Statistical Mechanics and Quantum Mechanics

G. E. Uhlenbeck

Editor’s Note

Nature here reprints a notable address given by physicist George Uhlenbeck in a ceremony awarding him the Lorentz Medal of the Royal Netherlands Academy of Science. Uhlenbeck describes his long-standing interest in fundamental questions of statistical mechanics, and notes that while the foundational problems of quantum theory had occupied theorists for decades, phase transitions—such as the abrupt gas-liquid transition—and related phenomena continued to pose many unsolved problems. Uhlenbeck also claims that the idea of a generally apparent frontier of science—separating the known from the unknown—is mostly a romantic illusion. Instead, he suggests, there are always many frontiers, and they usually become identified whenever there is an advance, not the other way around.　　中文

ARE the problems of statistical mechanics truly fundamental? I have often changed my opinion and now I would like to elaborate on it. When I was a young student, kinetic theory of matter seemed to me an example of a theory which truly explains something. With much care and effort I worked my way through the Lectures on Gas Theory by Boltzmann and the Elementary Principles of Statistical Mechanics by Gibbs. Much escaped me and became clear only after I read the famous encyclopaedia article by the Ehrenfests. It was a revelation, not only because of its great clarity but also because it contained a careful summing up of the series of more than twelve lacunae in the work of the masters. These were like frontier posts and a young student could thereby learn where the real problems lay. How difficult it is to find this out nowadays. The present pollution of the scientific literature makes the finding of clear water, the fundamental concepts, an extremely time consuming occupation. This is true not only for the new student but for anyone who tries to learn something outside his own speciality, as I well know by experience.　　中文

Though I passed my examinations successfully, I knew very little of quantum theory and even less of the theory of spectra. I learned that, with Goudsmit’s help, when I returned from Rome in 1925 and became Ehrenfest’s assistant. I shall not elaborate on the collaboration with Goudsmit, which I shall never forget and which led to the discovery of electron spin. Both Goudsmit and I have often related our memories of this unforgettable period and I mention it only because at that time my conception of statistical mechanics changed completely. I considered it to be clearly on a secondary level. Quantum mechanics on the other hand provided a foundation from which everything should follow, including the behaviour of gases, liquids and solids. This seemed to be confirmed by the success of the electron theory of metals. Pauli and Sommerfeld (both recipients of the Lorentz Medal) showed how all difficulties disappeared as soon as one applied the true quantum statistics. A few riddles remained, such as superconductivity, but in our optimism we felt sure that all would be straightened out eventually. My dissertation in 1927 about statistical methods in quantum theory was therefore a kind of optimistic synthesis of the encyclopaedia article of the Ehrenfests and the new quantum mechanical ideas. The number of unproved assumptions was reduced to three.　　中文

Later in Ann Arbor, the beautiful experiments of N. H. Williams on thermal noise and shot noise aroused my interest in the theory of Brownian motion, one of the nicest applications of statistical mechanics. I thought it very interesting but of course it was not fundamental. I remember very well that when I told Pauli about it he called it “desperation physics”. I didn’tlike this but I really agreed with him. For a physicist of the quantum mechanics generation to which I also belonged, the fundamental problems of the 1930s were the theory of the positron, quantum electrodynamics and the developing theories of nuclear structure and beta radioactivity; these were the things on which to work.　　中文

Let me say at this juncture that the image of progress in science as a kind of conquest of an unknown domain with a definite “frontier” and successive “breakthroughs” seems to me more and more to be only a romantic illusion. This picture was clearly inspired by the great breakthrough of quantum mechanics and it has influenced my judgment for a long time. I might even say that I was afflicted by it.　　中文

My opinion about the fundamental character of statistical mechanics began to change in 1937 to 1938 when I, together with Boris Kahn, became involved in the so called condensation theory. The question why a gas condenses below a sharply determined critical temperature at a sharply determined density has never been called to attention since Van der Waals and the proper understanding of it seemed difficult to us. During the lively discussion about this question at the Van der Waals Congress in 1938 it was even doubted whether the basic assumptions of statistical mechanics contained the answer even in principle. This doubt was not justified, but it made a deep impression on me. As long as such common phenomena as the equilibrium between liquid and vapour and the existence of a critical temperature were not truly understood, the field was not yet conquered, not everything had been explained in principle and thus there existed fundamental aspects of statistical mechanics which I had not appreciated.　　中文

