Judge a man by his questions rather than by his answers.
In thinking about what makes work good for me, I explored an element of the creative process for me revolving around answering questions. If one doesn’t have the right question, the work isn’t framed correctly and progress will stall. A thing to consider in this frame of reference is what makes a good question? This itself is an excellent question! The quality of the question makes a great difference in framing the whole scientific enterprise, and can either lead to bad places of “knowledge cul-de-sacs” or open stunning vistas of understanding. Where you end up depends on the quality of the question you answer. Success depends far more on asking the right question than answering the question originally put to you (or you put to yourself).
truth, like gold, is to be obtained not by its growth, but by washing away from it all that is not gold.
― Leo Tolstoy
A great question is an achievement in itself although rarely viewed as such. More often than not little of the process of work goes into asking the right question. Often the questions we ask are highly dependent upon foundational assumptions that are never questioned. While assumptions about existing knowledge are essential, finding the weak or invalid assumptions is often the key to progress. These assumptions are wonderful for simplifying work, but also inhibit progress. Challenging assumptions is one of the most valuable things to do. Heretical ideas are fundamental to progress; all orthodoxy began as heresy. If the existing assumptions hold up under the fire of intense scrutiny they gain greater credibility and value. If they fall, new horizons are opened up to active exploration.
If we have no heretics we must invent them, for heresy is essential to health and growth.
― Yevgeny Zamyatin
It goes without saying that important questions are good ones. Defining importance is tricky business. There are plenty of important questions that lead nowhere “what’s the meaning of life?” or we simply can’t answer using existing knowledge, “is faster than light travel possible?” On the other hand we might do well to break these questions down to something more manageable that might be attacked, “is the second law of thermodynamics responsible for life?” or “what do subatomic particles tell us about the speed of light?” Part of the key to good scientific progress is threading the proverbial needle of important, worthy and possible to answer. When we manage to ask an important, but manageable question, we serve progress well. Easy questions are not valuable, but are attractive due to their lack of risk and susceptibility to management and planning. Sometimes the hardest part of the process is asking the question, and a well-defined and chosen problem can be amenable to trivial resolution. It turns out to be an immensely difficult task with lots of hard work to get to that point.
I have benefited mightily from asking some really great questions in the past. These questions have led to the best research, and most satisfying professional work I’ve done. I would love to recapture this spirit of work again, with good questioning work feeling almost quaint in today’s highly over-managed climate. One simple question occurred in my study of efficient methods for solving the equations of incompressible flow. I was using a pressure projection scheme, which involves solving a Poisson equation at least once, if not more than once a time step. The most efficient way to do this involved using the multigrid method because of its algorithmic scaling being linear. The Poisson equation involves solving a large sparse system of linear equations, and the solution of linear equations scales with powers of the number of equations. Multigrid methods have the best scaling thought to be possible (I’d love to see this assumption challenged and sublinear methods discovered, I think they might well be possible).
As problems with incompressible flows become more challenging such as involving large density jumps, the multigrid method begins to become fragile. Sometimes the optimal scaling breaks down, or the method fails altogether. I encountered these problems, but found that other methods like conjugate gradient could still solve the problems. The issue is that the conjugate gradient method is less efficient in its scaling than multigrid. As a result as problems become larger, the proportion of the solution time spent solving linear equations grows ever larger (the same thing is happening now to multigrid because of the cost of communication on modern computers). I posed the question of whether I could get the best of both methods, the efficiency with the robustness? Others were working on the same class of problems, and all of us found the solution. Combine the two methods together, effectively using a multigrid method to precondition the conjugate gradient method. It worked like a charm; it was both simple and stunningly effective. This approach has become so standard now that people don’t even think about it, its just the status quo.
At this point it is useful to back up and discuss a key aspect of the question-making process essential to refining a question into something productive. My original question was much different, “how can I fix multigrid?” was the starting point. I was working from the premise that multigrid was optimal and fast for easier problems, and conjugate gradient was robust, but slower. A key part of the process was a reframing the question. The question I ended up attacking was “can I get the positive attributes of both algorithms?” This changed the entire approach to solving the problem. At first, I tried switching between the two methods depending on the nature of the linear problem. This was difficult to achieve because the issues with the linear system are not apparent under inspection.
