INTER ACTIONS 2001

Crack Physics

by J.S. Langer

Jim Langer (B.S.’55) was a member of the Carnegie Mellon Physics faculty from 1958- 1982. He then moved to the University of California in Santa Barbara. He was the director of the Institute for Theoretical Physics at UCSB from 1989 to 1995, president of the American Physical Society in 2000, and has recently been elected to a four-year term as vice president of the National Academy of Sciences. 

This writing assignment makes me think once again about how much I owe to my many years of associations with Carnegie Mellon. After my first physics courses at what was then Carnegie Tech, I couldn’t imagine a career in any other field. That was a long time ago – Ed Creutz was department chair, and some of those courses were taught by very young incarnations of Sim Friedberg and Lincoln Wolfenstein. With advice and encouragement from Walter Kohn, I left Tech briefly to do a quick Ph.D. with Peierls at the University of Birmingham in England, and then returned to spend more than 20 wonderful years on the Carnegie Mellon physics faculty.

I’ve always been a theorist with a weakness for field theories and for wandering around in the complex plane – I’m sure I’d have done that anywhere. What I picked up that was special at Tech/Carnegie Mellon was a curiosity about theoretical questions in areas outside of mainstream physics. Bill Mullins (who died this year and was a very special person to me) and Bob Sekerka enticed me into nonlinear, nonequilibrium problems in materials science – questions about precipitation patterns, dendritic crystal growth, and the like. That was a great learning experience, in effect, doing a postdoc with Bob Sekerka for a few years. And I’m pleased to see that many of those topics have rejoined mainstream physics since Bob and I began working on them.

Throughout the rest of my career, I’ve wandered at regular intervals onto other scientists’ turf. That’s not always a smart thing to do, especially in today’s competitive environment; I’ve learned that lesson from people who have reviewed my papers and research proposals. Now that I’m supposed to act like a scientific elder statesman, I guess I should be even more careful. However, by following a curious path from snowflakes to fluid fingering patterns to fracture to earthquakes, I’ve arrived again at an unconventional position. In short, I’ve come to the conclusion that the large and very important field of solid mechanics – the science of how solids deform and break – is badly in need of a thorough reformulation. Let me tell you a little about this. For over half a century, solid mechanics in engineering practice has consisted of increasingly sophisticated analyses of phenomenological rules – stress-strain curves, yield criteria and the like.

During that same period, the science of solid mechanics has been dominated by the theory of dislocations – a beautiful picture of how crystals deform when defects move through them. In all that time, however, we have not come even close to being able to use dislocation theory to predict the mechanical properties of realistic structural materials. The conventional approaches fail to address many fundamental questions, all of which are well known to experts in the field.

For example: What are the fundamental distinctions between brittle and ductile behaviors? A brittle solid breaks when subjected to a large enough stress, whereas a ductile material deforms plastically. Remarkably, we do not yet have a fundamental understanding of the distinction between these two behaviors. Conventional theory says that dislocations move more easily through ductile crystals than brittle ones, thus allowing deformation to occur in one case and fracture in the other. But the same behaviors occur in noncrystalline solids such as glasses and even soils, where the concept of a dislocation makes no sense. Thus the dislocation mechanism cannot be the essential ingredient of all theories. Moreover, some materials – “silly putty” for example – are ductile when loaded slowly and brittle when subjected to sudden stresses, which implies that a proper description of deformation and fracture must be dynamic, i.e., it must be expressed in the form of equations of motion rather than phenomenological rules and yield criteria.

A second question: What is the origin of memory effects in ordinary materials? Standard, hysteretic, stress-strain curves for deformable solids tell us that these materials have rudimentary memories. Roughly speaking, they “remember” the direction in which they most recently have been bent. When reloaded in the original direction, they respond almost elastically, that is, they don’t undergo additional deformation. On the other hand, when loaded in the opposite direction, they deform plastically back toward their original shapes. The conventional way of dealing with such behavior is to specify phenomenological rules stating how the response to an applied stress is determined by the history of prior loading; but such rules provide little insight about what is actually happening or what might be the nature of a more satisfactory theory.

My third question is a bit more technical but I think very important: How can breaking stresses be transmitted to crack tips? Solids generally deform plastically under high stresses such as those in the neighborhood of a crack tip. The stresses at crack tips, supposedly, must be large enough to break the bonds between neighboring molecules; therefore, except possibly in special cases such as cleavage fracture, they must be more than large enough to deform the material and blunt the tip. If the material near a crack tip always flows before it breaks, how can cracks ever propagate in a brittle manner? The currently most popular answers to this question invoke hardening via dislocation entanglements; but, once again, the same phenomena occur in noncrystalline materials where dislocation mechanisms cannot be relevant.

Finally: What is the origin of instabilities in brittle fracture? Fast brittle cracks are unstable against bending and sidebranching. The fracture surfaces are characteristically rough, and the energy dissipated in forming these complex fracture patterns limits the speeds at which cracks can propagate. We still do not know what mechanisms control fracture stability. In some respects, the present state of the theory of dynamic fracture resembles that of solidification theory almost half a century ago, before Mullins and Sekerka had identified the instability that underlies dendritic pattern formation in crystal growth.

The reader will have guessed that I think I have some answers to these questions. Indeed, I do; but I don’t intend to say much about those answers here. Most of my results are new, and my years of experience tell me that they’re probably not nearly so good as they seem to me at the moment. Rather, I’d like to use solid mechanics as the starting point for more general remarks about the present state of physics.

This is a wonderful time to be a research physicist. The array of fascinating research topics – from astrophysics and elementary particles to condensed matter and biophysics – has never been so broad and so full of opportunities for productive investigation. Why, then, do I work on solid mechanics, a subject that has long been dropped from most physics curricula? Why do I think there’s any chance that I can make a useful contribution to such a well developed field? The answer is that I, like all scientists these days, have extraordinary new tools to work with – tools that we did not imagine might be possible when I was a student, and which can help us answer questions now that recently seemed completely out of reach. We can see individual atoms and molecules on crystal surfaces and inside biological cells, we can measure the forces that they exert on one another, and we can manipulate them to build devices literally one atom at a time.

Figure 1: Brittle crack simulation

We also have the computer. That’s the tool that I – or, more accurately, my students – have been using to get new information about fracture mechanics. The figure shows a molecular-dynamics simulation of fracture in a simple, two-dimensional model of a glassy solid. This is work by Mike Falk, formerly at UCSB and now on the faculty at Michigan. Basically, Mike solved Newton’s laws for a system of about 40,000 interacting atoms in a situation that corresponds directly to a bench-top fracture experiment. The little dark blotches near the crack tip indicate regions where the atoms have undergone local rearrangements typical of plastic deformation, that is, where “non-affine” transformations have occurred. By studying the behavior of these little transformation zones, and deducing how to describe them mathematically, Mike and I constructed a fairly simple theory that may answer all the questions I listed above. This has turned out to be a neat way of doing research, combining numerical simulation with real theory and real experiment.

It remains to be seen, of course, whether our theoretical approach will actually provide a useful connection between fundamental physics and the properties of real structural materials. If so, it might have applications well outside the conventional boundaries of solid mechanics – in biology, for example, where the materials have esoteric mechanical properties that soon will need to be understood quantitatively. Whether or not this particular adventure turns out to be successful, however, I think it’s a good example of what’s happening more generally in physics. Our new tools are allowing us to probe an ever growing range of scientific phenomena, some – like fracture – old but not well understood, and others – perhaps like parts of biology – so new that we haven’t discovered them yet. It is indeed a wonderful time to be a physicist.