Confessions of a slightly frayed continuum mechanician
by Morton E. Gurtin
, November, 2004
This award is a great honor: although I’m a mathematician, my career began as a mechanical engineer. After graduating from RPI with a Bachelor’s degree in Mechanical Engineering, I worked as a structures engineer for Douglas Aircraft and for General Electric, where I spent many hours studying Timoshenko’s books on vibration analysis and plates and shells.
My third year at General Electric was in a consulting group concerned with structures and vibrations. My work was interesting: during one period I worked on a problem involving a vibrating washing machine and at the same time performed a vibration analysis of a nuclear aircraft-engine. Our group consisted almost entirely of Ph.D.’s, and I wrote a few papers on topics related to my work. I was greatly influenced by two colleagues, Bob Plunkett and Paul Paslay, who strongly suggested that I go back to school. Under their counseling I applied to Stanford and MIT in Engineering Mechanics and to Brown University in Applied Mathematics. My first choice was MIT, but because of my college-grades (which is another story for another time) MIT offered me a probationary assistantship, but Brown ignored my grades and offered me a National Defense Fellowship, which I accepted.
I wrote my thesis with Eli Sternberg and remained on the faculty for five more years. During my last few years at Brown the department became factionalized, with Ronald Rivlin on one side and the remaining senior faculty on the other. Midafternoon the faculty would have coffee at a nearby delicatessen. This could be unpleasant, as it was necessary to decide with whom to sit. I solved this problem by going to coffee with Jack Pipkin, another young faculty member, and sitting with him. I’ve heard all sides of the story behind the split, and to this day don’t understand what happened; all I know is that it made my last few years at Brown very difficult. Things were so bad that almost the entire senior faculty left within a three year period.
The direction of my scientific career was changed by Clifford Truesdell’s classic 1952 paper on nonlinear continuum mechanics and Walter Noll’s thesis, written in 1955. These papers and a course I sat in on by Albert Green introduced me to the rational study of nonlinear continuum mechanics, a subject I have pursued ever since. A scientist who had great influence on my work was Bernard Coleman. His papers, partly in collaboration with Noll, made thermodynamics understandable, at least to me. I had detested this subject since my undergraduate days at RPI, where thermodynamics was synonymous with steam tables. Coleman had a marvelous knowledge of the physical world and worked with great intensity. We would discuss work over the telephone, usually after midnight. One problem with Coleman is that he loves to talk and hates to end a conversation. Often I would put the phone down and work until I stopped hearing his voice; I would then pick up the phone and say; ``Bernard, I agree completely''.
As a young faculty member I was asked by Josef Meixner and Joseph Kestin, who were thermodynamicists, and Rivlin to present some lectures for the faculty on the thermodynamics developed by Coleman and Noll. Meixner, Kestin, and Rivlin despised this work, as did most senior people working in thermodynamics and continuum mechanics. They did not like the idea of defining temperature outside of equilibrium, they did not like the idea of entropy as a primitive quantity, and they did not like abandoning the classical ideas of state. I was attacked continually during these lectures, with Rivlin, who has a great sense of humor, continually making jokes, mostly at me expense, but I do believe I held my own. Today the Coleman-Noll view of thermodynamics is generally accepted by workers in continuum mechanics, most often without acknowledgment, but a generation of scientists had to be replaced.
I have had more angry discussions about thermodynamics than about any other scientific topic. Thermodynamics is a strange, almost mystical subject. It is at the same time both abstract and practical. It’s been my experience that engineers and applied scientists don’t often understand the nature of primitive objects in a physical theory: in books on thermodynamics one often finds temperature defined in terms of entropy on one page and entropy defined in terms of temperature a few pages later. This type of circular reasoning along with pseudomathematical definitions of standard mathematical objects lead students to either reject the subject or to accept it with an almost religious zeal.
In the midsixties Coleman and I, in partial collaboration with Ismael Herrera, wrote a series of papers on wave propagation in materials with fading memory, which is a fancy way of saying viscoelastic materials. When I presented this work at Brown I was attacked by many of the faculty who said that, because of dissipation, the waves of discontinuity that our theory predicts could never exist. Jack Pipkin agreed with this point of view, and told me that he was going to use a simple model to show that our theory was flawed. A few days later Jack came to my office and said that we were correct; his model established the actual existence of these waves. Later we found an earlier paper by Lee and Kanter that did the same.
