2001 Timoshenko Medal Lecture by Ted Belytschko
Ted Belytschko, November 13, 2001, New York
Well I have been sitting in the audience of Applied Mechanics dinners for more than 30 years now, never even dreaming that I would get the Timoshenko medal. I have enjoyed many of the talks, and heard many nuggets of wisdom to guide me in research and life. I still vividly remember one of the first talks I heard by Den Hartog- in those days every Timoshenko lecturer could still start with a reminiscence of their contact with Timoshenko. Den Hartog had worked for Timoshenko one summer, and when he wrote his study up as a report, Timoshenko told him to submit it for publication. Den Hartog responded that he did not think that this work was something the world was waiting for. Timoshenko replied-"How many publications that have appeared in the literature do you think the world was waiting for?" One outcome was that I proceeded to publish too many papers, but it is interesting that many of the papers I did not think much of had some impact, whereas many that I liked had no impact .
In preparing this talk, I noticed that many of the talks were autobiographical. But I quickly decided not to make mine autobiographical because I still remember that when I was program chairman, a very witty and brilliant Timoshenko medallist chose his autobiography as the topic. He was only eighteen by 10 PM, and I was at the edge of my chair because I was Program Chairman and the union crew that was waiting at the doors of the banquet hall to clean up.
So I will not give an autobiography, but I would like to say a few words about my teachers. The most important teacher in any research career is the Ph.D. advisor. My advisor was Phil Hodge, who many of you know and who was also advisor of Carl Herakovich, a former member of the Executive Committee who is sitting at the center table. Phil came from Brown, trained by William Prager, and he taught us many things: the importance of clarity and conciseness, personal integrity, and the joys of a career in research and teaching.
Phil also gave us some maxims that you might find useful. One was: "Any research worth doing is worth doing well." The other, which I have found even more useful, went something like this: "Academic paperwork has to be done, but it is usually not worth doing well."
My other mentor was Ernie Masur, who was Chair in my first position at the University of Illinois at Chicago. Ernie was quite different from Phil-whereas Phil trudged to the computer center every day with a box of cards for his daily run- in those days you were a computer jock if your computer cards filled one box, a superjock if it required two or more boxes -Ernie disdained to even type, saying that gentlemen did not type. But Ernie had impeccable taste and a terrific nose for what he called "substance", and he taught me to recognize the substance from the chaff. He also had a great sense of humor, though wit, like principles, can’t be taught
A Timoshenko talk I really enjoyed was Roshko's talk "Think Small." There were many precepts in his talk that I found very appealing, so I have decided to take a similar vein but call it "Think Big Persistently." Now you might think I am contradicting him, but some of the things I will say echo what he said.
I will address only two facets of thinking big persistently-what it means for young people, and what it means for our society, the Applied Mechanics Division.
First let me address the Applied Mechanics Division. Over the thirty years that I have been associated with this Division, the research of this group has continued to flower: the impact of this Division on the applied and theoretical issues of engineering and science has been simply amazing. Fracture mechanics, the theory of plasticity (which really underlies almost all rational nonlinear material models), micromechanics, composites, the finite element method have either originated here or owe a large part of their development to this Division. Yet, during this time, funding from NSF, which is still the best place for research support and supports many pure and applied fields very generously, has almost shrunk to zero.
This is astounding when one considers the impact of this Division on basic knowledge, basic knowledge that is not only intellectually beautiful, but has had tremendous impact on our society. This one of the most talented groups in analytic thinking in the world and the closed form solutions that have been produced by this group have provided the basic understanding of a host of important phenomena. I might add that although I am a computational mechanician, I often say that: “A good closed form solution is worth a thousand of computations."
