Douglas R.O. Morrison's Cold Fusion News
No. 14—28 May-1 June 1989

Back to Morrison Index

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


1. Introduction
2. Results on the Fleischmann-Pons Effect - Calorimetry
2.1 Summary
3. Possibilities of Use for Power Production.
4. Results on Possible Fusion Products
4.1 Neutrons
4.1.1 Conclusions
4.2 Tritium
4.3 Gammas
4.4 X-rays, helium
4.5 Other Experiments - Muon Bombardment, Deuteron Ion Implantation
4.6 Summary
5. Basic Studies of Hydrogen in Palladium
6. Compilation of Results. Regionalisation
7. Other Comments
8. Possible Future Meetings


A Workshop on Cold Fusion sponsored by Los Alamos and the US Department of Energy, was held in Santa Fe 23 to 25 May. Most participants were from North America and covered a very wide spectrum of interests. Apart from academic scientists, there were people from power companies, new companies set up in the last two months to exploit cold fusion, etc. The 20-strong Cold Fusion Panel of the Energy Research Advisory Board whose Co-chairs are Norman Ramsey and John Huizenga, attended and had their first meetings. The proceedings were broadcast live by satellite TV which interfered surprisingly little with the proceedings. Profs. Fleischmann and Pons refused to attend, but most major participants were present.

Although one of the summary speakers said that nothing much had changed over the course of the Workshop and that there had been very roughly equal numbers of papers with positive and null results, workers active in the field that I talked to afterwards felt that distinct progress had been made. There were a number of positive results presented not seen at the APS meeting - in particular calorimetric results from Appleby (Texas A&M), Huggins (Stanford), and a very large tritium yield from Wolf (Texas A&M) and preliminary evidence for bursts of neutrons from Menlove (Los Alamos). Among the new null results were the very low neutron counting rates (2 per 5 days) in the Frejus tunnel reported by Declais (Annecy), and for the first time calorimetric experiments using good techniques (Paquette of Chalk River used a catalyser to recombine the gases and Hayden of British Columbia used a closed system with a catalyser and Redey of Argonne used a constant heat loss calorimeter). Crooks of MIT reported the non-observation of helium in a palladium electrode as did Appleby who had a positive heat effect.

There were talks on previous knowledge of hydrogen in palladium where Besenbacher of Aarhus expressed grave doubts about the possibilities of fusion there. Garwin and Morrison indicated that there may be no cold fusion effects.

One good result is that some labs agreed to co-operate and arranged to operate their cells in another group's more powerful detector - and some did not agree.


The meeting opened with a talk by Prof. John Appleby of Texas A&M who used a microcalorimeter which had a precision of 1 microWatt over the range 1 microW to 8 W (it is used for work with pacemaker batteries and uses the Seebeck effect). The experiment appeared to be not a measurement of energy balance but a measurement of energy flow. They used small cathodes to avoid long charge-up times, rods of 0.5 or 1.0 mm diameter and 10 mm length, plus a 2mm diameter sphere. The cell had stainless steel walls and was said to be closed but in fact the D2 and O2 gases were allowed to escape. Several plots were shown of the excess rate of heat in mW against the time in hours. Variations of the order of tens of milliWatts were observed during runs which lasted typically 100 hours as the current was varied, e.g. from 60 to 600 to 1000 mA and then reduced again. The excess heat flow corresponded to changes in the current, to the cell being opened, or to changes in the electrolyte from LiOD to NaOD. Their calculations scaled up to an excess heat of about 16 to 20 Watts per cm3 of Pd for the rods and less 4 to 12 W for the sphere, but more (about 30 W) for annealed rods. The amount of 3He and 4He in the cathodes was measured to be less than 3 E9 and less than 0.3 E9 atoms per cm3 resp.[ Please note that my private comments are in square brackets - this would seem to exclude fusion as the origin of the effect observed]. He sought a chemical explanation and excluded D2 and O2 gas recombination. One check made was with a platinium cathode instead of a palladium one and no effect was observed, but as the current was kept at 600 mA, this was not a test of the effect of varying the current. In the abstract it is written that tests were made with light water in a cell and no effect was seen. [comment- the changes in the heat flow were clearly visible - but no details of how this was converted to excess energy were given and no errors were given]. At the start of his talk, Prof Alleby said that the results were not conclusive and that they would not stand up in a court of law.

