Douglas R.O. Morrison's Cold Fusion Updates
No. 12—October-December 1996 + January 1997

Back to Morrison Index

(Source: New Energy Times)


The Sixth International Cold Fusion Conference, ICCF-6 took place! It was generally considered more scientific than its predecessors. It was held in Japan, well supported by Japanese organisations. Reports were given on three major Japanese experiments which were well-funded, technically excellent and carefully carried out - all three gave no indications of cold fusion. This shows once again that Japanese science done seriously with governmental support, does excellent work. It is said that government funding for cold fusion is being wound down. Despite this, the Summary Speakers, Bressani and McKubre, gave encouragement to cold fusion. The new frontier of the conference was transmutations with remarkable results that may have conventional explanations. Despite everything, a Seventh conference is planned. Post-scripts; The Siena experiment that claimed steady heat production, has been repeated but it has not been possible to justify the fusion claims and it is concluded that there is no power production. Two other important experimental results suggesting axions and a high H/D ratio, have been shown to be due to mis-interpretation of data - the way in which the scientists concerned behave is contrasted with some involved in cold fusion.

1. Introduction
2. Major Japanese Experiments on Excess Heat
3. Japanese Study of D-D Reaction Rates in Metals
4. Summary of Nuclear Products - Bressani
5. Summary of Excess Heat Experiments - McKubre
6. Transmutations
7. Studies of Material Science
8. Who am I? Who Pays me?
9. Court Case - La Repubblica versus Drs. Preparata, Bressani, Del Giudice, Fleischman, and Pons
10. Next ICCF Conference.
11. Short Notes -Preparata experimentalist/London theatre/Texas conf./Glow discharges/CETI/Siena bomb/Tom Droege/Error and fraud
12. Please Can I Have a Cup of Tea?
13. Conclusions
Post-scripts; (1) "Siena Bomb" Not Confirmed by New Experiment
(2) Other Wrong Results Disproved - Axions, H/D ratio
Appendix - Neutron Claims of Bressani et al. Critically Examined


The conference was sponsored by The New Energy and Industrial Technology Development Organisation, NEDO, which was set up by MITI as a branch of the Institute of Applied Energy. They have built a laboratory to study cold fusion in the Techno Park near Sapporo in the northern island of Hokkaido - it is called the New Hydrogen Energy lab, NHE, thus avoiding the words "cold fusion". Some $ 30 million was given by MITI over four years and this is fast running out. The basic research is being carried out by the government together with some 20 private companies (generally major ones), and 11 universities at 13 labs.

A second major organisation is IMRA which was set-up by the Toyota car company. They have two labs, one in Hokkaido and the other in the Sophia Antipolis Science Park near Nice where Stan Pons works.

This Sixth Conference was again held in a beautiful luxury hotel as in Monte Carlo and in Maui - why? Can only guess. The hotel has a golf course and two ski areas - was told it was only finished four years ago and is now almost bankrupt.

Of the 183 participants listed (some 250 actually attended), half, 91, were from Japan and 37 from the USA. Dr. Scaramuzzi once declared that "Cold fusion stops at the Alps", but now it is more accurate for Europe, to say it only appears in Mediterranean countries (Italy had 15 participants, France 6, and Spain one).

Cold Fusion Update No. 10 was Part I on the previous conference, ICCF-5. Update No. 11 should have been Part II, but only sections B1 to B5 were written due to lack of time. Section B4 is included here as a Short Note and section B5 is given as an Appendix.


2.1 Results from the New Hydrogen Energy Lab of The Institute of Applied Energy

Dr. K. Matsui, the Conference Organiser, described the Lab and said that faint proof of excess heat was not enough. The aims of the lab were to search for a strong proof of excess heat, to demonstrate the mechanism, and obtain controllable power generation.

Dr. Kubota said that previously with a fuel cell-type electrolysis system, 7 to 18% excess heat had been observed but the reproducibility was poor - a problem with this type of cell was that if the parts moved during assembly the calibration was lost. Hence they had adopted the mass flow calorimetry system developed by the McKubre group at SRI. Here water is made to flow through the cell and measurements are made of the input and output water temperatures and of the flow rate - here the calibration was more reliable. It was found that the three sigma limits were between 0.9 and 1.6%. So the limit for declaring a heat excess was taken as 2% which corresponded to 0.2 W out of a total input of 10 Watts. Palladium samples with various treatments were tried including some that had previously given excess heat with the old type of fuel cell. In all ten experiments performed, no excess heat was observed.

After the conference, some participants visited the nearby NHE labs - Melvin Miles and some friends, estimated that in the three large research rooms, there was some $10 million worth of equipment.

2.2 Energy Results from IMRA(Japan)

Dr. T. Nakata of IMRA (Japan) reported that after their earlier work with closed fuel cells which sometimes showed excess heat, they developed a new type of cell with mass flow. Water flowed through the top of the electrolytic cell and its input and output temperature were measured. An important new feature was that all the apparatus was immersed in a tank of water which was kept at constant temperature. A heater was used so that the total heat input was constant. In other words, the input was always 10 watts and if excess heat had occurred, then the heater's power would be reduced to keep the power at 10 Watts. This is the best and most accident-free type of calorimeter since there is no change in the heat transfer with the outside.

Twenty-six experiments were performed with palladium cathodes which had been treated in various systems to try and improve the amount of deuterium in the palladium (the loading). Some of these systems employed various treatments of the surface. In others the current was varied to load and deload the deuterium in the cathode. Distributions of the excess heat observed were shown giving clear Gaussian distributions with three standard deviation values of +/- 0.23 Watts or 2.3% of the input power. In all the 26 experiments, no excess heat was observed.

2.3 Results from IMRA(Europe)

The previous conference, ICCF-5, was held in Monte Carlo next door to the IMRA(Europe) lab near Nice. Everyone expected some results from them and a visit to the IMRA laboratory, but to our surprise, it was closed and no results were given. This time Dr. S. Pons reported that a new calorimeter called Icarus 9, had been developed. It was designed to operate at high powers, 300 to 400 Watts, and high temperatures up to the atmospheric boiling point. In three experiments excess power of 101, 73, and 75 Watts (150, 2000, and 80%) were observed while in four experiments no excess power was observed.

2.4 Comparison of the two IMRA Results

At the end of Dr. Nakata's talk, I asked why his results were different from those of IMRA Europe - no answer was given by him or by anyone from IMRA Europe.

The essential point is that when excess heat has been claimed, the heat loss from the system to the outside is poorly known, as shown by Wilson et al.1. With the IMRA(Japan) calorimeter, the water jacket surrounding the cell is kept at constant temperature so that any heat exchange with the outside is constant. With the IMRA(Europe) calorimeter, as the temperature changes up to boiling point, the heat flow to the outside must vary substantially and the calibration becomes critical. Instead of employing calculations and some doubtful controls, it is good standard experimental technique to use an external water bath at constant temperature, as IMRA(Japan) has done, but IMRA(France) has not.


Dr. J. Kasagi et al. of Tohuku University reported important results on what happens when low energy deuterium ions are fired into metals saturated with deuterium. The ion beam could extend down to about 3 keV giving results at lower energies than previously. Excellent experimental technique was employed for the lowest energies where the rate is exceedingly low due to the potential barrier. Three major (and interesting) experiments were performed.

