Douglas R.O. Morrison's Cold Fusion Updates
No. 5—7 July 1991

Back to Morrison Index

(Source: New Energy Times)
Dear E632 and WA84 Colleagues,



Over 200 people attended the Second Annual Conference on Cold Fusion which last 5 complete days. 58 talks were given plus 5 "Survey" talks plus two Round Table discussions and one Press Conference. No startling new positive results were presented though Believers considered good progress had been made. A few careful experiments gave negative results. A couple of the more interesting positive experiments refused to describe details because of "patent restrictions". The Kamiokande detector has a very high reputation. After not finding anything with Titanium, a switch to electrolysis with Palladium produced some neutrons causing excitement and discussion. The major problem of Cold Fusion - the disagreement of the amount of heat claimed and the corresponding expected number of nuclear products - still exists. Surveys still indicate other major problems, particularly reproducibility. A Third Annual Conference is planned.

1.1 Excess heat
1.1.1 McKubre, SRI + EPRI
1.1.2 Droege, Batavia, Ill.
1.1.3 Szpak, San Diego
1.1.4 Liaw, Hawaii
1.1.5 Fleischmann and Pons,
1.2. Neutrons
1.2.1 Kamiokande, Japan
1.2.2 Scaramuzzi, Frascati
1.2.3 Taiuti, Genoa
1.2.4 Bertin, Gran Sasso
1.3. Tritium
1.3.1 Will, NCFI
1.4. Helium
1.4.1 Miles, Naval Weapons Research Center, China Lake, Ca.
1.5 Rates of tritium, neutrons and helium
1.5.1 Cecil, Colorado
1.6 Surface or Bulk effect
2.1 Menlove - survey of neutron detection
2.2 Scaramuzzi - Survey on Gas-loading Experiments
2.3 Ikegami - Research in Japan
2.4 Tsarev - Research in the Soviet Union
2.5 Li - Research in China
2.6 Schlapbach - Hydrogen and its Isotopes in and on Metals.
4. GERISCHER - Review by a Neutral Person
6.1 Third Annual Conference
6.2 National Cold Fusion Institute
6.3 Pons and Fleischmann, Jones
6.4 Money


Many results were presented and a hundred pages of notes taken. It is impractible to present them all, especially as many were very small experiments which did not fulfil the criteria established at the BYU meeting which encouraged only major experiments looking at several pieces of evidence simultaneously. To appreciate the flavour of the Second Annual Conference, a selection of major experiments where normal controls had been performed, are discussed here plus a few others chosen for historical reasons. Please send me documents if you feel there is an error in this. My apologies to people not mentioned.


1.1.1 McKubre, SRI + EPRI

Mike McKubre presented a large experiment by Cold Fusion standards. This was perhaps the most impressive positive result. There were measurements of calorimetry, tritium, neutrons, gammas and autoradiography. No evidence was found for neutrons or gammas. Some indications for tritium formation but not "evidence". Some positive indication in one out of 50 audioradiograms.

The hypothesis was that positive results were obtained only with a high D/Pd loading, about 1.0 and some 100 - 120 experiments were performed on loading.

A closed calorimeter was used as this eliminates most of large corrections for heat losses. An "isothermal" flow calorimeter was used and some 30 experiments performed. There were still some problems with heat losses, eg flow streamlining at points where temperature was measured. The bath is about a meter square and contains four cells. The conditions could be varied widely, pressure from 40 to 10000 psi, 30 to 600 mA/cm2 and up to 6400 mA/cm2, 0.1 to 100 Watts, runs were 1000 to 2000 hours. It seems that Pd rods were used eg 3 mm diameter and 3 cm long.

Results for one rod were shown giving 8 or 9 bursts of heat in 2000 hours in total 45 MJ per mole of Pd. Excess power was often about 10%. One rod appeared to have a threshold of 300 mA/cm2. Another rod (results not shown) had an excess of < 250%. No negative heat bursts were found. No excess bursts were observed before certain "initial conditions". Did not observe bursts when D/Pd loading was < 0.9.

