Great research depends on taking big risks with a large chance of failure and mission-focus is a clear way to get there. Failure is the key to learning, and research is fundamentally learning. We need to avoid failing too early by shying away from solving the harder problems and devotion to a mission provides the drive to keep focus on results that provide value to that mission.
There is only one thing that makes a dream impossible to achieve: the fear of failure.
― Paulo Coelho
For a lot of people working at a National Lab there are two divergent paths for work, the research path that leads to lots of publishing, deep technical work and strong external connection, or the mission path that leads to internal focus and technical shallowness. The research path is for the more talented and intellectual people who can compete in this difficult world. For the less talented, creative or intelligent people, the mission world offers greater security at the price of intellectual impoverishment. Those who fail at the research focus can fall back onto the mission work and be employed comfortably after such failure. This perspective is a cynical truth for those who work at the Labs and represents a false dichotomy. If properly harnessed the mission focus and empower and energize better research, but it must be mindfully approached.
The measure of greatness in a scientific idea is the extent to which it stimulates thought and opens up new lines of research.
― Paul A.M. Dirac
As I stated, I believe the dichotomy of mission versus research is false. The mission imposes limitations and constraints on research. In a nutshell, the mission imposes a fixed problem to solve and one must adapt the solution to impact this mission. Conversely, pure research is unconstrained by a mission, which encourages people to change the problem to fit a solution. The fixed problem, adaptive solution mindset is much better for engaging innovation and producing breakthrough results. It also means a great amount of risk and lots of failure. Pure research can chase unique results, but the utility of those results is often highly suspect. This sort of research entails less risk and less failure as well. If the results are necessarily impactful on the mission, the utility is obvious. The difficulty is noting the broader aspects of research applicability that mission application might hide.
Examples of great mission-focused research abound and our modern world is testimony to the breakthrough nature of Cold War defense focused research. The shape of the modern world is a testament to the power of mission-focused work to succeed. Ubiquitous aspects of modernity such as the Internet, cell phones and GPS all owe their existence to Cold War research focused on some completely different mission. All of these technologies were created through steadfast focus on utility that drove innovation as a mode of problem solving. This model for creating value has fallen into disrepair due to its uncertainty and risk. Risk is something we have lost the capacity to withstand as a result the failure necessary to learn and succeed with research never happens.
Failure is a greater teacher than success
― Clarissa Pinkola Estés
Mission focused research falls prey to concerns over risk. In many mission organizations there is a fear of taking on too much risk in adopting research results into the mission delivery. The thought is that the research might not pan out and the mission will suffer as result. This is both shortsighted and foolhardy. The truth is vastly different than this fear-based reaction and the only thing that suffers from shying away from research in mission-based work is the quality of the mission-based work. Doing research causes people to work with deep knowledge and understanding of their area of endeavor. Research is basically the process of learning taken to the extreme of discovery. In the process of getting to discovery one becomes an expert in what is known and capable of doing exceptional work. Today to much mission focused work is technically shallow and risk adverse. It is over-managed and underled in the pursuit of false belief that risk and failure are bad things.
There is a key tension to maintain in harnessing this engine of knowledge. The successful delivery of value and success to the mission work must take priority. Those conducting the research should have a deep commitment to the mission and its success. Ultimately the success at the mission work must supersede the research objectives. Even better the research objectives need to be guided by the mission needs. In this sense the mission acts to constrain the research and shape its direction and focus. This sort of dynamic must be carefully and adroitly managed if it can be achieved. Unconstrained research without mission focus is quite tempting and much simpler to manage. It is also less successful at producing real value for society. Almost every breakthrough of great significance was the result of results-focused work although many of the breakthroughs had far greater reach beyond their intended use.
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
In my own experience the drive to connect mission and research can provide powerful incentives for personal enrichment. For much of my early career the topic of turbulence was utterly terrifying, and I avoided it like the plague. It seemed like a deep, complex and ultimately unsolvable problem that I was afraid of. As I began to become deeply engaged with a mission organization at Los Alamos it became clear to me that I had to understand it. Turbulence is ubiquitous in highly energetic systems governed by the equations of fluid dynamics. The modeling of turbulence is almost always done using dissipative techniques, which end up destroying most of the fidelity in numerical methods used to compute the underlying ostensibly non-turbulent flow. These high fidelity numerical methods were my focus at the time. Of course these energy rich flows are naturally turbulent. I came to the conclusion that I had to tackle understanding turbulence.
One Winter break my laptop broke leaving without the ability to work on my computer codes over the break (those were the days!). So I went back to my office (those were the days!) and grabbed seven books on turbulence that had been languishing on my bookshelves unread due to my overwhelming fear of the topic. I started to read these books cover to cover, one by one and learn about turbulence. I’ve included some of these references below for your edification. The best and most eye opening was Uriel Frisch’s “Turbulence: the Legacy of A. N. Kolmogorov”. In the end, the mist began to clear and turbulence began to lose its fearful nature. Like most things one fears; the lack of knowledge of a thing gives it power and turbulence was no different. Turbulence is actually kind of a sad thing; its not understood and very little progress is being made.
The main point is that the mission focus energized me to attack the topic despite my fear of it. The result was a deeply rewarding and successful research path resulting in many highly cited papers and a book. All of a sudden the topic that had terrified me was understood and I could actually conduct research in it. All of this happened because I took contributing work to the mission as an imperative. I did not have the option of turning my back on the topic because of my discomfort over it. I also learned a valuable lesion about fearsome technical topics; most of them are fearsome because we don’t know what we are doing and overelaborate the theory. Today the best things we know about turbulence are simple, and old discovered by Kolmogorov as he evaded the Nazis in 1941.
People who don’t take risks generally make about two big mistakes a year. People who do take risks generally make about two big mistakes a year.