Before cold fusion, all experiments (including muon-catalysed fusion at zero energy) had found that the reactions d-d ---> 3He + n and d-d ---> t + p had each 50% of the total rate, while the reaction d-d ---> 4He + gamma was negligible, about 10-7 of the other's rate. Here the charged particle spectrum was measured and peaks corresponding to 3He, tritium and proton emission were observed. As expected the ratio of tritium to 3He production was close to unity, showing that the ratio of tritium to neutron production is one, contrary to claims by cold fusion believers that in metals the ratio was 105 to 108.

Secondly, the protons emitted in the dd ----> pt reaction, were measured. After correcting for the potential barrier, the astrophysical S22 factor was obtained. It was found that at the lowest energy, the rate increased, by 10% for Ti metal and about 30% for Yb. Expressing this as an electron screening factor, Ue, values of 19 +/- 12 eV and 60 +/-10 eV were found for titanium and Yb respectively - they said these are higher values than expected - and a CERN expert confirmed these were very high. If confirmed, these results could have importance for the problems of the Standard Solar Model where the screening factors are poorly known and indeed this uncertainty constitutes a major source of error in the determination of the solar neutrino flux which may be different from the measured flux.

Thirdly, they investigated claims of abnormally high energy alpha particle emission. Firing energetic deuterium ions at Pd loaded with deuterium they observed an abnormal number of alpha particles with energies between 12 and 17 MeV. They proposed an explanation. First the reaction d + d ---> 3He + n occurs with a Q of 3.27 MeV. The 3He moves a short distance and interacts with another deuterium ion giving an alpha particle according to the reaction d + d ---> alpha + p with a Q of 18.35 MeV. Combining these two reactions together, it would appear as the three-body reaction, d + d + d ---> a + p + n with a Q of 21.6 MeV, but really it is two successive reactions. This experiment was performed with several metals such as Ti, Zr, Au, Pt.

These results clearly show that there is no indication of a strong rise in the rate towards zero energy as would be expected from cold fusion claims, but they demonstrate the very steep decrease in the rate as the incident energy decreases as expected from the potential barrier. Further they confirm that the branching ratios of the 3 reactions are constant with decreasing energy and there is no sign of the dramatic reversal claimed from some cold fusion experiments who write that neutron and tritium production are negligible while 4He production is dominant. Normal branching rations have already been found in muon-catalysed fusion which is at close to zero energy.


4.1 Bressani Review Talk

Dr. Tullio Bressani is a senior and respected figure in his world of low energy particle physics.

The summary of the important subject of nuclear products was allocated a 20 minute talk by Dr. Bressani. There was no possibility for questions or comments afterwards. It was a most remarkable talk, so to try and be fair, will give first the main points without comment apart from indices, a, b, c, etc. These indices will then be commented on. Finally, as an Appendix, a note is given about his five standard deviation measurements of neutrons having exactly the right energy, written after ICCF-5. This note was discussed extensively with Tullio.

He started by saying there were two problems; (1) Reproducibility, (2) the nuclear origin of the excess heat.

At this conference, there had been no solution for the problem of lack of reproducibility but progress had been made on the nuclear origin and it had been shown by different groups at different labs that excess heat did have a nuclear origin(a).

Fleischman and Pons(b) had shown that production of neutrons and tritium was lower than expected from the amount of excess heat, by a factor of 108 to 1010.

Over a hundred labs had tried to measure neutrons and tritium(c), but the solution has only come lately from measurements of 4He.

He listed about 7 experiments which included Isagawa of KEK (d), Yamaguchi(e), Miles(f), and Gozzi(g).

He described the experiment by Gozzi et al. as the best of all.

Yamaguchi's work at NTT was reported in 1993.

Dr. Isagawa at KEK obtained 4He when the Pd was heated - they had doubts but the apparatus was young yet. For neutrons , there was a weak correlation of two standard deviations.

He mentioned others (Okamoto) briefly.

Dr. Bressani concluded that the energy released is of a nuclear origin(h) from the reaction d + d ----> 4He + g (1)

The claims of Fleischman and Pons were correct(b).

The future of 4He lies with quadrupole mass spectrometers, QMS.

A workshop should be organised on 4He production.


(a) To say in a hand-waving way that some nuclear products have been detected does not justify claims of watts of excess heat coming from that reaction. In Science it is necessary to have the correct numbers. Thus if the origin of the excess heat is a d-d reaction giving 4He, then from the reaction (1), the gamma must have 24 MeV and for one watt some 1011 gammas of this high energy and 1011 ions of 4He should be produced. But the numbers from the experiments do not give these yields of 4He. Further if 1011 gammas of 24 MeV were produced, they would give a large number of other nuclear products - and Dr. Bressani also did not comment on the absence of such high energy products.

(b) Dr. Bressani seems to have forgotten the scandal of the F&P neutron measurements which is well-documented e.g. in Frank Close's book. After the 23rd March 1989 press conference, on the 28th Fleischman gave a talk at Harwell where he showed a plot of gammas produced with a peak at 2.5 MeV as would be expected from simple calculations, the two reactions in series ;

d + d ----> 3He + neutron (2.45 MeV) (2)

followed by the fast neutron interacting with protons in water bath giving

neutron(2.45 MeV) + proton ----> d + g(2.5 MeV) (3)

The agreement with this calculation seemed wonderful, but people at Harwell immediately pointed out that such fast neutrons barely interact and that in fact, the neutrons are slowed down, and when at rest are captured by a proton to give the well-known gamma of 2.2 MeV via;

neutron(zero MeV) + proton ---> d + g(2.2 MeV) (4)

Two and three days later, Fleischman gave talks at Lausanne and CERN resp. where he showed a modified graph with the gamma peak now at the correct value of 2.2 MeV.

Later the man who made the measurements wrote to Pons and others saying there was definitely no peak at 2.2 MeV. There was a miserably small one at 2.5 MeV but he thought it was an electronic artefact

It is not too clear, but it seems that Fleischman has withdrawn both the neutron and tritium measurements, so it is surprising that Dr. Bressani says that the F&P results are confirmed.

(c). In discussing the neutron and tritium results, a neutral reviewer would have said that there are more null results than positive results; and would have added that the positive results disagree numerically with one another.

It is surprising that Dr. Bressani did not mention his own results which claimed to observe neutrons with a peak energy near 2.5 MeV in agreement with reaction (2), and further that this effect was very significant - five standard deviations. Could this unusual modesty of a scientist with decisive results have anything to do with my conversations with Dr. Bressani described in the Appendix which showed that his results do not justify his claims?

(d). It was a surprise to hear the KEK experiment of Dr. Shigeru Isagawi described as supporting cold fusion as this was not his interpretation. In preliminary experiments it was found that the 4He observed could come from contamination. With improved experimental equipment no 4He was observed from the gas when the Pd was heated to 770 C. When the furnace temperature was increased up to 1180 C, large amounts of 4He were observed but the stainless steel of the furnace body had become permeable to gases so no conclusion could be drawn. It is hard to understand how Dr. Bressani could consider this as satisfactory for evidence for 4He production in cold fusion.

An experiment2 has now been performed with new equipment which is leak-proof up to 1200 C. No 4He production was observed although there was boiling several times. This apparatus has very high resolution and can detect down to 7 ppt of 4He. Previously they had also looked for 3He and found none.