No bursts were observed when operating with H2O but Mike said that the amount of running was inadequate.

Question(Bockris) Reproducibility? Ans; 10 successful runs if apply criteria - initial time was 300 hours for first burst.

Question(Bush) If use PdCl to blacken electrodes, time to start is only 2 hours. Ans. Often have shiny rods afterwards (and some blackened).

Note that these were not constant temperature calorimeters as at Harwell and therefore the corrections for temperature measurements could still be reduced.

In private conversation, if one takes the total power out and the total power in over the entire run, the excess was between 1% and 2 to 3%.

1.1.2 DROEGE, Batavia, Il.

This calorimeter constructed by Tom and Lee Droege, was the finest presented to the conference. It is a closed calorimeter and has inner and outer shells which are held at constant temperature. Being a null-balance technique (like the Wheatstone bridge) it has no heat loss errors to worry about and correct for by assumptions or by special analyses. It is highly automated, eg by servo-controlled thermo-electric devices. When operated at 10 Watts, long-term drifts are only 1 mWatt or less. Depending on the "noise" from the cell, measurement limits are from 4 to 10 mWatts.

The calibration is done in a blind manner - heat bursts whose size is unknown to the operator, are introduced by a random number generator and the output is then studied to determine the size of the burst - ingenious! A continuous measurement is made of the absorbed deuterium. D/Pd values of between 0.6 and 1.1 were recorded - grinding and polishing the surface appeared to increase the loading.

Many anomalous heat effects were observed, but on further study rational explanations were found. The authors write "It is disturbing that as the sensitivity of our apparatus is increased, the anomalous heat effect seems to become smaller and smaller. This is one of the signatures of Pathological Science".

The final result was zero +/- 0.2% or in terms of watts, 0.2 W/cm3.

1.1.3 SPZAK, San Diego

S. Szpak et al. of the Naval Ocean Systems Center, claimed that reproducibility could be greatly increased by a special preparation technique - preparing the Pd electrodes by the electrodeposition from Pd++ salts in the presence of evolving deuterium. The reproducibility was measured by observing tritium. However the amount of tritium involved was small and when asked about errors, correction for enrichment and checks on tritium contamination of the Pd, it appeared that the controls and checks had had been partially but not yet fully performed.

1.1.4 LIAW, Hawaii

Previous Cold Fusion meetings have been electrified by claims of excess heat of over 600% over input power when a molten salt technique was used at 370 C. These claims were repeated and it was said 4He had been measured but not 3He, though it was concluded that the 4He excess was slight and could be ambient gas. The questioning afterwards was unusually critical. It was pointed out that the 4He level was ten millions time less than that of Miles. Dr. Bush questioned the base line of the excess heat calculation. Fritz Will said he was impressed by the experiments but worried that very little Deuterium dissolves in Pd at 370 C - was told that the D/Pd loading was about 0.1 up to 0.3 or 0.4. It was answered that there had been two positive experiments and 12 others (the impression was that the first two had apparently given excess heat but it had not been possible to reproduce this effect since). It was also replied that there was no correlation between current density and excess heat.


Stan Pons said that the apparatus and calorimeter had been modified but the conclusions were not significantly modified - the biggest change mentioned seemed to be that the top of the cell now had a silver mirror to reduce heat losses. Most of the talk was a list of sources of heat loss and how to correct for them - the phrase "non-linear regression analysis" occured frequently.

The second half of the talk was unusual as it was handed over to Dr. Hansen. He introduced himself as a physicist from the Fusion Energy Council of the State of Utah who had been asked to analyse the non-released data of Pons and Fleischmann (a no-win situation as he said). He had taken selected data, 8 runs of which 2 were blank. Five of the six remaining showed definitive excess heat and the sixth was unclear - it looked like modest effects. Did a non-linear regression analysis with Pons and Fleischman and Chaves and Walling. The excess heat was 6000 eV per Pd atom which is a 1000 times greater than chemical energy. He thought Pons and Fleischmann knew why the cells worked so well.

