As support for fusion erodes, and the sponsor constantly asks more and more for less and less, the entire program becomes caught between the devil and the deep blue sea. What can we do which is both useful and affordable? The community seems to be coming together around the idea of proposing a low cost ignition experiment, for instance FIRE. The purpose of this web submission is to argue first, that putting such a large amount of resources into such an ignition experiment is a bad mistake, and second, that there is a much better strategy for the fusion program.

Ignition Experiments: Apparently there have been two small ignition experiments proposed, FIRE by Princeton, and IGNITOR by the Italians. I have only looked at the FIRE proposal, which I got from its web site. To start, I have no technical arguments with the proposal. As far as I can see, the authors did a professional and creditable job; I have no doubt that they have scoped out the project as well as anyone could have. If it were to be built, I am sure that, barring a major scientific or technical surprise, it would work about as designed.

My opposition is to the use of fusion resources for this project. First of all, it is not cheap. The cost is about $1B, or about $0.1B/yr for ten years. Since it is unlikely that congress will appropriate all of this in new $$; much would necessarily come out of the existing fusion program. Who volunteers? But it is really much worse. I am convinced that FIRE is a dead end project, little more than a stunt. The magnetic field is 100-120 kG. A tokamak with such a high field has virtually no possibility of extrapolating to an economical reactor. Also, probably because of the high field, there is no provision for heating with neutral beams, almost certainly the principal power source for a commercial reactor. Thus FIRE will teach us very little of what we need to know to operate a commercial reactor. Furthermore, its life is quite limited. Each shot will only be 10-20 seconds, and there will only be 3,000 of them. Let's say that FIRE is built, works well and is decommissioned in 2015 after its 3000 shots. When a sponsor then asks, what can fusion do for me now, we will have only one answer, nothing. When he then asks, how much closer to commercial fusion are we now, we will have only one answer, hardly any closer than we were when TFTR shut down. By this time, fusion will have been supported by the government for something like 65 or 70 years and the program will have produced nothing of value. How much patience can we expect sponsors to have? To me it seems clear that building an ignition experiment like FIRE for a billion dollars is a real squandering of scarce resources.

An Alternate Strategy for Fusion: Here I would like to consider an alternate strategy for the fusion project, the return to fission fusion. I have given a seminar on this in several national labs and universities and have published two papers on it [1,2]. To motivate this, let's see how the time scale for the implementation of fusion has evolved. As an adolescent, around 1955, I remember reading a Life magazine article predicting fusion powered rocket ships in about 30 years. Now jump to 1990 When Secretary of Energy Watkins commissioned the Fusion Policy Advisory Committee (FPAC) to report on the implementation of fusion power. They concluded that a commercial reactor could be built in 50 years, by 2040, assuming large fusion budgets and also assuming that the whole world cooperates. [To see this go to www.doe.gov > Sources and Production > fusion > FESAC > Report on Criteria, Goals and Metrics, Oct 1999] . Of course we have already lost 12 years from this schedule. Also, as far as I could see, nothing on the DoE web site now discusses implementation of fusion in the economy. From this I can only conclude that the DoE is thinking of an economic benefit from fusion occurring at best late in the century, perhaps not even until 2100. In other words, before fusion begins to make an impact, we expect it to be supported by the government for about 150 years, that is through about 5 or 6 generations of sponsors! Perhaps my mind is warped by dealing too much with military sponsors, but I just do not believe that any sponsor (or generations of sponsors) will have this kind of patience. It simply goes against human nature. I believe it is absolutely essential for the fusion project to deliver much sooner.

In considering how soon we ought to deliver, let's look at what world energy needs are likely to be. A simple fact is that by mid-century, the world will have ten billion people; all of them will demand a middle class life style. As a community we should absolutely reject the alternative, namely, that the majority of these people are condemned to live in poverty. This means a great deal of energy will be required. This concept has been quantified, (including considerations of CO₂ emission and efficiency enhancement) [3]. A simple, canonical number taken from Ref [3] is that by 2050, the world will need an additional 10 terrawatts of carbon free power. Thus under the current plan, fusion it is absolutely unable to make an impact on the crucial mid-century energy requirements. Below we give estimates of various world energy resources in terrawatt years[4]:
 
 

Source	Energy (TWyrs)
fossil	7500
coal	5000
oil	1250
gas	1250
mined uranium	60-300

Clearly for large amounts of carbon free power, not only is it likely that nuclear power will be required, it is also likely that breeding of nuclear fuel will be required as well. Since the mined uranium estimate is the energy content of the ²³⁵U, and breeding makes available the energy content of the ²³⁸U (or ²³²Th for the thorium cycle), it multiplies the available energy by more than a factor of 100.

