chapter 9

A Mathematical Dream and Its Interpretation

 

 

On sabbatical from my position as professor at Brandeis, I spent the 1992–1993 academic year in France, visiting colleagues and teaching courses at two universities—Université Paris 7, in the center of Paris, and Université Paris-Sud, in Orsay, a half-hour’s train ride to the south—in preparation for a possible move to Paris. Boston was then and still is one of the world’s great mathematical centers, and by attending Harvard’s number theory seminar and the MIT representation theory seminar, I kept in touch with all the most important developments relevant to my own work in automorphic forms, on the border between these two subjects. Paris, however, was not only actively and consciously exercising its role as the natural headquarters of mathematical research in Europe, with the most extensive seminar schedule anywhere; it was also home to the world’s largest concentration of specialists in automorphic forms, most of them roughly my own age. This meant that for nearly twenty years we had followed developments in the field and neighboring fields in the same sequence, had witnessed the same breakthroughs and had met one another repeatedly at the same international meetings, and were deeply familiar with one another’s complementary contributions to a highly active, influential, and competitive branch of mathematics.

A year after I wrote a thesis in pure number theory in 1977, I switched to the field of Shimura varieties, a geometric structure invented by Goro Shimura (one of my professors at Princeton) in his work relating automorphic forms to number theory, an early inspiration for the Langlands program. In this way I gradually became a specialist in automorphic forms. My interests, reflecting my start in number theory, were somewhat peripheral from the standpoint of most of my Paris colleagues, who were mainly guided by the priorities of the Langlands program. Of all the possible techniques for proving his conjectures, Langlands preferred those connected with the Selberg trace formula and its vast generalization by (his student and fellow Canadian) James Arthur. In this, Langlands has been consistent through most of his career, frequently to the point of criticizing proofs of his conjectures that avoid use of the trace formula. The general idea of the trace formula is not hard to explain and is quite similar to the classical Lefschetz fixed point formula in algebraic topology, the source of Weil’s topological intuition, which, vastly generalized by Grothendieck and his collaborators, was central in their approach to the Weil conjectures.

Both the Lefschetz and the Arthur-Selberg trace formulas can be seen as examples of index formulas, which arise in one form or another in most branches of pure mathematics as a means of deriving often unexpected consequences for large and complicated global objects—such as differential equations, solutions of polynomial equations, or Galois theory—from purely local data that are, in principle, elementary and amenable to calculation. It was one’s attitude to this “in principle” that determined where one stood with respect to Langlands’ program. To begin calculating the local data relevant to his program, one needed to assimilate a mass of complex, specialized notation and terminology that had mostly been developed by Langlands and his closest collaborators, some of them Parisians, much of it in articles by Langlands himself that were notoriously difficult to read. Arthur’s version of the Selberg trace formula not only involved local data, but also presumed the solution of global problems in simpler situations and hence introduced a recursive structure into the problem with its own complications. Finally, the heart of Langlands’ plan involved use not of Arthur’s trace formula, but a hypothetical stable version thereof, whose construction of the stable formula relied on yet another series of difficult articles by Langlands, as well as the fundamental lemma, which, as mentioned in chapter 2, was not resolved by Ngô until fifteen years after my Paris visit, following the latter’s work with (his former thesis adviser) Gérard Laumon, based on yet another new version of Grothendieck’s trace formula.

For all these reasons—and also because my original interest in Shimura varieties derived from number theory and geometry, rather than from group theory—those parts of the Langlands program based on the trace formula were not to my taste, and I had avoided learning the relevant techniques, although inevitably I was exposed to the methods in international conferences and to the phenomena they were designed to explain in my own work. Langlands had been a frequent visitor to Paris, however. This was where he had first presented his vision of the stable trace formula in a series of lectures I had attended in 1980. At the time I had understood nothing whatsoever, but the Parisian specialists had studied these ideas over the years in their weekly automorphic forms seminar. A few of these specialists were recognized internationally as experts in the Langlands program; nearly all had made direct use of Langlands’ techniques in one way or another in their own work.

