Reprinted from Physics Today, June 1996, page 21.
©
Copyright 1996, American Institute
of Physics, S-0031-9228-9606-010-3
A centerpiece of almost any discussion about the future of magnetic fusion is the proposed International Thermonuclear Experimental Reactor (ITER). Physics Today invited Thomas Stix and Andrew Sessler to present their case against continuation of the ITER project, and Marshall Rosenbluth to reply. The debate closes with a brief rebuttal by Stix and Sessler. The views of the authors are not necessarily those of their employers. A glossary of fusion terms is provided.
Controlled fusion represents an opportunity to replace fossil fuels and nuclear fission as energy sources. Intensive research aimed at the peaceful utilization of thermonuclear energy, now in its 46th year, has benefited enormously from vigorous international scientific exchange and collaboration. Much has already been accomplished. In the approach to controlled fusion that uses magnetic confinement---the subject of this opinion piece---plasma temperatures obtained in experimental devices have risen from a few electron volts to over 40 keV; energy confinement times have stretched from tens of microseconds to over a second; total nuclear energy output has gone from zero to a few megajoules, amounting to about 30% of the externally supplied plasma-heating energy.
Successful controlled fusion will require knowledge that can be gained only by research in plasma physics and materials science. In the last few years, the proposed International Thermonuclear Experimental Reactor has become the focus of future fusion-power research. The international fusion research community will soon have to decide whether or not to recommend its construction.
The ITER mission emerged from the 1985 summit meeting between Mikhail Gorbachev and Ronald Reagan in Geneva. It is "to demonstrate the scientific and technological feasibility of fusion power. The ITER will accomplish this by demonstrating controlled ignition and extended burn of a deuterium and tritium plasma with steady state as an ultimate objective, by demonstrating technologies essential to a reactor in an integrated system, and by performing integrated testing of the high heat flux and nuclear components required to utilize fusion power for practical purposes."[1]
Even though 11 years have passed since it was formulated, the ITER mission still appears to us as premature.
A conceptual design was completed in 1990, and July 1992 saw the start of the ITER Engineering Design Activities (EDA), a six-year international program to perform the detailed physics and engineering design for an engineering test reactor to reach ignition and remain in a state of equilibrium burn for 1000 seconds, while producing 1500 MW of fusion power.
The ITER machine would be genuinely huge.[2] The toroidal field coils would be 17-m high. The plasma volume would be 20-40 times larger than that of today's largest tokamaks---the Joint European Torus in the UK, JT-60 in Japan, the Tokamak Fusion Test Reactor at Princeton University and DIII-D at General Atomics in San Diego. Toroidal and poloidal field coils would both be superconducting, with magnetic fields up to 13 tesla. Construction time has been estimated at 10-12 years, and construction costs, in 1996 dollars, at $10 billion.
Not surprisingly, the immense cost of the ITER machine has caused the US to back away from participation as a major partner in its construction. Russia---succeeding the US's original ITER partner, the USSR---is eager to participate but unable to offer significant financial support. It has been suggested that Japan, with minority support from the European Community and with scientific encouragement from Russia and the US, may undertake to construct the ITER machine. On the other hand, we believe that the US fusion strategy should not hinge on Japan's funding and building the machine as now proposed.
We believe that construction of the ITER machine as it is
now being designed would be a seriously inappropriate next step for
the world's fusion community. There are too many unresolved
questions. They include how to
Other technical challenges include how to construct the largest of the superconducting coils on-site, maintain magnetic field errors below the extremely stringent locked-mode threshold and limit eddy-current heating of the superconducting coils.
Yet another concern is the immense emphasis on conventional tokamak design. It is true that the magnetically confined plasmas most closely approaching fusion conditions have been produced in tokamaks. But an eventual fusion reactor will likely look very different. Proceeding with ITER may not only preempt funding for alternative concepts, but also could freeze reactor design and engineering at a premature stage.
