At Madison a few years ago Rosenbluth summarized the community feelings very well when he quipped we "yearn to burn." The scientific rewards of a burning plasma experiment are exciting and widely recognized. At last a plasma that sustains itself with alpha heating while producing significant fusion energy. Assuming we select a design that allows reasonable flexibility in operation, and we undertake the necessary diagnostic development to deal with a hostile radiation environment, difficult access, and more extreme plasma conditions, the results will provide a major benchmark in understanding, which will be of great benefit to any of the conventional magnetic approaches to fusion. Many consider this "the holy grail" of fusion, and others predict we will finally "convince our increasingly skeptical friends that fusion is still worth pursuing" [Politzer’s remarks in these opinion articles].

But wait. What differs now from the same argument made in the 1980s and 1990s? Why have we failed to garner support for earlier burning-plasma or scientific next-step experiments like CIT, BPX, ITER, and TPX? Some have argued that the problem is within the community because we fail to display unity and a willingness to sacrifice collectively on necessary and costly next-step facilities. That is really not the problem. The fundamental problem is that many, probably a majority, of the well-informed and influential people outside the fusion community simply cannot imagine a tokamak or tokamak-like device, ever leading to a practical energy source. Too complicated and too expensive. Therefore, they conclude (incorrectly) that a billion-dollar-class tokamak experiment of any kind is not worth the cost. If you are not convinced, recall what Martha Krebs said repeatedly. Read the program restructuring documents from 1996. Read the language in appropriation bills year after year. Ask knowledgeable insiders like Mark Haines. If you have an opportunity, talk to Congressional staff yourself and listen carefully. Even our allies in policy circles, who draft nice authorization words like the "Fusion Energy Sciences Act of 2001" (see HR 4 on the fire web page, at fire.pppl.gov) are careful not to emphasize the tokamak path to fusion energy, but to emphasize the "need for a magnetic fusion burning plasma experiment to address key scientific issues and as a necessary step in the development of fusion energy."

In fact, some of our critics have concluded our community is brain dead. No matter how clearly we are told "no next-step tokamak" we seem to come back again and again with pretty much the same request for a tokamak burning plasma experiment. While FESAC and other leaders believe and claim that our story has changed, the critics remain skeptical. Events like Snowmass will be watched to see if we have really changed or not. Do we or don’t we understand that while tokamaks are a great scientific tool, they do not look like a practical reactor? Formulating a position on this key issue is our biggest challenge.

What can we do? One answer would be a radical shift in program logic such as a politically dangerous breeder emphasis (see accompanying opinion article by Mannheimer). I recommend instead that we pursue even more aggressively the course embarked upon at the time of restructuring. Ours is a "science" program, which means more than anything else that we do not have an obvious path towards practical energy. Accept this reality and advocate a program based on this awareness. Do not let our program get associated with less informed enthusiasts who make indefensible claims like "a burning plasma is the last step needed before a demonstration plant." Besides the show-stopping issues of size, complexity, and cost, such claims ignore the enormous issue of radiation-resistant materials that have yet to be developed and tested. Be careful when dealing with naïve enthusiasts. Do not let them put words in our mouths about how fusion is just around the corner if only we do this next-step experiment. Remember, even though it might not have been intentional, the magnetic fusion program still carries a burden of overselling itself. After all we named TFTR the "Tokamak Fusion Test Reactor."

Fortunately, the Europeans, who have tended towards aggressive claims that ITER was the only step necessary before a demo, have softened their rhetoric in this regard. Even the recent "fast track" analysis by senior officials, where one might expect to find aggressive rhetoric, actually admits that materials are a major issue that must also be addressed (see "Fast Track Strategy" at fire.pppl.gov).

How do alternates relate to a burning plasma experiment? Primarily, we should view them as an independent research activity aimed at finding the optimum fusion solution. This is what our critics want to see! They don’t like the tokamak, but most of them do want fusion. So a program that has a portfolio approach, and does not assume the tokamak is the only pathway to fusion, is highly desirable.

Obviously, if a burning-plasma tokamak experiment operates in a similar physical regime as say a stellarator, then stellarator research will benefit from the scientific understanding gained. But not all fusion approaches depend upon sustained operation. A more limited and defensible justification for a burning plasma experiment is that it will provide scientific insight for a large class of magnetic confinement ideas. But we must not be grandiose and claim such an experiment is absolutely necessary to develop fusion energy. It is too early to tell. After all, the main alternative to tokamaks is inertial confinement fusion, which has almost zero benefit from a tokamak burning plasma experiment. Less explored ideas like magnetized target fusion, inertial electrostatic fusion, muon catalyzed fusion, and others are similarly orthogonal in their physics and technical issues. This diversity is an excellent answer to our critics, and our diversity needs to be emphasized repeatedly.

To my many dedicated tokamak friends, I have one main recommendation. Be humble. Acknowledge that the path to fusion is still unknown, and speak with enthusiasm for the importance of a scientifically prudent portfolio approach to the problem. If that is too much to ask, then at least speak quietly about your conviction that tokamaks are the only answer, and they are on the right track to make "real energy." Such a view has simply become laughable to outsiders, and provides a basis in itself for refusing a new initiative.

If this community could agree that our position, at least in a collective sense, is one of continued open-minded evaluation of all scientifically credible promising options, then by all means we should speak out with equal enthusiasm about the benefit of a burning plasma experiment. Argue as Pitcher does that the integration of important physical effects can only be accomplished at present in a tokamak. Argue as Politzer does that magnetic fusion research needs revitalizing. Join Baldwin in observing that a burning plasma experiment advances the scientific understanding of what can be done in the intriguing mode of sustained operation. Just keep in mind that the experiment is not a prototype reactor, and in fact addresses issues relevant to only a subset of fusion possibilities. If this can be our "community posture", then I think we have a better chance than ever of selling a burning plasma experiment. It is this balance between tokamak research and a search for innovative confinement concepts that stabilized our budget in recent years. However, the critics are watching closely to see if we meant what we said during restructuring. Unless we propose a burning plasma experiment that is fully justified in the context of a restructured program, then we run the very serious risk of appearing to revert to the earlier schedule-driven program logic with its pretense of being a straightforward march towards a tokamak-based fusion solution. That didn't sell then and it wouldn't sell today.