― Peter F. Drucker
In today’s world we have allowed a system to come into power that funds useless research. We have created vast swaths of safe research topics that ultimately produce rafts of papers, but little or no real utility for society. A big driver behind this mentality is the need to fund “sure things” that can’t fail. This pushes research into the realm of squalid incrementalism. Incremental research is safe and almost never prone to the risk of failure. It is also an actual waste of money that can produce the appearance and guise of success without actual achievement. Our unremitting fearful society including the worry of the appearance of scandal has driven us to this horrible point. Research has become cowardly and uninspired so that it doesn’t ever fail. Being mission-focused is too hard and too risky because the mission is too important to ever fail at. The true attitude should be that the mission is too important not fail at!
The main reason of fear of failure lies in people’s being unaware of the impact of misfortune on achieving success
― Sunday Adelaja
The current sorry state in high performance computing is a direct result of the current milieu where mission-focus is neglected in favor of carefully managed projects with sure things as targets. Project management is not leadership, and without leadership we will continue to steadfastly underachieve. For example, we have utterly eviscerated applied mathematics by pushing a product-oriented approach that demands the delivery of results in software. Producing software in the conduct of applied mathematics used to be a necessary side activity instead of the core of value and work. Today software is the main thing produced and actual mathematics is often virtually absent. Actual mathematical research is difficult, failure prone and hard to measure. Software on the other hand is tangible and managed. It is still is hard to do, but ultimately software is only as valuable as what it contains, and increasingly our software is full of someone else’s old ideas. We are collectively stewarding other people’s old intellectual content, and not producing our own, nor progressing in our knowledge.
This trend would be bad enough on its own, but it is the tip of a proverbial iceberg of underachievement. The second pillar for underachievement in high performance computing is, ironically, a devotion to computer hardware. Again computer hardware is tangible and easy to measure. To a naïve person (or congressman) the ability to measure our ability to do things with computers should be a one-to-one match with the raw power of our computers. Nothing could be farther from the truth as computing is a completely multi-disciplinary field depending on a huge swath of science for success. The computer hardware is actually one of the least important components in our modeling and simulation competence. Instead of producing a program that strives for true success in modeling and simulation based on real mission value, we have constructed programs that are intellectually vacuous because they are easier to fund and explain to unsophisticated people. The hardware program more naturally lends itself to management and simple metrics of success. It can be sold to uninformed people. Its current form is the abdication of leadership and antithetical to the concept of mission-focus. Our approach to high performance computing is only likely to achieve supremacy for the Chinese in the field.
Success is stumbling from failure to failure with no loss of enthusiasm.
― Winston S. Churchill
What is gained by this mission focus? The focus on mission-focused research means the problem being solved is fixed and unwavering, and the results and knowledge must contribute to the solution of this problem. This forces the research to adapt itself to the needs of the problem rather than the problem to the research. The result of this model is the tendency to confront difficult thorny issues rather than shirk them. At the same time this form of research can also lead to failure and risk manifesting itself. This tendency is the rub, and leads to people shying away from it. We are societally incapable of supporting failure as a viable outcome. The result is the utter and complete inability to do anything hard. This all stems from a false sense of the connection between risk, failure and achievement.
If a single characteristic is contributing to a societal feeling that we have lost greatness, it is that we cannot accept failure. Without failure, great things cannot be achieved. Failure is the vehicle of achievement and learning whether we are talking about individuals, organizations or nations. The inability to accept failure as a possible outcome is the tacit acceptance of not wanting to do anything that matters, or anything great. The road to greatness is paved with many failures and the unerring drive to learn and grow from these failures. For the complex missions we are charged with, the commitment to mission focus in research means accepting failure as a necessary outcome of endeavor. This is the hard message that our spineless politicians and managers cannot give us. The inability to grasp this core truth is utter societal cowardice. True leadership would provide us the necessary support and encouragement to be courageous and steadfast. Instead we succumb to fear and the false belief that achievement can be managed and had without risk.
Research is about learning at a fundamental, deep level, and learning is powered by failure. Without failure you cannot effectively learn, and without learning you cannot do research. Failure is one of the core attributes of risk. Without the risk of failing there is a certainty of achieving less. This lower achievement has become the socially acceptable norm for work. Acting in a risky way is a sure path to being punished, and we are being conditioned to not risk and not fail. For this reason the mission-focused research is shunned. The sort of conditions that mission-focused research produces are no longer acceptable and our effective social contract with the rest of society has destroyed it.
If we are to successfully do great things again as people, as organizations, as laboratories and as a nation, the irony is that we need to fail a lot more. One way to assure the sort of failure we need is mission-focused research where providing value to a difficult mission is the primal goal of research. Better research is founded on devotion to meaningful outcomes, taking big risks and tolerating lots of failure.
Only those who dare to fail greatly can ever achieve greatly.
― Robert F. Kennedy
Launder, Brian Edward, and Dudley Brian Spalding. “Lectures in mathematical models of turbulence.” (1972).
Frisch, Uriel, and Russell J. Donnelly. “Turbulence: the legacy of AN Kolmogorov.” (1996): 82-84.
Pope, Stephen B. “Turbulent flows.” (2001): 2020.
Grinstein, Fernando F., Len G. Margolin, and William J. Rider, eds. Implicit large eddy simulation: computing turbulent fluid dynamics. Cambridge university press, 2007.
Margolin, Len G., and William J. Rider. “A rationale for implicit turbulence modelling.” International Journal for Numerical Methods in Fluids 39, no. 9 (2002): 821-841.
Margolin, L. G., W. J. Rider, and F. F. Grinstein. “Modeling turbulent flow with implicit LES.” Journal of Turbulence 7 (2006): N15.