Some fundamentals: Nuclear fuel can be bred via either fission of fusion. There are two cycles, breeding ²³⁹Pu from ²³⁸U, or breeding ²³³U from ²³²Th. The energy resource from the thorium cycle is about the same as from the uranium cycle. To eliminate the proliferation hazards of the raw fuel, we consider only the breeding of ²³³U which can be mixed with ²³⁸U in a subcritical mixture. A fission breeder has the advantage that the technology is here and now. However it has strong disadvantages as well. A fission breeder can typically supply itself and a single other burner. Also it must operate for a long time before sufficient fuel is bred. A fusion breeder is certainly not here and now, but it does have significant advantages if it could be made to work. First of all, there is almost no doubling time consideration. Secondly, each fusion breeder supplies roughly 10 burners. Thus there are many fewer fusion breeders than there would be fission breeders. Since any breeder (whether fission or fusion) is a proliferation hazard, it would have to be secured, with fences, guards, and the like. However in a fission fusion economy, only about 10% of the reactors would have to be secured, instead of half in a fission breeder economy. Thus for a thorium fusion breeder, only thorium enters, only a sub-critical mixture of ²³³U and ²³⁸U leaves. The reason a fusion breeder has this advantage is that each 14 MeV fusion neutron, in a well designed blanket, breeds about one triton and one ²³³U. However when the ²³³U is burned in a conventional burner, it releases about 200 MeV. Thus by going to fission fusion, we increase the fusion Q by about a factor of 15. In other words, fission is energy rich and neutron poor, while fusion is energy poor and neutron rich, a perfect marriage. That is, the fusion community and the fission burner community (if not the fission breeder community) are natural allies, not natural competitors.

Given this, can fusion contribute to mid century energy requirements? I feel strongly that it can. TFTR and JET have each generated 10¹⁹ neutrons in DT plasmas with 40 MW of beam injection in a one second pulse. The Q is about 0.5. However these machines have no average power capability. The essential next step, to my mind, is to dip our plasma physics buckets where we are, that is build another TFTR, (now with Q~1), but with average power capability in a DT plasma. Let's call this a scientific prototype. Now 40 MW of beam power generates 40 MW of neutrons. These 40 MW of neutrons then generate 600 MW of ²³³U. This could be used as nuclear fuel. While many plasma physics problems would have to be successfully confronted and solved in building such a device, equally important would be the nuclear engineering. It would have to be located at a nuclear facility, preferably one with a great deal of water and power, perhaps Oak Ridge or Savannah River. Assuming the typical 15 year life time of a tokamak experiment, then in 2018, when a sponsor asks what can the fusion program do now, we have an answer. We can generate 40 MW of 14 MeV neutrons. These can be used for a number of applications. I feel convinced that the best application is the breeding of ²³³U, but perhaps other applications would garner more support, perhaps transmuting nuclear waste from previous energy or weapons programs. In any case, with the scientific prototype, fusion would demonstrate a capability to actually do something useful and difficult, even if not yet economically relevant.

Let's estimate very roughly how much such a program would cost. CIT/BPX was proposed at $1.6B in 1991, and TPS was proposed at $0.75B in 1996. Since there is no requirement for ignition in the scientific prototype, the physics regime is less stressing than BPX, so we estimate the cost for the plasma physics as $1B. However there is also the nuclear engineering and materials research. If this costs the same as the device itself, the total cost is about $2B over about 15 years, or about $150M/yr. Let's say congress authorizes this program, but in a worst case scenario, tells us to take it out of our $250M/yr budget. We could (and should) do this. There would still be $100M/yr for other fusion research, perhaps 5 or 6 advanced concepts of small to mid size. Of course these would now include not only plasma science, but also nuclear engineering. For instance one of them might involve liquid or flowing liners. While it would be no easier to find volunteers than in the previous case of the ignition experiment, at least this path leads somewhere.