In answer to questions, it was said that the electrodes were an alloy of silver, about 10% but many alloys had been tried. The excess heat was 1.2 to 1.4 watts for an input power of about 6 watts. It was replied that as the rods are 1mm diameter and 1.25 cm long, the Pd volume is only 1/100 of a cc and hence the power per cc is large, about 100 Watts. When asked if the electrodes were prepared in a special way, the answer was "Maybe". Several times the point was made that one only obtained excess heat when the D/Pd loading was above 0.9, but when asked how the loading was measured, it was answered that electro-chemical techniques were being used, the measurements were being made now but there was good reason to believe that they were 1.0 to 1.1.

Quite a few Believers complained of the lack of new information and the non-answering of certain questions. Basically the talk was very similar to last year's. No mention was made of the large series of 32 and then 64 cells that had been set up early last year at NCFI. Many times it had been said that if they changed to a cell which is (a) closed, and (b) in constant temperature baths,then all these many large corrections for heat losses would be avoided and the analysis would be very simple. This may have been partially answered when they said they wished a cell of a simple design so that many tests could be made.

In the poster session, a brief paper was presented where results of measurements of gammas were given, the gammas being of 2.20 MeV from capture of thermalised neutrons in water. They had concluded that measurements of the very weak spectrum of gammas was not possible using NaI detectors in the presence of the dominant background due to the daughter products of the Uranium and Thorium decay chains, but that one should use instead high resolution(but low sensitivity) germanium detectors. The spectra shown had sharp peaks though they were mainly background. The peak from neutrons was small. The paper did not show whether these neutrons were from the cell or from general background. No rates were given, though later Martin quoted a figure of 5 to 50 neutrons/sec - however the efficiency is not known, but it is clear that there is no agreement with the normal experimental results that give a billion billion neutrons per second for a Watt of d-d fusion. The full paper with all experimental details is awaited.



Have great admiration for this Japanese experimental team working on detection of neutrinos from Surpernovae and Solar Neutrinos (see CERN preprint PPE/91-104 that have just finished on this subject). They are a large group, adequately funded, who do careful work, many calibrations, and who publish generously and reply frankly to questions. They have obtained excellent results. Steve Jones and Howard Menlove have been putting Cold Fusion cells inside the detector since January. Even with the surrounding salt solution for the neutrons, the volume taken up is small relative to the 3000 tons of water and does not interfere with the detection of Solar Neutrinos. The idea is that any neutrons produced would be slowed down and interact with chlorine in a container filled with salt water, giving gammas which would create electrons which give Cherenkov light which the photomultipliers on the walls recognise. Have always felt that if Kamiokande detected neutrons at the low level as Jones and Menlove described, then this confirmation would be decisive.

The first talk on the Sunday morning at 09.00 hours was by Dr. Ikegami from the Fusion Research Institute(almost all "hot' fusion) in Japan - he has the special responsibility of co-ordinating Cold Fusion research in Japan. He finished his review by suddenly showing a newspaper cutting of two weeks ago which he translated as saying that Kamiokande had found neutrons!

Facts were few but with Howard Menlove's help it was possible to establish;

1) Initial experiments were made with Titanium and gas filling with as far as possible the same conditions as previously and where random neutrons and also bursts of neutrons had been claimed. In the clean low-background Kamiokande detector, no evident signal of neutrons were found over several months, but as Steve Jones says, the analysis is not yet complete.