Now it is difficult to ascertain to what to exactly ascribe this decline, but I have long felt that it is not strictly due to external forces. I believe it stems from our lack of self knowledge, our lack of identity and our reluctance to sell ourselves. Many disciplines, like computer science, have actually hired lobbyists to plead their cause, but as a Division, we almost never talk to the upper echelons of NSF or Congressional staffers. There have been a few attempts at this, but they always seem to wane, and that is why I have added that we must think big persistently-the benefits of interactions do not come overnight
Another source of our difficulties is our fuzzy self-identity. For many years, this Division has attempted to represent fields that were no longer a part of it- the fluid mechanicians have departed for the American Physical Society, but we still included fluids, and most dynamicists are in other places, but we still pretend that it is part of our Division. Perhaps even the name of our division is no longer appropriate. For one thing, the name is not appealing to younger people-most young people starting careers in research and teaching want a more attractive name, they don't want to be confused with those who fix their cars. Furthermore, most of us are not really engineers-much of our work is indistinguishable from physics or from materials science. I daresay the contributions of some members of the Applied Mechanics Division, such as Jim Rice and John Hutchinson, rank with the most important in materials science. So maybe we should look at another name-it was very beneficial for soils engineers, who changed their name to geotechnical engineering, and have much improved their image with the public.
What should such a name be? I have asked a number of people. Some would not even give it an attempt, because they consider it sacrilegious. Lalit Anand, a former member of the Executive Committee, proposed “Solid and Mechanical Engineering and Sciences.” He suggested we would then go by the acronym SMEC. My preference is "Science and Engineering of Solids" -SES. I think it is high time we recognize that we are scientist as well as engineers, and that we get a name that accurately reflects what we do and what we have done!
But more important, the Executive Committee and its past members should be in constant contact with people at Congressional staffers, NSF and other funding agencies. There are 10,000 of us in ASME and more in ASCE, and I think we should have a strong voice. We have to let them know what we do, why it is important, and what we can do for the country. This can not be a one-shot effort, it needs to be done persistently. (for example, Mathematics has just won a commitment for a fourfold increase in funding through such long-term efforts)
My second theme pertains to young people, to whom I would like to give some advice based on my past successes and mistakes. To think big is to look for important problems at the cutting edge. Too many young researchers choose their topics by reading a paper and seeing how they can extend it- that is not how the important problems are found. You have to talk with many people, read both the literature of your disciplines and other fields, and identify the emerging fields and important problems. I fortunately stumbled into nonlinear finite elements through my consulting work early in my career-I wrote a crash code in 1971 when a visionary in DOT initiated a research program by selling the idea that crash testing could be replaced by computer simulation. Well at that time, computers were so slow that even a 500 element simulation (500,000 are customarily used today) cost more than a test, so the program was quickly shelved. But it gave me the opportunity to do some work in a new area that had considerable impact.
To highlight the importance of working on new problems, I quote Arno Penzien, the Noble Prize winner who discovered the background radiation that underpins the big bang theory: “ there are two types of scientists: 2% discover new things and blaze new frontiers, the other 98% fix up their mistakes; the accolades go to the former.”
It is also crucial for the success of this Division that we nurture our young researchers- our future obviously lies with them. In this, I think that we must de-emphasize the role of money in our promotion criteria. We have now reached the point where in many schools, the volume of money supersedes all other factors in a professor’s promotions and recognition. This is really quite absurd, since a university does not exist to make money- our purpose is to teach and do research, and money is only a means to that end. But in many places, right at the top of your annual report is your dollars spent. Everyone seems to have become obsessed with the U.S. New and World Report ratings, in which money plays a dominant role. If this trend continues, I can see two young assistant professor talking one day and wondering: "What is the fuss over Einstein all about?- I hear he never brought in 100k per year.”
So I think we ought to persistently remind our administrators that our goals are not to bring in money. Administrators have incorporated indirect funds into operating budgets, so they are becoming addicted to large research fund flows. It will be a big job to bring this to an end, but if we can think big and persistently, we can at least moderate this.
There are tremendous opportunities for us in emerging fields such as micromechanics, nanomechanics, cellular mechanics, biomechanics, computer simulation, and many that are only barely visible on the horizon today. But to enjoy these, we must do the things that need to be done persistently.
To conclude, I would like to thank my family, my wife Gail and my children Peter, Nicole, and Justine; my colleagues at Northwestern in the field of mechanics, Wing Kam Liu, Brian Moran, Jan Achenbach, Cate Brinson, Zdenek Bazant, Jian Cao, Isaac Daniel, and John Rudnicki (we have the best group in the world, and their collaboration, collegiality and competitiveness have helped me immensely), my students and post-docs, and my professional colleagues, particularly Tom Hughes and Tinsley Oden, who were so instrumental in my winning this award.