Unfashionable Pursuits

Unfashionable Pursuits* Freeman J. Dyson

Introduction I am delighted to be talking today as a representative of the Institute for Advanced Study to an audience of Humboldt Foundation alumni, since the Institute and the Foundation are both trying to support science on an international scale and are facing similar dilemmas and difficulties. We are both trying to carry on the tradition established by Alexander von Humboldt 150 years ago. Wanting to learn a little about von Humboldt, I went to the eleventh edition of the Encyclopedia Britannica, printed in 1910, and found a splendid article written by the historian of science Agnes Clerke. If you go to later editions, you find Clerke's account only in shreds and tatters. In her article she describes the work of von Humboldt in setting up the first international network of meteorological and magnetic observation stations and concludes with this resounding sentence: "Thus that scientific conspiracy of nations which is one of the noblest fruits of modern civilization was by his exertions first successfully organized." So that is what we are trying to do, the Institute and the Foundation, following the good example of von Humboldt. We are trying to strengthen and extend in our own era the scientific conspiracy of nations.

finally I shall say a few words suggesting how we may try to deal more wisely with the problem in the future. It has always been true, a n d it is true now more than ever, that the path of wisdom for a young scientist of mediocre talent is to follow the prevailing fashion. Any young scientist who is not exceptionally gifted or exceptionally lucky is concerned first of all with finding and keeping a job. To find and keep a job you have to do competent work in an area of science which the mandarins who control the job market find interesting. The scientific problems which the mandarins find interesting are, almost by definition, the fashionable problems. Nowadays the award of jobs is usually controlled not by a single mandarin but by a committee of mandarins. A committee is even less likely than an individual to break loose from the fashionable trends of the day. It is no wonder that young scientists who care for their own survival tend to keep dose to the beaten paths. The leading institutions of h i g h e r learning offer security and advancement to those who

Freeman J. Dyson

Fashions in Science I decided to speak about the problem of fashions in science, since this is a problem of serious and growing importance for science generally and for the Institute and the H u m b o l d t Foundation in particular. I shall speak first about the problem of fashion as we see it here at the Institute, then about lessons we may learn from the history of science on a longer time scale, and *This talk was delivered to the Alexandervon Humboldt Foundation Bi-NationalColloquiumfor Humboldt Awardees in cooperation with the Institutefor AdvancedStudyat Princeton,New Jersey, on August 24, 1981. The talk was subsequentlypublished by Alexander von Humboldt-Stiftungin the Proceedingsof that conference and also in the Mitteilungen (January 1983, No. 41). The Intelligencer wishes to thank the author and Alexander von Humboldt-Stiftung for their permission to reprint this artide. THE MATHEMATICAL INTELLIGENCER VOL. 5, NO. 3 9 1983 Springer-Verlag New York

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It has always been true, and it is true now more than ever, that the path of wisdom for a young scientist of mediocre talent is to follow the prevailing fashion. skillfully follow the fashion, and only a slim chance to those who do not. Our Institute here is no exception. When I first came here as a visiting member 34 years ago, the ruling mandarin was Robert Oppenheimer. O p p e n h e i m e r decided which areas of physics were worth pursuing. His tastes always coincided with the most recent fashions. Being then y o u n g and ambitious, I came to him with a quick piece of work dealing w i t h a fashionable problem and was duly rewarded with a permanent appointment. That is the way it was at the Institute then, and that is the way it still is now. Somebody who knows the history of the Institute may object at this point, saying that, after all, the Institute also gave a permanent appointment to Kurt G6del. That is true. G6del was one of the few indubitable geniuses of our century, the only one of our colleagues who walked and talked on equal terms with Einstein. G6del worked in profoundly unfashionable areas of mathematics and became even more unfashionable as he grew older. Our Institute can justly be proud of having made room for him on its faculty. There is only one fact which must temper our pride. It took the Institute 14 years to make G6del a Professor, measured from the year he came to live and work here as an ordinary member. G6del was such an independent and recalcitrant spirit that I suppose we deserve some credit for making him a professor at all, even after 14 years of hesitation. Better late than never. The young physicists who come to the Institute as members today are under much stronger pressure than I was 30 years ago. To begin with, they mostly come with money from government contracts which legally oblige them to work in a definite area of science for a definite length of time. Of course we do not take the

