Comments on "Complexity and the Future of Science"

• Background
• The "New" Science of Complex Systems, Is it more than soup yet?
• Self-organization, theories of
• My theory's bigger than your theory
• Theories of Future Theories
• Is it complex? Or is it dynamics?
• Struggling against the tide, in good company
• Future Prospectus
• Soup into Nuts

Wednesday 17 January 1996

Dear Colleagues,

A week or so ago Melanie Mitchell posted a copy of her essay Complexity and the Future of Science, an Op-Ed piece that was solicited by and will appear in Scientific American (SciAm). The posting was sent to this mailing list --- researchers@santafe.edu, which comprises over 400 SFI-affiliated scientists and other institute associates. Due to the wide initial public distribution and the eventual national exposure, it seems natural to air several concerns I have about Melanie's essay in this same electronic forum. If these particular concerns are not of interest to you, I hope that you will at least see how the essay brings up a number of issues that bear on future research in complex systems and SFI's public reception and its scientific reputation. And if these are not of interest to you, I would hope that at a minimum my recounting of an alternative view of this general area is informative.

--- Background
(return to Contents)

A little historical context will be helpful. Melanie's piece is a response to the SciAm June 1995 staff article written by John Horgan. As many know, that article was critical of research in a number of newer fields ("complexity", dynamical systems, catastrophe theory, ...). It was also unsparing in its criticism of SFI and a few SFI researchers. Notably, the SciAm editors considered the criticisms important enough to provide a front-page lead-in "Is Complexity a Sham?"

A number of friends of SFI and of research in complex systems responded with letters to the SciAm editor critical of Horgan's article. As far as I know, of these only Mike Simmons's letter appeared, greatly compressed, in a later SciAm issue. Following Mike's letter Edward O. Wilson's letter was excerpted in a single sentence that lauded Horgan's article as "investigative reporting". Point, counterpoint.

Curiously, one recurring theme in the original letters to the editor, especially those posted to sfi-discuss@santafe.edu, was to call into question the very quality of Horgan's investigations. Indeed, what the SciAm editor left out of Mike's letter was a brief listing of SFI's research contributions. That is, what was left out was exactly the sort of content needed to counter Horgan's editorial bias. Melanie's original letter to the editor responded in a similar vein, pointing out that Horgan had focused on a very few individuals to the exclusion of many, many other researchers. My letter to the editor, available in the sfi-discuss archive, rebutted Horgan's dismissal of incontrovertible progress in dynamical systems theory and experimental results in nonlinear science over the last two decades.

Whatever we choose to group under the rubric of "complex systems", dynamical systems and nonlinear science have a large and unassailable history of mathematical development and experimental demonstration. Thus, in misrepresenting these areas, it was clear that Horgan simply hadn't met the most basic investigative requirements.

Seen in this light, it's not clear that Horgan's article deserves a response. The main problem with such a strategy comes from the fact that Horgan had access to a national audience for his views, access rarely available to most researchers in complex systems. Even notions with a vanishingly small content can have substantial influence when amplified so widely.

--- The "New" Science of Complex Systems, Is it more than soup yet?
(return to Contents)

Given the debate fueled by Horgan's article, an obvious question is, Does "Complexity and the Future of Science" (CFS) adequately respond to criticisms of research in complex systems and of SFI? Does it fairly represent past results and the current state of our understanding of complex systems? I think the answers are important. After all, the SciAm editors have given a member of our community the chance to respond in kind in the same national forum.

There are several ways in which the essay successfully responds. For example, it's a relief to see measured argumentation, a lack of stridency, and thoughtful and constructive suggestions. (In contrast, Horgan's phraseology, selection of facts, and quotation out of context, truly set new minimum standards for reportage in SciAm.)

Unfortunately, CFS exhibits some of the same shortcomings as found in Horgan's article, shortcomings to which my letter to the editor was addressed. That is, my main concerns are an inadequate representation of (i) historical context and (ii) our current understanding of complex systems. The net result is that CFS falls short of a contentful reply to Horgan's editorializing. Along the way, it perpetuates a similar unbalanced view about research in self-organization, dynamical systems, and even complex systems.

To be more specific, let me explain what in CFS led me to these these conclusions.

