In the interest of stimulating some new thinking, this essay explores the idea that the reason why there is no scientific consensus about how to proceed in magnetic fusion is that there is no sufficiently detailed, coherently-articulated physics & engineering "Standard Model" with which to compare all available options and reach objective conclusions.

The fusion energy community needs its own Standard Model, a basic scientific-engineering paradigm which provides an objective foundation from which to move forward. In the absence of such a community-wide, mutually agreed-upon, fundamental objective paradigm, any "consensus" about how to proceed is a purely "political consensus" (a temporary consensus based on perceived self-interest) rather than a "scientific consensus" (an enduring consensus based on unchanging objective truths understood by all). Furthermore, without a Standard Model, proposed new projects can only be justified (or "sold") using political arguments, not rigorous science. Because the lifetime of a political consensus is much shorter than the lifetime of a scientific consensus, and large projects tend to die when they are no longer justified by a strong consensus, it's obvious that a project which is only politically-justified is much more likely to die before completion than a project justified by a scientific consensus. To revitalize the U.S. magnetic fusion program it is not enough for Snowmass to simply result in a consensus - the consensus has to be sustained long enough to complete the project. That means it needs firm science that EVERYONE (from all areas of fusion) will agree upon. Unless the scientific consensus is firmly based in real science, the history of fusion leaves little reason to hope that any major new facilities will ever actually be built and operated.

From this perspective it is easy to see why the fusion program as a whole has survived for 50 years. There has always been value in creating a better energy source, so the objective scientific promise of fusion has not changed. Similarly, we will always want to know more about the universe and its fundamental constituents, so astrophysics and particle physics will also continue (as long as the incremental progress is worth the incremental price of continuing each year). Conversely, the same perspective explains the U.S. magnetic fusion community's abject failure over the past 20 years to complete the design-construction-operation of any major new experiments: in the absence of a Standard Model covering all the physics and engineering aspects of fusion, the political justifications that have been used have not lasted long enough to complete the projects. It is not enough to have a "Physics Basis" providing technical credibility for a proposed design. A community-wide Standard Model is necessary to provide the fundamental conceptual framework for objectively evaluating disparate concepts and proposals, and for objectively comparing the relative potential of diverse program goals.

Consider the situation in magnetic fusion relative to that in particle physics and astrophysics. At about the same time that the fusion community was building the big tokamaks in search of breakeven, the particle physics community assembled the Standard Model of Fundamental Particles, and the astrophysics community assembled a coherent picture of the universe starting with the Big Bang and Inflation and evolving to the present day. Over the same time period both of these other communities have successfully built many major new experiments, many of which have individually been larger in cost than TFTR or ITER. The new accelerators and telescopes have been designed and then justified to funding agencies in terms of their potential to test and improve upon critical aspects of the fundamental paradigm in each field, and also by indicating how the new facilities (and their associated engineering advances) would benefit multiple areas of science, technology, and society. Furthermore, with each new experiment and observation, the particle physicists and astronomers have steadily extended the reach and explanatory power of their basic paradigm theories and models.

Magnetic fusion has often ignored this highly successful standard scientific process (use of experiments to test, improve, and extend a comprehensive theoretical foundation) in favor of a wind-tunnel engineering approach (build a small one, then scale up to a big one). However, real-world wind tunnels work because the fundamental laws of hydrodynamics can be scaled fairly rigorously, whereas the wind-tunnel approach to fusion fails because fusion plasmas in real-world devices are more complex and do not obey enough scaling laws. The result, as we have all seen looking back over the last 50 years, is that unexpected phenomena invariably emerge in each new regime. But the wind-tunnel approach also fails because it neglects to formulate a complete, rigorous paradigm theory, which makes it difficult to link one area of endeavor with another. The good news is that we DO have bits and pieces of such a theory—but they are implemented in so many different ways and so many different places that few codes have been rigorously tested, hardly any can be used to evaluate more than a handful of devices of the same basic kind, and none can be used to model the whole range of possible fusion concepts. We have built our own Tower of Babel: a world of lab-specific, machine-specific and concept-specific experiments, data, theories and codes.

We all know that despite this fusion has made enormous progress. But our Tower of Babel gives us no firm foundation, no general paradigm with which to create and sustain a scientific consensus on the path forward. The research done to make fusion energy real is at least as much fun, at least as interesting scientifically, and at least as valuable to humanity as what the astrophysicists and particles people do. So why is it that they can build big collaborative experiments, while we all tend to just point at our own labs and say "give me more money"? The Snowmass premise is right: if we want to achieve the same level of success that other fields have, we should try doing things the way they do. But that means more than just trying to "reach a consensus" we also need to build our own rigorous, shared scientific foundation for our whole field: our own Standard Model. And perhaps this should be done before we build a burning plasma experiment.