He also showed results on tritium production made at the same time - these results were discussed in more detail by Kevin Wolf of Texas A&M. In a period of 10 hours the tritium yield rose very sharply from 10 disintegrations per min. to almost a million. In the one graph shown by Appleby, the rise was very sharp [ comment - it was not linear as might have been expected from the excess heat results].

Prof. Robert Huggins of Stanford gave a somewhat unusual talk much of which was concerned with "major quandries" where he suggested various reasons as to why the results were not reproducible, both from group to group and within a group. He mentioned cast versus wrought palladium, dislocations serving as traps for hydrogen, blocking layers at the palladium surface, influence of carbon when the palladium crucibles are made of carbon, effect of H2O on D2O, but this discussion was purely speculative - no numbers were given e.g numbers of failures to number of excess heat observations, nor was any attempt made to correlate the statements with experimental observations [e.g. Fleischmann and Pons had appreciable H2O in their experiments; Case Western Reserve who claimed observation of excess heat, used annealed rods that he had previously equated with failure]. For his own experiment, he showed plots of the heat rise, delta T, as a function of the heater power, for the calibration and for D2O and H2O - all were straight lines. For H2O, the heat rise was slightly less than for the calibration but for D2O it started the same but after some time diverged giving finally a 12% higher value. Thus his basic claim is that they have observed a 12% heat excess (he also says that D2O is 22% more than H2O, but this is not a heat excess). At the APS meeting Prof. Meyerhof had suggested that his results could be due to lack of stirring. Prof Huggins said they had added a water bath shaker and showed that there were no effects that could be ascribed to lack of stirring. Since it was said that there would be a full evening devoted to asking questions of the speakers, there were few asked immediately. In the evening quite a few questions were asked of Prof. Huggins, but he tended to answer that he had already given a full description and they should talk together afterwards. He was asked by Nathen Lewis if he could measure one of their cells and replied yes, but not just now as they were too busy - similar replies were given later. No temperatures were given at this calorimetry talk, but from the APS meeting I had learnt that speakers often speak more freely when they are being questioned by a few journalists who are often very well informed - so I was the only scientist at Prof. Huggins' press conference. There he said that the total temperature rise was 10 degrees and that the D2O rose by between one and one and a half degrees more than the H2O [should it not be more than the calibration?] and this was the heat excess. [ comment - this is almost the same as the value of 2 degrees measured by the Tata Institute in their full account of their work - they do not claim excess heat but simply note that the cathode is hotter with D2O than with H2O]. He also said that he thought it was caused by material effects [another reason for calling it the Fleischmann- Pons effect and not calling it cold fusion]. He said his calculation was very conservative, they subtract the 1.54 Volts and do not include heat of recombination of the gases.

Both Profs Bockris in his frequent interventions, and Huggins said that maybe the reason for groups not getting excess heat was that the palladium rod was not sufficiently loaded with deuterium - they suggested that the D/Pd ratio or "loading ratio' namely the ratio of deuterium atoms to Pd atoms, should be higher, above 0.8. However they seemed not to have measured this themselves and when Huggins was asked how it was possible to go above 0.8 which is the normal limit, did not reply effectively.