Even had I wished to sign on to the Langlands program, I had no hope of catching up with specialists who enjoyed a fifteen-year head start. I preferred to remain on the margins, where my work would not be judged by comparison with a preestablished set of goals and milestones. By 1992 I had spent fourteen years using Shimura varieties to study special values of L-functions, which is, roughly speaking, a way of relating two different classes of transcendental numbers using algebra. I entered this field by accident, because I knew how to put together two kinds of methods, one from geometry and one from group theory, whose conjunction I had recognized under another form in an article by Shimura himself. During the intervening years I had learned to vary the specific ingredients, initially as a close reader of Shimura’s work, and in this way I learned a good deal more geometry and group theory, but the kind of combination was invariably the same. I did not so much set myself specific goals as discover new problems similar to those I had already considered in the articles I read while pursuing my education or in conversations with my collaborators. Already in 1989, I was getting tired of this, and when I spent a year in Moscow I hoped to switch fields—or at least to look at a class of special values of L-functions I hadn’t previously considered. Five years earlier this had been a major priority for the Russians with whom I was expecting to work, especially for Alexander Beilinson, but in the interim most of them had radically shifted their priorities, and although I returned from Moscow with a host of new ideas, they were very much along the lines of what had been on my mind when I had arrived and owed little or nothing to my interactions with my Russian colleagues.

The projects I had begun in Moscow were nearly exhausted by the time I arrived in Paris three years later. I was looking for something new, not only because I was tired of the old subject but because it was tired of me and had no new problems to offer. My most promising new departures of the previous years had turned out to lead to problems far beyond my powers to solve. While waiting in Paris for inspiration to strike, I had found the key to completing the last of my Moscow projects. Once again it was a matter of aligning geometric and group-theoretic ideas, and although I knew clearly enough what was involved, I could tell it would be long and tedious to write out the details, and I was not eager to begin. I must have been complaining to my friends, because one of them wrote me at that time:

Dear Michael,

It is time for a good book on special values of L-functions but I don’t know if you really want to write one. On the other hand, it does seem perfectly rational to be dismayed at the prospect of another 30 years of results about period relations in the setting of Shimura varieties. So I understand your desire for change…. I don’t think it can be that satisfying to be thought of as Mr. Coherent Cohomology and I can see the desire to get beyond that pigeonhole.

My only other project was a long shot, an attempt to understand yet another kind of special value of L-functions by comparing a version of the relative trace formula—in some respects a refinement of the standard Arthur-Selberg trace formula—with a sort of refinement of the Grothendieck-Lefschetz trace formula called arithmetic intersection theory (or Arakelov theory). The goal was to find an abstract framework to explain, and ultimately to generalize, the constructions in the landmark work of Benedict Gross and Don Zagier on the Birch-Swinnerton-Dyer conjecture, in which two infinite collections of terms (one geometric, one group-theoretic) are shown at the end of nearly one hundred pages of computations to match miraculously, term by term, with striking consequences.

This is the sort of fuzzy idea that inevitably occurs to a number of people when they have nothing better to do, and though I had nothing very definite in mind, two talks I had heard the previous summer had revived my interest in the question. At a conference in Jerusalem, I had heard Steve Rallis talk about his new and abstract approach to the relative trace formula; at a conference at the MFO in Oberwolfach, I had heard Michael Rapoport explain his new work with Thomas Zink on the p-adic properties of Shimura varieties, which I hoped would explain the geometric side of the Gross-Zagier formula.1

Rapoport, now at Bonn, at the time a professor at Wuppertal, was going to be in Paris for a few weeks in December in connection with his participation in a jury overseeing the Orsay thesis defense of one of Laumon’s graduate students, named Alain Genestier. I had seen Rapoport at the Tuesday seminar at Orsay and had proposed that we meet for lunch, to talk about the work he had described in Germany. The lunch took place on Thursday, December 10, the day before Genestier’s thesis defense.

Rapoport and I were both satisfied with the meal, which was unusual in itself. I raised my question; Rapoport expressed interest and had even brought some relevant documents to the table, but after a brief discussion, we agreed that neither of us was sufficiently prepared to go more deeply into the question and decided to postpone further consideration of the problem until we had had time to read the relevant background material. We made tentative plans for me to visit Wuppertal in January. The conversation then turned to matters connected with Genestier’s thesis. Genestier was studying an analogue of Shimura varieties called Drinfel’d modular varieties, and he was doing so from the point of view of their p-adic uniformization. This was a property they shared with certain Shimura varieties, a fact that had only recently been established by Rapoport and Zink as an application of the ideas Rapoport had explained in Germany. This is not quite right. Actually, Genestier was not thinking about p-adic uniformization but about the Drinfel’d upper half-space, also known as Ω, an object with both geometric and group theoretic properties that needed to be understood before moving on to the more elaborate questions of p-adic uniformization. A primary motivation for studying Ω, Rapoport explained, was that it was widely expected to give a geometric model (cohomology) for a group-theoretic object—the local Langlands correspondence for GL(n) of a nonarchimedean local field. For the kind of Ω treated in Genestier’s thesis, this local Langlands correspondence had been established by Laumon and Rapoport in collaboration with Rapoport’s Wuppertal colleague Ulrich Stuhler. But there was no geometric model for this correspondence, and the correspondence was still a major open problem for p-adic fields, where p-adic uniformization was known.