Several major considerations, then, lead us to believe that a decision to construct the ITER machine would be a poor choice. They are the machine's untested attributes and the unresolved technical issues; questions of science policy, including the narrowed focus on conventional tokamaks; the diversion and dedication of great human, scientific and fiscal resources to this single project; the 10 or more years to "first plasma"; the time periods typical for fusion innovation and for political change of will; and the negative impact on future research that would redound from a mechanical or physics failure in this single device. In a few words, the step is too large and the overall concept, for all its attractiveness, is both premature and overambitious with respect to current knowledge.
It is also essential to remain aware of the many long-range issues involved in attempting to develop an economically competitive fusion reactor. Such issues as profile control, burn control, plasma disruption, wall erosion, heat exchange, steady-state operation and helium-ash disposal are still largely unsolved. Dependence on the deuterium-tritium nuclear reaction introduces its own research requirements---in particular, low-activation materials to withstand damage to the first wall by the 14-MeV neutrons.
Given the many short- and long-range questions in the field, we encourage the formulation of a strategy that would seek answers through the utilization and enhancement of existing facilities, through the building of new facilities that can be considered reasonable next steps and through the exploitation of emerging concepts that could make fusion power more accessible. Among substantial new ideas that can be explored on existing machines are reversing magnetic shear to produce greatly enhanced confinement, using waves to transfer fusion alpha-particle energy directly to the ions, and creating localized energy transport barriers. Other critical needs include additional theoretical work and a significantly increased capability in computer simulation.
Additionally, we suggest the development of a coordinated multinational program of research that would lead to the experimental achievement of near-ignition conditions.
Recent fiscal constraints on research emphasize the demand for cost-effective solutions. The costs of some experiments are still within single-nation budgets---for example, the Ignitor, an ignition experiment currently under construction in Italy. Upgrading an existing large tokamak in the US to demonstrate near-ignition conditions in the plasma core could also be a near-term goal. A follow-on objective would be a multinational plasma ignition facility that would invoke advanced tokamak concepts to reduce size, construction time and cost. All are reasonable next steps, entailing costs that would even allow them to overlap in time. Ignition, or near-ignition, is the first requirement for a fusion reactor. Unless reproducible plasma conditions close to ignition can be achieved, work on other aspects of a reactor will be without meaning. Achievement of near-ignition conditions, together with the exploration of alpha-particle and burning-plasma physics, would be truly impressive research achievements and would signal a major advance toward an economically viable fusion reactor.
We believe that the above suggestions are in full accord with the goals identified in recent months by two major committees, the President's Committee of Advisers on Science and Technology,[3] and the US Department of Energy's Fusion Energy Advisory Committee.[4] Concerning ITER, the report of the DOE committee calls for a broad-based independent assessment---to be available in December 1996---based on the EDA plan. We support such an open review, and we vigorously encourage public discussion here and abroad of the policy questions cited earlier.
It seems inevitable that design optimization as well as still-outstanding technical, administrative and political issues will cause the European Community and Japan to defer their decisions on ITER construction well past the mid-1998 completion date for the EDA. US contingency planning for this circumstance also needs to be addressed. For example, if extending the EDA were to absorb, as at present, 20-25% of the US fusion budget, would that be an acceptable and appropriate use for these funds?
The path to economically competitive fusion power still
encounters unresolved issues. As the needed research continues, it
should involve using and enhancing existing facilities, increasing
present capabilities in computer simulation, encouraging
near-ignition experiments and constructing new experimental
facilities that can be considered reasonable next steps. Certainly it
is appropriate to continue strong international scientific exchange
and collaboration, but let it follow routes for planning and
implementation that are more attractive and more cost effective than
the one now emerging from the EDA.