What does "building a Standard Model" mean? At a minimum, it means recognizing that the various approaches to fusion have much in common, more than our current Tower of Babel would indicate. It means that all the first-principles physics relevant to all areas of fusion (magnetic, inertial, innovative and insane) should be identified, collected and synthesized theoretically, including the evolution of a complete set of standard notation applicable to all fusion concepts. It means this core theory needs to include all the fundamental engineering principles and accumulated technical data relevant to the plethora of reactor design approaches. It means that all this theory should be embodied in a set of Standard Codes: open-source, user-oriented computer tools, shared and developed by the whole community, which can be used to evaluate and interpret all of our experiments. It means it is okay if the theory or the code isn't complete, because the whole point to work on fixing that. It means new experiments should be designed not to push parameters in a particular confinement geometry, but to rigorously test the theory and understand the limits of the approximations that will necessarily be incorporated into the computer models. It means the experimental emphasis should not be to build new capabilities for their own sake, or to make incremental improvements to existing facilities, but to create a small, but sufficiently large set of fully-diagnosed user facilities that will enable everyone in the community to team up and elucidate any physics that our Standard Codes may be missing, especially where different models disagree. It means vacuum vessel port sizes and diagnostic hardware and software should be standardized nationwide so that instruments can be ported from one machine to another, or moved around for different experiments on a single machine as needed. (This latter technique is already being used with tremendous success in various U.S. inertial fusion facilities.) It means that all our efforts will have a common scientific context, so that when we go to propose a new experiment, we all agree that our best theoretical predictions stand behind it, and that it's the best way to take the right next step forward. That gives us the scientific, not just political, consensus that we need.

A program emphasizing the fundamental physics and engineering issues common to all of fusion, instead of my-machine-versus-your-similar-machine, or my-concept-versus-your-concept, could be a way to enable real national cooperation and collaboration, since each major institution would be able to take the lead role in a specific aspect of the national program, without being threatened by activities at other institutions. Maybe one organization could focus on plasma heating, another can do MHD stability, a third can handle confinement physics, etc. Larger institutions would naturally get larger components of the overall program, yet smaller institutions and university collaborations would still have an essential role to play. They could even have increased roles in the national code and diagnostic development efforts. Working from a broad community foundation, everyone could genuinely participate in a positive-sum game ("How can we all grow together?") instead of continuing to fighting the negative-sum game of the past 20 years ("How do I protect my institution's share of the ever-dwindling national budget?"). Small program components could be periodically reorganized to maintain both institutional balance and the support of Congresspeople from many states.

Suppose we work together and really do all that. Then each time we have a Snowmass meeting, we could all present our latest results in the same scientific context, and see exactly where our Standard Model is being improved, where it is breaking down, and what it predicts in terms of potential future reactors in any configuration. New ideas would require adding new components to the Standard Codes implementing the Standard Model, but that would strengthen the Standard Model. Then the code could be used to rapidly evaluate new ideas, producing credible results which might immediately justify new experiments. Because of the common scientific context, it would be much easier to prioritize opportunities, apportion expected resources, and evolve new program goals. Then when we go to Congress each year to ask for the next billion dollars, we would already be in agreement on which parts of the model we are going to be testing and how the tests will bring us closer to the eventual goal. But the only way to get out of the political quicksand of the past 20 years is to build ourselves a rock-solid, first-principles technical foundation, and that needs a serious community-wide scientific approach.

Why haven't we all worked together like this before? I'm certainly too young to know, but for the sake of stimulating discussion, I'll advance a plausible theory. Fusion had its origins as a set of classified projects expected to produce quick results in an era of intense cold-war competition. Now, whenever everyone at every laboratory has a promising concept that looks like it will succeed, there will be few incentives for real collaboration. A scientific culture of competition can develop. This was seen in the "Plasma Olympics" events at the early IAEA conferences. More recently, such a cutthroat competitive culture has apparently evolved in biotechnology, where budgets are steadily increasing and individual investigators can reap huge rewards by being the first to discover major new results with high economic value? and as a result people are becoming unwilling to share either their ideas or their data. Scientific cultures change slowly. In fusion, it seems to me that even though everyone now agrees that scientific cooperation is essential, national and institutional parochialism is still widespread, and the budget battles of the past 20 years have left behind some hard feelings. But funding for science need not be a zero-sum game ("If you win, I lose."). By now it should be obvious to everyone that once anyone can get to the pot of gold at the end of the rainbow, we all can. So instead of pulling the other guys back and trying to get to the front of a race that isn't going anywhere anyway, we should all be pushing each other forward. We should rebuild our community into a place where we all work together to get maximum science out of our funding, and be generous with giving and sharing credit, because fusion is such a big challenge that the only way any of us will every get any glory out of this before we die, is if we all do. In the end there will be no individual winners, so why are we always fighting?

What legacy do the current fusioneers want to leave for the future? My story is all too typical of the legacy being left now: I entered the magnetic fusion community in 1993 as an enthusiastic and highly motivated graduate student with a naive, but very real, passion for doing fusion. TFTR and JET were about to break even using D-T fuel, TPX was about to be built, and ITER, though a long way off, was moving forward as the wave of the future. When I finished my PhD in 1999, I was still enthusiastic and highly motivated, but TFTR was being torn apart, TPX was long since cancelled, and ITER was still a long way off. Once more, the magnetic fusion community had failed to build The Next Big Machine. More importantly, the community had again failed to solve the problems that destroyed all the previous Next Big Machines for the past 20 years. Although I had become a bit less naive, I still had a passion for fusion, but I saw no point in spending (wasting?) any more of my life working at the lower levels of a program which clearly had serious non-scientific problems at the management levels - problems which its leaders had acquired an excellent track record at NOT solving. So I moved to a closely related field with upcoming opportunities (which, I found, was full of other fusion refugees), and gained a broader perspective on ways of doing plasma physics. I have not met many scientists outside fusion who do believe the program will succeed, but at the same time I have not met many non-scientists who do not strongly support the goal of fusion energy. But many wonder whether it might be time to try doing things differently.