2) A new set of experiments were started using Palladium and electrolytic cells. It was here that some six bursts of neutrons were recently detected

3) The bursts of neutrons were from 2 up to 6 neutrons per burst. Some comments can be made;

a) previously bursts of about 50 neutrons were claimed - it was said that the new number is only a tenth of that previously claimed - however some correction for the detection efficiency may be required which might or might not change this conclusion.

b) Suggested that the observation is consistent with a small contamination of Uranium or plutonium which occasionally fissions. The contamination could be in the palladium or the D2O but not in the Titanium or H2O.

When Uranium fissions it gives about 2 to 3 neutrons on average, but the spread is 1 to 6 - as observed (note happened to see that the probablilty of 7 neutrons is about 1%), again some correction for efficiency of neutron detection may be needed. Plutonium gives a higher average number of neutrons.

Now this is a hypothesis, that the neutrons come from uranium or other contamination and give fusion reactions, but as it is quite possible. It should be eliminated before claiming a new Cold Fusion effect. This is surely being done - eg by replacing the D2O by H2O and the palladium by another metal. Note that Kamiokande is possibly one of the most sensitive detectors of very small amounts of uranium or plutonium!

In previous correspondance, Steve Jones said one should wait for the full analysis before drawing any conclusions, and this is correct in general, but the publication (unknown to Steve) in a newspaper and the presentation at a conference, rather cancel that argument.

If it should turn out that all the experiments with Titanium and with palladium that previously gave claims of random neutrons and bursts of neutrons, fail to be repeated when placed in the low-background, high-efficiency detector that is Kamiokande, the natural conclusion is that they are unlikely to exist. Would like to add a further important comment; Kamiokande can detect the Cherenkov light from electrons produced by gammas. It is suggested by some that since not enough neutrons and tritons are produced by Cold Fusion, then the third reaction,

d + d ====> 4He + Gamma of 23.8 MeV

must be dominant(though many experiments have shown it is only ten millionth of the others). If this were true, then such high energy gammas would be easily detectable in Kamiokande. They seem not to have been observed. This would appear to close that loophole. Some escape from this difficulty by postulating that the 23.8 MeV of energy does not appear as a gamma but the lattice absorbs the energy. This is considered by most as impossible as the reaction time is less than ten to the power -20 seconds while the time for the lattice to transmit energy is ten to the power -10 seconds. This factor of ten thousand million might seem to kill the idea, but see Section on Theory below. The Kamiokande result should eventually give a limit on how often the gamma appears as a gamma and how often its energy is spread over the lattice.

Thus it may be that in a few weeks time the Kamiokande experiment may give strong evidence in favour of neutron production, but it may be able to deliver what some would consider to be a fatal blow to Cold Fusion; but True Believers will probably still believe. At present it appears to have provided evidence that no random neutrons or bursts of neutrons have been found coming from cells previously claimed to give positive effects.


Dr. Scaramuzzi has continued measurements of neutrons from cells with Titanium loaded from D2 gas and temperature cycled. After the first experiments in April 1989 where only a single BF3 counter was used, the counting efficency has been improved, but it has still proved difficult to reproduce the earlier results. Now a third generation of experiments is under way looking for short bursts of neutrons in the Menlove manner (rather than the long bursts originally claimed). To lower the background the experiments have been performed in the Gran Sasso tunnel, however the reduction is much less than would be expected and there must be a suspicion that gammas are being measured rather than neutrons (indispensible pulse shape analysis was not mentioned). Reproducibility is still a problem but three short Menlove-type bursts have been recorded but they occur at a temperature of -120 C in apparent contradiction with the value of -30 C published earlier - this was mentioned but not cleared up.


This experiment is unusual in that great care has been taken to reduce background, in particular the indispensible gamma - neutron discrimination is achieved by pulse-shape, energy and neutron life-time analysis. Further there are anti-coincidence detectors to detect bursts from cosmic rays. The Scaramuzzi technique was tried by cooling Ti loaded with D2 gas at 20 bar, and warming up. No neutrons were found. With Ti powder the low upper limit of E-25 dd fusions/s is found (initially Jones et al. reported E-23).