The scientific problems which the mandarins find interesting are, almost by definition, the fashionable problems. wording of the contracts too literally. The officials of the National Science Foundation and the Department of Energy who administer the contracts are reasonable people and allow us to interpret our obligations with some flexibility. If some of our members on contract money decide to work in areas which have nothing to do with the contracts, we are not obliged to turn them out onto the street. People whose interests do not fit 48

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Kurt GOdel

into the contracts can usually be supported with Institute funds. But still, the contracts are a serious constraint. The contracts define in a general way the areas of work within which the visiting members of the physics school at the Institute will be active. The contracts define where the mainstream of physics is supposed to be. And inevitably the people we invite to come here as members tend to be people whose work fits smoothly into one or another of the contracts. I am now, after 30 years, one of the mandarins. I try in a vague and feeble way to encourage young physicists to work outside the fashionable areas. I try to keep alive a few areas of research which are not supported by contracts. I try to keep this institute open to independent and recalcitrant spirits. I try to keep a door open here in case another Kurt G6del should one day come knocking. But I have to admit that m y efforts to hold back the tide of fashion are about as effective as the efforts of my illustrious predecessor King Canute to hold back the tide of the Atlantic Ocean. The young people are compelled nowadays to follow the fashion by forces stronger than the wording of contracts and the authority of mandarins. The forces which drive the y o u n g people toward fashionable pursuits are peer pressure and the excitement of the chase itself. They know where the action is, and they want to be part of it. They know that they have only a short time to prove themselves as scientists. They know that their best chance of achieving something worthwhile in the short span of time allotted to them is to go with the crowd, to grab the scientific fruit quickly where it is ripe for picking. The running of young scientists after quick success and quick rewards is not in itself bad. The concentra-

tion of their efforts into narrow areas of fashionable speciahzation is not necessarily harmful. After all, the fashionable problems become fashionable not by the whim of some dress designer but because a substantial majority of scientists judges them to be important. As a general rule, the judgment of the majority is well founded. The fashionable areas are often those in which crucially important discoveries are made. There is nothing wrong in a young scientist rushing into these areas in the hope of making a sensational discovery. Indeed, the joy and excitement of daily life at the Institute are greatly enhanced by the gregarious nature of research in the fashionable areas. When you are exploring in a fashionable area, every petty success and every e p h e m e r a l triumph can be shared with friends at the lunch table or the seminar. Without this communal interest in fashionable problems, without this sharing of news and rumors, our life here would be much the poorer. Why then am I dissatisfied? Why am I grumbling at the young people for doing what I myself did when I was their age? I am grumbling because I do not think the fashionable stuff ought to be a hundred percent of what we do here. The fashionable stuff is useful and important and exciting. We can be p r o u d that our young people do the fashionable stuff and do it well. We can expect that a majority of them will always prefer to do the fashionable stuff, for reasons which I understand and respect. I am only saying that we ought to have room here also for a minority w h o do not do the fashionable stuff. We ought to seek out and encourage the rare individualists w h o do not fit into the prevailing pattern. We ought to bias our admission of members a little towards unorthodox and unconventional spirits. If we here do not give the practitioners of unfashionable science a home and a place to work, who will?