--- Self-organization, theories of
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The essay in part is a review of arguments for an interest in "self-organization" and for research on "complex systems"; that is, for studying how interacting components cooperate to produce large-scale coordinated structures. The review, however, ignores a long history and much progress in complex systems, so defined. Consider, for example, statistical mechanics, dynamical systems, and the study of pattern formation.

• One of the central goals of statistical mechanics is to explain the emergence of large-scale, macroscopic thermodynamic properties from low-level entities, such as atoms, molecules, and now even artificial neurons. The theories of phase transitions and especially of critical phenomena provide probably the widest range of concrete results on cooperative systems. It's no wonder that the methods, concepts, and results in statistical mechanics are powerful descriptive metaphors for researchers in complex systems. Occassionally, these metaphors are rendered into hard results on complex systems --- such as the adaptation of renormalization group methods to show that qualitatively higher levels of computation appear at phase transitions than away from them.
• Dynamical systems explains the emergence of the apparent randomness of deterministic chaos as the product of the moment-to-moment application of elemental, but nonlinear, operations. It also explains, via bifurcation and singularity theories, how qualitatively new behavior and structure can arise with the smooth variation in experimental controls. Dynamical systems theory and its applications have been pursued for decades now. So it's no surprise that the basic theory and results are available in over 30 textbooks (my estimate a few years ago).
• The field of pattern formation, in a sense, splits the difference between statistical mechanics and dynamical systems theory. It focuses on systems with many components, like statistical mechanics, but attempts a level of detailed analysis of underlying mechanisms, as done in dynamical systems theory. Its mandate is to explain the emergence of patterns in spatial processes. Pattern formation theory has a very long history that includes Alan Turing's work in the 1950s on morphogenesis and that of Prigogine and Nicolis on dissipative structures and of Haken on the slaving principle in the 1970's, and, most recently, the mathematical articulation of the original methods under the heading of center manifold theory.

Pattern formation theory and experiment have experienced a tremendous growth over just the last decade. And it's been quite successful. The product of this effort is a large body of results on patterns at the onset of turbulence (in a range of fluid flows), on spiral waves and Turing patterns in chemical oscillations, on patterns of cooperation and competition in spatially-distributed animal and plant populations, on the formation and role of animal coloration, and on synchronization and the function of electrical activity in the brain, to name but a very few of the natural phenomena that have been analyzed. In fact, the study of pattern formation is now pretty much a standard subfield of nonlinear physics. One of my favorite textbooks is that by Paul Manneville --- Dissipative structures and weak turbulence, Academic Press, (1990).

It's very important to emphasize that many of the basic concepts and results in statistical mechanics, dynamical systems, and pattern formation apply across many disciplines. They're found not just in physics, but are used from biology to computer engineering. Am I arguing for a theory of everything here? No, this generality just reflects the nature of the underlying mathematics and physics. Am I making unjustified and vague generalizations about some future desired theory? No, not at all. As just one recent example, I would urge you to read the wonderful papers by Budrene and Berg on pattern formation in bacterial colonies (Nature vol. 376 (1995) 49-53).

So much for explicating some of the intellectual and historical context for complex systems and self-organization. Despite all this work, in CFS's review of "complex systems" we find statements like:

This problem [of self-organization] remains almost completely unsolved.

It makes me so happy. To be at the beginning again ...

Such a theory --- one that explains and predicts aspects of "emergent phenomena" across disciplines --- is, I believe, vital to the future of science, which is, from the point of view of complexity, not at its end but at its beginning.

There are professional, rhetorical, and scientific consequences of the essay's stance. The first is the very real possibility of alienating many researchers in phase transitions, dynamical systems, and pattern formation with such sweeping negative summaries and with the implied novelty of the "new" view the essay proposes. A second consequence is that, even when taken on its own terms as a response to Horgan, the argument for complex system studies is greatly weakened. By painting a picture of complex systems that lacks historical context the essay can argue that a foundational theory is only "plausible". In fact, by the essay's conclusion we find hedge phrases like "I believe" when it turns to prospects for the future. The power (or failure) of argument by personal opinion turns on the readers' respect for and knowledge of the writer's professional experience with the issues at hand. It's often better to argue by sticking to what is known.