Dr Bertin recalled that in April 1989, a result was obtained on neutron production with Jones-type cells in the Gran Sasso tunnel and the rate was in good agreement with the results of Jones et al. However the reader of these notes may remember that at the Santa Fe meeting in May 1989, Yves Declais pointed out that the background rate was very high so that what was being measured must have been gammas. The numbers given by Dr. Bertin seemed to confirm this. He described how in the interim they have now developed an excellent system of measuring neutrons with 6Li glass as well as NE213 scintillator and pulse-shape analysis so that the contamination of gammas can confidently be expected to be small. New results should be available soon.


1.3.1 WILL, NCFI

Fritz Will and Katherina Cedzynska presented results from the National Cold Fusion Institute (other than the work of Pons and Fleischmann). They concentrated on achieving high D/Pd loadings, tritium and neutron measurements. This was because they had found that if D/Pd < 0.7 then they found no effects but if D/Pd > 0.8 then they found effects. They used a volumemetric method with a sealed cell to measure the loading.

With 2mm diameter rods of 3 cm length, it took 2 to 4 days to achieve loadings of 1.0, a saturation value, but the rods were not uniformly loaded. Later some members of the audience said they were surprised that such high loadings were obtained - they were told the answer was a secret following the patent attorney's request.

Light water controls were run simultaneously with heavy water experiments.

Neutrons were measured with two 3He counters and bursts of up to 280 n/s were obtained. Only triples or quads were counted in 40 microseconds. There were a factor of 2.3 more with deuterium than with hydrogen.

Tritium was measured in the gas, electrolyte and in the metal. The background rate was unusually low, 27 dpm/ml. Dr. Cedzynska said in four out of 8 experiments the tritium count was above background, a few hundred dpm/ml. Dr. Will said that latterly four out of four cells gave tritium in each of gas, electrolyte and metal with deuterium but not with hydrogen. Yields were 4.3 to 11 E10 atoms of tritium per cm3 of Pd in the Pd, but less in the gas phase, few times ten to the eight.

There was a tentative result of excess heat measured in one of four cells with a small current density.

The t/n ratio was ten million, but unreliable.

It was replied that the effect did not seem to be a surface one.


1.4.1 MILES, Navel Weapons Center, China Lake, Ca.

Dr. Miles said that if few neutrons and tritons are observed, then by elimination, 4He must be produced. During episodes of excess heat, effluent gas samples were sent to Univ. of Texas at Austin by Bush et al. for analysis. 4He was found with deuterium but not with hydrogen. The mass spectrometer could separate 4He and D2 peaks.

When asked by David Worledge whether helium diffusion through the glass walls could explain the results, and why was no helium found with hydrogen, Dr. Miles replied that 1000 times more atoms of hydrogen wanted to escape through the walls than helium atoms wanted to enter and hence the atmospheric helium could not enter to contaminate the samples.

From an earlier preprint it may be read that the 4He detection limit is 0.14 Watts which corresponds to 2 E12 atoms of 4He in a 500ml flask. The 4He observed corresponded to 0.14 to 0.52 watts.


1.5.1 CECIL, Colorado

Ed Cecil et al. have measured d-d reactions at low energy, 170 to 2000 eV in the cm with beams of deuterons of 2 to 15 keV in the lab. using a Cockcroft-Walton accelerator. They measured the cross sections for the three reactions;

d + d =====> 3He + n (1)

=====> t + p (2)

=====> 4He + Gamma(23.8 MeV) (3)

They also fired the deuterons on to a 6Li target and measured p, alpha and gamma production. Down to the lowest energy they found the t to n ratio for reactions (1) and (2), was unity with no indication of any rise at lower energies. Also the rates agreed very well with theoretical calculations. All the other reactions were also in agreement with expectations, in particular 4He production was much less(ten million times) than tritium and neutron production as would be expected since it is an electromagnetic process and the others are strong reactions).