(e). On the first day of the ICCF-3 conference in 1992 at Nagoya, Nippon Telephone and Telegraph company, NTT, announced that the problem of cold fusion has been solved in their labs by Dr. Yamaguchi. At that time NTT had the largest share capitalisation in the world. Their shares increased in that day by 8 billion dollars, but within a few days had returned to normal. Dr. Yamaguchi's work has been widely criticised because he operated his mass spectrograph outside its working range. In addition at Nagoya he was asked if he had glass in his apparatus and replied "No" - later he retracted and admitted he had glass. Ever since Paneth and Peters claims in 1926, it has been well known that large amounts of 4He are stored in glass but are released when hydrogen is passed over the glass.

After Nagoya, Dr. Yamaguchi did not stay long at the NTT laboratories but went to IMRA in the South of France - neither he nor anyone else at NTT has reported at any ICCF meeting any later work supporting the 8 billion dollar share peak.

(f). The work of Miles et al. has been very controversial and strongly criticised. From his talk it was not clear if he had done any new experiments to answer his critics - his talk appeared to be a repeat of his controversial results (privately was told that his funding has been stopped). He claimed to be able to answer his critics, but they seemed to be talking of somewhat different aspects of the work.

(g). Dr. Gozzi gave the opening talk at the ICCF-6 meeting. Since 1989 his chemistry group at La Sapienza in Rome has been trying to establish a correlation between excess heat and nuclear products. Initially they proved that the neutron and tritium channels are of "very low-probability". At this meeting they claimed to have observed excess heat, 4He and X-rays. The X-rays were observed using an X-ray film and from an analysis of the spots it was deduced that the X-rays had an energy of 89 +/- 1 keV, a remarkably accurate value to derive from spots. Also one expects characteristic X-rays of about 24 keV from Palladium but these were not observed. It was suggested that X-ray film was a poor way to detect and measure the energy of X-rays to which Dr. Gozzi replied that they were a poor group and could not afford modern apparatus, but I replied that Steve Jones had made miniature X-ray detectors which could easily fit inside anyone's apparatus - he had offered it free to anyone but said that Dr. Oriani was the only one to accept his offer.

Dr. Gozzi concluded that the 4He channel "is not the principal source of energy being about 0.5% of the energy measured by calorimetry". Dr. Bressani did not mention this very important statement or comment on the continuing mystery which is in contradiction with his conclusion.

(h). If the excess heat claimed is of a nuclear origin, then the rate of nuclear reactions should give the same power output - but Dr. Bressani did not make it clear in his review that this essential condition had not been met. Another important aspect that Dr. Bressani did not bring out, was the branching ratios. At this conference, the Tohuku group has shown that the branching ratios are as expected for neutrons, tritium, 3He, and protons contrary to the True Believers claim that they are suppressed relative to 4He. Also from the zero energy muon catalysed fusion data, the branching ratios are normal down to the lowest energy. So the 4He channel is suppressed - by a factor of 10-7 and there is no evidence that it could become dominant.

4.3 Conclusion

It is the duty of a reviewer to present all the evidence - this did not happen here. Looking at all the results, the overall conclusion must be that the balance evidence argues strongly against cold fusion giving nuclear products.

One might be surprised that a physicist of Dr. Bressani's seniority could give such a talk. At ICCF-5, he had stated very strongly that his Turin experiment had observed a peak of neutrons at exactly the expected energy of 2.5 MeV, and this evidence was significant at the five standard deviation level. For the Cold Fusion Update No. 11, the paper was studied and it was found that the data did not justify this claim - indeed the data suggested that there was something wrong with the experiment. A draft of the Update was written and shown to Tullio and discussed with him. Later there was a second discussion where he concluded essentially, "I do not agree with you but you are free to publish". However he did not disagree with any specific statement in the draft. This draft is now given as an Appendix to this update where it can be seen that there is no clean peak at 2.5 MeV and there are significant deviations at many energies indicating that there was an experimental or analysis problem.


5.1 McKubre Review Talk

Mike McKubre had also 20 minutes to summarise his allocated subject of excess heat. He listed three points;
a) He drew a smiley and said he was pleased with the results of the conference
b) He said there were a number of positive things - there was a fever of enthusiasm linked to a seriousness of purpose.
c) Existence - he listed and awarded ticks to;
Nuclear products - two ticks - 4He, 3He and tritium
Heat - one tick - more than 20 groups find it
Transmutation - one tick - a wild card. If it holds up, it will dominate future work.

He said that for tritium, Ed Storms had presented the work of Tim Claytor at Los Alamos.

For heat there was a robust mass of observations.

d) Reproducibility - has not been achieved. It was "Important but not enabling".

For electrochemical heat - for mass flow calorimeters there was a problem(a).

The IMRA(Japan) work was probably the most systematic attempt to explore the input variables with 32 experiments - which gave no excess heat.

The New Hydrogen Energy, NHE, labs of IAE and MITI, have an exquisite calorimeter, beautifully engineered. My notes show that Mike said they had no results, but their abstract says "10 flow calorimetry experiments have been performed until April 1996. Excess heat is not yet measured by the flow calorimetry system." In Dr. Kuota's talk, no comment was made about any experiments being performed in the period April - October though most people do extra hours before a conference in their home country.

For Mike's SRI lab, he said that there had been lots of null results. (Earlier during his talk, Mike had said that during the poster session he had deliberately carried out an experiment to see if people really looked at the posters. He had shown one graph where there was a negative heat pulse and waited to see if anyone noticed it. He said that Morrison was the only one to notice - "You have watch these people, they pay attention". He did not explain how this pronounced negative heat burst could have been produced).

Dr. McKubre declared that mass flow calorimeters were the most sluggish of animals(a). It is better to pass series of current pulses through the cell.

Fleischman and Pons load a cell, raise the temperature and find excess heat.

The electro-migration effect helps loading and should be explored (i.e. also add an electrical field).


(a). Dr. McKubre and also Dr. Celani, said that the mass flow cell is sluggish - hinting that one needs a dynamic change to obtain cold fusion. This shows a fundamental misunderstanding of the mass flow cells of NHE and IMRA(Japan) which found no excess heat. The point is that one can make sudden and dramatic changes to the cells themselves - it is only the outer system which is stabilised, not the inner cell. But if this sudden change causes excess heat, then that will be measured and recorded. To say the cell is sluggish is incorrect - it sounds like an excuse.

Mike McKubre has a good reputation among True Believers as a scientist because he occasionally says things that, in the mouth of others would be taken as a criticism of cold fusion. And if asked will answer even if the reply is not in favour of cold fusion - but if one does not ask, one does not learn. For example, he has in the past claimed some 30% excess heat, but if asked, he admits that this is only during a rare burst. Also if one asks what is the excess of "heat out" over "heat in" taking the entire run, he will say that it is of the order of 1%. Now for running a power plant, it is this last figure of 1% which counts, not the 30% burst. This also raises the question of whether there could be a long term drift.

When Mike says there is a problem with flow calorimeters, maybe the problem is that they are better than previous ones which used calculation instead of measurement to make corrections for outer heat flows. So his problem with flow calorimeters with stabilised jackets, is that they are good and find no excess heat. But there was a reluctance to draw the obvious conclusion that from the good experiments such as the recent Japanese ones, there is no cold fusion.


At ICCF-3 in Nagoya, a new front was opened when some people started to claim transmutation of elements. The first to tell me of this was John Bockris who claimed with his associate, to be able to produce gold - the alchemists dream! They had some later legal and academic problems with this. However others claimed publicly to have produced transmutations but the evidence was not taken too seriously by relatively responsible Believers.

