Fifteenth International Conference on Plasma Physics
Seville, 26 September - 1 October 1994

Mr. Chairman, ladies and gentlemen,

It is a great honour for me to give the Artsimovich Memorial Lecture at the IAEA Conference on Plasma Physics and Controlled Nuclear Fusion Research. This is already the 15th conference in this series and ninth lecture devoted to the memory of Academician Lev Andreevich Artsimovich. Just this fact by itself already gives us some impression of the time-scale of research on controlled thermonuclear fusion, a problem of unprecedented complexity but also a problem whose eventual solution will have a tremendous impact on the future of humankind.

I have also a more personal appreciation for this time-scale: in September 1960, just 34 years ago, I first entered the gate of Kurchatov Institute. Though during the subsequent years I had many opportunities to meet Lev Andreevich (let me refer to him in this traditional Russian way, with a patronymic) personally, I and the people of my generation were, of course, relatively distant from him. None the less, what we could immediately feel at the institute was the vast effect of his personality on everything going on there. His brilliant scientific talks, the sharpness of his spontaneous remarks on scientific and non-scientific subjects, the touch of artistic insight that he brought to whatever he did, dimension of this unique personality. The experience of talking to him, for us young people, despite the harsh criticism we might sometimes hear, was always inspiring and elevating.

I am going to devote my talk to the role of innovations in fusion research. More specifically, I am going to discuss the role of technology breakthroughs, in their interplay with new physical ideas and in the progress of fusion research. I shall also make a few broader remarks on the role of creative inventiveness in our endeavour. At the end of my talk I shall take some time to discuss the problem of resource limitations. My talk today echoes the following remark made by Lev Andreevich in 1962:

"The problem of controlled thermonuclear fusion belongs to

the border region between science and technology which

can be called 'scientific invention.' When we survey the

work on nuclear fusion as a whole we find that new ideas

born in the creative imagination of inventors are

intermingled with the results of theoretical experimental

research on plasma physics..."

Indeed, the interaction between physics and technology in fusion research has always been very strong. Quite often our activity was a stimulus for major technological developments. A good example is the tokamak concept. When Sakharov and Tamm put forward this idea in the early 1950s, they conceived a device with a deuterium plasma, water cooled copper magnets and, of course, without neutral beam or radiofrequency heating or current drive.

As a principal means of avoiding the loss of toroidal equilibrium, they considered a current in a levitating coil. A plasma current was considered as a secondary option. Let me quote from Sakharov's 1951 (then highly classified) paper on that issue:

"A second method of antidrift stabilization, which is

technically much more admissible and which it is therefore

necessary to examine carefully, is the formation of an

axial current directly in the plasma by the method of

induction. It is not clear if, in using this method, the high

temperature plasma is not destroyed at the moment when

the induction current vanishes."

From the present viewpoint, this device looks absolutely impossible--there are so many ingredients missing without which the ITER type tokamak just cannot work! Like many other concepts, this one was really born as an 'ugly duckling', a metaphor already used once in this context by Academician Velikhov. But still, the work began, and gradually researchers came to recognize the desirability of non-ohmic heating and, later, of current drive systems. They also recognized the necessity, on the one hand, and feasibility, on the other , of superconducting windings. And, with a certain pressure from and direct involvement on the part of the fusion community, all these technologies have been developed at the industrial level. The tritium breeding blanket is yet to come.

One of the lessons which we can learn from this example is that, even if the technologies that are required for the realization of some sound physical idea do not exist at the moment when the idea is born, it does not mean that this idea is not worth pursuing (at least at a modest experimental level).

I have given examples of situations in which some new technologies were developed directly in response to the needs of the fusion community. In other cases the sequence of events was the opposite: the development of certain technologies initially unrelated to fusion research prompted the invention of new fusion schemes. Examples are laser fusion, light ion beam fusion and heavy ion beam fusion. the last two examples are particularly characteristic: these fusion schemes were absolutely unthinkable as late as the mid-1970s, but then, with the remarkable technology breakthroughs that occurred in just two or three years, they became a focal point of large research groups and institutions.

We should not forget the possible appearance of new ideas in physics itself, ideas whose realization does not require the development of any new technologies. In the past this was not a rare event. Remember the advent of non-circular tokamaks, the invention of tandem mirrors, with their further improvement by means of thermal barriers, or the recognition of the feasibility of a continuous mode for the reversed field pinch, based either on helicity injection or on self-sustained field reversal. This list could easily be extended. Though the extent to which these inventions affected the fusion programme was very different, I would say that, conceptually, they were of a comparable level. What is interesting and important here is that these improvements occurred decades after the emergence of the initial basic concept.

Why should we then think that nothing of a similar kind will happen in the next 40 or 50 years, the time which will be required, as is commonly recognized, for the broad commercialization of fusion energy? In fact, we can expect breakthroughs in any of three directions: the development of the technologies related to existing fusion concepts, the appearance of new technologies outside the domain of present day fusion research but prompting new approaches in that research and, last but not least, the invention of new concepts and/or conceptual improvement of the existing ones.

Let us consider just a few arbitrarily chosen (and highly speculative) examples illustrating the possible impact of new technology developments.

What if in the coming decades a new generation of robots were to be developed that were more intelligent and more resistant to radiation? This would probably allow a more frequent replacement of the reactor core and would raise the chances for compact, high power density devices, including compact tokamaks. A more frequent (say, once every two months) replacement of the reactor core would also considerably broaden the choice of candidate materials (as they would not have to withstand a fluence of 30 MW-a-m-2) and increase the probability of finding materials that become only weakly activated.