1. International Thermonuclear Experimental Reactor, Establishment of ITER: Relevant Documents, IAEA/ITER/DS/1, ITER Documentation Series, IAEA, Vienna (1988). (back)
2. M. Huguet, in Proc. 15th IEEE/NPSS Symposium on Fusion Engineering, IEEE, New York (1994), vol. 1, p. 1. (back)
3. President's Committee of Advisers on Science and Technology, The US Program of Fusion Energy Research and Development: Report of the Fusion Review Panel, Washington, DC (July 1995). (back)
4. Fusion Energy Advisory Committee, A Restructured Fusion Energy Sciences Program, US Department of Energy, Office of Energy Research, Washington, DC (27 January 1996). (back)
I agree with Thomas Stix and Andrew Sessler on many of their key conclusions: the potential importance of fusion as one of a very limited number of future energy possibilities, the great progress that has already been made, the need to diversify and explore alternate fusion approaches and basic plasma science, the key importance of exploiting existing facilities, the opportunities being opened up by rapid advances in parallel computation, the critical need for a burning-plasma environment for experimental study and the necessity for international collaboration.
How to proceed using limited resources involves subjective judgment, and here I disagree strongly with the Stix/Sessler point of view regarding the International Thermonuclear Experimental Reactor.
There is not space here to engage in any meaningful discussion of the very complex physics problems underlying ITER design. The technical discussion presented by Stix and Sessler is a laundry list of well-known issues being addressed in the course of the ongoing ITER Engineering Design Activities (EDA). They do not identify any showstoppers; nor do they attempt to quantitatively assess the likely success of the EDA's proposed solutions, which are still evolving through an international R&D effort aimed at providing a "physics and engineering basis" for ITER construction by the end of the EDA, two and one-half years from now. A great number of theoretical and experimental tasks have been proposed for this period. Many of the issues are generic to most fusion reactor designs---high-heat-load divertors, 14-MeV neutron effects, multimegampere disruptions, confinement at the reactor scale and so on. Many of these issues are being faced in a realistic way for the first time by ITER designers with the help of the international fusion community. Stix and Sessler appear to be prejudging the outcome of the EDA design effort as unsatisfactory, and even prejudging the political reactions of the European Community and Japan to this outcome.
In my opinion, Stix and Sessler seriously misstate the recommendations of the Fusion Energy Advisory Committee for ITER review.[1] The committee's executive summary recommendation is to "Plan for the review of the ITER EDA and its results and establish criteria for a decision on future US participation." Clearly, such a final review of results can only come at the end of the EDA. In appendix G of the committee's report, mechanisms for this planning are spelled out, including a proposal that "The U.S. program should consider launching an assessment of the ITER detail[ed] design [end of 1996] modeled after the European Domestic Assessment of the ITER Interim design [1995]."[1] The European assessment was quite favorable and useful in highlighting certain areas for more intense study. Such US reviews of intermediate ITER milestones would certainly be important in preparing the US for the required in-depth final review.
The work of the ITER design team is monitored by a technical advisory committee of distinguished fusion scientists and engineers from the four international partners who judged the interim (midpoint) design to be satisfactory progress towards fulfilling ITER's objectives. The physics issues are being addressed with the assistance of seven international expert groups composed of non-ITER personnel. ITER needs and welcomes more active participation by the worldwide fusion community.
It is my conviction, shared by my ITER coworkers, that the nonlinear physics and novel engineering issues of fusion are so complex that only a real experiment at the approximate parameters required for ignition will ever resolve them quantitatively. In fact, it is precisely the existence of the laundry list of physics issues that justifies a realistic ignition experiment. This has been the position of the US fusion community for over a decade. It is critical that ITER be designed with sufficient flexibility, and I believe it has been, to incorporate new physics knowledge as it evolves in existing facilities or in early ITER experiments. (Stix and Sessler cite reversed-shear confinement improvement and alpha channeling as good examples.) Of course, it may turn out that a new idea is so successful that, with hindsight, ITER could safely be redesigned to be smaller and less expensive than the present conventional design. It seems to me, however, that fusion research requires a test bed such as ITER that we could use to design a desirable reactor by interpolation rather than continual extrapolation from undersized experiments. It will always be possible to argue for indefinite delays in building such a test bed while awaiting more perfect knowledge.