As the above list of fields documents a foundational theory is more than plausible. Many pieces are already well-understood and those pieces deserve credit. Independent of SFI's integrative efforts and that of individuals to reformulate the task at hand, there's a tremendous amount of scientific momentum behind the issues that make up what is so recently labelled "complex systems". Spending the time to responsibly formulate the latter's connections to existing work would reap large benefits.

One rejoinder, often heard around SFI, to this appeal for inclusion is to point out that these pieces miss something. Indeed, they do. But this argument strikes me as largely content-free to the extent that it itself can only refer to possible futures. To the extent that it ignores recent results that address the missing pieces (see below), it is simply wrong. My suggestion is to stick with concrete results and then use them, possibly by analogy, to argue for an important and bountiful future for a science of complex systems. Indeed, the extrapolation from a long and colorful history in mathematics and nonlinear physics and from recent results is easy to make. The prospects are excellent for complex systems.

--- My theory's bigger than your theory
(return to Contents)

There is a recurring issue in Horgan's and in Melanie's stories about what complex systems presumes to be. They both address some vague notion of a "theory of everything" or of explaining phenomena "across disciplines". In CFS this issue is introduced as follows.

It is plausible that the problem of self-organization is ... the same in all disciplines ...

Nonetheless, an interesting mathematical irony does come to mind and it just so happens to illuminate the issue of sticking to content that was just raised.

Despite the lack of utility in debating theories of everything, there are important mathematical developments which show that certain types of universality across phenomena can be consistently and usefully formulated. Furthermore, to a certain extent these sorts of commonality across phenomena are to be expected. Let me mention two notions of universality that already exist in the theory of phase transitions and in dynamical systems.

• In the theory of phase transitions, it's been appreciated for over thirty years, if not longer, that many differences in detail do not matter when materials change their structure as some external parameter -- e.g. temperature, magnetic field, ... -- is varied. There are, in fact, various universality classes of substances that undergo essentially the same change in macroscopic structure. These classes are parametrized by one or several "critical exponents" that describe how physical observables vary in going through a phase transition.
• The theory of dynamical systems is nothing, if it's not a geometric view of time or, more precisely, of temporal behavior. We view a phenomenon's unfolding in time in a space of states and we ask what structures in that space guide and constrain the behavior. If two systems share the same state space structures then we say they have the same behavior. Mathematically speaking, if the set of states in two different systems can be warped into each other -- i.e. the sets are topologically equivalent -- those two systems are, for all intents and purposes, the same.
  To put this in a more picturesque way, take a dripping faucet, on the one hand, and a superconducting Josephson junction, on the other. In what useful way can we say these systems are the same? At first blush they are entirely different. One is human scale, is at room temperature, concerns the flow and breaking of a fluid, and is described in terms of classical physics. The other is microscopic, occurs near absolute zero, concerns the flow of electrons, and requires the theory of quantum mechanical tunnelling. We measure the mass of water drops in one and quantum phase via voltages in the other. But it turns out that both systems exhibit the period-doubling route to chaos. And as such, for a wide range of experimental conditions, they have topologically equivalent state sets or "attractors". In this sense their behavior is the same. And, more to the point here, the theory of the period-doubling route to chaos is the universal theory for both (and a good many other systems in physics, chemistry, and biology).

To the extent that a body of concepts and methods or a particular theory describes properties of materially different systems, then they are candidates for universal theories. Equally important in such a setting, we understand in what manner they are general, since we know the type of equivalence that underlies them.

To sum up, it strikes me as an ironic twist that debates on theories of everything miss good evidence that much recent work in mathematics and nonlinear physics suggests broad applicability of theories to different phenomena and to different disciplines. On the one hand, I find the dismissal in CFS of "theories of everything" too facile. On the other hand, I find CFS's hope for transdisciplinary theories uninformed. While theories of everything are not interesting, universality has been and will continue to be a key aspect of complex systems. Without it each and every complex system would be a discipline unto itself and the very enterprise of scientific explanation doomed from the start.

(Actually, there is one additional type of universality that can be observed in some studies of "complex systems". This is "universality though ignorance". To the extent that one is ignorant of the details and structure of two different problems or fields, they can appear similar.)