Morrison said that these results went down to the lowest values possible experimentally, but some people thought that at the still lower energies of Cold Fusion it might still be possible to produce a factor of ten million. However there are two pieces of evidence against this;

(1) Models of the burning of stars such as our Sun are very successful and involve still lower energies - any factor of even ten times would show up in astrophysical observations such as the neutrinos from Supernova 1987A observed by Kamiokande which agree to a factor of two in estimating 3 E54 neutrinos produced.

(2) Muon catalysed fusion proceeds at effectively zero energy and people who work on it find the normal ratio of 1 ; 1 ; (very small), for reactions 1 to 3 resp.

Fritz Will commented that a crystal lattice was different. Morrison replied that the time of the interaction was ten billion times faster than the lattice response time.

It was interesting that these results of Cecil et al. were never referred to again at the meeting.


This was one of the more controversial questions among Believers. Some such as John Bockris, strongly supported surface effects with Pd and Ti, others such as Fritz Will, considered it was not a surface effect. Some use Pd rods, others use Ti powder. Many arguments and theories were advanced, but what was noteworthy was the absence of direct evidence - for example, no one presented a measured "effect" as a function of the surface to volume ratio.


2.1 MENLOVE - Survey of Neutron Detection

Howard Menlove said that in Ed Storms's review there 38 papers with positive results and 44 with negative results. At Como there were 38 papers and 5 posters and 2/3 gave positive results. The source rates of neutron production varied from 1/100 to 100 000 neutrons/sec. This either reflects the equipment is faulty or the source is non-linear. He reviewed types of detectors and gave a list of a dozen different ways of getting false positive results. He then talked mainly of the Los Alamos experiments.

2.2 SCARAMUZZI - Survey of Gas Loading Experiments

Dr. Scaramuzzi listed the large number of parameters that must be chosen and controlled. He said the experiments are complex but concluded that despite this, gas-loaded experiments are better controlled than electrolytic ones.


Dr. Ikegami said some 20 groups were working on Cold Fusion, 12 on neutrons, 4 on excess heat and the others on charged particles, helium etc. They can get their metals free of charge and the Fusion Institute(essentially hot fusion) helps with meetings etc. Many positive results but most of the experiments are small, except Kamiokande.


Dr. Tsarev said that the first conference of Cold Fusion workers was in March 1991 in Dubna where 45 institutes were represented, but with zero funding. After the initial interest some got positive results but then stopped perhaps because of the mass media. Positive and negative results were obtained but generally only the former were published. He then gave a long list of groups and results. A Dubna group that was well-known for its excellent work on muon-induced fusion, found no effect four times and put the strong limit of E-25 d-d fusions/s but then tried the Menlove type of experiment and analysis and claimed bursts of neutrons.


Dr. Li said that the attendance at the meeting in 1990 was 28 groups with 77 persons on 10 May 1990, while in 1991 there were two meetings, one for the South-West with 5 groups on May 4th and one in Beijing on May 15 with 7 groups; so it can be seen that the numbers are shrinking with time. Some groups found effects but sometimes could not reproduce and stopped, others continued and tried new techniques. Several used simple inexpensive plastic detectors such as CR39 which gave tracks for charged particle detection.


Prof. Schlapbach of Friburg gave a very serious, witty and cultured talk which seemed to please everyone. He gave many technical points and his written version is awaited. He recommended reading "Topics in Appld. Physics", vol 63, 1988. Among the points made were;

If the metal surface is oxidised this can create a barrier which could greatly reduce the rate at which hydrogen enters

explained in detail that the isotopes of hydrogen diffuse at different speeds in metals and hence this will give an isotopic separation

at high loadings of deuterium in palladium, > 1, the d and Pd ions are closer together but never close enough to cause fusion

intermetallic compounds can take up more hydrogen - his preference was LaNi5 which expands 25% in volume, but it is very brittle

also Ca3Pd2, where one can achieve Ca3Pd2H7

the Pd-hydrogen system was very well studied

in answer to a question - if you wanted a non-equilibrium state, would expect to occur near the surface not in bulk. The best bet would be to study rare earths.