Prof. Bockris of Texas A&M give a talk entitled "Seven Chemical Explanations of the Fleischmann-Pons effect" where he estimated the heat excess produced but always got values much less than the early claims of F-P and of Huggins of the order of 10 Watts - the highest he calculated was 0.9 W for the Pauling suggestion of PdH2 formation. He was asked about the Wigner effect, but had not considered it [ comment - this is a favourite explanation of many people. It was responsible for a large release of radioactivity in about 1957 at Windscale - the neutrons absorbed by the graphite had stored a lot of energy in the graphite by changing its structure and the subsequent release of this energy caused the trouble. It had previously been predicted by Wigner. Similarly the absorption of hydrogen or of deuterium by palladium causes the palladium to swell and this stores a lot of energy in the cathode. When the loading stops (e.g. the current is switched off or the level of the electrolyte falls and exposes part of the cathode), then this Wigner energy can be released].

These two positive results have been discussed in some detail, but both are in principle technically inferior to the two Canadian experiments. Dr. Paquette of the Chalk River - Whiteshell Collaboration said the leaving gases went through a catalyst. They found that the power in and the power out were both 5.0 Watts with an error of 0.1 Watt. This was with a current of 100 mA [at times Bockris et al. suggested much higher currents were needed, but Fleischmann and Pons obtained large excess heat with similar currents]. They tried 13 cathodes of Pd in the form of wires, sheets, rods and tubes with masses varying from 1.4 to 41 grams [people with positive results had suggested that those finding null results had too small cathodes but this seems to answer that]. In 11 of the cells the Pd was annealed. The Pd from Johnson Matthey was 99.995% pure [which seems to answer other objections]. The electrolyte temperature varied between 16 and 50 degrees C. The D/Pd ratio was 0.7 and no variation was found to at least a depth of 20 microns - this after 25 days.

Dr. Hayden of the University of British Columbia, used a completely closed system [at last], with a Pd catalyser near the top of their cell giving a 100% efficiency in the recombination of gases. The experiment was thermally isolated by multiple layers of heat shields. The Pd cathodes are 4 by 0.8 by 0.4 cm3 and weigh about 10 grams. Several cells were used with loading factors of 0.8 to 0.84 by weighing. Controls were done using platinium cathodes. the ratio of the power produced of Pd to Pt cathodes was 1.000 +/- 0.003, i.e. 0.3% over the range of input powers from 4 to 18 Watts. He emphasised the importance of the latent heat of vaporisation which at 20 degrees C is only 2% but at 40, 60 and 80 degrees is 6.5, 18 and 44 % resp. so that if the temperature rises for some reason [e.g. electrolyte level falling and releasing the Wigner energy], then an apparent excess heat would be observed temporarily. It is important to know if the gases escaping in other experiments are saturated with D2O vapour and where does this heat go. He showed a graph of the variation with time of the D/Pd ratio - it initially rises linearly then flattens off at 0.8 after 10 hours. This would tend to show that very long charging times are not necessary as had been suggested by finders of positive results. The subsequent run was 12 days. They say they would be pleased to accept cells from others to test. The paper describes other controls in detail - this is the best calorimetric experiment so far.

Dr. Scott of Oak Ridge described their normal cell. They observed no excess power to less than 10%. There were short temperature excursion up to 70 degrees but they could account for them by evaporation processes.

Dr. R. Crooks of MIT described their calorimetric measurements in a constant temperature bath and looked for variations in the heater power needed to keep the temperature constant [a very good technique]. No significant change in power was observed to better than 9%. The palladium rod was analysed for helium and a number of 4 E11 atoms per cm3 found - this would correspond to a maximum power output of 1.8 microWatts. Prof. Bockris said there were many sources of possible errors for experiments that found no effect - the current should be greater than 150 mA - reply "The current was chosen to be 100mA to correspond to the middle of the Fleischmann and Pons range". Bockris said that first the experiment must show that it can find excess heat and then its futher measurements can be believed - this comment rather surprised many people.

Dr. L. Redey of Argonne National Lab. described their experiments using a constant heat loss calorimeter with baths of 30 and 21 degrees C round the cell. This gives an accuracy of 0.1 Watt or 0.8 mW per cm3 of Pd. The cell was semi-sealed which meant the gases could escape. The rate of recombination was found to be very low. The loading ratio D/Pd quickly rose to about 0.8. No excess heating was observed when the current was varied between 12.5 and 500 mA. The experiment was interupted 3 or 4 minutes to weigh the Pd rods to find the D/Pd ratio.