At this meeting, a sensational paper was presented by George Miley who claimed to have observed "massive transmutations". George is a well-respected fusion physicist who has in recent years, been best known as editor of the journal Fusion Technology. Until 1989 this journal published hot fusion papers but then added cold fusion papers, many of which were quite wild - but the hot fusion people continued to publish in this journal.

This paper of 14 pages, is the main item in the glossy journal "Infinite Energy" that is published by Gene Mallove. Mallove, Rothwell and Tinsley describe it in rapturous terms "At least as important as the discovery of nuclear fusion fragments in the 1930's - probably much more so", and "This is a remarkable turning point in the history of cold fusion". That is what happens with non-scientists who do not check.

At the University of Illinois, Urbana, they used the Patterson-type cell which is being marketed by the CETI company (Clean Energy Technologies Inc.). This has a large number of very small beads with an exceedingly thin layer of a metal - here nickel - and the electrolyte flows over them. They claim to confirm the observations of Patterson to observe excess heat for long periods. They claim to have observed heavy and light elements deposited on the beads e.g. Si, Mg, Zn, Cu, Ag, Pb by using Secondary Ion Mass Spectroscopy, SIMS, and Neutron Activation Analysis, NAA.

At first sight, it looks impressive. I was asked several times my opinion and said that if there was one unexpected result, then it was worth looking at it, but here there were so many contradictory miracles, that it was hard not to doubt it.

Recently Richard Blue has studied Miley's paper and found a large number of obvious discrepancies as soon as you look carefully at the mass spectrum from SIMS and at the table of results. He posted this on the net. I checked by magnifying the spectrum, and agree with him.

Essentially the isotopes in the spectrum have possible natural sources. Thus elements in glass such as silicon, have been transferred to the beads; and the titanium isotopes in the spectrum would be expected from the titanium electrodes, etc. In addition some isotopes have been omitted from the table of results although clearly visible in the spectrum. Overall the elements have the natural isotopic abundances contrary to the claims made.

It would be polite to say it is simply sloppy work and even worse analysis.

The analysis was so poor that it hardly seems worthwhile to add that the experiment was done with light water, H2O and not D2O. Dr. Preparata would not have approved! - see section 11.1.

George is such a pleasant character and sounds genuinely puzzled and worried when you talk with him, that when he sits down and studies Dick's comments, I would expect him to retract.

Note added later. Have been having an exchange of Email with George and also asked Richard Blue to send him his comments. Regret to say that although I tried to make the issues sharp and clear, do not feel that I have had a satisfactory answer to any question - usually it was another subject or theory that was brought up. Guess that George is now a True Believer. Also his work fulfils several of Irving Langmuir's six criteria for Pathological Science.

More recently, further analysis by Richard Murray and Jim Carr have shown further major problems with the results and analysis of Miley. Perhaps the kindest thing would be to quietly ignore this work as one does Bockris's claim to transmute mercury to gold.


For many years the irregular and irreproducible results on excess heat and nuclear products have been explained away by saying that there are other unknown factor(s). This could be solved if only the material science of hydrogen isotopes in palladium and other metals was better understood. Further it was said that excess heat only occurred with a high D/Pd ratio (loading). Again at this conference Mike McKubre showed results indicating that a high loading, up to 0.95, had been attained but not for long, often the loading would decrease suddenly, in minutes. He declared that if only they could have high loading, and high current for a long time, then constant excess heat would be possible. This high loading hypothesis has justified a target for many workers and has attracted funding.

Many groups have devoted considerable efforts to seek this holy grail or at least, to understand the road to take. This is particularly true of groups who have once claimed to find excess heat, often in large quantities, but who since then, can never repeat their early result - now they study instead material science. Some of the results are very interesting, such as the group that made a transparent cell so that they could study the grain structure on-line. But no new major result has been found.

It is surprising that the people holding this philosophy have not studied the experimental results to see if they are consistent with this hypothesis. The highest loadings reported by regular cold fusion explorers is 0.96 obtained by the Senjuh et al. of the Japanese NHE group but they find no excess heat. The Los Alamos group of Tom Claytor used gas at only one atmosphere pressure so the loading was very low, about 0.5 replied Ed Storms - yet they claimed large amounts of tritium, in direct contradiction to the high loading hypothesis. Similarly the first claims of Drs. Fleischman and Pons to very large amounts of excess heat, up to a thousand times input, were obtained at various low current densities where the loading must have been very small. Later some experiments have been done at very high loadings, greater than unity, and no evidence of cold fusion was found - these very high pressures were obtained with a diamond anvil, and by ion implantation.

Thus this high loading hypothesis is not supported by the totality of experiments. Let us consider another hypothesis - the "No Cold Fusion Hypothesis". Here two major results are noted.

Firstly when palladium is exposed to high currents, it is found that the material changes, becoming black and cracks appear. With electrolysis, the surface becomes covered with "crud" which has been studied by several groups. This surface layer can slow deuterium ions entering or leaving the palladium. Sometimes the surface breaks off and exchange of deuterium with the outside becomes possible. Thus it is not surprising that short term effects occur which can have the appearance of excess heat bursts. In fairly careful experiments, such as those by the SRI group of Mike McKubre, such short bursts give excess heat of about 30% at that instant though the overall excess heat claimed is about 1%. Then there is the question about the stability of the calibration to one percent over a long run (this follows discussions with Mike).

Secondly in the history of cold fusion, it is noticeable that when good fail-safe experimental techniques are used, excess heat is not observed. The great problem is that the cell is heated and hence the heat flow out increases and the problem is to measure this outflow. Sometimes this is done by calculation using a variety of assumptions, as Fleischman and Pons4 did, and their analysis was severely criticised by Wilson et al1. Most make some attempt to insulate the cell, but the only good technique is that used by the IMRA(Japan) group who plunge the entire experiment in a water bath and compensate the variations of the temperature in the closed cell by varying the current to a heater in the bath so as to keep the temperature of the bath constant. Thus the outside world sees only the walls of the bath which are at constant temperature - this is a fail-safe system as any errors in calculations of heat flow and balance are not important. Note that this system has been used before, e.g. by the Harwell group in one of their many experiments.


In previous ICCF meetings, have often been approached by participants asking curious questions about myself. But at this meeting many asked me and I formed the impression that they believed that I was an agent of some mysterious rich organisation which was anti-Cold Fusion. And that I must be well paid to make such clear statements about the quality of the cold fusion studies reported and their inconsistencies.

Usually I simply explain that I am a physicist with an interest in astrophysics. Finally was forced to explain that I have been spokesman of international collaborations for over thirty years and have just come from a meeting of our E632 collaboration at Fermilab which has eight European groups, seven US groups, two Indian groups and three Russian groups. When I retired two years ago, was given the finest present I have ever received - for 7 months before my retirement party, three friends had searched the literature and selecting only collaboration papers, some 280 of them, they listed each author - over 800 of them - and then wrote to as many as they could find and asked them to contribute something for a book to be presented. The book contains the first page of each of the 280 collaboration papers. For each co-author the number of papers with shared authorship was calculated and listed and the number of the first shared paper is given. The contribution of each co-author has been inserted on a page near that first shared paper. It is quite a book.

The other point is that I love good science and dislike bad science.