If these ideas were familiar to me at all, it was only in the vaguest way. Four years earlier I had given a presentation at a conference in Ann Arbor (as “Mr. Coherent Cohomology”), in which Henri Carayol, then as now at Strasbourg, had given several lectures on Ω, setting out the conjectures Rapoport sketched to me over lunch. I remembered Carayol’s lectures and the notes he had distributed at the conference, but I could not relate what I remembered to what Rapoport was telling me. Rapoport advised me to reread the article based on Carayol’s lectures in order to prepare for Genestier’s thesis defense. I did so that night, motivated by the potential relevance of this work to my understanding of the Gross-Zagier formula. Carayol’s article was written very clearly, and although the notions he treated were unfamiliar, I could see a parallel with other geometric constructions of group representations, specifically Wilfried Schmid’s proof in the mid-1970s of a conjecture of Langlands to the effect that the discrete series of real Lie groups occur in L₂ cohomology of period domains—an object for which Rapoport and Zink claimed to have found an analogue for p-adic groups—and the Deligne-Lusztig construction of representations of finite groups of Lie type, originally inspired by work of Drinfel’d. A curious feature of the conjectures outlined by Carayol was that they involved the actions of three groups: the group GL(n, F), where F is a p-adic field; the multiplicative group J of a certain division algebra over F, and the Weil (or Galois) group W of F. Drinfel’d had proved in a very difficult paper that his Ω was the first of an infinite family of unramified coverings Ω_1, Ω_2, Ω₃, … and Carayol’s conjecture, an elaboration of earlier conjectures of Deligne and Drinfel’d, was that the natural action of W × J × GL(n, F) on the cohomology (cf. chapter 7) of this family simultaneously realized the (conjectural) local Langlands correspondence between representations of W and GL(n, F) and the (known) Jacquet-Langlands correspondence between representations of J and (certain) representations of GL(n, F).

Genestier’s thesis was a difficult piece of work, his defense was professional but intended primarily for experts, and I was not an expert. Nevertheless, I understood enough to be struck by the resemblance of his irreducibility theorem to a theorem I had studied as a graduate student, due to Ken Ribet. I wondered whether Genestier might not be able to derive his irreducibility result as Ribet had, by studying the action on the unramified coverings of the stabilizers of certain natural points on the base space. The reader will not be surprised to learn that Genestier’s thesis defense was followed by the customary champagne reception, and I remember insisting on this idea in conversations over champagne with Laumon, with Rapoport, and with Genestier himself. It is more than likely that at the reception I drank more than four glasses of champagne, which I have learned in the course of many thesis receptions marks the border beyond which my remaining capacity for coherent thought is no longer equal to the demands of the profession.

The following morning was Saturday. My wife had an early appointment and we had set the alarm early. I drifted into consciousness with the certainty that I had just dreamt about the cohomology of unramified coverings of Drinfel’d upper half-spaces and that the dream had brought me an insight I could not quite recover but that I was certain I should not let slip away. Warding off my wife’s attempts to rouse me completely, I remained at the edge of wakefulness for several minutes, until the insight solidified to the point of being expressible in words—or, more accurately, a combination of words and images to which I could associate mathematical content. Over the next few weeks my ideas grew clearer as I reread Carayol’s article and discussed the problem with colleagues in Paris and Orsay, so that by December 29 the insight that came to me in my dream had taken the form of a research program that I described in detail in a letter to Rapoport.

Dear Michael—

It is probably a good time to think about organizing my visit to
Wuppertal, if this is going to happen. Since I saw you I started
thinking about a related but very different problem, namely, the one
you mentioned of trying to construct the discrete series of GL(n)
by imitating Atiyah-Schmid for the Drinfel’d modular varieties. I
came up with a crazy idea that is impossible (for the moment) to put
into practice but that is probably right nonetheless. It is inspired by
Schmid, rather than Atiyah-Schmid, and actually more by Zuckerman’s
algebraic version of Schmid, and even more by recent work of Schmid
and Vilonen on realizing the characters of discrete series by a Lefschetz
fixed point formalism. The basic idea is the following….2

… I think I can come to Wuppertal during the week of January 18.