Where might it lead? If we think of a TFTR sized Q~1 tokamak as a scientific prototype, it is natural to consider the next larger, ITER sized Q~10 tokamak, but operated as a breeder, as a commercial prototype. Taking ITER estimates, we envision 150 MW of beam producing 1.5 GW of neutron power. However in a breeding blanket, this produces about 24 GW of ²³³U, enough to power 8 conventional nuclear reactors of 3 GW (1 GW electric power). Let us estimate the fuel cost. The ITER estimate is that the device will cost about $10B, or about $0.6/yr if amortized at 6%. The operating cost has been estimated at $0.5B/yr, or a total of about $1.1B/yr for 8 GW of electric power. This translates into a fuel cost of about a penny and a half per kilowatt hour as the fuel cost for a nuclear power plant. The cost of gasoline or oil, at a dollar a gallon, is just under three cents per kilowatt hour. Since these are occasionally used as fuels for power stations, this is a cost that power plant operators are apparently willing to pay for their fuel.

Let see how this plan might affect mid-century energy needs. We assume the lifetime of such tokamak experiments is about 15 years. Thus starting right away in 2003, the scientific prototype takes us to 2018. If this is successful, the commercial prototype takes us to 2033. If this is successful, the world builds several hundred or a thousand such fusion breeders to breed several terrawatts to ten terrawatts of carbon free fuel by mid-century. There is a real chance that the fission fusion hybrid can go a long way toward economically satisfying carbon free world energy requirements by mid-century. Even its the most optimistic proponents do not see how fusion alone can do this.

The above program seems to me like a much more sensible use of limited fusion resources than a small ignition experiment. This is doubly true where the Italians may well do an ignition experiment anyway. Let the Italians do the ignition experiment. In conjunction with an American breeder experiment, its impact could be greatly magnified. For instance their experience would surely help greatly as we move from the scientific to the commercial prototype. However we Americans should concentrate on cracking the really tough nut in fusion research, namely figuring out a way to satisfy mid-century energy requirements.

Of course for the world to accept nuclear power on this scale, it would have to be convinced that both the proliferation and waste problems were well in hand. Using the thorium cycle solves the proliferation problem, at least for the raw fuel. The waste disposal problem is much more difficult. If we need one Yucca Mountain for America's hundred nuclear power plants, then by mid-century the world will need some 30 to 100 Yucca Mountains for the proposed 3-10 TW of total nuclear power. However, as we see from today's headlines, getting even one Yucca Mountain is difficult enough. It seems as if transmuting at least the long lived radioactive wastes must be a part of the world's energy plan. Yucca Mountain will almost surely be a temporary repository, but the world's people will never accept the idea that we have created a plutonium or ²³⁵U mine which will last for millions of years. The cost of transmuting the long lived waste products will simply have to be added to the fuel cost. However this is the case of fossil fuel as well. If the world decides to meet its energy requirement with fossil fuel and CO₂ sequestration, this latter part will also have to be added to the fossil fuel cost. While transmutation is not our problem as fusion scientists (unless a fusion reactor is used for the transmutation), we should take a great interest in it and be strong advocates for it (but not pay for it with the fusion budget!!).

The problem of waste disposal illustrates the great advantage of a pure fusion economy over a fission fusion economy. In fact one of the strongest arguments for a fission fusion economy is that it can be a stepping stone to a pure fusion economy. With the experience of developing a fission fusion economy, a pure fusion economy may develop in the future. However this is not our decision to make. Unquestionably the people to decide this will live in the future, in fact they are at least 50-100 years from even being born! The development of a fission fusion economy in the next 50 years may be the best way we can help these future generations switch to a pure fusion economy.

References

1. W. Manheimer, Fusion Technology, 36, 1, 1999
2. W. Manheimer, Physics and Society, 29, #3, 5, 2000
3. M. Hoffert et al, Nature, 395, 881, 1998
4. Nakiecenovic, Grubler, and McDonald, Global Energy Perspective, p.52, Cambridge University Press, 1998