In 1991 the Science Editor of the Repubblica mentioned in a book review, that cold fusion was similar to scientific fraud. Drs. Preparata, Bressani and Del Giudice protested in letters but the Science Editor, Giovanni Maria Pace, was unrepentant. This allowed them to sue together with Drs. Fleischman and Pons for some $5 million. Dr. Gozzi was asked to be their expert and I was asked to help La Repubblica. This year the judges made a carefully written judgement5 which said that there was such confusion and doubts that Dr. Pace was entitled to make his statements. They particularly noted that in 1989, Dr. Pons had claimed to have a cold fusion boiler which was capable of making a cup of tea. They wrote that the plaintiffs had lost touch with reality. Costs were given against Drs. Preparata, Bressani, Del Giudice, Fleischman, and Pons.

In a letter6 to Nature, Drs. Preparata and Del Giudice (why not also Dr. Bressani?) attacked Nature and "the widespread innuendo, defamation, and vituperation" they have suffered. They said they were going to appeal the court judgement.

It is a remarkable letter. I replied7 to it adding some facts that had been inadvertently omitted and ended by mentioning that ICCF-6 would be held and "Those attending will be delighted if Pons can bring his boiler and use it to make us all a cup of tea."


It was previously suggested in the journal "Infinite Energy" that the next international cold fusion conference, ICCF-7, would be held in the autumn-winter of 1997 in the US. However at ICCF-6 it was announced it would be held in the spring of 1998 in Vancouver (the losing bidder was Italy).

It was not said who would sponsor the next conference. From conversations with people who did not wish to be quoted, there did not seem to be any rush by the Japanese agencies who had funded this present conference, to fund the next. It was said that the funding will be basically from ENECO - the business organisation who hold most of the cold fusion patents or patent claims, of Fleischmann, Pons and others and who advertise themselves as "an intellectual property clearing house.

Will the meeting be early enough in the spring for some skiing?

Hope a cup of tea will be provided.


11.1 Preparata Does an Experiment!

Dr. Preparata continues to be a very firm Believer in cold fusion. Apparently not discouraged by strong criticism8 of his theory of cold fusion at ICCF-4 by Drs. M. Rabbinowich, Y.E. Kim, V.A. Chechin, and V.A. Tsarev, he and some theoretical colleagues have set up a small experiment. He described it and said they had suffered from a power failure - I tried to tell him that was normal, but he brushed aside my comment and seemed unaware that experimentalists take precautions against power failures.

The experiment was a typical True Believers one of an electrolytic cell and a minuscule palladium cathode and D2O. It was poorly designed for calorimetry and was quite different from the MITI/NEDO and IMRA(Japan) designs which measure all heat flows and do not rely on doubtful assumptions. Dr. Preparata claimed9 "Remarkable quantities of excess heat" of some 200%. He said it was related to the g-phase of Pd-D, a phase which others cannot find.

When I asked if his theory predicted excess heat also with light water, H2O, he replied it did not. It will be interesting to see if this has any effect on the many True Believers who claim to do find cold fusion effects with H20.

11.2 London Theatre Play "Blinded by the Sun"

The Journal Nature does not often review theatre plays, but it reviewed two in its Sept. 1996 edition. One was "Blinded by the Sun" and as one might guess it is about a scientist with a good reputation who succeeds in obtaining hydrogen from water and it will solve all the World's energy problems. He decides it is so important he will not wait for peer review and publication in a scientific journal, but instead will first hold a press conference - "sounds familiar" as Nature comments. The play is by an experienced playwright, Stephen Poliakoff, and is well-recommended by non-scientific critics - when I went all the seats were sold and I had to wait an hour for a returned ticket - but is was well worth it. The theatre programme is interesting as it contains a long article by David Jones who writes the marvellous Daedalus column in Nature. He compares the events in "Blinded By the Sun" with "the recent famous scientific scandal which came close to fraud in its pure form" - he writes carefully to avoid being sued!

I would recommend it as a good play about the interplay of scientists confronted with a difficult situation. When I told Martin about it he said he would definitely go.

11.3 Second International Low Energy Nuclear Reactions Conference, ILENR2

This is an impressive title and no one would expect that it was a cold fusion conference organised by John Bockris of Texas A&M. Indeed the Texas A&M authorities did not realise it and last year approved holding the first meeting on campus. However when a second meeting was proposed this year, "a 12-person Chemistry Department advisory committee voted unanimously to ban the meeting" according to "Infinite Energy", so it was held off campus.

11.4 Glow Discharge and Sputtering experiments

There are a number of experiments which do not use electrolysis or gas pressure as Fleischman and Pons and Steve Jones initially proposed. In particular there are many which use electrical discharges. Unfortunately it is not clear whether they are zero-energy (cold) fusion or are intermediate energy (lukewarm) fusion. The point is that in so-called glow discharges, quite high energies can be occasionally created by sparking and as Dr. Kasagi showed deuteron ions of about 3000 eV can cause nuclear interactions giving low levels of nuclear products such as n, p, t, and 3He. An example of this is the work of Kucherov et al. from the "Luch" labs near Moscow, which made such an impression on some at ICCF-3 in Nagoya. Hence it would be unsafe to consider experimental claims to have observed such levels until a proper detailed study has been made of the energy distribution of the incident ions.

11.5. About the Conference

The conference was held in the Apex Toya hotel which is about 2 hours from Sapporo in the northern island of Hokkaido. It is high on a ridge with ski lifts going down to the Pacific on one side and on the other side are ski lifts going down to a large volcanic crater lake with steep islands in it. Must be nice in good weather but it finally snowed towards the end of the week. The hotel was very luxurious and the Chinese restaurant was one of the best I have visited.

The only sponsor named was the government organisation, New Energy and Industrial Development Organisation, NEDO. However others contributed, for example, heard of a major Japanese car company looking after four Russian delegates.

Participants generally considered it by far the most scientific conference in the series. There were three probable reasons. Firstly, out of the 50 talks, there were only two theory talks (by Chubb and Chubb, and by Kim et al. of Purdue University) and no theory summary talk. Secondly, major Japanese laboratories presented serious experiments with carefully controls and calibrations - and they gave believable errors. Thirdly, the conference Chairman, Prof. Okamoto said that some 40 papers had been excluded (not quite enough).

Media interest has declined steadily - from the feverish atmosphere with official and private press conferences of the first meeting - this time was not aware of any outside media interest whatsoever.

Analysis of the official lists (slightly different from reality) gave 170 participants, 50 talks, and 77 posters - i.e. 170-50-77. The corresponding numbers for the major countries are; Japan 91-22-19; USA 32-11-16; Italy 15-6-4; Russia 8-4-15; China 4-1-15; France 6 -2-1

11.6. CETI - The Patterson Power Cell

Dr. James Patterson and Jim Redding have been making large claims of continuous excess heat from the Patterson power cells and they have set up a company called Clean Energy Technologies Inc., CETI, to sell them. Their cells have been propagandised by Mr. Rothwell on the net but he withdrew after he was severely attacked (e.g. he said it could produce for hours 1300 watts out for one watt in, but it was pointed out that this would boil all the water away and end the experiment quickly, so he changed his story).

There should have been a CETI session, but this disappeared apart from a talk by George Miley mainly about transmutations.

After ICCF-6, Gene Mallove posted that CETI had a stall at the American Nuclear Society meeting in Washington DC on the 11 and 12 November. They were selling kits at $3,750 each and claimed to have sold 40 of which some 15 were sold at the ANS meeting!. They supplied a number of things including two research cells and a monthly newsletter edited by Prof. George Miley and mandatory on-site training in the use of the cells at the University of Illinois - suppose the university approves?