Rereading this letter, it is clear to me that I had learned a phenomenal amount of mathematics from my colleagues in Paris during the last two weeks of December. At the time of my lunch with Rapoport, I had no precise idea of many of the notions described here; certainly I would not have written about them with such confidence. The allusions to Laumon’s suggestions refer to conversations that took place the week after Genestier’s thesis defense, mostly with Genestier in attendance. Laumon made clear his preference for a cohomology theory that “really exists,” as opposed to the one, implicit in my letter, recently developed by Vladimir Berkovich, which did indeed “exist” but which did not obviously have all the properties needed to prove the a Lefschetz formula. The paragraph (see note 2) beginning Hypothesis (d) would follow is an almost verbatim account of what, after the dream itself, was the most uncanny incident of the whole experience: when Genestier asked me how I hoped to carry out the comparison in (d), I proceeded without the slightest hesitation to explain the argument involving Lubin-Tate groups, of whose possible relevance to the problem Genestier, Laumon, and I learned simultaneously from the unconscious source to which I had tuned in during the dream and which had not bothered to provide this detail until it was specifically requested.

By chance, that same week Laumon’s Orsay colleague Guy Henniart was hosting two visitors, Phil Kutzko of the University of Iowa and Colin Bushnell of London’s King’s College. Bushnell, Henniart, and Kutzko were the three leading experts in the representation theory of GL(n);³ they had been interested for years in the local Langlands correspondence for p-adic fields and had begun writing a long series of articles on the subject, following Henniart’s proof of the “numerical Langlands correspondence”⁴ and the monumental book of Bushnell-Kutzko.

I had known Kutzko for some time and met Bushnell at a conference in the soon-to-be-former East Germany in December 1989, when the two of them presented the results that soon appeared in their book. Due to a misunderstanding, I had not realized this was the main point of the conference—which Rapoport also attended—and my own presentation was interrupted before the end by the main East German organizer, who loudly protested that it was not only incomprehensible to everyone else in the room but that it was irrelevant to the proceedings. In 1989 I had nothing to tell Bushnell and Kutzko, nor was I in any way able to appreciate their work. Three years later, though, I eagerly followed the two of them, and Henniart, to a brasserie in Montparnasse, where I spent much of the meal asking their opinions of what my dream had taught me.

The story of the dream is only halfway done, and although I will spare you most of it, I have not yet told you whether or not it has a happy ending, nor whether or not it is the one the text thus far seems to have prepared. But I already want to stress the point of this story, which is that it does not follow the standard account of the role of the unconscious in scientific thinking, as exemplified by Kekulé’s (possibly apocryphal) dream about the benzene ring, or Poincaré’s celebrated discovery of the relation between Kleinian groups and non-Euclidean geometry as he stepped onto the omnibus, or the dream of Robert Thomason to which I devoted a speculative article.5 Max Weber wrote famously that

[i]deas occur to us when they please, not when it pleases us. The best ideas do indeed occur to one’s mind in the way in which Ihering describes it: when smoking a cigar on the sofa; or as Helmholtz states of himself with scientific exactitude: when taking a walk on a slowly ascending street; or in a similar way. In any case, ideas come when we do not expect them, and not when we are brooding and searching at our desks. Yet ideas would certainly not come to mind had we not brooded at our desks and searched for answers with passionate devotion.⁶

Kekulé, Poincaré, Thomason, and dozens of others have recounted the dreams and unconscious interludes that helped them solve problems that had long troubled them, perfect instances of Weber’s ideal-type. The contrast with my situation could not be more striking: the dream I have described provided a strategy for solving a problem about which I had never brooded and to which I had devoted no passion, a problem I had considered altogether irrelevant to my interests one week earlier. And though I was unable to bring the dream argument to a successful conclusion, the dream and the interest it inspired in this question did change my mathematical priorities radically and was instrumental in my acquiring the degree of charisma to which I allude in chapter 2.

For three months I thought intensely about how to transform the research program proposed in my dream into rigorous mathematics. Concretely, this meant I read widely and spoke to all the colleagues I could reach in an attempt to solve problems (a)–(d) described in note 2. I did visit Wuppertal in January and explained my ideas at length to Stuhler as well as Rapoport.⁷ I accepted an invitation to Strasbourg to visit Carayol a few weeks later, and although my lecture was on another topic, most of my conversations were again about the ideas of my dream. Carayol was in Strasbourg, as was Jean-François Boutot, and their papers on the subject were my main source of inspiration.