The key was moving from considering the algorithms as different options whole cloth, to combining them. The solution involved putting one algorithm inside the other. As it turns out the most reasonable and powerful way to do this is make multigrid a preconditioner for conjugate gradient. The success of the method is fully dependent on the characteristics of both algorithms. When multigrid is effective by itself, the conjugate gradient method is effectively innocuous. When multigrid breaks down, the conjugate gradient method picks up the pieces, and delivers robustness along with the linear scaling of multigrid. A key aspect of the whole development is embracing an assault on a philosophical constraint in solving linear systems. At the outset of this work these two methods were viewed as competitors. One worked on one or the other, and the two communities do not collaborate, or even talk to each other. They don’t like each other. They have different meetings, or different sessions at the same meeting. Changing the question allows progress, and is predicated on changing assumptions. Ultimately, the results win and the former feud fades into memory. In the process I helped create something wonderful and useful plus learned a huge amount of numerical (and analytical) linear algebra.
The second great question I’ll point to involved the study of modeling turbulent flows with what has become known as implicit large eddy simulation. Starting in the early 1990’s there was a stunning proposition that certain numerical methods seem to automatically (auto-magically) model aspects of turbulent flows. While working at Los Alamos and learning all about a broad class of nonlinearly stable methods, the claim that they could model turbulence caught my eye (I digested it, but fled in terror from turbulence!). Fast forward a few years and combine this observation with a new found interest in modeling turbulence, and a question begins to form. In learning about turbulence I digested a huge amount of theory regarding the physics, and our approaches to modeling it. I found large eddy simulation to be extremely interesting although aspects of the modeling were distressing. The models that worked well were performed poorly on the structural details of turbulence, and the models that matched the structure of turbulence were generally unstable. Numerical methods for solving large eddy simulation were generally based on principles vastly different than those I worked on, which were useful for solving Los Alamos’ problems.
Having methods I worked on for codes that do solve our problems also model turbulence is tremendously attractive. The problem is the seemingly magical nature of this modeling. Being magical does not endow the modeling with confidence. The question that we constructed a research program around was “can we explain the magical capability of numerical methods with nonlinear stability to model turbulence?” We combined the observation that a broad class of methods seemed to provide effective turbulence modeling (or the universal inertial range physics). Basically the aspects of turbulence associated with the large-scale hyperbolic parts of the physics were captured. We found that it is useful to think of this as physics-capturing as an extension of shock-capturing. The explanation is technical, but astoundingly simple.
Upon study of the origins of large eddy simulation we discovered that the origins of the method were the same as shock capturing methods. Once the method was developed it evolved into its own subfield with its own distinct philosophy, and underlying assumptions. These assumptions had become limiting and predicated on a certain point-of-view. Shock capturing had also evolved in a different direction. Each field focused on different foundational principles and philosophy becoming significantly differentiated. For the most part they spoke different scientific languages. It was important to realize that their origins were identical with the first shock capturing method being precisely the first subgrid model for large eddy simulation. A big part of our research was bridging the divides that had developed over almost five decades and learn to translate from one language to the other.
We performed basic numerical analysis of nonlinearly stable schemes using a technique that produced the nonlinear truncation error. A nonlinear analysis is vital here. This uses a technique known as modified equation analysis. The core property of the methods empirically known to be successful in capturing the physics of turbulence is conservation (control volume schemes). It turns out that the nonlinear truncation error for a control volume method for a quadratic nonlinearity produces the fundamental scaling seen in turbulent flows (and shocks for that matter). This truncation error can be destabilizing for certain flow configurations, effectively being anti-dissipative. The nonlinear stability method keeps the anti-dissipative terms under control, producing physically relevant solutions (e.g., entropy-solutions).
A key observation makes this process more reasoned and connected to the traditional large eddy simulation community. The control volume term matches the large eddy simulation models that produce good structural simulations of turbulence (the so-called scale similarity model). The scale similarity model is unstable with classical numerical methods. Nonlinear stability fixes this problem with aplomb. We use as much scale similarity as possible without producing unphysical or unstable results. This helps explain why a disparate set of principles used to produce nonlinear stability provides effective turbulence modeling. Our analysis also shows why some methods are ineffective for turbulence modeling. If the dissipative stabilizing effects are too large and competitive with the scale similarity term, the nonlinear stability is ineffective as a turbulence model.
It is dangerous to be right in matters on which the established authorities are wrong.
I should spend some time on some bad questions as examples of what shouldn’t be pursued. One prime example is offered as a seemingly wonderful question, the existence of solutions to the incompressible Navier-Stokes equations. The impetus for this question is the bigger question of can we explain, predict or understand fluid turbulence? This problem is touted as a fundamental building block in this noble endeavor. The problem is the almost axiomatic belief that turbulence is contained within this model. The key term is incompressible, which renders the equations unphysical on several key accounts: it gives the system infinite speed of propagation, and divorces the equations from thermodynamics. Both features sever the ties of the equations from the physical universe. The arguing point is whether these two aspects disqualify it from addressing turbulence. I believe the answer is yes.