Thus the issues raised by Stix and Sessler are real and well recognized, but the conclusions they draw are a subjective judgment as to what constitutes a reasonable next step. If objective phrases were substituted for the pejorative terms they use---"premature," "genuinely huge," "immense cost," "enormous power," "extremely stringent," "over-ambitious," "immense emphasis" among others---then one might reach the same conclusions as most of the international fusion community has in proposing ITER as its next step.
Conceptual designs similar to ITER's, and with similar objectives, were earlier proposed by the European Community (Next European Torus) and Japan (Fusion Experimental Reactor) as national programs, now superseded by the international ITER. The US fusion research community has long agreed that a not-too-long-delayed ignition or near-ignition experiment is crucial for fusion development. There was support in the 1980s in the US for an ITER-style national machine, but there was more support for a nonsuperconducting short-pulse ignition physics experiment such as BPX (which, for budgetary reasons, ended up not being constructed). This line of development was again recommended in the recent study by the President's Committee of Advisers on Science and Technology, which proposed an international cryogenic copper, 100-second-pulse experiment, which could meet many ITER physics objectives at 40% of ITER's cost. In contrast to the views of almost all my ITER colleagues, this seems to me to be a very reasonable proposal, but not one that the US can expect to impose on its partners, who strongly prefer a design incorporating more technology, especially superconducting magnets, allowing 1000-second pulses, possibly steady-state operation, and high neutron fluence. This preference arises naturally, especially in the case of Japan, from a more urgent perceived energy need and a desire for nondefense-oriented joint government/industrial high-technology development.
I fear that Stix and Sessler have not come to terms with today's realities. With the US program now perhaps 15% of the world fusion program, probably slipping to the 10% level in the near future, we can no longer dictate the nature of the international fusion program. Rather, as suggested by the Fusion Energy Advisory Committee, we have to exploit and nourish our scientific strengths as best we can on our declining budgets by strengthening theory and computational efforts, exploring alternate fusion concepts and testing new ideas on existing facilities or modest new ones.[1] But, what is equally important, we must seek to contribute to and benefit from the crucial large experiments existing or being built (alas!) abroad. They include the JT-60 upgrade tokamak in Japan; the Joint European Torus, which, if desired, might be upgraded much more plausibly than US facilities to a short-pulse high-gain (Q = 5) experiment; the German and Japanese stellarators; Ignitor, should it actually be constructed (as I very much hope it will); and, of course, most important of all---ITER.
Stix and Sessler allude to a much-discussed hypothetical but quite plausible scenario in which Japan assumes the major financial role in constructing ITER, with US support at about its present level of 20% ($55 million) of the annual US fusion budget. Stix and Sessler oppose this as overreliance by the US on Japan's fusion program. To me, on the other hand, it would appear to be a wonderful bargain if for 5% of the cost we could participate in designing and experimenting on fusion's flagship experiment.
While preserving our scientific strengths with the non-ITER
75-80% of our fusion budget, we should also
After 46 years of effort and progress, the US fusion community should think very carefully before turning its back---for whatever reasons---on an internationally agreed upon experiment designed as the first exploration of the burning plasma environment.
Reference
1. Fusion Energy Advisory Committee, A Restructured Fusion Energy Sciences Program, US Department of Energy, Office of Energy Research, Washington, DC (27 January 1996). (back)
Our major purpose in writing the opinion piece above has been to stimulate vigorous open examination, here and abroad, of the technical and policy issues relevant to constructing the currently proposed ITER machine. At stake is the future of fusion-power research and the professional future for literally thousands of physicists and engineers.
We three authors all pursue a common goal, an optimal strategy for magnetic-fusion research. We agree on maintaining strong programs in basic plasma science, on exploiting existing facilities to address problems known to be critical for the operation of every large tokamak, on the dedicated exploration of both advanced tokamak scenarios and alternative fusion concepts, and on the strong desirability of near-term ignition or near-ignition experiments.
We disagree with Rosenbluth as he notes, over the manner in which limited resources should be distributed to accomplish our common objectives. We would place priority on the areas just cited and, at the same time, seek out new paths that would better employ the substantial international resources.
