations. It is still in its very early days, but I feel confident that the ideas developed here will have further application to understanding the large energy behavior of other nonlinear evolution equations. This is the topic I am still immensely interested in.
You have worked on problems quite far from the main focus of your research, e.g. Horn's conjecture. Could you comment on the motivation for this work and the challenges it presented? On your collaborations and the idea of collaboration in general? Can a mathematician in this day of specialization hope to contribute to more than one area?
My work on Horn's conjecture stemmed from discussions I had with Allen Knutson in graduate school. Back then we were not completely decided as to which field to specialize in and had (rather naively) searched around for interesting research problems to attack together. Most of these ended up being discarded, but the sum of Hermitian matrices problem (which we ended up working on as a simplified model of another question posed by another graduate student) was a lucky one to work on, as it had so much unexpected structure. For instance, it can be phrased as a moment map problem in symplectic geometry, and later we realized it could also be quantized as a multiplicity problem in representation theory. The problem has the advantage of being elementary enough that one can make a fair bit of progress without too much machinery we had begun deriving various inequalities and other results, although we eventually were a bit disappointed to learn that we had rediscovered some very old results of Weyl, Gelfand, Horn, and others by doing so. By the time we finished graduate school, we had gotten to the point where we had discovered the role of honeycombs in the problem. We could not rigorously prove the connection between honeycombs and the Hermitian matrices problem, and were otherwise stuck. But then Allen learned of more recent work on this problem by algebraic combinatorialists and algebraic geometers, including Klyachko, Totaro, Bernstein, Zelevinsky, and others. With the more recent results from those authors we were able to plug the missing pieces in our argument and eventually settle the Horn conjecture.
Collaboration is very important for me, as it allows me to learn about other fields, and, conversely, to share what I learned about my own fields with others. It broadens my experience, not just in a technical mathematical sense but also in being exposed to other philosophies of research, of exposition, and so forth. Also, it is considerably more fun to work in groups than by oneself. Ideally, a collaborator should be close enough to one's own strengths that one can communicate ideas and strategies back and forth with ease, but far enough apart that one's skills complement rather than replicate each other.
It is true that mathematics is more specialized than at any time in its past, but I don't believe that any field of mathematics should ever get so technical and complicated that it could not (at least in principle) be accessible to a general mathematician after some patient work (and with a good exposition by an expert in the field). Even if the rigorous machinery is very complicated, often the ideas and goals of a field are often so simple, elegant, and natural that I feel it is frequently more than one's while to invest the time and effort to learn about other fields. Of course, this task is helped immeasurably if you can talk at length with someone who is already expert in those areas; but again, this is why collaboration is so useful. Even just attending conferences and seminars that are just a little bit outside your own field is useful. In fact, I believe that a subfield of mathematics has a better chance of staying dynamic, fruitful, and exciting if people in the area do make an effort to make good surveys and expository articles that try to reach out to other people in neighboring disciplines and invite them to lend their own insights and expertise to attack the problems in the area. The need to develop fearsome and impenetrable machinery in a field is a necessary evil, unfortunately, but as understanding progresses it should not be a permanent evil. If it serves to keep away other skilled mathematicians who might otherwise have useful contributions to make, then that is a loss for mathematics.
Also, counterbalancing the trend toward increasing complexity and specialization at the cutting edge of mathematics is the deepening insight and simplification of mathematics at its common core. Harmonic analysis, for instance, is a far more organized and intuitive subject than it was in, say, the days of Hardy and Littlewood; results and arguments are not isolated technical feats but put into a wider context of interaction between oscillation, singularity, geometry, and so forth. PDE also appears to be undergoing a similar conceptual organization, with less emphasis on specific techniques such as estimates and choices of function spaces, and instead sharing more in common with the underlying geometric and physical intuition. In some ways, the accumulated rules of thumb, folklore, and even just some very well chosen choices of notation can make it easier to get into a field nowadays. (It depends on the field, of course; some have made far more progress with conceptual simplification than others).
Can you describe your research in accessible terms? Does it have applications to other areas?
