It isn’t all over; everything has not been invented; the human adventure is just beginning.
― Gene Roddenberry
Listening to the dialog on modeling and simulation is so depressing. There seems to be an assumption implicit to every discussion that all we need to do to unleash predictivesimulation is build the next generation of computers. The proposition is so shallow on the face of it as to be utterly laughable. Except no one is laughing, the programs are predicated on it. The whole mentality is damaging because it intrinsically limits our thinking about how to balance the various elements needed for progress. We see a lack of the sort of approach that can lead to progress with experimental work starved of funding and focus without the needed mathematical modeling effort necessary for utility. Actual applied mathematics has become a veritable endangered species only seen rarely in the wild.
Often a sign of expertise is noticing what doesn’t happen.
― Malcolm Gladwell
One of the really annoying aspects of the hype around computing these days is the lack of practical and pragmatic perspective on what might constitute progress. Among the topics revolving around modeling and simulation practice is the pervasive need for singularities of various types in realistic calculations of practical significance. Much of the dialog and dynamic technically seems to completely avoid the issue and act as if it isn’t a driving concern. The reality is that singularities of various forms and functions are an ever-present aspect of realistic problems and their mediation is an absolutely essential for modeling and simulation’s impact to be fully felt. We still have serious issues because of our somewhat delusional dialog on singularities.
At a fundamental level we can state that singularities don’t exist in nature, but very small or thin structures do whose details don’t matter for large scale phenomena. Thus singularities are a mathematical feature of models for large scale behavior that ignore small scale details. As such when we talk about the behavior of singularities, we are really just looking at models, and asking whether the model’s behavior is good. The important aspect of the things we call singularities is their impact on the large scale and the capacity to do useful things without looking at the small-scale details. Much, if not all of the current drive for computational power is focused on brute force submission of the small-scale details. This approach fails to ignite the sort of deep understanding that a model, which ignoring the small scales requires. Such understanding is the real role of science, not simply overwhelming things with technology.
The role of genius is not to complicate the simple, but to simplify the complicated.
― Criss Jami
The important this to capture is the universality of the small scale’s impact on the large scale. It is closely and intimately related to ideas around the role of stochastic, random structures and models for average behavior. One of the key things to really straighten out is the nature of the question we are asking the model to answer. If the question isn’t clearly articulated, the model will provide deceptive answers that will send scientists and engineers in the wrong direction. Getting this model to question dynamic sorted out is far more important to the success of modeling and simulation than any advance in computing power. It is also completely and utterly off the radar of the modern research agenda. I worry that the present focus will produce damage to the forces of progress that may take decades to undue.
A key place where singularities regularly show up is representations of geometry. It is really useful to represent things with sharp corners and rapid transitions geometrically. Our ability to simulate anything engineered would suffer immensely is we had to compute the detailed smooth parts of geometry. In many cases the detail is then computed with a sort of subgrid model, like surface roughness to represent the impact of the true non-idealized geometry. This is a key example of the treatment of such details as being almost entirely physic’s domain specific. There is not a systematic view of this across fields. The same sort of effect shows up when we marry parts together with the same or different materials.
An expert is someone who knows some of the worst mistakes that can be made in his subject, and how to avoid them.
― Werner Heisenberg
Again the details are immense, the simplification is an absolute necessity. The question that looms over all these discussion is the availability of a mathematical theory that allows the small scale to be ignored, which explains physical phenomena. This would imply a structure for the regularized singularity, and a recipe for successful simulation. For geometric singularities any theory is completely ad hoc and largely missing. Any such theory needs detailed and focused experimental confirmation and attention. As things work today, the basic structure is missing and is relegated to being applied in a domain science manner. We find that this is strong in fluid dynamics, and perhaps plasma physics, but almost absent in many other fields like solid mechanics, the utility of modeling and simulation suffers mightily from this.
If there is any place where singularities are dealt with systematically and properly it is fluid mechanics. Even in fluid mechanics there is a frighteningly large amount of missing territory most acutely in turbulence. The place where things really work is shock waves and we have some very bright people to thank for the order. We can calculate an immense amount of physical phenomena where shock waves are important while ignoring a tremendous amount of detail. All that matter is for the calculation to provide the appropriate integral content of dissipation from the shock wave, and the calculation is wonderfully stable and physical. It is almost never necessary and almost certainly wasteful to compute the full gory details of a shock wave.
Fluid mechanics has many nuances and details with important applications. The mathematical structure of fluids is remarkably well in hand. Boundary layer theory is another monument where our understanding is well defined. It isn’t quite as profoundly satisfying as shocks, but we can do a lot of wonderful things. Many important technological items are well defined and engineered with the able assistance of boundary layer theory. We have a great deal of faith in this knowledge and the understanding of what will happen. The state is better than it is problematic. As boundary layers get more and more exciting they lead to a place where problems abound, the problems that appear when a flow becomes turbulent. All of a sudden the structure becomes much more difficult and prediction with deep understanding starts to elude us.