At their stall, they had a cell running at 5 watts out for 1.5 watt in - much more modest than their previous claims of over 1000 watts out - are they going backwards?

They also claim to reduce the radioactivity of heavy elements such as uranium or thorium by "conservatively" 50%. Amazing!

Apparently people are very interested in Miley's transmutation paper (according to Mallove) and he has been invited to present his latest work at the American Nuclear Society meeting in June.

Mallove says the US Patent Office has allowed them a patent (suspect it does not contain the words "cold fusion").

Mallove writes "according to CEO Redding" an organisation has already purchased the 'exclusive world rights' to licence and sub-licence this patent. The organisation has paid CETI $1 million ($1,000,000) for this. The organisation's identity, for now, is private'. Well we have already heard this before about mysterious buyers putting up a million - think the last was hinted to be Motorola but equally discrete word was that Motorola was not putting up a million dollars.

Seems like a case that might interest the Regulators.

11.7 The Siena Bomb

In January 1994, the Italian press was full of a great discovery at Siena of a cell that produced 50 watts by cold fusion - and this was followed by a paper10 by S. Focardi et al. .

They heated a nickel wire to about 500 C in a hydrogen gas and got out much more heat than they would have expected - the calibration being done in vacuum.

I have suggested many times to Prof. Focardi that it was a question of either fusion or of heat transfer - for hydrogen gas is the second best material to transfer heat. A quick way to settle the matter would be to run the experiment with helium gas which transfers heat efficiently but cannot give fusion. Despite urgings, they have always refused to do this simple but decisive experiment.

Two things have happened since - they have been funded by a major company and they have stopped talking to any audience which might ask probing questions, though I did manage to attend one. It was most disappointing as it hardly discussed the experiment or the results - it was mainly a superficial account of the World's energy problems. They did not talk at ICCF-5 and did not appear at ICCF-6.

Although Prof. Focardi has been an experienced scientific administrator for many years, he seems to have lost touch with experimental Science and its code of conduct.

See Post-script below for later official information.

11.8 Tom Droege

Recently some people have been asking what has become of Tom Droege who made a good reputation for himself by carry out experiments to check cold fusion claims and reporting the results on-line. As he used good experimental technique and scientific methods, he could not verify any claim mentioned. When I was at the E632 Collaboration meeting in Fermilab, met Tom. He is very busy working on cosmic ray detectors for Jim Cronin's big experiment - has developed some interesting new techniques. He was interested in my new theory for the production of ultra-high energy cosmic rays, > 1019 eV, from micro-quasers in our galaxy which were discovered by Felix Mirabel. Tom has put cold fusion completely behind him.

11.9 Macmillan Encyclopaedia of Physics

Have just received the four handsomely bound volumes of the new Macmillan Encyclopaedia of Physics. Some might be interested in the section on "Error and Fraud", pages 316 to 320.

12. Please Can I Have a Cup of Tea?

In July 1989, Stan Pons gave an interview11 where he is photographed with a cell that he claims is a boiler of which he said "It wouldn't take care of the family's electrical needs, but it certainly could provide them with hot water year round" and later "Simply put, in its current state it could provide boiling water for a cup of tea."

Now seven years later we went to ICCF-6 hoping for this boiler to provide us with a cup of tea, but there still seems to be a problem - wonder what it could possibly be?


1. Japanese government and major Japanese companies have done good and careful experiments to confirm and to test cold fusion. Their experiments show no evidence in favour of cold fusion even though they had the advice of the leading cold fusion experimentalists.

2. In all experiments except those performed by cold fusion Believers in metals, the branching ratios of n, p, t, 3He are equal and 107 times larger that for 4He. The True Believers find many different ratios often disagreeing, and say that the 4He channel is dominant instead of being minor. Now new and careful experimentalists with deuteron beams fired into metals, find the normal branching ratios. Further they studied the variation of rate down to very low energies and found no anomaly such as the very sharp rise in the rate at low energies which would be required by cold fusion claims. Note these experiments were carried out in the metal lattice itself.

3. All this strong evidence against cold fusion claims, seem to have had little effect on the summary speakers who kept smiling.

4. In the past there have been weak claims of transmutation of elements. At ICCF-6 George Miley made extravagant claims that from nickel he can produce many elements all the way up to lead. Critics say that his data can be interpreted without transmutations.

5. Considerable data has been obtained on the structure of materials. It is noted that with time the metal can have cracks and be covered with crud. This may help to explain why after long periods, bursts of excess heat are observed - this in experiments which are not well-designed and which do not have an outer bath maintained at a constant temperature.

6. In the law suit brought against La Repubblica by Fleischman, Pons, Preparata, Bressani and Del Giudice, the judges refused it and awarded costs against the five. They are appealing

7. Despite all the failures to reproduce cold fusion in careful experiments by Japanese researchers, a seventh conference is planned for 1998 - but probably with little Japanese money.


The claim by Focardi et al.10, to have maintain 44 Watts of power production over 24 days, and which they claim to have repeated, has been checked by an independent group. This was the LAA project who performed their experiment on the CERN site - note they are independent of CERN, also I was not involved.

This major paper by E. Cerron-Zeballos et al., will be published in Nuovo Cimento soon - it was submitted 3 July 1996 and approved 18 November 1996. The Abstract reads;

"Anomalous heat production in a nickel rod loaded with hydrogen has been reported by Focardi et al. (Nuovo Cimento A, 107(1994)163). We have investigated this phenomenon by repeating the experiment. We found the results to be consistent with our observations. : namely we measured higher temperatures for the same input power when hydrogen is absorbed during a heating cycle. Nevertheless this temperature rise does not appear to correspond to an increase an heat production. We have added a temperature sensor to the container of the experiment. The temperature of the container follows the same temperature with input power curve irrespective of whether there is an anomalous absorption of hydrogen or not: therefore we have no evidence of that this temperature increase corresponds to another source of heat. In conclusion, we have observed all the effects discovered by Focardi et al., but our results imply that there is no production of power associated with the absorption of hydrogen by nuclei."

Thus there is are strange effects, but the experiment is complicated and not easy to interpret. Essentially they say, in a very polite way, that the interpretation of Focardi et al. was rather enthusiastic. This confirmed what I had been trying to suggest to Prof. Focardi, that before having press conferences and arrangements with industry, he should repeat the experiments with more instrumentation and should vary the conditions to try and prove himself wrong, e.g. by trying helium.

There is no blame for making a mistake - the question is how you react afterwards. This is beautifully illustrated in the current 10th January issue of Science in two cases described.

Gary Taubes (author of Bad Science - the Short Life and Weird Times of Cold Fusion" recounts the history of the claim to have discovered the axion at Darmstadt. In 1969 Walter Greiner proposed that when two heavy ions e.g. Uranium, touched they could form a "quasi-atom" which could generate enormous electrical charge which could produce electrons and positrons giving new particles. In 1983 -87 two experiments observed peaks in the positron spectrum of six standard deviations which was sometimes interpreted as being axions which are a serious candidate for the missing Dark Matter of the Universe. However the results were not reproducible and the position of the peaks shifted. Jack Greenberg of Yale and Tom Cowen of Livermore strongly supported the existence of peaks and criticised those who disagreed. It was said that the conditions had to be just right to observe the peaks, and if you did not find them, it was because your target was too thick or the energy resolution was not quite right. Berndt Muller at a nuclear physics meeting in 1986, compared the work and ideas with Irving Langmuir's six criteria of Pathological Science and showed great similarity - he was not popular with some.

