Nonlinear Dynamics --- Flows in 3-D and beyond.  
Copyright 1995 by Nicholas B.  Tufillaro.

Nicholas B.  Tufillaro 
Center for Nonlinear Studies 
Los Alamos, NM 87545 USA 

Thursday 2PM, 22 June 1995 HP-LABS Bristol, UK. 
BRIMS---Basic Research in the Mathematical Sciences


 An informal discussion on current research in nonlinear dynamics with
an emphasis on topological methods applied to experimental systems.  I
will begin by giving a brief overview of the current state of the art
of the analysis of low-dimensional dynamical systems (nonlinear time
series analysis of experimental data, empirical model construction,
and model verification using chaotic synchronization), and then sketch
out possible research paths where a dynamical systems perspective
would be useful in understanding systems with a moderate number of
degrees of freedom.


	About 25 years ago, V.I.  Arnold wrote in his book on
classical mechanics that "the analysis of 2-degree of freedom
Hamiltonian systems is currently beyond the capability of modern
science."  I first read this statement by Arnold when I was about 20,
and I knew exactly what he was talking about.  You see my interest ---
no obsession --- with nonlinear dynamics grew from a very specific
incident.  When I was 19, at the end of my freshmen year at Uni, I
decided to spend the summer learning classical mechanics in the
standard fashion, from the text of Goldstein.  I think somewhere in
Chapter 3 or thereabouts, Goldstein introduces the Lagrangian
formulation of classical mechanics.  To me, learning about Lagrangian
mechanics was a real thrill --- and a relief.  I say relief because I
was never really very good at getting those Newtonian force vectors
all lined up and accounted for properly --- I guess I had a touch of
Newtowian dislexia.  But with Lagrangian mechanics all I had to do was
write down the difference between the Kentic and Potential energy and
BAM --- out came the equations of motion.  All during the next day I
was in heaven and began calculating Lagrangians for everything in
site.  My elation was only match by the depth of my depression as I
soon realized that having the equations of motion was not enough ---
you also had to "solve" them.

   My reactions at this point where two:  first I (now mistakenly)
realized that theoretical physics was a bit of a sham --- I mean how
good can science really be if we can not check it out in even the most
simple cases of few rods and balls stuck together and left free to
swing in the wind.  My second reaction was that I was very impressed
with the fact that I could really see no more "fundamental" problem on
the mathematics/physics horizon than finding ways to "solve" nonlinear
equations.  I also soon discovered that this problem had been on the
"horizon" for about 100 years --- ever since Poincare's discovery of
homoclinic tangles and their implications for the global solutions of
ordinary differential equations.  There had been progress in the past
hundred years associated with the likes of Birkhoff, Cartright and
Littlewood, and Smale to name a few, but most working physicists had
been (quite rightly) concentrating their vision on quantum mechanics
and had little time to continue untangling the perplexities possed by
classical mechanics.

I no longer think science is a sham, I now have used science and my
training in physics to solve many specific problems (for example,
constructing semi-conductor lasers for communications systems) and I
now see that the real power of science lies not so much in its
"solutions" of problems but in providing the entire framework --- the
language --- in which we can constructively posse and discuss

The second impression though, that finding a framework, or frameworks,
for solving nonlinear equations as being fundamental to making
progress in many scientific enterprises, I still see no reason to
revise.  It is a fundamental issue which we must address.  So the
question is:  "what's to be done."

In this talk today I would like to review the progress we have made in
nonlinear science in the past 15 years say, and then to promote a
discussion of what questions we should be solving on both the short
term (say next 5 years) and the longer term (say the next 100 years)
research horizon.  I would be happy if at the end of this discussion
we could write down something like 100 questions in nonlinear dynamics
for the next 100 years.  This will not be a normal techanical talk
then, in fact I would be happy if it did turn into more of a
discussion then a talk.