Ancient History There are many kinds of unfashionable science. One of the main difficulties of supporting it is the problem of selection. Unfashionable science comes in a thousand different shapes without any unifying structure. Let me give y o u an example. Last week I was walking across the Forrestal Campus of Princeton University and came upon two graduate students sitting quietly in the middle of a field. I thought at first they were just enjoying the sunshine and the silence of an August afternoon, but w h e n I came closer I saw that they were working with intense concentration, performing some delicate manipulations which required steady hands and f r e e d o m from distracting interruptions. Coming closer still, I saw that they were busily gluing little lead weights to the backs of honeybees. I watched in silence until they were finished, then walked with

them back to their experimental hive which is equipped with cameras and videotape recorders. They are refining and extending the classic experiments of Karl von Frisch on the dance communication system of bees. They have found that bees dance more vigorously and

We ought to seek out and encourage the rare individualists who do not fit into the prevailing pattern. more accurately when they have found a source of honey at a considerable distance from the hive. Unfortunately, the majority of bees find honey close to the hive and make only a brief and perfunctory dance when they return. The students want to observe the dance with high accuracy, so they have found a w a y to trick the bees into dancing more vigorously. A bee weighed down with 45 milligrams of lead thinks she has made a long flight w h e n she actually made a short one. She measures the length of a flight by the effort it costs her to fly. So the bees which carry weights dance accurately after every find. That is a typical example of unfashionable science, being done right here on our doorstep in Princeton. I am not suggesting that the Institute for Advanced Study ought to support a school of entomology. But the example of the bee experiments shows all the characteristic features that make unfashionable science difficult to support: small scale, diversity of objectives, idiosyncratic style, and a certain lack of superficial seriousness. To make clear the real and lasting importance of unfashionable science, I return to the field in which I am expert, namely, mathematical physics. Mathematical physics is the discipline of people who try to reach a deep u n d e r s t a n d i n g of physical p h e n o m e n a b y following the rigorous style and method of pure mathematics. It is a discipline which lies on the border between physics and mathematics. The purpose of the mathematical physicists is not to calculate phenomena quantitatively but to u n d e r s t a n d them qualitatively. They work with theorems and proofs, not with numbers and computers. Their aim is to clarify with math-

Unfashionable science comes in a thousand different shapes without any unifying structure. ematical precision the meaning of the concepts which physical theories are built. Mathematical physics has three qualities which it peculiarly relevant to the present discussion. it is important in the larger scheme of things,

upon make First, sup-

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plying basic ideas and vocabulary to the more practical areas of physics. Second, it is slow, taking typically 50 or 100 years to develop a n e w concept from its origin to its fruitful application. Third, it is almost always unfashionable, since its rhythms run about 10 times slower than the rhythms of scientific fashion. And because it is unfashionable, it has always been more highly regarded and better supported in Europe than in the United States. As an example of a great mathematical physicist whose work is of crucial importance to the development of physics at the present time, I mention the name of Sophus Lie. Lie has been dead for 80 years. His great work was done in the 1870s and 1880s, but it has come to dominate the thinking of particle physicists only in the last 20 years. Lie was the first to understand and state explicitly that the principles of physics have a group-theoretical origin. He constructed almost single-handed a vast and beautiful theory of continuous groups, which he foresaw would one day serve as a foundation of physics. Now, 100 years later, every physicist who classifies particles in terms of broken and unbroken symmetries is, whether he is aware of it or not, talking the language of Sophus Lie. But in his lifetime Lie's ideas remained unfashionable, little understood by mathematicians and not at all by physicists. Felix Klein was one of the few leading mathematicians w h o understood and supported him. Lie was one of those people who seem to have more than their fair share of bad luck. He was wandering around France as a young man when the Franco-Prussian war of 1870 broke out. He was Norwegian and spoke French with what sounded like a Prussian ac-