Now three major second generation experiments have been done with ten times the statistics and almost all the authors consider that the erratic peaks are not real. Rudi Ganz of Illinois, showed that by making careful selections (cuts) of random data, it was possible to generate similar peaks. However Greenberg and Cowan insist that the peaks are real and even that if they re-analyse the data, they can find peaks. - they have become True Believers. Observers of Cold Fusion may find some similarity between this case history and that of cold fusion.

In contrast is the case of the Hydrogen to deuterium ratio, H/D. measured by astrophysicists. The H/D ratio is a crucial ingredient of Big Bang Nucleosynthesis which is a key evidence in favour of the Big Bang theory of the origin of the Universe. This ratio was for long thought to be 10-5 and this allowed the numbers of neutrino families to be about three as found by LEP (2.998 +/- 0.004). Then measurements from the Keck telescope gave a ratio ten times higher, 10-4. Many measurements were made and they formed two groups about the two values. At the biannual Texas conference on astrophysics held in Chicago in December which I attended. David Tytler gave a new long analysis of his and the other results which showed that the higher ratio values came from a subtle mis-interpretation of the data and 10-5 was the best value. One of the leaders of the higher ratio, Craig Hogan, was scheduled to speak before the new analysis was known. It was a difficult situation, but fortunately Craig is an excellent astrophysicist as well as a responsible scientist and he acknowledged that David Tytler's data were "clearly superior and his arguments were real. How different from cold fusion - here there is no True Believer to continue arguing.

So this is the message for people like Profs. Focardi, Miley etc. - it is no crime to make a mistake, but it is irresponsible to continue when the evidence against accumulates - a good responsible scientist tries to prove himself wrong.

In the same issue of Science, there is third analysis which may be wrong, (though the experiment is correct) but as I am a member of the small, though growing minority who thinks so, it is better to wait.

1. J. Wilson et al., J. Electroanal. Chem. 332(1992)1.
2. S. Isagawa and Y. Kanda, KEK preprint 96-138 (1996).
3. S, Isagawa, Vacuum, 47(1996)497-499.
4. M. Fleischman and S. Pons, J. Electroanal. Chem. 261(1989)1,
5. Nature, 363(1993)107.
6. E. Del Giudice and G. Preparata, Nature 381 (1996) 729.
7. D.R.O. Morrison, Nature 382(1996)572.
8. M. Rabbinowich, . Kim, V.A. Chechin, and V.A. Tsarev, ICCF-4, pages 3 to 13, 1993.
9. G. Preparata, J. Electroanal. Chem. 411(1996)9-18.
10. S. Focardi, R. Habel and F. Piantelli, Il Nuovo Cimento, 1897(1994)163-167.
11. Deseret News, Salt Lake City, 8 July 1989.

APPENDIX - was Cold Fusion Update No. 11 Neutron Claims of Bressani et al. Critically Examined. B5. Bressani et al., Turin

The group of Tullio Bressani et al. in Turin, has published1 an important result based on experiments where they claimed to have observed neutrons emitted from Titanium in deuterium gas. What was particularly striking about these measurements, was their claim that the energy of each neutron was measured and a peak was obtained near the value of 2.45 MeV which would be expected if the neutrons came directly from the reaction;

d + d ---> 3He + n(2.45 MeV)

Previously F&P in their 23 March 1989 press conference and in the original version of their first paper, claimed that they had established this as they observe a sharp peak of gammas at 2.5 MeV from the reaction of these energetic neutrons with the protons of the water

n(2.45 MeV) + p ---> d + g(2.5 MeV)

But it was pointed out to Fleischmann at Harwell on the 28th March 1989, that this was impossible as the neutrons slowed down before interacting and were thermal when captured by the protons of the water, so that the reaction should have been;

n(0 MeV) + p ---> d + g(2.2 MeV)

giving the well-known gammas of 2.2 MeV. Two days later at Lausanne, Fleischmann showed almost the same graph of gammas with the peak at 2.2 MeV - this disturbing change is discussed in detail in Frank Close's book2. It can be seen why the result of Bressani et al. excited such great interest.

In 1991 Bressani et al.3 used 3 grams of Titanium shavings which they temperature cycled from 25 C up to 540 C, called "UP", and back down again, "DOWN". A very broad peak can be observed centred near 2.45 MeV which they say is about 2.5 standard deviations. They say no enhancement was observed with hydrogen instead of deuterium, but they do not use the hydrogen data as a background as might be expected, but surprisingly use the "DOWN" distribution. No real explanation for this choice is given except that the shape is better - there are problems with the background which is mainly instrumental and not natural. The loading was D/Ti = 0.32 which is surprisingly low and almost all True Believers declare that to obtain cold fusion effects one needs the loading to be > 0.8, or > 0.9, or >1.0.

A more complete experiment was performed in 1992 and reported1 by Botta et al. Three experiments were performed, Ti with D2 gas, Ti with H2 gas and Pd with D2 gas for times of 13933, 4631 and 2820 minutes (a total time of less than 15 days - short for such a crucial experiment). This time the background was taken as the hydrogen run. It is claimed that all the events above background in the bin from 2 to 3 MeV are neutrons corresponding to a 2.45 MeV peak and a significance of 5 standard deviations claimed - this statement is really sensational - clean, convincing statistically significant evidence for cold fusion!

However there is a major problem for there is not a clear peak at 2.45 MeV as claimed, but rather a sharp rise at 2 MeV and a slow fall-off above the 2 to 3 MeV bin going out to 6 MeV. It is essential to understand the asymmetry and the origin of these high energy neutrons before any claim can be made for a single symmetric peak of 2.45 MeV neutrons. If one takes fig. 2 of the ICCF-3 paper, then measuring this figure, the statistical significance of the excess in the bins, 2 to 3, 3 to 4, 4 to 5, and 5 to 6 MeV is resp., about 5.3, 4.7, 3.7, and 2.8 standard deviations. Thus anyone who wishes to claim that the excess counts in the 2 to 3 MeV bin means something, has also to explain the overall more significant excesses in the neighbouring bins (Note their resolution, FWHM was about 1 MeV). It must be concluded that any claim to observe 2.45 MeV neutrons is not justified.

At ICCF5, Tullio4 presented their results entitled "Search for 4He production in Pd/D2 systems in a Gas phase". He said they decided to improve their experiment but rather than increase the number of neutron detectors, they decided to improve their helium detector system since there had been several claims of large amounts of helium, and in particular the amount of helium was sometimes almost commensurate with being the sole source of excess heat (e.g. Miles).

He said that most of their experiments gave no helium but perhaps there were indications of helium in one experiment4.

They now found no neutrons of 2.45 MeV, more precisely, the rate was less than 0.4 neutrons/second per gram of Pd at the one sigma level. They consider this result to be compatible with their earlier result of 0.02 +/- 0.01 neutrons/s/gram of Pd because the older experiment used 54 grams of Pd while the new one used 0.5 grams. Well. maybe. There is a major assumption here that the rate depends on the volume of the palladium. And if one has made this assumption, then why reduce the volume of palladium by a factor of 100 since one expects then to reduce the neutron signal also by a factor of 100? To use 0.5 grams is poor experimental design.