Development of small bore (10-15 cm), very high field choke coils would considerably improve the performance of some modern types of mirror device, in particular those that are being studied at the University of Tsukuba (Japan) and in my home institute at Novosibirsk.

If materials with improved thermonuclear properties appear, we might witness a new surge of interest in pulsed fusion devices, intermediate between magnetic and inertial confinement, with a plasma density in the range 1017-1019cm-3, a concept which at the moment looks like a lost child in our research programme.

It is impossible to confidently predict the form of the new ideas in physics, but why should we think they will not appear? And we should remember that most new concepts at the beginning do not look fully self-consistent and sometimes imply the use of non-existent technologies (remember the proposal by Sakharov and Tamm!).

In order to fully employ the potential amenability of fusion research to all kinds of innovation, it is very important to maintain the spirit of creativity and openness to these innovations within the fusion community. Otherwise the people who are willing (and able) to adapt the new techniques to the existing schemes and to invent new schemes prompted by technology advances will soon disappear from its ranks. One should recognize that fusion will remain a scientific research endeavour for at least three or four decades to come. Every possible effort should be made to pursue, along with the undoubtedly necessary and promising ITER project, some smaller scale activities on the non-tokamak magnetic confinement concepts and unconventional tokamaks. Continuation and expansion of the inertial confinement programme are also very desirable in this respect. This atmosphere of openness will make our activity more attractive for creative young people.

We should resist the temptation of eliminating prematurely one or another non-tokamak fusion concept. A good example in this sense is Lev Andreevich's attitude to the problem of whether to continue or abandon stellarator research, a question that was the focus of heated debates in 1969-1970. As is well known, stellarators were not doing very well in those days, and Lev Andreevich himself was strongly committed to tokamak research, which had received a big boost from the temperature measurements made by the British group of fusion researchers on the T-3 tokamak at the Kurchatov Institute. However, as he was a broad-minded person, with a clear understanding of the time-scales and uncertainties to be faced by the fusion programme, he acted in favour of continuing stellarator research. In order to raise the spirit of stellarator researchers (at least in the Soviet Union), he even made a comment that the issue of understanding the reasons for poor stellarator performance and possible ways for its improvement was an issue of their "scientific honour." He gave his support to the project of the Liven stellarator at Lebedev Institute. The 25 years that have passed since these discussions have clearly shown, especially in the recent experiments of our German colleagues, the interesting potential of the stellarators as fusion devices and the rightness of Lev Andreevich's vision.

I believe we should recognize that still existing non-conventional devices, especially if they are operated by qualified and experienced groups, are a very valuable asset of the fusion programme. They could quickly accommodate new ideas related to their physics and thereby save considerable resources that would otherwise be required to start from the very beginning. Maybe the time has come to prepare a 'Red Book of Fusion' that would include the experimental facilities representing endangered and nearly extinct species and provide them the necessary protection.

The feeling that we should look for something better than what we have at hand now is rather widespread among fusion physicists and engineers. And it would be a challenging (but rewarding) task for our administrative leaders to find the forms of organization which would allow the great potential of these groups and individuals to be fully and peacefully realized in the interests of the fusion programme.

I would think that some organizational framework could and should be created at both the national and international levels. This could be done on the basis of the large national research centres. Concrete forms are yet to be developed. I have found very encouraging the initiative of the Lawrence Livermore National Laboratory (which I am currently visiting) in this direction.

Creative spirit and fantasy are required in administrative activity, probably not less than in physics itself. And Lev Andreevich, who was a very successful administrator, liked to emphasize the importance of this component for successful management. I am sure that, as has happened many times in the past, this part of the problem will also be solved to the benefit of fusion.

If anyone perceives any 'antitokamak' stance in my talk, this is a gross misunderstanding. I think that it would be suicidal for the fusion programme to do anything that would undermine the ITER project or slow down the research on the conventional tokamaks and large inertial fusion devices. I just think that a reasonable breadth of our research is equally important.

Here we come to the problem of resource limitations. What makes our task of raising funds for our research more difficult is the remoteness of the final goal. However painful it might be, we have to recognize that the first commercial fusion reactors will not appear earlier than in 2030-2040. But in fact, 30-40 years is not a time-scale in which the present generation is uninterested. When people of the age of 20-30 make investments in their homes, in the education of their children, and in health and retirement programmes, they clearly show that they are seriously interested in what will happen 50 years from now. So we just should work more actively, more creatively, on the education of the public and the policy makers. This will not be mere propaganda: there are so few alternatives to the burning of carbon based fuels! We just should make our case more clear. And this is a task not only for the management of the programme but for every one of us who feels that he or she can contribute to this process. The results will not appear immediately--education is a slow process. And we should understand that this effort is as important to us as doing our everyday experimental or theoretical work. Those who are working on or are going to build large fusion devices should be particularly concerned with this problem, as their facilities are very expensive.

In this sense, a better education of the fusion community itself in the related environmental issues, the potentials and the hazards of the competing energy technologies, the views of the utilities, etc., is highly desirable. Probably, large national research centres could again take the lead, providing some compact lecture courses for their fusion scientists and engineers to give them the necessary initial information.

Before I finish, let me give one more quotation from Lev Andreevich:

"The tremendous importance of the ultimate goal and the

enormous difficulties that lie in the way combine to stamp

the problem of thermonuclear fusion with a quite

distinctive character. For the time being we find ourselves

as it were on the dividing line between dream and reality.

It is this that brings an element of emotionalism into the

study of this problem -- the succession of hope and

despair, the searching doubts followed by assurance of

success."

I think these words very precisely describe the spirit of our work. Let me finish with my best wishes for the success of this conference and of your future research.

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