Many theories of Cold Fusion were presented and often strongly supported during various question times. A review of the theories was given by Dr. Preparata with a sub-title "Possible and Impossible Theories". He presented the problems faced by theory to fit all the experimental results including the t/n ratio of E+7 - he almost sounded like an arch-sKeptic. He required a "possible" new theory to explain the new results without un-explaining the old.

He required there to be deep holes of 100eV and 2Ang. wide, one per Pd atom - this is to penetrate the potential barrier. Theories which cannot do this are "impossible" - he quoted the theories of Schwinger, Bush, and Chubb and Chubb as being impossible.

To explain the relative absence of tritium and neutrons compared to the excess heat assumed to come from fusion, he said that the dominant reaction must be (3) ie 4He plus energy of 23.8 MeV. Since such high energy gammas are not observed, the energy is taken up by the lattice. As the reaction time is very fast, E-21 seconds, the lattice must react quickly and he calculated that for a lattice spacing of 3 Angstroms, this means the energy must move at a thousand times the velocity of light - this surprising effect he justified by asking the audience to remember EPR. Afterwards someone asked him about the EPR paradox as he thought matter and energy could not go faster than light. Dr. Preparata replied they were the same thing as there was no release of information as in Quantum Mechanics. (Comment - was at the Symposium in memory of John Bell and thought the Einstein-Podolsky-Rosen paradox had been resolved by the Aspect experiment and by considering Quantum Mechanics was dominant over Locality).

Fritz Will also asked if there was a problem in the fast release of energy in E-21 seconds. He was told there was no problem as the transfer was between wave functions.

John Bockris pointed out that his theory was for a bulk effect and was fine for Palladium rods, but was not good for other metals such as Titanium powder, and people had talked about steel? The behaviour of hydrogen isotopes is quite different in different metals. Dr Preparata said he will get to that, he did not know the facts for Titanium etc.


Prof. M Gerischer of Berlin is a distinguished Physical Chemist who specialises in Electro-chemistry and is an old friend of Martin Fleischmann.

He said he was invited at rather short notice and had been busy reading since as he had done no experiment on Cold Fusion.

In general he noted that there had been great initial enthusiasm but when the big labs could not reproduce the results, this died away though a few groups continued. At this meeting had heard a lot of new information. He divide his talk into pros and contras

4.1 General

Pro; anomalous phenomen observed widely - excess heat, n, t, 4He only with deuterium not with hydrogen

Contra; Comparisons of D2O and H2O often not performed. In many experiments no effects found. Contrary to what was said, people are more inclined to publish positive than negative results.

Pro; t and n found

Contra; the t/n ratio found is not the expected 1;1. Pro; Calorimetric measurements show occasional large bursts of excess heat Contra; Amounts of nuclear reactions observed not of the same level as would be expected for fusion. Often no time coincidence between excess heat and nuclear products

Pro; 4He now supposed to be the main source of heat with 23.8 Mev from d + d ===> 4He + gamma of 23.8 Mev. The 4He was found in the evolved gases and very little in the metal

Contra; Quantity of 4He too small to account for excess heat claims

Question; Why does electrochemistry give more anomalous effects than gas phase?

Question 1; Where does the helium originate? If in the volume then the 4He should be found in the metal rather than in the gas. But Miles found in the gas.

Question 2; tritium is found in the electrolyte - this suggests it is a surface effect. need more rigourous system of analysis.

Question 3; Role of Lithium? Are impurities essential? as a monolayer? LiH is a product

Question 4; Is it justified to relate heat to volume? -is risky. If relate heat to surface - is misleading. Therefore now relate heat to input.