Carayol’s Ann Arbor lectures clearly made the connection between his conjecture and Shimura varieties, and his article with Boutot was the main reference for Drinfel’d’s Ω, other than Drinfel’d’s original and ferociously difficult short note. I spent half my time looking back and forth between Genestier’s thesis, which had developed a new way to calculate with the coverings of Ω, and the Boutot-Carayol article, unable to apply Genestier’s methods to problems (a) and (b), especially the latter, but hoping that inspiration would strike. The other half of my time I spent catching up on fifteen years of work on the trace formula in connection with the Langlands program.

In the spring, I was teaching an undergraduate course at Orsay and sharing an office with Luc Illusie, who had been Laumon’s thesis adviser and, by that token, Genestier’s mathematical grandfather. Early in May, Luc arrived at the office one morning and announced, in English, “You’re cooked!” He showed me a message he had received from a California colleague named Arthur Ogus: the German algebraic geometer Gerd Faltings, one of the most overpowering mathematicians of his generation, had just given a lecture in Berkeley on the cohomology of Drinfel’d’s coverings of Ω based on an approach apparently very similar to mine, but he had claimed much more than I could dream of proving. “You and Genestier are both cooked!” I entertained hopes that there had been a misunderstanding until notes taken at Faltings’s lecture arrived in Paris, including a calculation roughly equivalent to (c) and (d) of my message to Rapoport (note 2), and—much more importantly, to my mind—the announcement of a proof of a version of (b).⁸ Question (a) was left as a conjecture except in the two-dimensional case. The details appeared a few weeks later when Ogus mailed photocopies of his notes, most notably: Faltings’s effective use of the Berkovich cohomology theory, in which he was able to make sense of the Lefschetz trace formula; his ingenious (partial) solution of problem (b); and his very difficult solution to problem (a) in the first nontrivial case, that of dimension 2.

In the meantime I had written to Carayol. In my files, my message is dated May 12, 1993. The original was in French, but it loses nothing in an English translation:

Henri—

It seems that Ogus is at the origin of a rumor according to which Faltings has proved “Drinfel’d’s conjecture” on the cohomology of coverings of the non-archimedean half-plane. You must be aware of this. No one has seen Ogus’s notes, so we don’t know what this is about. I can hardly imagine he has proved the local Langlands conjecture.

If by “Drinfeld’s conjecture” one means the conjecture that all discrete series representations can be realized in the cohomology of the coverings, without specifying the multiplicity, nor possible non-discrete components, then the claim seems strange to me, because I had the impression that you had given a more or less complete argument in your Ann Arbor talk. In any case, I think I can complete your argument for supercuspidal representations, using the results of Kottwitz and Clozel on twisted unitary groups9 … But I suppose you already knew how to do this. Nevertheless, if Faltings is really in the process of proving the conjecture (by local methods, perhaps), it would be useful to make the global proof public (for example, the people at Orsay don’t know it).

There follows a final technical paragraph in which I sketch my approach to the “global proof.” Rediscovering this message, I find myself a little surprised by the timing. I had thought the conversation with Illusie had taken place in March and that the ideas described in my message to Carayol were developed in the two intervening months, as a way of channeling the disappointment at learning the news about Faltings. My message to Rapoport described what I had hoped would be a completely new research project to occupy me for five years or more—a chance to give Mr. Coherent Cohomology a rest. Apparently the reality was quite different. Between March and May, I had convinced myself of the possibility of a global argument. But my dream’s appeal lay precisely in the absence of global techniques. Devotion to an ideal of methodological purity led me to prefer a purely local approach to a problem that was itself purely local; and the problem offered what looked like the prospect of a five-year vacation from Shimura varieties.10

The news about Faltings put an end to these daydreams, and I reluctantly resolved to save what could be salvaged from the six-month apprenticeship. A few weeks later, Carayol came to Paris for a day or so (to see his dentist). In the interim I had described my global approach to Henniart, who quickly showed that my results implied that the cohomology of the coverings of Drinfel’d’s Ω gave a “numerical correspondence”¹¹ that was both constructive and natural—what mathematicians call canonical, meaning insensitive to the ambiguities of identity that were explored in chapter 7. I met Carayol at a not particularly memorable café on the Place d’Italie and explained how the global argument to which I had referred in my message led to a natural candidate for the local Langlands’ correspondence. He had predicted as much in his Ann Arbor talk, but at the café he denied he had thought through the consequences of the global argument.