A poster presentation was made by Dr. H. W. Randolph of the Savannah River Site. "An argon purged D2O electrolysis cell is mounted inside a dry calorimeter which measures heat output to +/- 0.2% at 10 Watts thermal. Constant flow Argon sweep gas is dried for evaporation water measurement and analysed by an on-line quadrupole mass spectrometer to measure off-gas species and amounts. Electrolysis power is measured at 10 sec intervals, integrated, and compared with the sum of calorimeter heat, electrolytic heat of formation, evaporation heat, and argon heat gain." [Seems a very good calorimetric experiment.] The result given on their poster was;
Power in = 1.944 E5 joules
Power out = 1.912 E5 joules.
The errors were about +/- 0.1 Watt.

Dr. D. J. Wesolowski of Oak Ridge National Lab. said that some simple tests of calorimetry had shown no excess heat production - their main experiment was to measure neutrons.

Nathan Lewis et al. of Cal Tech used a constant temperature bath accurate to a few mK. They found no excess enthalpy to 6%. The D/Pd ratio was 0.78 to 0.8. He explained various ways in which apparent power excess could be obtained - e.g. it is necessary to have continuous calibration of the heat loss, unlike some other experiments which find positive effects. Prof. Bockris said that to obtain positive heat excess it was necessary to have D/Pd ratios greater than 1.0 and the hydrogen content must be kept low. Lewis answered that 0.8 and 64 mA was the same as Fleischmann and Pons and their aim was to replicate their experiment. Details have been given in previous notes of their experiments using a wide variety of palladium cathodes - it is not impossible that they have comparable results for titanium.


The results of Appleby et al. and of Huggins et al. considered by themselves and if one does not ask too many questions, look impressive and some people watching on Satellite, said they were convinced of the reality of excess heat production. Initially Fleischmann and Pons said that cold fusion could be easily demonstrated on a table top and one did not need complicated apparatus. However with experience it is shown that calorimetry is NOT easy. There are many pitfalls and it is not difficult to get positive results - it depends on your technique and on the assumptions of the calculation. What was good about the Santa Fe meeting was that some groups were now reporting technically good experiments which meant that one did not have to make unverified assumptions. In particular having a closed system with catalyser to recombine the D2 and O2 gases is a major step forward. Several other experiments had constant temperature baths which meant that they avoided the uncertainties in using Newton's Law of Cooling. Thus there are 8 experiments reporting null results for excess power, the best experiment quoting an upper limit of 0.3%. An 8th experiment that finds no effect is by David Williams of Harwell - as the details have not been presented, it cannot be considered on the same level as the other ones, but many people are impressed by it as Martin Fleischmann is a consultant at Harwell and if there had been some special secret [as some believers say but not Fleischmann], they assume that Harwell would know it.

So the most reasonable conclusion from all the evidence is that there is no heat excess.

However there is some evidence from Tata and Stanford, that the cathode used with D2O runs 1 to 2 degrees hotter than the cathode used with H2O. So far I have not seen any comment on this from the 8 groups reporting null results, nor from theorists.

One of the workshop summary speakers, Prof. R. Schrieffer, said that "I personnally do not believe that the heat production is due to anything but chemical effects."

There are indications that the origin of the heat excesses observed by Fleischmann and Pons may be due to the long intervals between adding electrolyte so that as the level falls, part of the loaded Pd rod becomes exposed, releasing the D as gas. This relieves the structure of the lattice and raises the temperature. I had suggested this to Martin Fleischmann almost two months ago, but had been told it was impossible.


In talking with people not closely in contact with the results, when I summarise the experiments, they regret it as it would be so wonderful to have a new source of unlimited power with little pollution, and they often refuse to believe the data and ask if perhaps by developing the technique a litle bit more one could improve it enough to be useful. However there is confusion in the public mind between the claims of some groups to have observed excess heat and hence possibly a new energy source and the linkage with cold fusion. It is not appreciated enough that ALL measurements of fusion products are many many orders of magnitude lower. So that even if the claims of excess heat were true, they would not release fusion energy.