Through the years I have learned that in physics intuition can often be misleading: it’s an excellent guide but a poor leader. During a visit to Brazil I worked on the thermodynamics of diffusing, chemically reacting materials with a chemical engineer to whom I will refer as V. Thermodynamics often leads to an inequality involving the relevant fields. When I showed V the inequality I had derived he became very excited and lectured me for an hour on how this inequality, as interpreted term by term, made perfect physical sense. That night I discovered that the inequality went the other way. The next day V gave me another lecture demonstrating the physical correctness of the reversed inequality.
By the Fall of 1965 all of my continuum mechanics colleagues except Pipkin and Rivlin had left Brown, and I left in 1966. My departure from Brown made me very sad, as I really loved the place. I always felt I would return, but that never happened.
This is the approximate midpoint of my talk and it reminds me of a workshop chaired by L. C. Young, a great mathematician and the originator of Young measures, a mathematical tool central to the study of phase transitions. Young, then approximately 80 years of age, was asleep at the front of the room. The speaker was midway through the talk and a question from someone in the audience resulted in an animated discussion with the speaker. The discussion woke up Young who sat quietly listening and when the discussion ended Young stood up and said: ``Well, if there is no further discussion, let’s give our speaker a great big hand and retire for lunch.”
And, while we’re in a nonserious mood, let me add a quote from the writer Frederick Raphael about awards: Awards are like hemorrhoids; in the end every asshole gets one.
The early years at Carnegie Mellon were wonderful. We were possibly the best place in the world for nonlinear continuum mechanics. The 60’s, driven by the research of Toupin, Ericksen, Noll, and Coleman, saw the solution of many of the conceptual problems that had plagued continuum physics, and much of this work was carried out at Carnegie Mellon.
One of the main things I learned during this period is the importance of concepts, of ideas. There are many levels of understanding: a theory generally has a few major ideas that form its backbone, and these are usually discovered first, but the real understanding lies in the interconnections that arise when layer after layer of extraneous material is removed. I learned most of this from Walter Noll, who is the deepest mathematician I have known.
Because the basic framework of continuum physics was not well understood prior to the 60’s, the work during the 60’s was often axiomatic. Unfortunately, the insistence on axiomatics later became a disease in which ideas of little depth were flowered with trivial demonstrations of rigor; also, unfortunately, I was one of those stricken with this disease.
In 1975 Jerry Ericksen wrote a paper on the equilibrium of bars that instituted phase transitions as a branch of continuum mechanics. Ericksen, who was central to the 60’s renaissance of continuum mechanics and well known for his pioneering work on liquid crystals, began in the mid 70’s applying continuum mechanics in situations for which behavior at microscopic scales becomes important. Concurrently materials scientists such as Cahn, Eshelby, Frank, Larchie, and Mullins, among others, were developing theories of multiphase systems based on ideas of Gibbs and Herring. A central outcome of this work was the realization that problems involving phase transitions with sharp interfaces generally result in an interface condition over and above those that follow from the classical balances for forces, moments, mass, and energy. Granted equilibrium, this extra balance may be derived variationally, but such a variational paradigm is not available for dynamics; even so, materials scientists typically use, for dynamics, the variationally-derived interface condition for the system at equilibrium. In studying this body of work one is left trying to ascertain the status of the resulting interface condition: is it a balance, is it a constitutive equation, or is it neither? Successful theories of continuum mechanics are typically based on a clear separation of balance laws and constitutive equations, the former describing large classes of materials, the latter describing particular materials.
That additional configurational forces may be needed to describe phenomena associated with the material itself is clear from the seminal work of Eshelby, Peach and Koehler, and Herring on lattice defects. But, again, these studies are based on variational arguments, arguments that, by their very nature, cannot characterize dissipation. A completely different point of view was taken by Allan Struthers and me in 1990; using an argument based on invariance under observer changes, we concluded that a configurational force balance should join the standard (Newtonian) force balance as a basic law of continuum physics.