Very often scientists who have to report that an improved experiment does not explain their earlier published results, tend not to announce them too loudly, so it was very commendable of Tullio to say in public that their important new experiment did not confirm their claim of neutrons of 2.45 MeV which had made such an impression previously. It must have been difficult for him as he was, with Preparata and Del Giudice, author of a theory of cold fusion5 which was presented again at this ICCF-5 conference by Dr. Preparata; also after La Repubblica wrote that cold fusion was scientific fraud, he, together with Drs. Fleischmann, Pons, Preparata and Del Guidice, sued the newspaper for some $5million6 but had costs awarded against them7.

It is the hallmark of a serious scientist to present all results even if they do not confirm previous results. In this Tullio resembles most of the scientists who had been very strongly presenting data which they claimed showed evidence for the existence of a new neutrino of 17 keV mass. Some of them had been attacking those experiments which did not find it (just as some True Believers in cold fusion attack the Harwell, MIT and CalTech experiments). It may be remembered8 that when the weight of null experiments against the proposed new 17 keV neutrino became too great, they realised that their own experiments must be mistaken and hence carefully checked them for error and sometimes even repeated their experiments, to try to find the error and to prove themselves wrong - this is how good scientists follow the scientific method they try to prove themselves wrong.

The question of whether neutrons of 2.45 MeV are emitted or not, is a very important one. It is to be hoped that the Turin group will also do a good decisive experiment on this subject and it is to be expected that the neutron system will be improved, that the volume of metal will be increased by a factor of 100 and not reduced by a factor of 100, and the run will be long enough, some months, to give good statistics with D2 and H2. Also with their very low efficiency of 2.5x10-4, the counting rates are very low, so it would be wise to perform the experiment deep underground. Finally it is essential that an explanation is given of the asymmetric shape of the neutron spectrum, explaining or removing the large number of high energy neutrons so that a clear peak at 2.45 MeV can be seen - if it exists.

Below is given a more detailed discussion of the work and analysis of the Turin group since Tullio has stated4 "Since the start of the debate about the occurrence of D-D fusion phenomena in the lattice of some metals like Pd and Ti, the detection of neutrons, in particular 2.5 MeV neutrons, has been considered the most reliable signature of the effect"

Description of Experiments and Analysis of the Turin Group of Bressani et al.

The technique that allows the energy of the neutron to be measured at emission, is to use two sets of scintillation counters and time of flight. The neutron scatters in the first set giving a "start" signal, and the "stop" signal is given by the second set. However the price to be paid is low efficiency, measured to be 2.5x10-4. Thus any counting rate quoted, has to be multiplied by this small number to find out the actual counting rate per gram of metal. As the amount of metal is small, the counting rates are very low so this must be considered a difficult low-counting experiment of the type that should best be performed deep underground.

Three sets of runs have been made.


Deuterium gas was used with 3 grams of Titanium shavings. The loading ratio, D/Ti atoms, was only 0.32 which is very low - one can obtain 1.8 fairly easily with a higher D2 gas pressure. Generally True Believers say that the reason null results are obtained is because the loading was too low. However a signal of about 2.5 standard deviations was claimed. This would correspond to 1.3 +/- 0.5 neutrons/second/gram of Ti. However the analysis was rather curious and merits study.

Normally one compares the energy spectrum obtained with deuterium with that from hydrogen(as blank) and hopes to find a peak near 2.45 MeV, but the paper3 says that the event distribution showed some systematic effect. Instead the energy spectrum during the temperature increases, "UP", was compared with that during the decreases, "DOWN", and on subtracting, a broad peak near 2.5 MeV was shown. However no justification of such a curious choice of background was made since one might have expected the deuterium concentrations to be somewhat similar during the UP and the DOWN phases. 1992.

Experiments were performed with 20 grams of titanium, this time in the form of a sponge which greatly increased the surface area, and with 54 grams of palladium in the form of small cylinders. The loading, D/Ti, was 0.7 for 20% of the data and the standard 1.8 for the other 80%. For the palladium, the loading was about 0.7 - it is surprising that they tried to run with such a low loading as most True Believers, e.g. Mike McKubre, insist that with palladium, high loadings, above about 0.9, are necessary.

This time the raw data are given for H and for D resp., in fig 3 and 4 of ref. 1. There are less than a 100 counts in the 0 to 1 MeV bin but about 3600 counts in both cases for the neighbouring 1 to 2 MeV bin - this is hard to understand if the resolution has a FWHM of 1 MeV. Subtracting the two graphs, fig. 5a, gives about 380 counts in the 2 to 3 MeV bin but a small negative number of counts in the 1 to 2 MeV bin - it is again hard to understand why there is not more counts in the 1 to 2 MeV bin from smearing when the resolution is 1 MeV Full Width at Half Maximum, FWHM. The subsequent bins give about 280, 180, 140, and 60 counts for 3 to 4, 4 to 5, 5 to 6, and 6 to 7 MeV bins resp., which are too high numbers for a single peak at 2.45 MeV and a resolution of about +/- 0.5 MeV. Clearly there is something wrong with this analysis or with the data.

The above analysis gave 3.9 sigma. A second analysis gave 5.3 sigma. The neutron emission was given as 0.11 +/- 0.03 neutrons/second /gram of titanium, suggesting a 3.7 sigma result, so the first analysis seems preferred. It is noted that this rate is a factor of ten less than the rate of 1.3 +/- 0.5 n/s/g found in 1991 and this is explained as being due to the titanium having a greater surface area as it was now in the form of a sponge - but this reason seems unreasonable as the rate is quoted as per gram of titanium and hence the rate with the Ti sponge should have been much higher not ten times lower. If the rate had been quoted per unit of surface, the discrepancy would have been greater, not less. Yet the authors also say that a bulk phenomenon is preferred by the theoretical model of Bressani, Del Guidice and Preparata5 - but these data seem to contradict this model? Could the model possibly be incorrect?

It may be noted that the 1991 analysis technique of subtracting DOWN from UP was not used - not surprisingly since it is shown that for the 80% of runs with a loading D/Ti of 1.8, the deuterium was shown to stay in the metal for the whole cycle so that such a subtraction would be inappropriate.

With the 54 grams of palladium, only a small signal of 70 counts was observed which would correspond to 2 sigma - it would give a rate of 0.02 +/- 0.01 neutrons/s/gram.


At ICCF5, Tullio Bressani reported4 on an experiment using the same neutron detector, using 0.5 grams of palladium and said that the emission rate of 2.5 MeV neutrons was less than 0.4 n/s/gram. He later explained that this was fully consistent with the 1992 result of 0.02 +/- 0.01 n/s/g which was obtained using 54 grams of palladium. It is correct that they are not inconsistent, but it does not explain why if the first result was inconclusive, it was decided to run with the mass of palladium reduced by a factor of 100? Normally to solve a low counting problem, one increases the mass of palladium substantially, not decreases it.


Overall, there are so many internal contradictions that it is hard to believe that neutrons of 2.45 MeV have been observed. It would be good Science if each of the authors were to revisit these papers.

References for Appendix only.
1. Botta et al. NC 105A(1992)1663 and in ICCF3, page 433
2. F. Close, "Too Hot to Handle"
3. Bressani et al., Nuovo Cimento 104A(1991)1413
4. T. Bressani, ICCF-5, Monte Carlo, 1995
5. T. Bressani, G. Del Giudice, and G. Preparata, Nuovo Cim. 101A(1989)865 and G. Preparata, ICCF-5, page 65 (1995).
6. Nature 363(1993)107.
7. Nature 380(1996)
8. D.R.O. Morrison, Nature 366(1993)29-32.

c) Douglas R.O. Morrison.

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