In a Workshop summary, Prof. N. Hackerman said that "suspect few of us here look on it as a truely viable source of power" and no one objected (though it is very difficult to object to anything a workshop summariser says). However there was at least one person who would not agree. This was Prof. Huggins who at his press conference said that he thought it could be a practical source of heat. He said to be useful heat, one would need a higher temperature, several hundred degrees centigrade and perhaps a cheaper material than palladium.It would also be necessary to reduce the heat input, say by cutting it from 10 Watts to 3 Watts - but he would not suggest how he might accomplish this other than by using other materials - titanium. While he obtained 12% excess heat, if one recombined the escaping D2 and O2 gases, this would give more heat. When asked if he had counted the cost of the palladium, he replied that with hot fusion with big machines, one did not include the capital cost.

He did not believe that the source of his excess heat was fusion but was some material effect [comment - this seems a contradiction; to believe that one has a practical source of heat but has to derive it from a material that one has to prepare].

Being rather surprised by this, I talked to him privately next day and he confirmed that he believed that his work could lead to practical power output. When I tried to quote to him the argument that Dick Garwin had presented the previous evening, he replied "which argument, there were so many". When I explained that the real power in was more than just IV, he brushed it aside. There did not seem much point in continuing to try to discuss.



There were some half dozen "positive" results which were generally contested and "explained" and a slightly larger number of null results which tended not to be contested except by Prof Bockris who said that the cells were badly prepared (see Section 2 and later section 5 for replies).

Kevin Wolf of Texas A&M said they had altogether 5 groups working, had 25 cells and more than 200 experiments using electrolysis and absorption of D2 gas for both Pd rods of 1/2 to 6 mm diameter and Ti rods of 1/2 to 3 mm diameter. The NE213 scintillator used for neutron detection had an overall efficiency of 5%. Pulse Shape Discrimination, PSD, was used to separate gammas from neutrons. They have had negative results and positive results. They can measure between 0.5 and 50 MeV. The background rate is 0.8 n per min. and at times they observed 3 to 4 times this for the range 0.4 to 2.5 MeV which corresponds to a source of 50 n per min. over a period of 1 to 2 hours. The graphs of n/min as a function of time showed marked variation, sometimes appearing to correlate with current changes, but not in a clearly reasonable way. A calibration curve for 2 MeV neutrons was shown where the data and the Monte Carlo did not quite fit. Moshe Gai seized on this to say it was the same as he had observed initially and at that time he thought he had evidence for cold fusion. However he found that it was due to multiple reflections of gammas in his ring of neutron counters. Kevin Wolf refused to believe this though I tried to explain for Moshe, that in neighbouring counters if there were neutrons the signals would be displaced in time, whereas if they were gammas, the signals would coincide - and they found coincidences in time.

Prof. F Scaramuzzi of Frascati gave a sympathetic talk where he started by saying that his experiment was relatively crude with a BF3 detector placed next to the cell. They had 3 positive runs out of 10 attempts. They used 100 g of titanium outgassed at 200 degrees. There was some measure of correlation with changes of temperature or pressure. The fact that the counting rate was apparently quantised at 0, 20 or 40 counts could possibly be accounted for if one assumes that the neutrons are emitted in very short bursts as the dead-time of the counters is 2 to 3 microsec. However Dick Garwin objected that if the burst from the cell was so brief, it would be spread out to about 60 microseconds by the time it takes to slow down the neutrons in the moderator.

