Donald Knuth -“If you find that you’re spending almost all your time on theory, start turning some attention to practical things; it will improve your theories. If you find that you’re spending almost all your time on practice, start turning some attention to theoretical things; it will improve your practice.”
This week I visited Chicago for the 2014 SIAM Annual Meeting (Society for Industrial and Applied Mathematics). It was held at the Palmer House, which is absolutely stunning venue swimming in old-fashioned style and grandeur. It is right around the corner from Millennium Park, which is one of the greatest Urban green spaces in existence, which itself is across the street from the Art Institute. What an inspiring setting to hold a meeting. Chicago itself is one of the great American cities with a vibrant downtown and numerous World-class sites.
The meeting included a lot of powerful content and persuasive applications of applied mathematics. Still some of the necessary gravity for the work seems to be missing from the overall dialog with most of the research missing the cutting edge of reality. There just seems to be a general lack of vitality and importance to the overall scientific enterprise, and applied mathematics is suffering likewise. This isn’t merely the issue of funding, which is relatively dismal, but overall direction and priority. In total, we aren’t asking nearly enough from science, and mathematics is no different. The fear of failure is keeping us from collectively attacking society’s most important problems. The distressing part of all of this is the importance and power of applied mathematics and the rigor it brings to science as a whole. We desperately need some vision moving forward.
The importance of applied mathematics to the general scientific enterprise should not be in doubt, but it is. I sense a malaise in the entire scientific field stemming from the overall lack of long-term perspective for the Nation as a whole. Is the lack of vitality specific to this field, or a general description of research?
I think it is useful to examine how applied mathematics can be an important force for order, confidence and rigor in science. Indeed applied mathematics can be a powerful force to aid the practice of science. For example there is the compelling example of compressed sensing (told in the Wired article http://www.wired.com/2010/02/ff_algorithm/). The notion that the L1 norm had magical properties to help unveil the underlying sparsity in objects was an old observation, but not until mathematical rigor was put in place to underpin this observation did the practice take off. There is no doubt that the entire field exploded in interest when the work of Candes, Tao and Donoho put a rigorous face on the magical practice of regularizing a problem with the L1 norm. It shouldn’t be under-estimated that the idea came at the right time; this is a time when we are swimming in data from an increasing array of sources, and compressed sensing conceptually provides a powerful tool for dealing with this. At the same time, the lack of rigor limited the interest in the technique prior to 2004 or 2005.
One of the more persuasive cases where applied mathematics has provided a killer theory is the work of Peter Lax on hyperbolic conservation laws. He laid the groundwork for stunning progress in modeling and simulating with confidence and rigor. There are other examples such as the mathematical order and confidence of the total variation diminishing theory of Harten to power the penetration of high-resolution methods into broad usage for solving hyperbolic PDEs. Another example is the relative power and confidence brought to the solution of ordinary differential equations, or numerical linear algebra by the mathematical rigor underlying the development of software. These are examples where the presence of applied mathematics makes a consequential and significant difference in the delivery of results with confidence and rigor. Each of these is an example of how mathematics can unleash a capability in truly “game-changing” ways. A real concern is why this isn’t happening more broadly or in targeted manner.
I started the week with a tweet of Richard Hamming’s famous quote – “The purpose of computing is insight, not numbers.” During one of the highlight talks of the meeting we received a modification of that maxim by the lecturer Leslie Greengard,
“The purpose of computing is to get the right answer”.
A deeper question with an uncertainty quantification spin would be “which right answer?” My tweet in response to Greengard then said
“The purpose of computing is to solve more problems than you create.”
This entire dialog is the real topic of the post. Another important take was by Joseph Teran on scientific computing in special effects for movies. Part of what sat wrong with me was the notion that looking right becomes equivalent to being right. On the other hand the perception and vision of something like turbulent fluid flow shouldn’t be underestimated. If it looks right there is probably something systematic lying beneath the superficial layer of entertainment. The fact that the standard for turbulence modeling for science and movies might be so very different should be startling. Ideally the two shouldn’t be that far apart. Do special effects have something to teach us? Or something worthy of explanation? I think these questions make mathematicians very uncomfortable.
If it makes you uncomfortable, it might be a good or important thing to ask. That uncomfortable question might have a deep answer that is worth attacking. I might prefer to project this entire dialog into the broader space of business practice and advice. This might seem counter-intuitive, but the broader societal milieu today is driven by business.
“Don’t find customers for your products, find products for your customers.” ― Seth Godin
One of the biggest problems in the area where I work is the maturity of the field. People simply don’t think about what the entire enterprise is for. Computational simulation and modeling is about using a powerful tool to solve problems. The computer allows certain problem solving approaches to be used that aren’t possible with out it, but the problem solving is the central aspect. I believe that the fundamental utility of modeling and simulation is being systematically taken for granted. The centrality of the problem being solved has been lost and replaced by simpler, but far less noble pursuits. The pursuit of computational power has become a fanatical desire that has swallowed the original intent. Those engaging in this pursuit have generally good intentions, but lack the well-rounded perspective on how to achieve success. For example, the computer is only one small piece of the toolbox and to use a mathematical term, necessary, but gloriously insufficient.
