AN INTERVIEW WITH
JAMES A. YORKE
-- by Tim
Sauer (George Mason University)
January 8, 2004 in Phoenix
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Jim Yorke, 2003
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A brief biography of Professor Yorke
James Alan Yorke was born August 3, 1941 in Plainfield, NJ. He
went to
Columbia University as
an undergraduate, and received the Ph.D. degree in Mathematics from
the
University of Maryland in
1966. Yorke is a member and former director of the University of
Maryland's
Institute for Physical
Sciences and Technology, has joint appointments with the
Mathematics and Physics departments, and holds the title of
Distinguished University Professor.
He has published over 300 papers, including the often-cited works
Period Three Implies Chaos with T.Y. Li (1975), and
Controlling Chaos with Ed Ott and Celso Grebogi (1990). He has supervised 30 Ph.D. students in mathematics and physics, and has co-authored
three books on aspects of chaos and a monograph on epidemiology.
In 2003 he received the Japan Prize, along with Benoit Mandelbrot,
for fundamental work in the understanding of complex systems.
His current research topics include HIV epidemiology, better
methods for determining genomes, weather prediction and data assimilation,
topics in dynamical systems, and understanding computer network
traffic patterns.
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Yorke and Mandelbrot at the Japan Prize
ceremony, 2003 |
The interview
(Y = Jim Yorke, S = Tim Sauer)
S: How did you get interested in science?
Y: Well, I visited the
Hayden Planetarium in
fourth grade, and from then on I wanted to become an astronomer. It
was hard to believe there was anything more interesting than what was
going on out in the universe. I loved learning about planets and
seeing the photos from the great observatories using long exposure
times, though I had no interest in looking through small telescopes,
which simply could not compete. Perhaps that was the beginning of
a pattern: liking the results of physical experiments but not
wanting to carry them out.
S: Who were your mentors?
Y: My mentors were not my teachers in school. They were great
mathematicians and scientists whom I read about or who wrote
wonderful books, like Norbert Wiener's popular books "Ex-Prodigy", "I
Am a Mathematician", and "The Human Use of Human Beings". I read
these in high school. In the latter Wiener talks about feedback
control, entropy, non-equilibrium processes, all without
equations. I learned about Maxwell's demon and his theory of gas,
where colliding atoms play a key role. I think that was the
beginning of my understanding of chaos. Certainly Maxwell
understood the chaos. Brian Hunt and I wrote a paper entitled
"Maxwell on Chaos". Another great book from my high-school days is
"One Two Three ... Infinity" by George Gamow, with a lucid
discussion of countable and uncountable sets.
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High school yearbook photo |
Captain, Pingry High track team,
1958 |
S: How helpful was your early formal education?
Y: My elementary school teachers' primary interest was in
accuracy of computation, which relegated me to the half of my
eighth-grade class that learned to read gas meters and write
checks. Somehow I caught up and managed to get accepted into Columbia
anyway. Teachers can be really bad at evaluating a student's
potential.
S: So how good are you at evaluating potential?
Y: No better than anyone else, but I am very concerned
about potentially outstanding students who might fall through the
cracks. I had a friend in high school who was a great problem
solver, and he convinced me to go to Columbia. He was a year ahead
of me though a bit younger. Throughout high school and college we
discussed hundreds of problems and he was always faster at solving
them than I was. To put that into context, I was pretty fast,
since I was the top Columbia contestant on the Putnam exam two
years in a row. My friend got straight A's in advanced math
courses and went to graduate school at a famous east coast
university. I went to Maryland and when I got my Ph.D., he was
still struggling without a dissertation problem. I figured the
reason he could solve all those problems faster than I could was
that he thought like I did, but was better at it. I made one phone
call to him, and told him about a problem that was my kind of
problem: simple to state and probably very difficult to solve, but
didn't require a whole lot of background.
He turned this one conversation into a Ph.D. dissertation and got
his degree with the help of a very junior faculty member who got
interested in the question. By the time he graduated, he was
teaching four courses per semester at a local community college
and continued to do so after getting his degree.
He has since died of cancer. So I have a question for you: What
was that graduate school doing? Should we evaluate graduate
schools by how many outstanding mathematicians they graduate,
rather than how many potentially outstanding mathematicians they
destroy? To this day I have a major concern about potentially
outstanding students failing. People need help at various points
in time and without it they can fail.
S: What made you want to become a math major?
Y: I hated doing physics lab reports, and once a week I had
to stay up all night to get it done on time. I could deal with that,
but the next semester they wanted two lab reports every two weeks.
This was much worse. I couldn't stay up for two nights straight
and so I dropped the course that was required for physics
majors.
S: Why did you choose Maryland for graduate school?