We are fully aware of the special interests of each partner in ITER and in no way do we wish to dictate international strategy. But we would be less than honest if we failed to reiterate our opinion, that the ITER step is too large and that the time to "first plasma" is too long: 12-14 years from now, not including a decision-making delay of uncertain length after mid-1998. Conservatism, both fiscal and scientific, demands that the fusion community move ahead prudently while keeping open its options for significant breakthroughs. Accordingly, we advocate a collaborative multinational fusion strategy that we believe will answer the most important magnetic fusion reactor questions more reliably, quickly, flexibly and cost-effectively than the currently proposed single ITER machine.
alpha channeling: Using plasma waves to transfer fusion alpha-particle energy directly to the ions. D-T fusion alphas, starting at 3.5 MeV, are normally slowed down by the plasma electrons, through multiple Coulomb collisions. (back)
blanket: Lithium-containing material that surrounds a reactor plasma and moderates and absorbs the fusion neutrons to produce useful heat and to regenerate tritium fuel. (back)
burn control: Maintaining the plasma parameters (temperature, density, composition and so on) in the desired range for sustained nuclear power output. See also profile control. (back)
disruption: A large-scale nonlinear magnetohydrodynamic plasma instability that destroys plasma confinement. (back)
divertor: A magnetic channel that directs plasma "exhaust" to a remote location. (back)
eddy-current heating: Heating induced in the superconductor conduits and cables in the course of external electromagnetic stabilization of the plasma's position. (back)
equilibrium burn: A steady-state balance of plasma heating, by fusion alpha particles and external power sources, against plasma heat loss by conduction, convection, radiation and so on. See also ignition. (back)
first wall: Those portions of the mechanical structure surrounding the plasma, including the vacuum-chamber walls, through which fusion neutrons will pass before reaching the blanket. (back)
gain: The ratio of total nuclear power output (including neutron energy) to the externally supplied plasma heating power. (back)
halo currents: Electrical current along a path that passes through portions of the plasma and surrounding mechanical structure. (back)
heat exchange: The benign transfer and use, for electrical power production, of heat from the nuclear reactions in the plasma. (back)
helium ash: Spent fusion-produced alpha particles that have lost their energy keeping the reactor plasma hot. They must eventually be replaced by fresh deuterons and tritons. (back)
ignition: When plasma heating by fusion alphas exceeds plasma heat loss. See also equilibrium burn. (back)
locked-mode threshold: The threshold at which a nonaxisymmetric perturbation may induce the nonrotating magnetohydrodynamic instability called a locked mode. (back)
magnetic shear: The derivative, in the direction of the minor radius of the plasma toroid, of the angular rate at which the magnetic field lines spiral as they circumnavigate the toroid. (back)
profile control: Maintaining the desired dependence of the plasma current and plasma pressure as a function of the minor radius of the plasma toroid. See also burn control. (back)
reversed shear: A change of sign of magnetic shear as a function of the minor radius of the plasma toroid. (back)
steady-state operation: Operation with approximately constant parameters on a time scale long compared to that of alpha-particle slowdown (less than a second) or that of penetration by magnetic perturbations deep into the plasma (a few hours) or that of thermal equilibration of the mechanical structure (many hours). (back)
strike plates: The plasma exhaust channel of the magnetic divertor terminates on what are called strike plates. (back)
wall erosion: Damage, by energetic plasma particles, to the strike plates or to tiles lining the vacuum-chamber wall. (back)
Andrew Sessler is a distinguished senior staff scientist at Lawrence Berkeley National Laboratory, in Berkeley, California. (Back to "No")
Thomas Stix is a professor of astrophysical sciences at Princeton University, in Princeton, New Jersey, and has been a staff member of the Princeton Plasma Physics Laboratory since 1953. (Back to "No")
Marshall Rosenbluth is a professor of physics at the University of California, San Diego, in La Jolla, California, and a member of the San Diego Joint Central Team of the ITER Engineering Design Activities. (Back to "Yes")