Currently the public policy is predicated upon the notion that a bigger faster computer provides an unambiguously better solution. Closely related to this notion is a technical term in computational modeling and mathematics known as convergence. The model converges or approaches a solution as more computational resource is applied. If you do everything right this will happen, but as problems become more complex you have to do a lot of things right. The problem is that we don’t have the required physical or mathematical knowledge to have the expectation of this in many cases. These are the very cases that we use to justify the purchase of new computers.
The guarantee of convergence ought to be at the very heart of where applied mathematics is striving; yet the community as a whole seems to be shying away from the really difficult questions. Today too much applied mathematics focuses upon simple model equations that are well behaved mathematically, but only capture cartoon aspects of the real problems facing society. Over the past several decades focused efforts on attacking these real problems have retreated. This retreat is part of the overall base of fear of failure in research. Despite the importance of these systems, we are not pushing the boundaries of knowledge to envelop them with better understanding. Instead we spend effort redoubling our efforts to understand simple model equations. This lack of focus on real problems is one of the deepest and most troubling aspects of the current applied mathematics community.
We have evolved to the point in computational modeling and simulation where today we don’t actually solve problems any more. We have developed useful abstractions that have taken the place of the actual problem solving. In a deep sense we now solve cartoonish versions of actual problems. These cartoons allow the different sub-fields to work independently of one another. For example, the latest and greatest computers require super high-resolution 3-D (or 7-D) solutions to the model problems. Actual problem solving rarely (never) works this way. If the problem can be solved in a lower-dimensional manner, it is better. Actual problem solving always starts simple and builds its way up. We start in one dimension and gain experience, run lots of problems, add lots of physics to determine what needs to be included in the model. The mantra of the modern day is to short-circuit this entire approach and jump to add in all the physics, and all the dimensionality, and all the resolution. It is the recipe for disaster, and that disaster is looming before us.
The reason for this is a distinct lack of balance in how we are pursing the objective of better modeling and simulation. To truly achieve progress we need a return to a balanced problem solving perspective. While this requires attention to computing, it also requires physical theory and experiment, deep engineering, computer science, software engineering, mathematics, and physiology. Right now, aside from computers themselves and computer science, the endeavor is woefully out of balance. We have made experiments almost impossible to conduct, and starved the theoretical aspects of science in both physics and mathematics.
Take our computer codes as an objective example of what is occurring. The modeling and simulation is no better than the physical theory and the mathematical approximations used. In many cases these ideas are now two or three decades old. In a number of cases the theory gives absolutely no expectation of convergence as the computational resource is increased. The entire enterprise is predicated on this assumption, yet it has no foundation in theory! The divorce between what the codes do and what the applied mathematicians at SIAM do is growing. The best mathematics is more and more irrelevant to the codes being run on the fastest computers. Where excellent new mathematical approximations exist they cannot be applied to the old codes because of the fundamental incompatibility of the theories. Despite these issues little or no effort exists to rectify this terrible situation.
Long-term thinking has gone the way of the dinosaur. It died in the 1970’s. I came across a discussion of one of the key ideas of our time, the perspective that business management is all about maximizing shareholder value. It was introduced in 1976 by Nobel Prize-winning economist, Milton Friedman and took hold like a leech. It arguable that it is the most moronic idea ever in business (“the dumbest idea ever”). Nonetheless it has become the lifeblood of business thought, and by virtue of being a business mantra, lifeblood of government thinking. It has been poisoning the proverbial well ever since. It has become the reason for the vampiric obsession with short-term profits, and a variety of self-destructive business practices. The only “positive” side has been its role in driving the accumulation of wealth within chief executives, and financial services. Stock is no longer held for any significant length of time, and business careers hinge upon the quarterly balance sheet. Whole industries have been ground under the wheels of the quarterly report. Government research in a lemming like fashion has followed suit and driven research to be slaved to the quarterly report too.
The consequences for the American economy have been frightening. Aside from the accumulation of wealth by upper management, we have had various industries completely savaged by the practice, rank and file workers devalued and fired, and no investment in future value. The stock trading frenzy created by this short-term thinking has driven the creation of financial services that produce nothing of value for the economy, and have succeeded in destabilizing the system. As we have seen in 2008 the results can be nearly catastrophic. In addition, the entire business-government system has become unremittingly corrupt and driven by greed and influence peddling. Corporate R&D used to be a vibrant source of science funding and form a pipeline for future value. Now it is nearly barren with the great corporate research labs fading memories. The research that is funded is extremely short-term focused and rarely daring or speculative. The sorts of breakthroughs that have become the backbone of the modern economy no longer get any attention.
The government has been similarly infested as anything that is “good” business practice is “good” for government management. Science is no exception. We now have to apply similar logic to our research and submit quarterly reports. Similar to business we have had to strip mine the future and inflate our quarterly bottom line. The result has been a systematic devaluing of the future. The national leadership has adopted the short-term perspective whole cloth.
At least in some quarters there is recognition of this trend and a push to reverse this trend. It is going to be a hard path to reversing the problem as the short-term focus has been the “goose that laid the golden egg” for many. These ideas have also distorted the scientific enterprise in many ways. The government’s and business’ investment in R&D has become inherently shortsighted. This has caused the whole approach to science to become radically imbalanced. Computational modeling and simulation is but one example that I’m intimately familiar with. It is time to turn things around.