Y: When I was leaving Columbia, I already had a love for
mathematics but wanted to be sure that the graduate school I went
to avoided the severe, motivation-free abstraction that was
characteristic of Columbia at the time. I got similar teaching
assistant offers from Cornell and Maryland, but at the time,
Cornell's program was much like Columbia's. Even then, Maryland
was strong in interdisciplinary mathematics.
S: Did you find college and graduate school more helpful
than your early education?
Y: I learned a great deal in college and graduate school,
but I was never systematic about learning the material and in college
may have had a B average in math and physics, and worse in other
subjects. As a student on a full scholarship, that was dangerous.
When I got to Maryland I immediately took and passed the Ph.D.
qualifying exam. After that, grades were fairly irrelevant. It has
always struck me that you might understand a course well enough to
write a publishable paper about your ideas in the subject, but
that doesn't mean you've learned the material systematically
enough to get an A.
There's a great conflict for young people,
whether to be a mathematician or a student. Give a student a
problem that won't count for any grade, and he or she will say, I
don't have time, I have so many other homework assignments to
complete. So when I see a student with a 4.0 average I immediately
worry that he or she might lack the motivation to be creative when
grades are not in question. Of course, some 4.0 students are
creative despite their GPAs.
It reminds me of something I heard
when I was in high school, that excellent scientists generally
have poor memory, and have to rethink the same questions over and
over, and thereby learn to think. The really outstanding
scientists learn to think despite having a great memory. Myself, I
don't have the memory of a 20-year-old, and I never did.
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Jim and one of his pet elephants |
1998 |
S: Your collaborator Ed Ott says that sometimes you come up
with a way of thinking about a problem that seems totally bizarre, but
after a while it dawns on him that it's the only way to look at
the problem. Is this a conscious effort on your part? And is this
a hindrance in everyday life?
Y: I have often found it conversationally awkward that I make
connections between ideas or events that other people feel are
unrelated. They think I am changing the subject. Maybe they are
right. But for mathematical or scientific questions I feel that
whenever we have a question, or an answer, we have to try harder
to ask whether we have the right question. If we really understand
the question, we are a large part of the way to a solution.
Understanding a question well is often making connections between
apparently unrelated ideas. I tell the students they should spend
half their time asking what the right question is, and not the
first half. And even after they have a result, they must ask: what
is the precise question that it answers?
S: Do you have a working style? If so, what is it?
Y: I'll give you an example of one of our styles. We
published the first paper on fractal basin boundaries, aside from the
Julia set results. But we were far from the first to understand
them. People like Cartwright and Littlewood, the Berkeley and Moscow
schools of dynamics, and people like Mark Levi could have given you a
half-hour lecture on fractal basin boundaries with 5 minutes
notice. Much of what they wrote about was dynamical systems that
happened to have fractal basin boundaries. But they talked about
dynamics in a more general way, in which closed invariant sets
were the key concept, and basin boundaries are just one
unmentioned example.
We felt that the basin boundaries would be
very interesting to physicists, and our problem became how to
write an original paper on this topic that people knew well. We
wanted to reformulate ideas that mathematicians knew, in ways that
were more useful to scientists. If they don't know what the
boundary of a basin is like, it is impossible to ask how stable
under perturbations an attractor is. So we created a concept of
uncertainty dimension, a dimension of the boundaries that could
actually be computed and measured by a physicist. Physicists want
concepts that can be quantified.
Another example of reformulating ideas is illustrated in our most
quoted paper. Our goal was to take the ideas of chaos and mix in
well-known ideas of control theory. Ed Ott, as a part-time
electrical engineer, was quite familiar with control theory, as
was I from my college days. But we had to formulate the ideas in a
manner that would be useful to scientists. We did so in a way in
which equations were not written down, but yet scientists could
carry out the ideas in the lab. The mathematicians couldn't see
what it was about the paper that interested the physicists or how
it was new. The subtleties of what makes a paper valuable in one
field can be completely lost on experts in another. My efforts in
physics have always been heavily dependent on the insights of my
physics collaborators, especially Ed Ott and Celso Grebogi.
S: How do you write a paper for both mathematicians and
physicists?
Y: You don't. One should pick an audience and write a paper
for that audience and tell a story tuned to their ears. If the results
are of interest to two audiences, then you might write the paper
twice. But a paper that is aimed at two audiences is most likely
to miss both audiences, and fail.
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Jim with David Broomhead, 1997 |
Maryland-Penn State conference
2002 |
S: What was the origin of the "Period Three Implies Chaos"
paper with T.Y. Li?
Y: It was totally inspired by an effort to explain the
irregular behavior that Ed Lorenz was observing. While he mostly
talked about a three-dimensional system of ordinary differential
equations, he also showed how in some sense you could reduce the
interesting part to a one-dimensional return map. He wrote down
something like a tent map. So the paper we wrote explained how
complicated behavior could be proved for such processes.