I guess I can start with nonlinear PDE, which is perhaps the area of my research which is closest to "real life" applications. I am interested in many nonlinear PDE which arise in physics (Korteweg-de Vries, nonlinear Schrödinger, wave maps, Yang-Mills, Einstein, ...). However, in many cases these equations are only a simplified model of the physical reality, and the arguments which justify them as a good approximation to the actual situation are usually just heuristic. Thus, it is quite important to know whether these models are robust or not, in that they can tolerate the errors and approximations used to pass from reality to the model. In order for a model to be robust, it should first be well posed; in other words, solutions should exist for all time and depend in a stable way on the initial data (or on any forcing terms). If a model predicts instead that some physical quantity (e.g. the energy) should go to infinity in finite time, then that is pretty clearly not a good model for reality.
One of my main research interests is then in understanding the global existence, regularity, and asymptotic behavior of nonlinear evolution equations (particularly nonlinear Schrödinger and wave equations). These results are already interesting in themselves, but what I find most fascinating is that the very process of discovering results in these problems, especially if one enforces the discipline of working in a low regularity setting or under minimal assumptions on the data, leads one to uncover new insights and facts about such equations, which then become useful in many other settings too. To take one example, in my joint work with Colliander, Keel, Staffilani, and Takaoka, we were studying the scattering behavior of a certain subcritical nonlinear Schrodinger equation under the assumption of infinite energy. The case of finite energy was already handled before, so this research may have seemed of purely academic interest. However, the challenge of working in the infinite energy case took away several of the tools which were available for this problem, and forced us to come up with a new tool -in this case, we discovered a certain interaction Morawetz inequality which was totally new. This inequality not only solved our problem, but led to a substantial simplification of the original argument in the finite energy case, and later was a key ingredient in our resolution of the global regularity problem for the _critical_ nonlinear Schrodinger equation, which was previously unknown even for smooth, finite energy data. It is these sorts of discoveries that make the investment into even quite technical areas of a subject quite worthwhile. It seems unlikely that this inequality would have been discovered if we were only looking at the case of smooth solutions (in which many other techniques were available).
Much of my other work is not as directly related to physical reality as nonlinear PDE, but there are some connections, and again there is always the chance that while working on a technical problem, some new insight or tool will be discovered which can then be applied to other problems, and which clarify conceptually the field as a whole. For instance, linear and nonlinear PDE often encounters the issue of how to control a superposition of oscillating waves at various frequencies, positions, and directions; in many cases this issue can be dealt with by standard harmonic analysis techniques such as the Fourier transform, but one can consider model harmonic analysis problems (such as the restriction conjecture) in which the standard techniques give only partial results. This in turn turns out (by the harmonic analysis analogue of geometric optics, which converts questions about waves into questions about light rays) to be related to another problem about incidences of light rays and other geometric objects, which in turn connects to the purely combinatorial Kakeya problem mentioned earlier. This in turn connects (via the re-interpretation of lines as arithmetic progressions) to some questions in arithmetic combinatorics, and this in turn can connect to other areas of mathematics such as number theory. I find all these connections fascinating, and also give me an excuse to learn adjacent fields of mathematics; my investment of time has almost always been rewarded with new understanding and another collection of techniques to add to my "toolbox".
What advice would you give to young people starting out in math (i.e. high school students and young researchers)?
Well, I guess they should be warned that their impressions of what professional mathematics is may be quite different from the reality. In elementary school I had the vague idea that professional mathematicians spent their time computing digits of pi, for instance, or perhaps devising and then solving Math Olympiad style problems. In high school and lower-division undergraduate mathematics, one can often get the impression that mathematics is a "solved" science, and that all that one needs to do nowadays is remember all the tools and techniques that were derived centuries earlier. Conversely, in upper-division mathematics, the subjects that seem the most beautiful, and which sound like the most fun to work on - for me, they were C-* algebras and elementary number theory - often end up being very heavily studied already, and nowadays just the foundation for even more interesting areas of research. It's really difficult to tell, until late in graduate school, what the active areas of research really are, and which ones will be most suited to your taste. I myself was lucky that the field I chose (harmonic analysis) was one that was quite fruitful and enjoyable to me, even if the things I work on now are things I would not even have contemplated thinking about as a graduate student.