This discussion is important and appropriate for two reasons:  first,
we are at BRIMS whose mission is basic research so it is appropriate
that we think about "the big" questions here; second, nonlinear
studies, at least in the United States, is in a very precarious
situation.  The blunt fact is that the first generation of researchers
with specialized skills in nonlinear science are currently looking for
employment, and they seem to be doing none to well in already
difficult market place for scientists in general.  I do not want to go
into the reasons for this today --- it has to do with many things
ranging from the academic strutural barriers against interdisplinary
work, to the fact that there is no "national" funding for nonlinear
dyanmics in the states, so most University departments in physics,
mathematics, or enginnerring are reluctant to commit resoures to an
individal who has no visible means of external support, irrespective
of the quality of the science they may be doing.  In the United States
publishing in Physical Review is no longer enough, and publishing in
Physical Review E could actually hurt you when looking for a job.

I do not hope to solve this employment problem today.  What I do hope
to do is to begin to formulate a clearer vision of what nonlinear
science can and should be doing, and to articulate this vision to
anyone interested in listening.  I believe that by honestly apprising
what nonlinear has accomplished, and what we expect to learn in the
near and longer term, we will be in a better postion to develop our
field both intellectually and in terms of resources.

Phil Holmes has said that nonlinear dynamics is not a physical theory
in the traditional sense --- it is not like classical mechanics,
quantum mechanics, or electrodynamics --- it does not set out a grand
framework for the definition and calculation of physical quanities.
Phil compares it to a toolbox of techniques appropriate for a limited
class of problems.  According to this view, I think, nonlinear
dynamics is most usefully viewed as an important and emerging branch
of "applied mathematics", with close siblings in pure mathematics like
"dynamical systems" and "erogdic theory" as well as many other
siblings in the more applied sciences.  Interesting and sometimes
useful stuff, but not really all that fundamental.  I agree with Prof.
Holmes that today nonlinear dynamics is more like a tool box of
techiques than a "real" theory.  Fun stuff, nevertheless, something
keeps pushing me to study nonlinear dyanmics not just because it is
fun, but also because It promises to be fundamental as well.

A much more visonary, but no less honest view, of nonlinear dynamics
has been articulated by Bob Gilmore.  I must confess that the
unpractical romantic in me finds Prof.  Gilmore's vision awfully
aluring.  Prof.  Gilmore's vision of nonlinear dynamics is strongly
shaped by his experience in studying Lie Groups and more recently
Singularity theory (aka Catastrophe Theory).  Bob's view is shaped by
his understanding of the historical continunity to be found in the the
work of Poincare, Lie, to say Arnold in our own day.  The fact that
Lie's method should arise when discussing nonlinear dynamics I find
quite natural.  In fact, if I would name the two most seminal works in
nonlinear dynamics, Poincare's New Methods of Celestical Mechanics
would obviously come first, but I believe Lie's notion of a continuous
group, and it role in unifying the up to then ad hoc methods for
solving differential equations, would rank an easy second.

I hope I am not inaccurately stating Prof.  Gilmore's point of view
when I say that when Bob Gilmore speaks of studies in nonlinear
dynamics he envisions a theory which is ulitmately as rich as Lie
Group theory, and which is the natural successor to singularity
theory.  Bob hints at this vision of nonlinear dynamics in his book on
Catstrophe theory when he writes:

 "Castrophe Theory is a mathematical program in much the same way that
Felix Klein's Erlangen Program is a mathematical program.  The Erlagen
Program attempts to classify geometries by classifying the
transformation group which leaves the theorems of the geometry
invariant.  Castrophe Theory attempts to study how the qualitiative
nature of solutions of equations depends on the parameters that appear
in the equations."

In short, Singularity theory is the general study and classification
of equilbrium dynamical systems --- at least according to Bob.