(When I showed Pauli the article by Kahn and myself on condensation theory he looked at it and said, “Yes, one should read this”. He did so and ridiculed somewhat the quasi-mathematical rigour of our work but I believe that he appreciated the fundamental character of the problem.)　　中文

After the war, I continued to follow the new developments in quantum electrodynamics and the theory of beta radioactivity, and from time to time I contributed a little. But my interest moved more and more towards the fundamental questions of statistical mechanics. In the 1950s I began to write a book on statistical mechanics with my pupil and friend, the late T. H. Berlin. I hoped that it would become a modernized and expanded version of the encyclopaedia article which had made such an impression on me. I hoped that we could determine the foundations of the theory in the same critical way as the Ehrenfests, and that we could make clear the nature of the still unsolved basic problems. In short, I hoped that we could discover the “structure” of statistical mechanics.　　中文

We worked hard on it but did not get very far and the sudden death of Ted Berlin in 1962 makes it doubtful that our plan will ever be realized. I have learned a lot from it, however, and I have the feeling that I more or less understand the structure of classical statistical mechanics at least. I believe that one always has to keep in mind that the task of statistical mechanics is to study the relationship between the macroscopic description of physical phenomena and the microscopic molecular description. These two pictures are in a certain sense independent; moreover, they are, so to speak, on a different level and are therefore, even qualitatively, totally different. If one sticks to this idea, one can see that Boltzmann, Gibbs, Einstein, Ehrenfest and Smoluchowski have formulated the true basis on which one has to build further. One sees also that there are still many unsolved problems, such as condensation and other so called phase transitions, on which much work is being done. All these problems are very difficult but they are, as a mathematician would say, bien posés and therefore one can work on them.　　中文

In my opinion the situation is somewhat different for quantum theory. The relationship between the classical and quantum mechanical descriptions of molecular phenomena is rather clear, but this is not so for quantum mechanics and the macroscopic theory. I am aware that this opinion is not shared by most of my colleagues. I believe that the most widespread opinion is that quantum mechanics can be “grafted” onto the classical statistical mechanics of Boltzmann and Gibbs and that therefore quantum mechanics does not require anything essentially new. I had thought so earlier too, but I have slowly retreated from that conviction. The recent discoveries of so called macroscopic quantization and interference phenomena in liquid helium and superconductors have had a great influence on my ideas. They seem to me to show that the existing theories of superconductivity and superfluidity do not provide a complete explanation and that the true macroscopic description of the superfluids has not yet been found. It would be no surprise to me that this is so because the foundations of quantum statistical mechanics have not yet been sufficiently clarified. One only needs to think of the persistent currents to feel doubt about the general validity of the ergodic theorems in quantum theory. Questions like these make low temperature physics so fascinating for me; they have had a rejuvenating effect on me and I am convinced that there is still much to be done on this “frontier” of physics and that profound surprises are possible.　　中文

Because I use the word “frontier” let me finally return to the romantic image of advances in science which I sketched earlier. I do not believe in it any longer. There are many frontiers and it comes down to the fact that in science one can only sometimes talk of progress. Whenever there is an advance there is a frontier, not the other way around. As to the direction of the advance, every investigator follows his own nose and does what he can. In my opinion this applies equally to space travel and to high energy physics and radio astronomy. These pursuits exist because they are possible and as long as the expense does not become too exorbitant one must, of course, continue them. But I think that one must oppose all fashion and prestige arguments. There is no natural hierarchy of problems and moreover, as Poincaré remarked long ago, a problem is never completely but always only more or less solved.　　中文

It seems better to me to view progress in science as the expansion of different circles of investigation, each autonomous and often apparently entirely independent of the others. The deep problems are to determine how these areas hang together, and how one can arrive at a larger unity. Biology and physical–chemical research, for example, form two such large circles. Their interrelationship seems to me to represent one of the deepest questions man can ask, a real mysterium tremendum. On a much smaller scale macroscopic and molecular physics form two such circles and statistical mechanics attempts to fathom their relationship.　　中文

(232, 449-450; 1971)

G. E. Uhlenbeck: Rockefeller University, New York.