At some point our community must take the step to a burning plasma. The question is not whether to build a BPX, but when? The decision should be based on the internal logic of the program along with recognition of external circumstances. This raises three questions.

- Can we articulate a clear and compelling mission for a BPX which can convince the general scientific community and the government in addition to the members of our own community?

- Are we ready for this step? Do we know enough about the physics and engineering to make a reasonable risk benefit trade-off?

- Is it likely we will get the needed funding increment to carry out a demanding BPX experiment while maintaining the vigour and excitement of the base program?

Since a decision to move forward on this project as a community makes a strong statement about our scientific priorities and our judgement of programatic needs and political realities, a consensus can only be achieved after a thorough discussion and resolution of these questions.

What follows is my own attempt to examine just a few of the issues raised by the proposals to build a BPX now.

1. Is a BPX the best device for the science we need to do NOW?

There is clearly a unique mission for a burning plasma experiment within our program. However, given the cost to taxpayers of such a device, we should feel compelled to justify such a step as both critical and timely. This immediately raises questions about the relative priority - at this moment - between the set of physics and engineering issues that can only be done on a BPX and the broader set of issues that can be addressed on non-burning facilities. I would make the assertion that, as a rule, research is best done on the least expensive device capable of yielding definitive results and that a BPX would be reserved for those experiments that can only be done on such a facility. It seems inevitable that run time on a BPX would be more expensive, experimental time less discretionary and diagnostics more difficult and more costly. In general, non-burning machines would have a lower cost to build, operate and upgrade, have more operational flexibility, could have better sets of diagnostics and would be able to devote more run time to a broad range of physics experiments.

Further, it is unclear to what extent knowledge learned from a particular incarnation of a BPX extrapolates to alternate configurations or operating modes. Given that there is no consensus on what a commercial fusion reactor would look like, is it critical to address the alpha physics and integration missions (the latter only partially articulated) right now? Or, should these wait till we have a better idea what a reactor might look like? The integration mission seems the least likely component to extrapolate from configuration to configuration. On the other hand, basic physics understanding of MHD, transport, wave-particle interactions, etc, are more likely to have broad applicability.

2. Does a BPX help or hurt in the effort to recruit and retain students and young scientists?

The demographics of the fusion program is a ticking time bomb. Unless we can attract and retain students, young scientists and engineers, technical progress will avail us of nothing. The best strategy for defusing this bomb is an open question. On the one hand, the excitement and publicity generated by a large, visibile project is a good thing. It suggests that the field is has long term viability, is held in some esteem by the government and scientific community and is considered to be important to the national interests. All of this serves to attract new recruits. On the other hand, a very large fraction of the project's budget will be spent outside the program on detailed engineering design and construction. Relatively little of the funding, in the short term, goes for the sort of research that enables students to do theses and young scientists to launch careers. Thus without a strong and growing base program, we may not be able to capitalize on the good public relations that the project could bring.

3. Are we really serious about retaining a vigorous base program?

There is general agreement that a vigorous base program is a necessary complement to a burning plasma initiative. It has been stated that a BPX would only begin if the budget were increased sufficiently to pay for the project. Based on experience, I have doubts about our collective committment to such a principle. First, to get funding for a large project, it will be necessary to argue that it is essential that our program take the step at this time. That it is, in fact, the most important thing that we could do. It seems likely that we would be asked to back up this assertion by showing sacrifice in other areas. Secondly, even if there were not such a tradeoff at the start, tight budgets or increasing costs could force one at a later date. (I can't think of any large science projects in recent years which have not been subject to tight budgets and increasing costs.) I find it hard to believe that program leaders would walk away from the BPX at that point. Thus, if we go ahead with a BPX, we must accept the likelihood of substantial cuts in mainline experiments, innovative concepts and theory. A judgement to go ahead would imply to me, a collective willingness to make this tradeoff.

Often the argument is made "If we don't take this step now, the program won't survive". Political justifications like these are ultimately self defeating. Decision makers don't care about our program per se; they will only support us if we can make the case that the mission justifies the expense. Further, the suggestion that a burning plasma experiment is the ONLY possible next step and that to not build such a machine is "doing nothing" leaves us with no exit strategy. If the government decides that it can't afford a BPX now, then logic dictates that the program be terminated. (Imagine if similar arguments had been made for the SSC within the High Energy Physics community.)