So, I would not fixate too much on wanting to go into one specific subfield of mathematics (or even into mathematics altogether), based on one's experiences, say, at the undergraduate level; in many ways, the subject only just begins to get interesting at the graduate level and above. Conversely, subjects which seemed quite dry when learnt in an undergraduate context can become revitalized under the more modern perspective that one might learn later in one's career. To give just one example, the theory of matrices and determinants makes much more sense when viewed using the concepts of linear transformations and wedge products (and this in turn can be viewed even more clearly using even higher conceptual tools such as vector bundles, tensor products, categories, Lie groups, Clifford algebras, etc.). Not many people study determinants directly any more, but there are many fields that are descendants of the classical theory of determinants which are all very active and important.
The other thing is not to be too afraid (or too disdainful) of other fields, and to take the effort to at least get a little understanding of what is going on in neighboring fields of activity. You never know when it will come in handy. For instance, I have recently started encountering little algebraic geometry problems to solve in the Kakeya problem, which previously I thought to be a purely combinatorial problem involving elementary incidence geometry. This forced me to revisit my old graduate textbooks on algebraic varieties and the like, but this time with more motivation and experience I was able to learn a lot more, and eventually could use the rudiments of the subject that I had learnt to make some progress on the Kakeya problem.
You have some quite specific ideas about problem solving. Can you tell us about them?
Everyone has their own problem solving style, of course. Andrew Wiles worked on Fermat's Last Theorem more or less continuously for about seven years. I myself couldn't do that; if I don't see hints of progress within a week or two, then even if the problem is tremendously exciting I will feel inclined to shelve it and work on other problems. After a year or so I might return to the problem and hopefully with a fresh perspective and some new ideas and tools I can make further progress.
One good thing about analysis is that for every difficult unsolved problem, there is often a less difficult model problem which can be worked on first. Or if solving a certain problem requires one to resolve obstruction A and obstruction B, one can often locate toy subproblems in which only one of the two obstructions is present (or at least one may make an artificial hypothesis which suppresses one of the two obstructions). So often it makes excellent tactical sense to move away from your original target problem, and work instead on problems which are perhaps less intrinsically interesting, but which are simpler and which embody at least one of the difficulties you would also encounter in the original problem. So, a large part of my problem solving technique involves understanding the problem and its obstructions well enough that one can concoct reasonable models to work in. For instance, one might model a PDE by an ODE after making various assumptions on the solution which one could then justify by various non-rigorous heuristics. The ODE in turn might be modeled by a discrete difference scheme, and perhaps after a few more heuristic reductions of this type one may be left with a very simple problem, say involving just a finite number of quantities, which still contains the key obstruction; at this point, one should either be able to see what has to be done to resolve the obstruction, or else start concocting a counter example (which is then also interesting; or else the counter example construction, when passing back to the original problem; hits another obstruction, which you then work on again by passing to a model, and so forth). As such, my work on a problem often takes me in rather unpredictable directions, but even the directions which seem to waste a lot of time can often be quite educational, if only in a negative sense that certain techniques are unlikely to work. Of course, there are times when I cannot make progress on an obstruction even after I have simplified away all the other aspects of the problem; usually if I can't get anywhere from that point after a few days or so, I will move on to try something else instead (e.g. I will work on another problem which does not have this particular obstruction). Very occasionally, after some years pass, I work on what I think to be a completely unrelated problem, and discover (either by myself, by a collaborator, or by reading another paper) an idea which has a chance of resolving an obstruction which blocked me in an earlier problem. This, so far, has happened only a few times for me, but it is very satisfying when it does. Of course, if I had stayed focused on my original problem continuously, I might also have found the solution eventually; but I find that more difficult to sustain than the more scatter shot approach I am used to. It may work out differently for others, though.
What advice would you give to older people interested in mathematics as a hobby? What should they read? How should they proceed?