S: Why were you so fascinated by periodic orbits?
Y: One thing the period three implies chaos theorem says is
that a continuous map on the line with a period-three orbit must have
orbits of all other periods. This aspect of our paper was a special
case of an earlier result of Sharkovsky. But actually I rather
disliked periodic orbits as a way of understanding chaotic behavior.
It's just one leg of the elephant, so to speak. Our paper spends much
more time on the mixing behavior of one-dimensional maps. How you
could follow initial conditions and they move apart and come closer
repeatedly, that's another leg of the elephant. Mixing allowed us to
talk about uncountable sets, while the periodic orbits were countable
and, therefore, almost nothing.
S: Was that your first paper on chaos?
Y: Actually my first foray into the field of such maps was
with Andy Lasota. We looked at invariant measures for
piecewise-expanding maps. I remember feeling confused as to how
would I explain what my area of research was: sometimes we looked
at operators in Banach spaces to explain the measure theory of
such maps, and other times at the point-theoretic properties of
periodic orbits, which only depended on the continuity. Now there
is a field of one-dimensional maps, but back then these results
seemed unrelated. To me they all aimed at understanding
complicated behavior. They were just different legs of the
elephant. In these two works, the measure theory and topology of
one-dimensional maps, I had two different collaborators.
Throughout my career, I have found it immensely beneficial to work
with people who had excellent ideas to mix with my ideas. Two good
ideas on a problem are much better than two ideas on different
problems. By the way, I think it's hard to tell how many legs the
elephant has.
S: What makes a good question?
Y: From a trivial point of view, a good question is one for
which you can give a good answer. But from another point of view, the
point of research is to put questions together with answers, and
evolve the questions and answers together until you get a great
match: Co-evolution. Andrew Wiles had a monumental achievement in
solving Fermat's Last Theorem. But I fear it will strengthen the
concept that students have that you find a problem and then work
on it for years.
That is rarely how research is done. Students
must learn to co-evolve questions and answers. I look for
questions that give an interesting answer, but then I hope to be
able to build on the question with my collaborators and follow the
question in new directions and let the problem grow. It may start
out as a simple problem, but after several stages of evolution it
becomes more interesting. As it evolves, I personally keep the
audience in mind. What can I tell the audience about this problem
that I feel they need to know, or that I feel will surprise them?
S: What do you tell a student who is stuck on a problem?
Y: I tell students that when they think about a problem,
they shouldn't take notes. If they don't understand what's going on,
they should start over from the beginning each time, hopefully
having forgotten their wrong approaches. Taking notes allows them
to remember their wrong approaches. Too much writing interferes
with the thinking. I advise mathematicians to buy a dog who will
need long walks, and in extreme cases, several dogs.
You should never work nonstop on a problem because you need time
to forget your wrong approaches, which is another reason why
people with lousy memories can be excellent scientists.
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Maryland
genome analysis group, 2003 |
Advisors Kalnay, Hunt, Ott, Yorke with new
Ph.D. D.J. Patil |
S: What is your advice to young people interested in
mathematics?
Y: One view of mathematics it that it is based upon the
three core legs of topology, analysis and algebra. That view is valid
in a certain sense, but I prefer to ask how mathematics interacts with
the world, and draw the core from that. The three legs of this
interaction tripod are differential equations, numerical methods,
and probability and statistics. Even for someone writing a
dissertation in topology, algebra, or analysis I feel it is
important to know about the legs of the interaction tripod. But we
allow our graduate students to get PhD's without having taken any
courses in the latter three areas. We require more of our
undergraduates. We sometimes allow graduate students so much
freedom that they can hurt their professional careers and their
ability to get a job at universities where non-math students must
be taught. I recommend to students that they take one course at
least in each of the three areas of the second tripod.
S: What do you see as the future of dynamical systems?
Y: I think everybody, including me, is rather poor at
foreseeing the future. Generally we can't even see the present. For
example, there are many seminal papers in dynamical systems that had
trouble getting published. Sheldon Newhouse tells the story that
he refereed Hénon's original paper for David Ruelle, the
editor, and thought it wasn't rigorous, it wasn't math, it wasn't
physics, and he recommended rejection. But Ruelle liked the paper and
fortunately overruled him. Newhouse has a record of wonderful
discoveries in dynamical systems but missed the value of that
paper. He couldn't see the future when it was in front of him. And
I think we are all that way. Instead of trying to predict the
future, I look for ideas that can surprise people, or interest
them. I am not the kind of mathematician who tries to develop a
general theory of something. Neat examples are good enough for me.
S: What is it with wearing the red socks?
Y: Nothing really, just a reminder to think differently.