Sophus Lie 50

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cent. So the patriotic citizens of Fontainebleau decided he was a Prussian spy and threw him into jail. Meanwhile, France lost the war and conditions became generally chaotic. Lie was sitting quietly in his cell, working out his new mathematical discoveries, when his French friends finally found out where he was and succeeded in getting him released (Lie, 1877). In Rouse Ball's history of mathematics, published around the turn of the century, the account of Lie's work ends on a melancholy note (Rouse Ball, 1908): "Lie seems to have been disappointed and soured by the absence of any general recognition of the value of his results . . . . He brooded over what he deemed was the undue neglect of the past, and the happiness of the last decade of his life was much affected by it." Another great genius of mathematical physics, even more unfashionable in his o w n day than Sophus Lie, was Hermann Grassmann. As a gymnasium teacher in Stettin he published in 1844 a work entitled Die Lineale Ausdehnungslehre (The Calculus of Extension), introducing for the first time the basic notions of a vector, of a vector space, and of an anticommuting algebra. All these notions have been of central importance for the physics of the twentieth century, but not of the nineteenth. In his own century, Grassmann remained an obscure gymnasium teacher in Stettin, ignored by the academic mandarins of his time. But he had a greater resiliency of spirit than Sophus Lie. Instead of brooding like Lie over his lack of recognition among the mathematicians, Grassmann started a second career as a student of Sanskrit and achieved a modest fame as translator of the Rig-Veda into German. Perhaps, if it is your fate to be an unrecognized mathe-

Hermann Grassmann

matical genius, it is better for your health to earn a living as a gymnasium teacher rather than to be a university professor. While preparing m y remarks for this meeting I went to the Institute library and was happy to find there a copy of the 1878 edition of the Ausdehnungslehrewith the name of Minkowski, teacher of Einstein and first among mathematicians to understand relativity, written on the front page in pencil. The 1878 edition has a preface by Grassmann, still writing from Stettin and cheerfully expressing the hope that the n e w edition will receive more attention from the learned world than the first edition had 34 years earlier. At the end of the preface is a footnote saying, "Der Verfasser ist w/ihrend des Druckes gestorben" (The author died while this book was in press). It was only in the 1890s that Felix Klein, always generous in fighting for unfashionable causes, organized the official recognition of Grassmann and the publication of his collected w o r k s (Grassmann, 1844, 1878, 1894). A more recent example of a great discovery in mathematical physics w a s the idea of a gauge field, invented by Hermann Weyl in 1918. This idea has taken only 50 years to find its place as one of the basic concepts of modern particle physics. Q u a n t u m chromodynamics, the most fashionable theory of particle physicists in 1981, is conceptually little more than a synthesis of Lie's group algebras and Weyl's gauge fields. The history of Weyl's discovery is quite unlike the history of Lie groups and Grassmann algebras. Weyl was neither obscure nor unrecognized, and he was working in 1918 in the most fashionable area of physics, the n e w b o r n theory of general relativity. He invented

gauge fields as a solution to the fashionable problem of unifying gravitation with electromagnetism. For a few months gauge fields were at the height of fashion. Then it was discovered by WeyI and others that they did not do what was expected of them. Gauge fields were in fact no good for the purpose for which Weyl invented them. They quickly became unfashionable and

But in his lifetime Lie's ideas remained unfashionable, little understood by mathematicians and not at all by physicists. were almost forgotten. But then, very gradually over the next 50 years, it became clear that gauge fields were important in a quite different context, in the theory of quantum electrodynamics and its extensions leading u p to the recent d e v e l o p m e n t of q u a n t u m chromodynamics. The decisive step in the rehabilitation of gauge fields was taken by our Princeton colleague, Frank Yang, and one of his students, Bob Mills, in 1954, one year before Hermann Weyl's death (Yang and Mills, 1954). There is no evidence that Weyl ever knew or cared what Yang and Mills had done with his brain child. So the story of gauge fields is full of ironies. A fashionable idea, invented for a purpose which turns out to be ephemeral, survives a long period of obscurity and emerges finally as a cornerstone of physics. Such ironies are not unusual in the long history of mathematical physics. Hamilton's invention of quaternions, hailed as a panacea for the problems of nineteenthcentury physics, was discarded as useless at the turn of the century, rejuvenated in the form of spin matrices in the quantum mechanics of the 1920s, and has now ascended in glory to the quark field theories of the 1980s. Gauss's invention of differential geometry, originating as a by-product of his work on the practical p r o b l e m s of g e o d e s y and m a p making, w a s transformed into a new world of abstract generality by the genius of Riemann, emerging 50 years later as the conceptual basis of Einstein's theory of gravitation. Common to all these histories are the long time scale,

Gauge fields were in fact no good for the purpose for which Weyl invented them.