It is unfortunately difficult to get into an advanced field of mathematics these days without being in contact with people already in the field; there is only so much one can learn from books alone (although the web and internet, if used correctly, is a great resource also nowadays). Some fields change so rapidly that one can take a vacation from a field for, say, five years, and barely recognize the field when one returns. But if one already has mastered one area of mathematics, that often gives enough confidence to start exploring other areas. As a graduate student, I was daunted by analytic number theory and PDE, two subjects I was quite interested in, because both subjects also required a fair understanding of harmonic analysis, which I did not have at the time. But once I had some experience in harmonic analysis I was able to revisit those fields and learn them more effectively.
As I said earlier, the actual experience of research in a field may differ quite dramatically from what one might imagine it to be like as an outsider. Number theory, to give an example, is very accessible (at least at first) and thus attracts a lot of interest from recreational mathematicians, but they can become discouraged upon learning that modern progress in the field relies in such sophisticated tools as exponential sums, zeta functions, modular forms, elliptic curves, and so forth. This is not to say that there is no longer any place for elementary number theory - witness, for instance, the recent excitement over the first deterministic polynomial time primality testing algorithm - but the field is not what one may believe it to be from the outside.
As I have spent my entire life with mathematics, perhaps I am not the best qualified to discuss how to get into the field at a later age, but perhaps it would make sense to stay close to one's existing strengths; for instance, if one has an engineering background, then mathematical physics, dynamical systems, or ODE might make sense, or if one has a computer science background then discrete mathematics or complexity theory might make sense.
Your education and now your teaching career is divided between two countries. Is this by choice?
Partly by choice and partly by visa considerations; I had a visa requirement that required me to spend 24 months in my home country before applying for permanent residency. But now I have completed that requirement, and am settled in Los Angeles with my wife and son, so will probably be spending much more time in the US now.
How has maintaining your ties with the Australian mathematical community influenced your research?
Most directly, I have had several collaborations with Australian mathematicians, or with international mathematicians who were visiting Australia. But while Australian mathematics has a slightly different character from, say, American or French or Japanese or Russian mathematics, it is not so distinct that one can readily separate any distinctly Australian flavors from other aspects of my research. I get a lot out of visiting mathematics departments throughout the US and internationally, because every department has a slightly different focus and set of strengths in mathematics, and I have collaborators from all over the world; I think the internationality of mathematics is one of its great strengths.
Can you comment on the culture of research mathematics in Australia? How does it compare to the U.S.?
Culturally, they are fairly similar. The two major differences are firstly, that Australia is much smaller in population and more isolated geographically, which means that it is more difficult (though not impossible) to maintain an active visitor program. Still, there is enough interaction between Australia and the rest of the mathematical community that I believe the research in Australia is quite competitive by international standards. The other major difference is that there are very little sources of private funding (either corporate or philanthropic) in Australia for higher mathematics research, and as such we are almost entirely reliant on state and federal government support. This may create some difficulties for Australia in the long term, as it may be difficult to recruit and retain good talent with the limited financial resources available.
How has your Clay fellowship made a difference for you?
The Clay has been very useful in granting a large amount of flexibility in my travel and visiting plans, especially since I was also subject to certain visa restrictions at the time. For instance, it has made visiting Australia much easier. Also I was supported by CMI on several trips to Europe and on an extended stay at Princeton, both of which were very useful to me mathematically, allowing me to interact and exchange ideas with many other mathematicians (some of whom I would later collaborate with).
Recently you received two great honors: the AMS Bôcher Prize and the Clay Research Award, for results that distinguish you for your contributions to analysis and other fields. Have your findings opened up new areas or spawned new collaborations? Who else has made major contributions to this specific area of research?