He also reported the work of Dr. F. Magni of the ENFA CASACCIA who used a sponge of titanium loaded with D2, cooled and then pumped - a small peak of neutrons was observed after about 700 minutes. Further he reported that Dr. G Massoni et al. had the opposite idea of taking used blades of Ti 0.5 mm thick heating them very quickly (20 sec.) to 1000 degrees C. add D2 and cool to 500 degrees. The BF3 counters were inside shielding. Bursts of neutrons were observed when the conditions were changed. Both sets of results looked very preliminary and had apparently not been repeated or controls performed. There were two reports of experiments performed deep underground in tunnels where the cosmic background is expected to be low. Prof Bertin of Bologna who had been collaborating with the Brigham Young group of Steve Jones, reported their results (described in a previous note) in the Gran Sasso tunnel. The background was 10 counts per hour and the signal 35 +/- 5 counts/hour giving effectively 875 +/_ 183 counts per hour from the cell which was in good agreement with the rate observed by Jones et al. in Nature. Moshe Gai pointed out that these rates were very high for a deep underground observatory and were probably due to gammas.

Yves Declais of Annecy presented the results of the College de France, Marseille, Grenoble, Annecy Collaboration who used the Frejus Tunnel. They used the new liquid scintillator NE320 loaded with 0.15% 6Li. They observe both the proton recoils from the slowing of the neutron and also the reaction products when the thermal neutron is captured by the 6Li to give 3He + t in coincidence after a 30 ns delay. PSD gives a very good separation of the neutrons from the gammas. So they have 4 constraints and not only one with NE213. First experiments were done at the Bugey site where they have developed their detectors over a number of years. One point that is very important is to have a good Monte Carlo which fully takes into account the shielding. Their detector was calibrated in the Gran Sasso Tunnel when the background was 1 count per day. The efficiency was 2.7%. The background obtained after off-line analysis was 2 per 5 days. Four different cells with palladium cathodes were used. No neutrons were seen above a background of 0.017 neutrons per hour. If one were to make the ultra-pessimistic assumption that all the background of 2.5 Mev neutrons were in fact signal, the 2 Std. Dev. limit would be less than 1.2 neutrons per hour (but this is an unreasonable assumption). Dr. Declais finished by inviting other groups to come to the Frejus Tunnel where they have a well-established and tested neutron detector which has place inside for several cells. Several groups said they were interested (in particular Prof. Bertin). [Comment - the fact that background rates of Declais et al. are so much lower than those of the Bologna-BYU Collaboration, lends support to Moshe Gai's argument that the latter group's "neutrons" are largely gamma induced].

Moshe also gave a short evening talk about possible errors that can occur. Firstly he said that BF3 counters should not be used! - they were too unreliable and subject to false counts from temperature changes, humidity, vibration.... Also PSD could cause errors and calibration was necessary. Further gammas could give multiple reflections simulating neutrons.

Howard Menlove of Los Alamos reported very recent measurements at LANL in an experiment in which Steve Jones of BYU collaborated. Their results were spectacular and encouraged some people to believe that neutrons are emitted in bursts. They use stainless steel cylinders containing Ti chips and sponge. D2 gas at pressures up to 20 to 50 atm. is used to load the Titanium and then the cylinder is placed in liquid nitrogen then in the neutron detector system beside a control cylinder, and it then warms up. After about 40 min. (sometimes 80 min.) a burst of neutrons is recorded - this time corresponds to a temperature of about -35 degrees C. The normal random neutron emission is 0.05 to 0.2 n per sec. while the bursts are from 10 to 300 n/s. The burst lasts less than 100 microsec. The neutron detector consists of 18 3He tubes and has a high efficiecy of 34%. The dummy cylinder gave no counts over 2 hours. The active one was followed for longer periods up to 25 hours but the burst only occurred in the first 40 to 80 minutes. The result looks very significant but the experiment has a major problem. I asked if they had done the control experiment with H2 in place of D2, and the answer was "No"! Now most people have said that one should not accept experiments where the most elementary checks have not been made and should not have press releases - and co-author Steve Jones is quite strong about it as a major article in Nature accused him and Fleischmann and Pons in very strong language of not having tried H2O as well as D2O. Now this accusation was justified for Fleischmann and Pons but was untrue for BYU (incidently have not seen a written apology from Nature, only a brief correction - should Steve take this to the Press Council or does this only apply to newspapers that falsely accuse someone?). One has some sympathy for LANL as it is natural to present recent results when the lab organises the workshop, still.... So for the present one should suspend judgement even though there is a Reuters press release.

