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 Internet: firstname.lastname@example.org http://cnls-www.lanl.gov/nbt/intro.html Thursday 2PM, 22 June 1995 HP-LABS Bristol, UK. BRIMS---Basic Research in the Mathematical Sciences Abstract: 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 questions. 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 ourselfs. 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 world." 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. Etc. 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 problems. 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. (SHOW DEMO) In very generic terms the bouncing ball system and problems like it present us with two (orthogonal) challenges: (SHOW WEB PAGE) 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 synchronization. Complete topological theory of 1-Dim (Cont) Maps (Welington de Melo and Sebastina van Strien), and results on 1-D (DisCont) Maps (Hubbard/Sparrow). Scaling function theory at selected points in parameter space (Feigenbaum/Sullivan). 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 etc). 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). etc 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 physics. 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. (SHOW MOVIES) 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? Acknolwelgements: 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.