The work on wave maps (the main research designated by the Bôcher prize) is still quite active; after my own papers there were further improvements and developments by Klainerman, Rodnianski, Shatah, Struwe, Nahmod, Uhlenbeck, Stefanov, Krieger, Tataru, and others. (My work in turn built upon earlier work of these authors as well as Machedon, Selberg, Keel, and others). Perhaps more indirectly, the mere fact that critical nonlinear wave equations can be tractable may have helped encourage the parallel lines of research on sister equations such as the Einstein equations, Maxwell-Klein-Gordon, or Yang-Mills. This research is also part of a larger trend where the analysis of the equations is moving beyond what can be achieved with Fourier analysis techniques and energy methods, and is beginning to incorporate more geometric ideas (in particular, to use ideas from Riemannian geometry to control geometric objects such as connections and geodesics, these in turn can be used to control the evolution of the nonlinear wave equation).
The Clay award recognized not only the work on wave maps, but also on sharp restriction theorems for the Fourier transform, which was an area pioneered by such great mathematicians as Carleson, Sjolin, Tomas, Stein, Fefferman, and Cordoba almost thirty years ago, and which has been invigorated by more recent work of Bourgain, Wolff, and others. These problems are still not solved fully; this would require, among other things, a complete solution to the Kakeya conjecture. The relationship of these problems both to geometry and to PDE has been greatly clarified however, and the technical tools required to make concrete these connections are also much better understood. Recent work by Vargas, Lee, and others continue to develop the theory of these estimates.
The Clay award also mentioned the work on honeycombs and Horn's conjecture. Horn's conjecture has now been proven in a number of ways (thanks to later work by Belkale, Buch, Weyman, Derksen, Knutson, Totaro, Woodward, Fulton, Vakil and others), and we are close to a more satisfactory geometric understanding of this problem. Lately, Allen and I have been more interested in the connection with Schubert geometry, which is connected to a discrete analogue of a honeycomb which we call a "puzzle". These puzzles seem to encode in some compact way the geometric combinatorics of Grassmannians and flag varieties, and there is some exciting work of Knutson and Vakil that seems to "geometrize" the role of these puzzles (and the combinatorics of the Littlewood-Richardson rule in general) quite neatly. There is also some related work of Speyer that may shed some light on one of the more mysterious combinatorial aspects of these puzzles, namely that they are "associative".
What research problems are you likely to explore in the future?
It's hard to say. As I said before, even five years ago I would not really have imagined working on what I am doing now. I still find the problems related to the Kakeya problem fascinating, as well as anything to do with honeycombs and puzzles. But currently I am more involved in nonlinear PDE, with an eye toward moving toward integrable systems. Related to this is a long-term joint research project with Christoph Thiele on the nonlinear Fourier transform (also known as the scattering transform) and its connection with integrable systems. I am also getting interested in arithmetic progressions and their connections with combinatorics, number theory, and even ergodic theory. I have also been learning bits and pieces of differential geometry and algebraic geometry and may take more of an interest in those fields in the future. Certainly at this point I have more interesting directions to pursue than I have time to work with!
What are your thoughts on the Millennium Prize Problems, the Navier-Stokes Equation for example?
The prize problems are great publicity for mathematics, and have made the recent possible resolution of Poincaré's conjecture—which is already an amazing and very important mathematical achievement—much more publicized and exciting than it already was. It is unclear how close the other problems are to resolution, though they all have several major obstructions that need to be resolved first. For Navier Stokes, one of the major obstructions is turbulence. This equation is "supercritical", which roughly means that the energy can interact much more forcefully at fine scales than it can at coarse scales (in contrast to subcritical equations where the coarse scale behavior dominates, and critical equations where all scales contribute equally). As yet we do not have a good large data global theory for any supercritical equation, let alone Navier Stokes, without some additional constraints on the solution to somehow ameliorate the behavior of the fine scales. A new technique that would allow us to handle very turbulent solutions effectively would be a major achievement. Perhaps one hope lies in the stochastic models of these flows, although it would be a challenge to show that these stochastic models really do model the deterministic Navier-Stokes equation properly.
Again, there are many sister equations of Navier-Stokes, and it may well be that the ultimate solution to this problem may lie in first understanding a related model equations—the Euler equations, for instance. Even Navier-Stokes is itself a model for other, more complicated, fluid dynamics. So while Navier-Stokes is certainly an important equation in fluid equations, there should not be given the impression that the Clay prize problem is the only problem worth studying there.