Hermann Weyl

usually longer than a h u m a n lifetime from start to finish, and the totally unpredictable quality of the final outcome. In no case did the inventor of the crucial concept have the slightest inkling of the physical context in which his invention would find its ultimate fruition. That is enough about the past. I think I have given THE MATHEMATICAL INTELLIGENCER VOL. 5, NO. 3, 1983

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you enough historical examples to prove my point, that unfashionable people and unfashionable ideas have often been of decisive importance to the progress of science. The time has n o w come to talk about the present and the future. I see no reason to expect that the pattern of development of scientific ideas in the future will be different from what it has been in the past. We must expect unfashionable ideas to emerge into importance as frequently in the future as they have done in the past, usually after long periods of gestation and in unfamiliar contexts. The problems which we face as guardians of scientific progress are then: how to recognize the fruitful unfashionable idea, and how to support it.

The Monster and the Moral To begin with, we may look around at the world of mathematics and see whether we can identify unfashionable ideas which might later emerge as essential building blocks for the physics of the twenty-first century. If we are lucky, we may find some good candidates for future prominence. Of course we cannot expect to know in our lifetimes whether we picked the right ones. Roughly speaking, unfashionable mathematics consists of those parts of mathematics which were dedared by the mandarins of Bourbaki not to be mathematics. A number of very beautiful mathematical discoveries fall into this category. To be mathematics according to Bourbaki, an idea should be general, abstract, coherent, and connected by clear logical relationships with the rest of mathematics. Excluded from

We must expect unfashionable ideas to emerge into importance as frequently in the future as they have done in the past, usually after long periods of gestation and in unfamiliar contexts. mathematics are particular facts, concrete objects which just happen to exist for no identifiable reason, things which a mathematician would call accidental or sporadic. Unfashionable mathematics is mainly concerned with things of accidental beauty, special functions, particular n u m b e r fields, exceptional algebras, sporadic finite groups. It is among these unorganized and undisciplined parts of mathematics that I would advise you to look for the next revolution in physics. They have a quality of strangeness, of unexpectedness. They do not fit easily into the smooth logical structures of Bourbaki. Just for that reason we should cherish and cultivate them, remembering the w o r d s of Francis Bacon which our director Harry Woolf used as theme

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song of the Institute's Einstein Centennial celebration two years ago: "There is no excellent beauty that hath not some strangeness in the proportion" (Woolf, 1980). As an example of strangeness in the proportion, I will speak briefly about sporadic finite groups (Conway,

Roughly speaking, unfashionable mathematics consists of those parts of mathematics which were declared by the mandarins of Bourbaki not to be mathematics. 1980). Their history begins with the French mathematician Emile Mathieu, w h o discovered the first of them in the year 1861 and the second in 1873. Mathieu, as is usual in such cases, did not know that he had invented sporadic groups. In fact the word "group" does not appear in the titles of his papers (Mathieu, 1861, 1873). But he knew very well that he had found something beautiful and important. Using the language of geometry, we may say that he had found that there exist in spaces of 12 and 24 dimensions structures of a peculiar symmetry which do not occur in spaces with any number of dimensions different from 12 or 24. His work was published, but remained for 100 years unfashionable. It was, as orthodox mathematicians like to say, an isolated curiosity, not leading anywhere. About 75 years later the Mathieu groups turned out to be of some practical importance in the business of code making. Each Mathieu group forms the basis for the design of a uniquely efficient error-correcting code. This m u n d a n e utility of the Mathieu g r o u p s did nothing, of course, to raise their status in the eyes of mathematicians whose tastes were formed by Bourbaki. Then rather suddenly, in the last 20 years, a magnificent zoo of new sporadic groups was discovered by a variety of mathematicians working with a variety of methods. Some of them were discovered by following the ideas of Mathieu, others by studying the peculiarly unfashionable problem of packing 24-dimensional billiard-balls as tightly as possible into a 24dimensional Euclidean space (Leech, 1967), others by testing permutations and combinations with big computers. The only thing these various discoveries had in common was a concrete, empirical, experimental, accidental quality, directly antithetical to the spirit of Bourbaki. Altogether 25 sporadic groups, including those of Mathieu, were discovered. Meanwhile the fraternity of professional group-theorists, using more general and abstract methods, succeeded in proving that the total number of sporadic groups could not be larger than 26. So we reached the situation two years ago that only one more sporadic group remained to be