I think that Bob would say --- at least to a first approximation ---
that nonlinear dynamics is the general study and classificaton of
nonequilibrium (either automonous or forced) dynamical systems.  And
that this classification, at the present time, strongly depends on
dimension.  Thus we study the flows and maps in R^1, R^2, R^3, etc.
Nonlinear dyanmics is the next natural step after singularity theory,
and the theory of Lie groups should serve as a guide showing what this
classification theory should look like.  That is what, I think, Prof.
Gilmore thinks.

      My own belief is that nonlinear dynamics proper --- as opposed
to dynamical systems theory or applied mathematics, lies somewhere
between Holmes toolbox definition and Gilmore's Ergalen.  But it is
not necessary or perhaps even desirable for us to provide a specfic
definition now.

    Of course Bob is not alone in his belief, this is more or less the
original vision of Smale for dynamical systems theory.  I would modify
this statement in a lot of ways (for example nonlinear science is much
more practical, detailed, and pragmatic then dynamical systems
theory), but unlike Holmes view, this is a visonary statment.  That
much can not be denied.  In fact, Smale, before he discovered the
horseshoe, thought he had "solved" this problem, or at least he spent
some time trying to prove that generically dynamical systems in any
dimesion tended to gradient flow systems consisting of simple fixed
point attractors.

 I believe we now have several questions before us.  First, Is this a
resonable vision for what nonlinear dynamics is ultimately all about?
That is, does past research give us any reason to hope that we can
make some progess on this quest.  Second, what specific research
questions and programs should we follow for such a grand (hopefully
not gradiouse) vision.  Third, can we begin to guess at what the
practical consequences might result both in scientific understanding
and specific (say engineering applications) that would follow from
theoretical results in line with this vision.  And forth, are the
problems we hope to solve with break throughs in nonlinear science
better solved by other means --- that is what is our theoretical
competation, and why do we think we can do things any better.

     I will tell you what I think about some of these questions in the
reamaider of this talk, but my real hope is to hear what you all might
think about these things.  So instead of professing my point of view I
would rather set up a matrix for discussing these things.  Before I do
that though, let me say a word or two about what I think are the
competing methodolgies for solving nonlinear and complex problems and
why I think they (and not people working in nonlinear science) get
what research bucks there are to be had at present.

  In attempts to solve the nonlinear problems, equations, and systems,
that arise in science and enginnering, I think we can identify several
distinct "methodolgies" or frameworks for discussing and solving these
problems.  I would list these as:

Strong Computation

Fundamental Research into very specific problems

Complex systems

Strong Discrete School (Wolfram)

Intellgent Agent School, Computing as a metaphor for everything (SFI)

Nonlinear Dynamics

  Let me say a few words about each of these approaches.  Lets say we
want to design a space-plane capable of flying at Mach 50, or analyze
the strutural vibrations in a building or bridge, or understand the
dyamics of the interactions between material and electromagnetic field
inside a laser cavity, or predict the large features of the global
atmospheric and ocean flows.  In all these instances science can
provide us with a mathematical model, large sets of PDE's, ODE's, or
finite-element codes, which have a good chance of capturing and
mimicking important dynamical features of these phenomenon.

What I call the "strong computational" school is simply the belief
that a rather brute force approach to these problems, combined with
technical innovations in hardware and alogrithms, will provide
effective numerical simulation of these systems in the near and medium
term horizon, and that such simulations will provide "solutions" for
most of the problems one is interested in --- like designing a space
plane or predicting the next El-Nino event.  The strong computational
view has a lot going for it, not the least of which it is easy to
explain to people and it is easy to point at the rapid progress in
computers and algorithims in recent history.  I suspect that the
simplicity of this vision explains why the strong computational point
of view is so successful in funding terms.  I don't know how much has
been spent by NSF to set up and maintain the super-computer centers,
nor do I think they are necessarily a bad use of research funds ---
for certain classes of problems they provide the only possible
solution on the near term horizon.  But what I do raise as a questions
are, what would the benefits be of providing a similarly funded
local-workstation based computing power to researchers?  What problems
can we realistically expect to solve with this brute force approach?
And what are the inherent limits to such an approach?  I simply raise
these question now, and remind you of Hamming statment "computing
without out insight is ...", or more succintly put, "garbage in,
garbage out".  I am simply suggesting that there will always be a
healthy size of important problems that will always reqire more
insight to simulate, and to understand the simulations than the strong
computation school might have us to believe.