The same can’t be said by and large for turbulence. We don’t understand it very well at all. We have a lot of empirical modeling and convention wisdom that allows useful science and engineering to proceed, but an understanding like we have for shock waves eludes us. It is so elusive that we have a prize (the Clay prize) focused on providing a deep understanding of the mathematical physics of its dynamics. The problem is that the physics strongly implies that the behavior of the governing equations (incompressible Navier-Stokes) admits a singularity, yet the equations don’t seem to. Such a fundamental incongruence is limiting our ability to progress. I believe the issue is the nature of the governing equations and a need to change this model away from incompressibility, which is a useful and unphysical approximation, not a fundamental physical law. In spite of all the problems, the state of affairs in turbulence is remarkably good compared with solid mechanics.
Another discontinuous behavior of great importance in practical matters are material interfaces. Again these interfaces are never truly singular in nature, but it is essential for utility to represent them that way. The capacity to use such a simple representation is challenged by a lot of things such a chemistry. More and more physics challenge the ability to use the singular representation without empirical and heavy-handed modeling. The ability to use well-defined mathematical models as opposed to ad hoc modeling implies essential understanding that belies a science that is compelling. The better the equations, the better the understanding, which is the essence of science that should provide us faith in its findings.
An example of lower mathematical maturity can be seen in the field of solid mechanics. In solids, the mathematical theory is stunted by comparison to fluids. A clear part of the issue is the approach taken by the fathers of the field in not providing a clear path for combined analytical-numerical analysis as fluids had. The result of this is a numerical background that is completely left adrift of the analytical structure of the equations. In essence the only option is to fully resolve everything in the governing equations. No structural and systematic explanation exists for the key singularities in material, which is absolutely vital for computational utility. In a nutshell the notion of the regularized singularity so powerful in fluid mechanics is foreign. This has a dramatically negative impact on the capacity of modeling and simulation to have a maximal impact.
All of these principles apply quite well to a host of other fields. In my work the areas of radiation transport and plasma physics. The merging of mathematics and physical understanding in these areas is better than solid mechanics, but not as advanced as fluid mechanics. In many respects the theories holding sway in these fields have profitably borrowed from fluid mechanics, but not to the extent necessary for a thoroughly vetted mathematical-numerical modeling framework needed for ultimate utility. Both fields suffer from immense complexity and the mathematical modeling tries to steer understanding, but ultimately various factors are holding the field back. Not the least of these is an prevailing undercurrent and intent in modeling for the World to be a well-oiled machine prone to be precisely determined.
I would posit that one of the key aspects holding fields back from progress toward a fully utilitarian capability is the death grip that Newtonian-style determinism has upon our models for the World. Its stranglehold on the philosophy of solid mechanical modeling is nearly fatal and retards progress like a proverbial anchor. To the extent that it governs our understanding in other fields (i.e., plasma physics, turbulence,…), progress is harmed. In any practical sense the World is not deterministic and modeling it as such has limited if not, negative utility. It is time to release this concept as being a useful blueprint for understanding. A far more pragmatic and useful path is to focus much greater energy on understanding the degree of unpredictability inherent in physical phenomena.
The key to making everything work is an artful combination of physical understanding with a mathematical structure. The capacity of mathematics to explain and predict nature is profound and unremittingly powerful. In the case of the singularity it is essential for useful, faithful simulations that we may put confidence in. Moreover the proper mathematical structure can alleviate the need for ad hoc mechanisms, which naturally produce less confidence and lower utility. Even where the mathematics seemingly exists like incompressible flow and turbulence, the lack of a tidy theory that fails to reproduce certain properties limits progress in profound ways. When the mathematics is even more limited and does not provide a structural explanation for what is seen like in fracture and failure in fluids, the simulations become untethered and progress is shuttered by the gaps.
I suppose my real message is that the mathematical-numerical modeling book is hardly closed and complete. It represents very real work that is needed for progress. The current approach to modeling and simulation dutifully ignores this, and produces a narrative that simply presents the value proposition that all that is needed is a faster computer. A faster computer while useful and beneficial to science is not the long pole in the tent insofar as improving the capacity of mathematical-numerical modeling to become more predictive. Indeed the long pole in the tent may well be changing the narrative about the objectives from prediction back to fundamental understanding.
The title of the post is a tongue and cheek homage to the line from the Big Lebowski, a Coen Brothers masterpiece. Like the dude in the movie, a singularity is the essence of coolness and ease of use.
If you want something new, you have to stop doing something old
― Peter F. Drucker