found. It was k n o w n that this last group, if it existed, would be the biggest and most beautiful of all (Conway and Norton, 1979). It was given the nicknames "Monster" and "Friendly Giant" by the people who were hunting for it. The end of the story came last year w h e n Bob Griess, visiting here at the Institute from the University of Michigan, f o u n d the w a y to construct the Monster (Griess, 1981). Just yesterday I received from Michigan the final installment of a long paper containing a complete and definitive account of his work (Griess, 1982). The Monster is now revealed in all its glory to

So far as we know, the physical universe would look and function just as it does, whether or not the sporadic groups existed. those who take the trouble to understand the details of Bob Griess's construction. The last and greatest of the sporadic groups, it n o w stands forever, unique and unassailable, a monument more durable than bronze. What has all this to do with physics? Probably nothing. Probably the sporadic groups are merely a pleasant backwater in the history of mathematics, an odd little episode far from the mainstream of progress. We have never seen the slightest hint that the symmetries of the physical universe are in any way connected with the symmetries of the sporadic groups. So far as we know, the physical universe would look and function just as it does whether or not the sporadic groups existed. But we should not be too sure that there is no connection. Absence of evidence is not the same thing as evidence of absence. Stranger things have happened in the history of physics than the unexpected appearance of sporadic groups. We should always be prepared for surprises. I have to confess to you that I have a sneaking hope, a hope unsupported by any facts or any evidence, that sometime in the twenty-first century physicists will stumble upon the monster group, build in some unsuspected way into the structure of the universe. This is of course only a wild speculation, almost certainly wrong. The only ar-

Wherever you look in the realm of ideas, you find hints of revelations still to come, whispers of hidden connections. gument I can produce in its favor is a theological one. We have strong evidence that the creator of the universe loves symmetry, and if he loves symmetry, what lovelier symmetry could he find than the symmetry of the Monster? The sporadic groups are only one example from the treasure house of weird and wonderful concepts which

unfashionable mathematicians have created. I could mention many others. Can you imagine a regular polyhedron, a body composed of perfectly symmetrical cells arranged in a perfectly symmetrical structure, having a total of 11 faces? Last year my friend Donald Coxeter in Toronto discovered it (Coxeter, 1981). Is it possible that the zeros of the zeta-function, whose properties were conjectured by Riemann 120 years ago and still remain one of the central mysteries of mathematics, will turn out to have hidden connections with the world of physics? Last year Andrew Odlyzko, a mathematician at Bell Laboratories working with a Cray computer, found some new and unexpected properties of zeta-function zeros. Is it possible that the incompleteness theorems of Kurt GOdel, proving that there are questions in pure mathematics which any given finite set of axioms and rules of inference are unable to answer, will one day give us a deeper understanding of the limitations of our knowledge of the physical universe? Wherever you look in the realm of ideas, you find hints of revelations still to come, whispers of hidden connections.