By fundamental research into specific problems I simply mean large and
small programs funded to solve a specific application.  This is the
lion share of funding at NSF and could range from Hidden Markov models
to do speech recognition to the Global Ocean Measurements program
(WOCIS?).  My only comment and observation here is that the benefits
of interdisplinary work are, and going to be far greater than we can
imagine --- this will certainly be one case where truth will be richer
than fiction.  I can not tell you how many times I have looked at,
say, a very specfic engineering problem and either 1) got a entirely
new and novel idea for approaching a much more general problem, the
germ of which comes from looking at the engineers solution, or 2)
after understanding the problem was able to immediately point to
relevant results in other fields which suggested new approaches to
solutions or explain why an approach tried again and again over the
years always fails.  My only point here is that great rewards are
waiting to be harvest from interdisplinary research.  This research is
already hard, but it is made impossilby hard by the current
academic/scientific structure.  This is a real leverage point I
believe, in that anything we can do to genuinely foster
interdisplinary work will pay us back many fold, and nonlinear
dynamics is at the forefront of such interdiscplinary research (much
the same way that science has been at the forefront of international
cooperation).  It's a point we can and should advertise about

The Complex Systems school of thought is by far the newest and most
radical departure from classical science and classical (smooth)
dynamical systems.  In many ways it does represent a profound pardigm
shift, but one which is undeveloped and untested.  I mentioned two
schools of thought here, the first (as advocated by Wolfram, for
instance) suggests that our current smooth dynamical pardigm for all
of science (from the Schrodger equation to global wheather models) is
a convention with a lot of analytical historical machinery behind it
and driving it.  Wolfram suggests that a perhaps more powerful pardigm
exists by completely discrete formulations of most physical processes,
and the only reason we don't have such a complete theory for such
discrete formulations is more of a historical accident then anything
else.  But once Wolfram book on complexity is published everything
will be clear (one way or the other).  I think a distinct school of
thought is represent by researchers at SFI.  Here Intellignet agents
and sophisticated computer programs are used as a metaphor for all
things complex.

 Compared to complex systems, which in either formulation seriously
considers rejecting our success over the last 300 years with smooth
dynammical systems in favor of a new "computational paridigm",
nonlinear dyanmics is a rather tamer and traditional school of thought
which arises from the arguments Poincare put forth for the complexity
of solutions arising from flows on smooth vector fields of
low-dimension over 100 years ago, and which are still as valid and
pertinent today.  Like madana's song material girl, nonlinear
dynamicst still believe we are "a material girl living in an analytic

I just mention these methodolgoies at this point to give them a name.
I do not mean to suggest that they are competative with one another
necssaryly for our hearts and minds (or dollars).  In fact, I see the
computational and nonlinear dynamics approaches as very complemnary,
so much so, that it would probably behove nonlinear dynamicist to
consider surfing on the ripples of the big waves of funding that
computational programs can generate.  Nonlinear dynamics should in the
short and medium term be able to deliver in the insight Department
both in developing alogrithms and interpreting data, and we should get
payed to do it.  Having a formulated vision, which in parts is easy to
communciate, would I think help immensly here in trying advocate what
we agree upon are the near and long terms benfits of research in
nonlinear dynamics.

OK.  Enough of my Bourbkiesqe rehtoric.  Let's try to now get down to
business and sketch out a frame work discussing the near and far
horizion for research in nonlinear science.

Let me try to sketch out for you a multidimensioal space I see where
nonlinear research lives.

