From: Haynes Miller Subject: What we do Date: Sun, 31 Jan 1999 17:42:34 -0500 (EST) This discussion of the goals of homotopy theory is definitely becoming an arena where angels fear to tread, and this has always been a red flag to me I am afraid, so .... No reasonable homotopy theorist has considered the explicit and complete computation of homotopy groups of a sphere as a plausible goal since the mid 1970's. This is not to say that computation has not continued to be an important activity in the subject - the minimal resolutions of Bruner, and the slightly more indirect methods described by Christian Nassau in Oberwolfach in October are testimony to the continued progress on that front. But as a defining activity it has subsided, and as a goal this or any other purely computational question that I know of has receded in importance. And a good thing, too, as such activites tend to be inward-looking and disconnected from the rest of mathematics. I believe that the past decade or so has seen the emergence of a new paradigm for the discipline. Its origin is in the work of Dan Kan and later Dan Quillen. One approach to the perspective underlying this paradigm is to start with combinatorics, which might be described roughly as the art of counting equivalence classes. When you wish to retain some information about the structure of the equivalence classes themselves - two elements may be equivalent in incommensurable ways, for example - you enter the realm of homotopy theory. The object of study is not a set (of equivalence classes), but rather a homotopy type (whose set of components recovers the combinatorics). The paradigm accomanying this perspective has been embodied in the theory of model categories. This formalization of what it means to "do homotopy theory," or of what a "homotopy theory" is, has proven extremely useful not just as an organizational device, but as a technical tool in proving deep and important theorems (beginning with Quillen's rational homotopy theory) and more recently as a means of transferring homotopical methods and insights to other fields (as in the work of Morel and Voevodsky). Today there is a multiplicity of constructions of homotopy theories, and the techniques of model categories have become indispensable in comparing them (cf work of Mandell, May, Schwede, and Shipley, for example). The family of homotopy theories, in fact, may be studied by the same methods, rather like the Mandelbrot set, according to Dwyer, Hirschhorn, and Kan, and, from a different approach, Charles Rezk. Along these same lines, once you view a homotopy type as an enriched set, the entire edifice of algebra begs to be transported into homotopy theory. A large portion of the efforts of the world's homotopy theorists has been directed at this task in the past ten or even twenty years. Waldhausen was an early exponent of this paradigm, and Quillen also in a less flamboyant approach. I would say we are just now getting the basic definitions in order (thanks to work of May and Smith and their collaborators), but nevertheless some stunning results have been achieved, in algebraic K-theory (which connects homotopy theory to algebra) and in the study of elliptic cohomology and other analogues of topological K-theory (which promise to connect homotopy theory afresh to analysis (via a form of index theory) and algebra again (via a definition of algebraic elliptic cohomology)). I regard this phase of the development of the subject as something akin to the algebraic geometers' search for the optimal definition of their subject, a search culminating in the definition of a scheme. In their case, the methods opened up by this definition, combined with many very innovative and clever special ideas, led to Deligne's proof of the Weil conjectures. This victory (and others) vindicated the abstraction, and forced respect from all quarters. We in homotopy theory are suffering, I think, from the lack of such a broad and precise vision or family of conjectures. Our understanding of the large-scale behavior of the traditional stable homotopy category was revolutionized by the work of Hopkins, Devinatz, and Smith, on nilpotence and periodicity. The phenomenon of periodicity, which at first seemed exceptional and dependent upon difficult special computations, was revealed to be a dominant shaping force, and one which must be at the root of any plausible approach to a description of the stable homotopy category or even of the full subcategory generated by spheres. (The work of Toda and others had, long before, shown a narrow focus on this subcategory to be an artificial and crippling restriction.) >From this perspective, the most interesting computations in the past decade have been Shimomura's analyses of the size of various types of periodic fragments of the stable homotopy of spheres. This work today is entirely dependent upon painful low-tech homological computations, but it admits rather beautiful and simply stated algebraic reformulations. My feeling is that one fundamental area of progress would be to find a more direct approach to these results, one offering the chance to greatly extend them. It's unlikely that a precise general computation will be possible by any means, and what is really needed is an appropriate way of localizing the problem so as to forget untamed details, by means of a zeta function or some such device. Work of Hopkins from the early '90's on the Picard group of the $K(n)$-local stable homotopy category offered some promise in this direction and perhaps this vein hasn't yet been exhausted. Thinking along these lines is not avoiding the issue. We say we know the cohomology of BU, but would someone care to tell me the rank of the millionth group? And if you know it, what enlightenment could it possibly bring? Just so with Kuperberg's challenge to say what some specific homotopy group of a specific sphere. What is needed is something akin to the algebra structure in H^*(BU), allowing us to remit the problem to the combinatorialists and get back to more enjoyable activities. Nishida's theorem showed that the algebra structure in the stable homotopy ring was woefully inadequate, and in a sense we have been searching for the replacement ever since. I could go on to try to capture some of the excitement of contemporary unstable homotopy theory, but perhaps I should leave that to others and thereby hope to avoid offending the other half of my colleagues. Haynes Miller January 30, 1999 ___________________________________________