Over the past ten years of so — partially in collaboration with Paolo Cermelli, Eliot Fried, and Paolo Podio-Guidugli — I have used configurational forces, with its peculiar balance, to discuss a variety of phenomena, examples being solid-state phase-transitions, solidification, grain-boundary motion, and epitaxy. In a forthcoming study, Cermelli, Fried, Dan Anderson, Jeff Mcfadden, and I discuss fluid-fluid phase-transitions; here the extra interface condition, being viscous, cannot be determined using a variational paradigm.
As a graduate student I was strongly influenced by a point of view — of my advisor and of others working in nonlinear continuum mechanics — that plasticity was not a field worthy of study because of its `` rotten foundations''. This view was strengthened by an undecipherable course taught by a major name in plasticity theory. But time has taught me that such a view is snobbish and unintellectual: if a theory that predicts well the qualitative behavior of real materials has questionable foundations, then, for a person interested in the foundations of continuum mechanics, that is all the more reason to study it.
Based in part on work of Aifantis, Anand, Asaro, Fleck, Hutchinson, Mandel, Needleman, and Rice, in part on my own work on phase interfaces, and in part on discussions with Lallit Anand, Alan Needleman, and Erik Van der Geissen, from which I have gained much, I have become interested in the description of crystalline and isotropic plasticity at small length-scales via dependences on strain gradients. Underlying my work is an accounting for the power expended by microstresses conjugate to plastic strain-rate and plastic strain-rate gradient, an accounting that leads naturally to a microforce balance for the microstresses that, with thermodynamically consistent constitutive equations, forms a flow rule in the form of a nonstandard partial-differential equation requiring boundary conditions. The resulting theories are shown to exhibit two distinct physical phenomena:
(1) energetic hardening associated with plastic-strain gradients and resulting in a size-dependent back-stress as well as boundary-layer effects;
(2) dissipative strengthening associated with plastic strain-rate gradients and resulting in a size-dependent increase in yield strength, with smaller being stronger.
The work on energetic hardening is in partial collaboration with Bittencourt, Cermelli, Needleman, and Van der Geissen; the work on dissipative strengthening is joint with Anand, Lele, and Gething; the strenghening phenomenon was discovered independently by Fredricksson and Gudmundson.
This recent excursion into plasticity has demonstrated to me, once again, the power of continuum mechanics and the importance of collaborations between continuum mechanicians of my ilk and engineers more interested in applications. But, unfortunately, at a time when technology requires sound models of exotic materials and of materials applied at smaller and smaller length scales, continuum mechanics is dying. This subject, with its focus on the rational formulation of theories and on the unification of disparate theories, is being dropped from engineering curricula in favor of separate sometimes archaic courses in solids and fluids — and this at a time when materials whose underlying structure is neither solely solid nor solely fluid are being developed and utilized. Ironically, physicists in droves are now turning to the use of continuum models, but are doing so without even a minimal understanding of the underlying mechanics. I am deeply saddened by this situation, and I don’t see it improving in the near future.
In discussions regarding life-choices I am often asked if I enjoy being a mathematician. My answer is always the same: I’m a lucky person; I can’t believe I get paid to do what I do. It’s diffcult to describe to a lay person that wonderful, almost magical moment of revelation in the solution of a problem or in the understanding of a concept. The problem or concept need not be grandiose, or even important, and often it is forgotten the next day.But that seems unimportant.
I try to frame rational theories of continuum physics. Once in a while I am successful, most often I am not. And the work is very painful. But the successful theories are worlds, exciting worlds through which I can roam, perhaps for just moments, but those moments, like no other, are free of the ambiguity, confusion, and meaninglessness that pervade most of everyday life.
Good theoretical science is done by a few dedicated people working alone or with one or two colleagues; this science does not need the large grants that have made prostitutes of most of us, including me. The need to be relevant, the need to be applicable to industry; these are not forces that lead to advances; what leads to advances, often spectacular, is simply the curiosity of the individual scientist, just as Einstein’s curiosity about the structure of space-time led to the theory of relativity. Big science is a driving force for mediocrity.
But I don’t know the answer. Perhaps we can one day return to the times of small individual grants for summer salary and occasional trips to meetings. Perhaps we can return to the times when one’s university salary was tied to quality of research and teaching, rather than to the amount of government support.
In many respects this diatribe is hypocritical, as I have received large amounts of government support, but often there is a dichotomy between what one does and what one believes would be best for society as a whole.
In closing let me thank you so very much for the Timoshenko medal, for your time, and for your interest. THANKS.