The story lasted another eight years, and in a significant sense it has not yet ended. The ideas I worked out with considerable help from my French colleagues that spring (and many others later, not only French) were finally published four years later, as “an elaboration of Carayol’s program.” Several articles, several ideas, and several years later, Richard Taylor and I wrote a book containing, among other results, the first proof of the local Langlands conjecture for p-adic fields.¹² But the one we solved was only one of the many local conjectures, those formulated by Langlands himself and those proposed by analogy, and there are currently several active branches of number theory that derive in part from the ideas I first encountered in my dream in 1992.

Just over midway through my career to date, that dream set in motion developments that changed my life in more ways than I care to name. But I have recorded this story because I want to understand its uncanny side, and this particular incident is more uncanny, I believe, than the typical intervention of the unconscious in science. The literature on the role of the unconscious in creativity contains many striking examples of dreams providing solutions that had long resisted the persistent efforts of scientists’ conscious minds. I know of no other example of a dream providing a strategy to solve a problem that had never previously laid serious claim to the dreamer’s attention. The dream did help me solve what I may well have felt to be my most pressing scientific problem, escaping the role of Mr. Coherent Cohomology. But that hardly suffices to explain the dream’s manifest content.

Not being inclined to seek supernatural explanations for life-altering events, I have been wondering for years how that marvelous idea found its way into my dreams and stayed there long enough for me to remember it. Just recently I have begun to piece together a tentative explanation. My theory does not show me in a particularly flattering light, but it is highly plausible. I suspect the unconscious drive behind my dream was, in a word, jealousy—long-forgotten jealousy, more precisely, directed at one person with whom I overlapped only briefly and a second who was a total stranger during the period in which the jealousy was experienced.

As a graduate student, I might not even have become aware of the local Langlands conjecture, were it not for the fact that Jerrold Tunnell’s Harvard thesis containing the first proof of the conjecture in a nontrivial setting was written the same year as my Harvard thesis on a totally unrelated subject. Tunnell’s thesis overshadowed all others that year; being naturally competitive, I suppose that must have made me uncomfortable. When I occasionally made use of Tunnell’s other work in subsequent years, I don’t remember any conscious residue of the jealousy of my last year as a Harvard graduate student. But, it’s certain that the incident persisted as an unconscious memory, and it’s plausible that it was triggered by the allusions to the local Langlands conjecture in my lunchtime conversation with Rapoport.

Even earlier, as an ambitious undergraduate math major in Princeton, I had been exposed to the local folklore of Princeton undergraduates who had realized their ambitions. The star shining on the distant horizon was John Milnor, the 1962 Fields Medalist, who at the time was a professor at the nearby Institute for Advanced Study but whose Princeton senior thesis was still being quoted by knot theorists. A more recent landmark was the undergraduate career of Wilfried Schmid. I no longer remember the stories told about him, but I was aware that, only a few years past his PhD, he was already recognized as a leader in two fields. While writing my own senior thesis, I looked up Schmid’s in the Princeton archives, although the subjects had no relation whatsoever. Even earlier, I had attempted to read his article entitled On a conjecture of Langlands13—same Langlands, different conjecture, already briefly mentioned as an analogue of Carayol’s Ann Arbor conjecture.

As an undergraduate, I was not able to make much sense of Schmid’s article, but ten years later I studied it very carefully when I started working on coherent cohomology. I have already mentioned that Schmid’s article made explicit use of local as well as global trace formulas, and if the strategy outlined in my dream struck me immediately as believable, it was precisely because of the analogy with Schmid’s work, specifically with the article I just mentioned.¹⁴

Psychoanalytic dream interpretation is based as much on the dreamer’s subsequent associations as on the content of the dream itself. It seems reasonable to conclude that my dream was motivated in part by an entirely unconscious but deeply buried wish to write an article like the one Schmid published in 1970 about a conjecture of Langlands. It’s hard to deny that, from a conscious point of view, publication of one particular article in a “great journal” and the acquisition of an indelible aura of charisma reflected from the Langlands program represented a satisfying epilogue to the story that began with my dream in December 1992. But it is disorienting to speculate that my unconscious mind might have begun preparing this outcome more than twenty years earlier.