In my opinion this question should have been rejected long ago based on the available evidence. Given that our turbulence theory is predicated on the existence of singularities in ideal flows, and the clear absence of such singularities in the incompressible Navier-Stokes equations, we should reject the notion that turbulence is contained in them. Despite this evidence, the notion that turbulence is contained whole cloth in these unphysical equations remains unabated. It is treated as axiomatic. This is an example of an assumption that has out lived its usefulness. It will eventually be tossed out, and progress will bloom the path of its departure. One of the key things missing from turbulence is a connection to thermodynamics. Thermodynamics is such a powerful scientific concept and for it to be so absent from turbulence is a huge gap. Turbulence is a fundamental dissipative process and the second law is grounded on dissipation. The two should be joined into a coherent whole allowing unity and understanding to reign where confusion is supreme today.
Another poorly crafted question revolves around the current efforts for exascale class computers for scientific computing. There is little doubt that an exascale computer would be useful for scientific computing. A better question is what is the most beneficial way to push scientific computing forward? How can we make scientific computing more impactful in the real world? Can the revolution of mobile computing be brought to science? How can we make computing (really modeling and simulation) more effective in impacting scientific progress? Our current direction is an example of crafting an obvious question, with an obvious answer, but failing to ask a more cutting and discerning question. The consequence of our unquestioning approach to science will be wasted money and stunted progress.
Trust is equal parts character and competence… You can look at any leadership failure, and it’s always a failure of one or the other.
― Stephen M.R. Covey
This gets at a core issue with how science is managed today. Science has never been managed more tightly and becoming more structurally mismanaged. The tight management of science as exemplified by the exascale computing efforts is driven by an overwhelming lack of trust in those doing science. Rather than ask people open-ended questions subject to refinement through learning, we ask scientists to work on narrowly defined programs with preconceived outcomes. The reality is that any breakthrough, or progress for that matter will take a form not envisioned at the outset of the work. Any work that pushes mankind forward will take a form not foreseeable. By managing so tightly and constraining work, we are predestining the outcomes to be stunted and generally unworthy of the effort put into them.
Whether you’re on a sports team, in an office or a member of a family, if you can’t trust one another there’s going to be trouble.
― Stephen M.R. Covey
This is seeded by an overwhelming lack of trust in people and science. Trust is a powerful concept and its departure from science has been disruptive and expensive. Today’s scientists are every bit as talented and capable as those of past generations, but society has withdrawn its faith in science. Science was once seen as a noble endeavor that embodied the best in humanity, but generally not so today. Progress in the state of human knowledge produced vast benefits for everyone and created the foundation for a better future. There was a sense of an endless frontier constantly pushing out and providing wonder and potential for everyone. This view was a bit naïve and overlooked the maxim that human endeavors in science are neither good or bad, producing outcomes dependent upon the manner of their use. For a variety of reasons, some embedded within the scientific community, the view of society changed and the empowering trust was withdrawn. It has been replaced with suspicion and stultifying oversight.
When I take a look at the emphasis in currently funded work, we see narrow vistas. There is a generally myopic and tactical view of everything. Long-term prospects, career development and broad objectives are obscured by management discipline and formality. Any sense of investment in the long-term is counter to the current climate. Nothing speaks more greatly to the overwhelming myopia is the attitude toward learning and personal development. It is only upon realizing that learning and research are essentially the same thing does it start to become clear how deeply we are hurting the scientific community. We have embraced a culture that is largely unquestioning with a well-scripted orthodoxy. Questions are seen as heresy against the established powers and punished. For most, learning is the acquisition of existing knowledge and skills. Research is learning new knowledge and skills. Generally speaking, those who have achieved mastery of their fields execute research. Since learning and deep career development is so hamstrung by our lack of trust, fewer people actually achieve the sort of mastery needed for research. The consequences for society are profound because we can expect progress to be thwarted.
Curiosity is more important than knowledge.
― Albert Einstein
One clear way to energize learning, and research is encouraging questioning. After encouraging a questioning attitude and approach to conducting work, we need to teach people to ask good questions, going back and refining questions, as better understanding is available. We need to identify and overcome assumptions subjecting them to unyielding scrutiny. The learning, research and development environment is equivalent to a questioning environment. By creating an unquestioning environment we short-circuit everything leading to progress, and ultimately cause much of the creative engine of humanity to stall. We would be well served by embracing the fundamental character of humanity as a creative, progressive and questioning species. These characteristics are parts of the best that people have to offer and allow each of us to contribute to the arc of history productively.
Curiosity is the engine of achievement.
― Ken Robinson
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