--- Theories of Future Theories
(return to Contents)

Okay, so "theories of everything" are at best over-conceived. But then what are we to think of the attempt to make sweeping comments on and proposals for the "future of science"? This is truly bold. One finds in CFS statements like

the phenomenon of self-organization ... is (to my mind at least) the central problem in biology, economics, and society ... [emphasis original to CFS]

such a theory .. is vital to the future of science

The presumption to comment so boldly and broadly is, sad to say, a recurring one in some works associated with SFI. The popular books by Levy, Leuwen, and Waldrop and even some SFI proceedings volumes and faculty books are peppered with this hubris. The problem is that in many of these cases it is a hubris of accomplishment that far outstrips concrete results, theoretical foundations, and professional experience and ethics.

--- Is it complex? Or is it dynamics?
(return to Contents)

CFS misidentifies the central problems as "complex systems", when in fact a good deal of what is called for already exists in the theory of dynamical systems.

The issue, therefore, is not whether we should argue about how to label a new conglomeration of fields. Rather the issue is how to adapt and extend dynamical systems theory to new classes of processes of relevance to wider and wider ranges of phenomena.

The same is true of discrete computation theory. Computation theory is useful to natural science to the extent that it provides a framework for quantifying structure. But it desparately needs to be extended to account for computation in continuous, stochastic, and spatial systems, for example.

--- Struggling against the tide, in good company
(return to Contents)

Much of the argument CFS makes for "complex systems" has already been made in the dynamical systems literature. In particular, when we read about the historical development in

The complex systems movement was born of a frustration over the specialization and isolation of scientific disciplines ...

--- Future Prospectus
(return to Contents)

The essay ends with a proposal for a theory of complex systems.

... I do believe (and am actively pursuing) the possibility of a theory that explains the emergence of high-level information processing structures from low-level interacting components, ....

Both impressions are wrong. Such a theory is not a future possibility; it is a reality. It is being actively and successfully used in a collaboration with Melanie and other SFI colleagues to understand how a simple evolutionary process interacts with a pattern forming system to perform spatial computations. The theory has been the main research focus for over a half-dozen years of several of my students and post-docs and myself. It provides both a mathematical foundation for a structural "complexity" and constructive methods to detect when "high-level information processing structures" arise from the interaction of low-level components. The theory has been successfully adapted to chaotic dynamical systems, hidden Markov models, cellular automata, and, most recently, spin systems. Four Ph.D. dissertations have been produced; two more are on the way.

For reference, much of CFS's constructive proposal for the "future of science", including its chosen vocabulary, can be found in the papers The Calculi of Emergence: Computation, Dynamics, and Induction** and Is Anything Ever New? Considering Emergence.** Much of the above commentary can also be found there.

Aside from the obvious difficulty I have with the essay's presentation of my student's and my work, it's clear that the essay as a response to Horgan is weakened again by the same sort of omission that plagues the essay's earlier arguments.

--- Soup into Nuts
(return to Contents)

In conclusion, "Complexity and the Future of Science" errs in a manner very similar to Horgan's article: a lack of appreciation of existing work. In particular, the portrayal of "complex systems" and self-organization does a disservice most particularly to dynamical systems, theory and experiment. When compared to the body of extant work, the essay makes a very weak case for complex systems and gives an impression of SFI and its faculty as being insular.

A corrective suggestion is immediate. The essay could be made substantially stronger and more contentful if connections and citation to the long history of research in self-organization and dynamical systems are made. Despite it's length I hope the preceding critique provides enough detail that it's clear how to do so.

Let me close by emphasizing that I believe an Op-Ed piece can be written, fully respecting the length constraints, that fairly, convincingly, and constructively argues for complex systems. I wouldn't be working in this area nor would I have taken the effort to response to CFS, if I wasn't enthusiastic about our making progress on the very difficult problems that comprise "complex systems".

Let me know what you think. May I suggest that any follow-up discussion be posted to sfi-discuss@santafe.edu?

Onwards,

Jim

James P. Crutchfield

Research Physicist_______________Research Professor
Physics Department______________Santa Fe Institute
University of California____________1399 Hyde Park Road
Berkeley, California 94720_________Santa Fe, New Mexico 87501

173 Birge Hall
chaos@gojira.berkeley.edu_________jpc@santafe.edu
Office: 510-642-1287_____________505-984-8800
FAX: 510-643-8497______________505-982-0565

http://www.santafe.edu/~jpc.

**These papers are available through the above web site.