(Sketch at black board)

On one axis I put the Time horizion for research --- today, 5 years,
10 years, 100 years --- near to far.

On another axis I draw the degrees of freedom, the dimension if you
like, of the problem.  By low dimensional I will mean effective
dimesions of say 1-10, with most of my talk focusing on what I know
about flows in 3 dimensions, or very low-dimesional systems which
result from "temporal" system where any additional spatial modes are
frozen out by the boundary conditions.  Next on the dimension axis I
would put systems of moderate degrees of freedom say 10-100 modes.
These systems typically have nontrival spatial structure and problems
in this regime are often refered to as spatial-temporal chaos.  One of
the main problems here would seem to be developing an effective
stardgey for separating and analyzing, that is factoring, the
"spatial" and "temporoal" modes.  Although no sure-fire method for
this factorization has been discovered yet, Bob Gilmore belives such a
factorization exists and has called the spatial modes of any nonlinear
factorization the "modalities", or nonlinear modes.  Nice name I think
since it suggests in my mind that any such factorization must encode
some temporal information as well as spatial structure.  Unlike linear
modes, modalities, I think, must capture the temporal recurrent
spatial structure of a solution compactly, thus they will not be
static objects like a strict linear mode.  Next up I would put
complicated systems for want of a better name, think of these as
systems with dimesion say from 10^3-10^10.  And after that I would put
"statistical" systems, with effective degress of freedom say greater
than 10^10.

On another axis we could put typical problems and questions.

On another axis we could put a description of the solution types.

On yet another axis we could put applications.

The last three axis I will dicuss in some detail for Flows in R^3.

On another axis we could put general scitific interest and cross
disciplinary revelvance.


  The construction of this "nonlinear problem space" is simply meant
to help provide a useful framework for discussion of what we currently
are and should be doing when we do nonlinear science.  I should say
that implicit in this space are two assumptions, (i) we are usually
dealing with closed systems (Global oceanic/atomospheric flows I would
generally consider a closed system, driven by a more or less peridioc
thermal forcing --- the sun; the brain I would consider an "open"
system and I think that perhaps the "complex" way of thinking might be
better framework to discuss such questions); and (ii) I am generally
thinking about systems which are at some level analytic, this just
reflects my prejudice as a physicist that, in the words of Smale that
the physical world is properly modeled by a:

"differentiable dynamical systems or equivalently the action
(differntiable) of a Lie Group G on a manifold M"

 Everyone has prejudices, and I am just trying to keep mine in the
open --- I defintely don't want a theory of everything, I would be
happy for the more humble (joke) task of understanding

"the global structure, ie., all of the orbits of M."

  In practice you will see I take quite a pragmatic attitude.  Just
understanding M = R^3 has kept me more than busy and happy over the
last ten years.

Well, at this point I would like to collapse the topic of this talk by
concentrating on filling in some of the elements of this nonlinear
problem space across the R^3 hyperplane.  After that I will sparsely
add elements to a few other points in this space away from the R^3

For the typical problems axis I would list any oscillator or resonator
in which the boundary conditions and/or dissipation only permit one
spatial degree of freedom.  There are many examples of such systems
including:  lasers whose oscillations are confined to one (TEM000)
mode; fluid experiments where the cell size = the box size; chemical
oscillators with very high dissipation (BZ); or any of a number of
electronic or mechanical oscillators or resonators.

      For applications I would mention the suggestion of the of use of
chaotic synchronization for secure communications, model verification,
process control and identificcation, nondesctrive testing, and
parameter estimation.

(Say more about these topics as specfic questions arise)

For an example problem to help illustrate this discussion I would like
you to consider the bouncing ball system.


In very generic terms the bouncing ball system and problems like it
present us with two (orthogonal) challenges:


1) For fixed parameter values, identify and classify the attractor,
and calculate important (invariant, and noninvariant) physical
quantities, (Cvitanovic --- cycle expansions (metric theory))

2) For different parameter values (or initial conditions), identify
the dynamical system over a wide range of parameters and identify and
understand significant invarant structures in the bifurcation diagram
(Gilmore --- Local and Global Normal forms (topological theory)).