We ought to give greater attention and greater support to unfashionable research. At any particular moment in the history of science, the most important and fruitful ideas are often lying dormant merely because they are unfashionable: But n o w my time is almost up, and I must keep my promise to give you some practical advice about the support of science. I am saying, both to the Institute for Advanced Study and to the Humboldt Foundation, that is is our duty and our privilege as independent organizations to be less short-sighted than our governments. Our role should be to take a longer view of science than either politicians or postdoctoral students can afford. What does the longer view of science teach us? What is the moral to be drawn from the various stories that I have told you? The moral is a simple one. We ought to give greater attention and greater support to unfashionable research. At any particular moment in the history of science, the most important and fruitful ideas are often lying dormant merely because they are unfashionable. Especially in mathematical physics, there is commonly a lag of 50 or 100 years between the conception of a new idea and its emergence into the mainstream of scientific thought. If this is the time scale of fundamental advance, it necessarily follows that anybody doing fundamental work in mathematical physics is almost certain to be unfashionable. We should not, of course, stop supporting the fashionable research which keeps most of our young scientists busy and happy. But we should set aside a THE MATHEMATICAL INTELLIGENCER VOL. 5, NO. 3, 1983

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certain fraction of our resources, perhaps a tenth or perhaps a quarter, for the support of unfashionable people doing unfashionable things. We should not be afraid of looking foolish or even crazy. We should not be afraid of s u p p o r t i n g risky ventures which m a y fail totally. Since we are independent, we have the right to take risks a n d to m a k e mistakes. Organizations which only s u p p o r t research where there is no risk and no chance of mistakes will in the e n d support only mediocrity. If we proceed with good sense and courage to support unfashionable people doing things that orthodox opinion considers irrelevant or crazy, there is a good chance that we shall rescue for science an occasional Sophus Lie or H e r m a n n Grassmann, people whose ideas will still be famous long after all our contemporary fashionable excitements are forgotten.

References Conway, J. H. (1980) Monsters and Moonshine, The Mathematical Intelligencer, 2, No. 4, 165-171 Conway, J. H. and S. P. Norton (1979) Monstrous Moonshine, Bull. London Math. Soc. 11, 308-339 Coxeter, H. S. M. (1981) "A Symmetrical Arrangement of Eleven Hemi-Icosahedra," to be published

Grassmann, H. (1844, 1878, 1894) Die Lineale Ausdehnungslehre, 1st ed. (Otto Wigand, Leipzig) 1844, 2nd ed. (Otto Wigand, Leipzig) 1878, 3rd ed. in Grassmann's collected works edited by F. Engel (Teubner, Leipzig) 1894 Griess, R. L. (1981) A Construction of F1 as Automorphisms of a 196883-dimensional Algebra, Proc. Nat. Acad. Sci. USA, 78, 689-691 Griess, R. L. (1982) The Friendly Giant, Invent. Math. 69, 1102 Leech, J. (1967) Notes on Sphere Packings, Can J. Math. 19, 251-267 Lie, S. (1877) Letter to A. Mayer, published in Sophus Lie, Gesammelte Abhandlungen, ed. F. Engel (Leipzig, Teubner, 1922), Vol. 3, Anmerkungen, p. 691 Mathieu, E. L. (1861, 1873) M~moire sur l'6tude des fonct-ions de plusieurs quantit6s, J. de Math. Pures et Appliqu6es, 6, 241-323, "Sur la fonction cinq fois transitive de 24 quantit6s," J. de Math. Pures et Appliqu6es, 18, 25--46 Rouse, Ball, W. W. (1908) A Short Account of the History of Mathematics, 4th ed. (MacMillan, London), p. 478 Woolf, H., ed. (1980) Some Strangeness in the Proportion: A Centennial Symposium to Celebrate the Achievements of Albert Einstein (Addison-Wesley, Reading, Mass.) Yang, C. N. and R. L. Mills (1954) Conservation of Isotopic Spin and Isotopic Gauge Invariance, Phys. Rev. 96, 191-195 School of Natural Sciences Institute for Advanced Study Princeton, New Jersey 08540

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