Question 5; Reproducibility? It is essential to be able to convince people. Little bit sad but we do not seem to see it very often. Are conditions which improve reproducibility to be kept secret?

Question 6; If heat generation proved, what are the prospects for applications as a source of energy? Basic problem of the Carnot cycle - need more energy out than energy in, therefore 100% is not breakeven point. A system works more efficiently at higher temperature, but the amount of deuterium in metals decrease with increasing temperature. Must know concentration of deuterium in all materials and experiments.

CONCLUSIONS; What would be really convincing?

There is not sufficient evidence for phenomenon that could be attributed to nuclear processes.

However there are many inconsistencies that should be settled if confirmation of beliefs of the church are to be accepted.

Shocked that people work on experiments where the products are allowed to escape. Think will only reach any conclusions with closed systems where no products escape.

More effort should be made to look for 4He.

Test runs with D2O should be done fully and in parallel with D2O.

All fragmentary results will not solve the problems. Doubt if we will reach full harmony but we can hope.


The first Round Table was before Prof. Gerischer's talk and was entitled "Similarities and Differences in Cold Fusion Experiments" With such an encouraging title i spent some going through the papers I had filled the boot of my car with in the hope of making a serious detailed contribution.

The Chairman, David Worledge made a serious review of Cold Fusion, not too different from that of Prof. Gerischer. However no one replied to all the questions he had raised and the round table was a disappointment although David tried.

The Second Round Table was the concluding item of the meeting with Martin Fleischmann as the Chairman. Like the first Round Table, it never had a consistent pattern - one person would say something, the next would say the opposite and no one would object or try to reconcile because no one seemed to be aware there was any contradiction. Many fine sentiments were expressed but everyone remained camped in their experiment or theory. For example no one said he would stop using open calorimeters although the wish had often been expressed.

The first Annual meeting finished with a standing ovation. That did not happen this time, indeed there was rather a sober attitude though the Believers were determined to carry on.



It was announced that in view of the progress made a Third Annual Conference on Cold Fusion would be held. It would be in Japan, probably September or October 1992. The news was greeted warmly.


Although in theory the NCFI is closed and no more money is coming from the State of Utah, the University of Utah is quietly providing money to allow it to tick over since the rent has been paid for some time in advance. Staff has been greatly reduced.


Stan and Martin were in great form at the Conference. Stan is working near Nice. A publication suggested that he was working for a Japanese company. Martin is still based at Southampton. Steve was busy during the conference working in Japan on Kamiokande.


Some of our Japanese colleagues were greatly angered by an article that $25 million had been given to Cold Fusion. The real sum from the Fusion Institute is only for meetings etc. and is rather little.

The biggest source of funds is probably the Electrical Power Research Institute which has given $3 million over several years.

In many countries such as the Soviet Union, no money has been allocated to Cold Fusion, the workers have done it mainly in their spare time and with material gleaned from many sources. Some US government agencies do fund Cold Fusion.


This was very different from the First Annual Cold Fusion Conference where hopes were high and the media was everywhere. Now it was a more restrained gathering. Believers who had been accustommed to expressions of doubt and sometimes even ridicule, from their neighbours, were pleased to be back in a company where they were appreciated and where people took their work seriously. However the early enthusiasm has gone and very few considered that Cold Fusion would be a source of useful power soon - maybe 5 or 10 years if the problem of reproducibility has been solved. Was frequently asked if hearing all these positive results had not changed my opinion of Cold Fusion, but replied that there were a tremendous number of experiments on fusion such as those described by Ed Cecil, and experiments on hydrogen isotopes in metals all performed before 1989, apart from the negative experiments on Cold Fusion.

Perhaps the most decisive result will turn out to be that in a really reliable detector, Kamiokande, the groups that had previously reported random neutrons and bursts of neutrons with Titanium and gas, now cannot find anything.

Will there be a Third Annual Conference - probably!

Douglas R. O. Morrison