  These two questions are complementary.  The first asks about the
invariant structure at fixed parameter values, and the second asks
about invariant structure across a range of parameters.

     I think it is not unfair to say that 25 years ago, to paraphrase
Arnold, the bouncing ball problem was beyond the capability of modern
science.  A few mathematicans may have be able to precisely formulate
the questions I have asked above, but most of the pragmatic procedures
of a physicst, or techniques of the pure mathematican, mentioned below
just did not exist.  The field has developed so much so that I believe
progress in nonlinear science in the last 25 years would make that
statement untrue today.  Specfically (and this list is not meant to be
exhaustive, it just reflects some topics I know something about) we
have seen definite progess in the last 15 years in these problems:

Discovery and suggestions of practical applications of chaotic

Complete topological theory of 1-Dim (Cont) Maps (Welington de Melo
and Sebastina van Strien), and results on 1-D (DisCont) Maps

Scaling function theory at selected points in parameter space

Outlines for a theory of the invariant structure and unfoldings 2-D
maps (3D flows) (Hall, Hansen, Cvitanovic)

Outline of a "normal form theory" for global bifurcations (Shilnikov,
Glendding, Sparrow, Tresser, Deng, Champneys, Collet, Takens, Palis

The unabmiguous detection of low-dimensional dynamical structure in
chaotic experimental time series, with applications to a wide range of
experimental systems (Packard, Takens, Ruelle, Santa Cruz, etc).

The identification, classification, analysis, modeling, and control of
very low-dimensional chaotic experimental time series (Maryland,NRL,
Spanno, Ditto, Roy, etc).

By hand calculation of some restricted Helium atom problems---
Quasiclassical Formalism (Witgen, Cvitanovic).


There is still much to be done.

I mention a few specific points now.

  For instance, it would be nice to have a complete and uniform theory
of global homoclinc/heteroclinc bifurcations and "normal forms" to go
with this theory.  This would be a lot of work, but a lot of the bits
are already in place, it would mainly consist of finding a
formalism/scheme to unify all the specific calculations done up to now
that get specific return maps resulting from given assumptions about
the local bifurcation struture and the global connection.  Actually, a
workshop bringing together say the 10 or 20 people working on these
types of problems might be a great help in working out a unified
formalism for global bifurcation theory in R^3.  Second, the purely
topological aspects of this structure must be distilled from the
specific normal forms.  Toby Hall's results on how to unfold a
horseshoe can serve as a model for what such results might look like.

Also, it seems that the periodic orbit formlism of cycle expansions
and orbit forcings should be able to be generalized from periodic
orbits to aperiodic (possibily) homoclinic orbits.  Toby Hall and I
are currently showing how to do this for horseshoe type maps.

And in terms of practical results, I believe we should be working
harder to apply our technqiques to identify, classify, and control
industrial process which are generating low-dimensional time series.
We really need a killer app --- and this is one place we should place
some bets.  I belive a lot can be gained here.  Many industrail
process are designed to be either an oscillator or resonator of
low-dimension, which begin to behave in a "bad" manner.  Such
industrial systems (we are currently working on analyzing bear wear in
drilling shafts, and casting using vibroformers) are much more
appropriate candidates for nonlinear time series analysis then are the
presumably high-dimesioanl and/or open systems like finanical markets
or the brain.

Oh, and getting back to Arnold's comment, I think that 2-degree of
freedom Hamiltonian systems are now at the boundary of what modern
mathematics can handle.  Advances here include Fomenko's
classification of ALL 2-dim integrable system.  Meyer's original
analysis (and subsequent advances) of generic bifurcations of such
Hamiltioan systems, as well as normal form reductions, numerical
explorations of phase space and the break up of invariant tori, and
most recently Politi's suggestion for how to put a generating
partition to do the symbolics for such systems.  For homogeneous
potentials we now have (Ziglin/Yoshadia) effective analytic tests for
integrablity/nonintegrablity of these Hamiltonians, the first modest
step toward answering one of the now classic problems in mathematical

The situation in R^3 looks pretty good, and this is one of the main
reasons why I feel optmistic about the future of nonlinear dynamics.
When I seriously began work on these questions more than 10 years ago
I really could not have imagined (i) that I would still be working
hard on such systems, and (ii) that I could honestly say that many of
the original questions that I (impresisely) asked I would now have
precise questions for and in many instances precise answers.  That is,
given a flow in R^3, I now have the analytic, numerical, and
experimental tools to get a good local and global understanding of
these things.  I am genuinely impressed and delight with this
progress, it is a modest begining, but it is also a solid one.

What are some of the specfic lessons we have learned from our study of
flows in R^3:

1) You must understand and quantify (encode) the toplogy of the
problem under study.  Symbolic dynamics is crucical, it our coordinate
system in a nonlinear space.

2) Current mathematical machinery is not well suited to many of the
questions we really want to ask --- we need some new mathematics.
Specfically we need to speak about the closness of dynmaical systems
and their solutions (invariant sets) in a quantitative way.
Toplogical conjuacy is the best we can do so far, but we would really
like a "metric" for such problems.  A little thought though shows that
a proper metric is not a sensible notion for such questions ---- what
is the mathemtically precise but sensible notion?

3) Even with out the right tools, we can still push forward.  For
example, we are currenlty using a Karhunen-Love decompition to get a
handle on spatial-temporal data, to get a handle on the "modalities",
this is really not the right tool, but it can be useful never the
less.  So the lesson is, do what you can with the tools you have and
perhaps in the process we will learn enough to craft better tools.


Leaving R^3 what other (sparse) additions can we make to our nonlinear
problems matrix?

I think a lot critical problems for the future of mankind will fall in
the moderate (10^1-10^3) dimesion class --- the class of problems
marked by modalities.  Examples of problems I suspect to lie in this
dimesion range would be long term climate models, large scale features
of ocean/atomospheric patterns (zones, El-Nino), pattern formation in
a wide host of chemical and biological oscillators and open flow
systems.  I think that important tools in understanding and analyzing
these systems will be based on a dynamical systems perspective,
although the particlar technqiues may or may not resemble the ones we
have developed for low dimesional flows.  The detection of symmetrices
(Gollubiski/Steward), for instance, I think will be critical for such
problems, because if properly detected and explotied they can greatly
reduce the effective dimesion of the soluton space.  I also think
problems orgianlly formulated to look like they are very large
dimensioal (POP models of ocean flow for example) will turn out to be
analzeable by a moderate number of degrees of freedom, and this will
be an important advance, but I suspect it will be forced onto those
believing in the strong theory of computation becuase in 50 years time
they still won't have answers that they promised for now (it will be
like the history of AI).  This is not to say that we will nor gain an
enormous amount by increased computation power, but in some instances
it just won't give us the answers we really need.  At the same time,
we are going to be over whelmed by data from the Mission Planet Earth
Initative, and again effective "compression" of all this informtion
will hinge on finding low dimensional ways to actually compress and
understand the data --- we are going to need insight, and lots and
lots of it, and at the current time the only rational path I can see
for getting this insight is a dynamical systems perspective.  It won't
be easy, but I think we can and will make steady progress.

Who know's, I will go out on a limb here and predict that I just might
understand flows in R^4 by my 60th birthday?


Many of the thoughts expressed here arose from extensive dicussions
with Bob Gilmore, and I hope my filtering of them has not increased
the signal to noise too much.  I also thank Lou Pecora and the Naval
Research Labs who organized a recent workshop on the future prospects
for researh in nonlinear science.