There was a talk by B. Emmoth representing three Swedish institutes. They used a BF3 counter close to an electrolytic cell with Pd and Pt electrodes. The efficiecy was 0.1%. Most of their runs gave no effect and were not discussed but they showed two plots where there were 2 or 3 peaks whose existence did not seem to be correlated with any other activity. They got up to 240 n/s. They were aware of moisture and vibration effects on their BF3 counter. They seem to have done no checks such as running with H2O. To some it was surprising that they presented such a result, but at the same time there was an AP press release which quoted "The results indicate fusion reactions can occur at low temperatures in the electrode material palladium. This gives certain support to Fleischmann and Pons ideas". "The results were reported in a paper to be published by the scientific journal 'Physica Scripta'. The Stockholm daily Svenska Dagbladet was told that the tests were easier to repeat using new palladium plates of sufficient size, rather than already used plates and small ones. "Also the character of the time limited 'bursts' of course are in line with (Pons and Fleischmanns) results even though theirs were longer, almost 24 hours". It surprised some that such a work was chosen for presentation while other careful pieces of work with controls and checks were not - it reminds me of the time when it was claimed that the A2 was split and organisers were delighted to ask speakers with positive results to speak but not those with negative results (as they were not capable of finding it).

Steve Jones gave essentially the same talk as at the APS. There I had said that his statistics were wrongly calculated and he had more like a 2 to 3 standard deviation effect. After we discussed privately he agreed that to evaluate the significance of the assumed peak, one had to take into account the scaling of the background curve under it and this was a serious effect. However the claims were uncorrected. This applied to Run 6 which is almost the only one that shows any significant effect. Including this run, he derived a fusion rate of

lambda(f) = E-23 fusions/d pair/sec.

However at Los Alamos he proposed that as Run 6 was unusual, he would not take it alone and this would make his rate

lambda(f) = E-24 fusions/d pair/sec.

Some such as Moshe Gai were puzzled but seemed to accept this sudden improvement by an order of magnitude when one wishes to compare experiments. However maybe it would be wiser to accept the earlier value in Nature.

Dr. Scott of Oak Ridge reported on neutron measurements using NE213 with PSD. The overall efficiency was 1.46 E-3. The temperature was nominally 28 to 45 degrees C but there was a controlled excursion to 70 degrees. The counting rate was about 4 per hour. No neutrons were seen over a period of 300 hours. Dr. Paquette of Chalk River also reported on measurements of neutrons using moderated 3He and BF3 counters with efficiencies from 0.1 to 1.5%. No neutrons were found with Pd electrodes or with Ti loaded by D2 gas pressure of 40 atm. lowering the temperature to -196 degrees C, releasing the pressure and warming to room temperature (as Frascati). No neutrons were observed and an upper limit of < 0.6 n per sec was established which is less than F&P and Frascati but not quite as low as Jones et al.

Matthews Broer of AT&T Bell Labs described their measurements of neutrons in electrolytic cells with 3 different Pd cathodes. The cells were in a large box with Pb and borax walls and then scintillators to veto cosmic ray muons. Neutrons were slowed in polyethelyne round the cells and the gamma rays produced measured by capture by protons (2.24 MeV) and by 23Na and 127I which give gammas in the range 3.5 to 7 MeV in the NaI and is the more sensitive. After 4 weeks they obtained a limit of < 0.007 n/sec/g Pd which corresponds to <2.2 E-24 fusions/dd pair/sec which is less than the Jones et al. value for titanium.

Nathan Lewis of Cal Tech reported their neutron measurements (described in an earlier note). They give an upper limit of < 100 n/hour/cm3 of Pd.

Dr. D. J. Wesolowski of Oak Ridge National Lab said they used BF3 counters to measure neutrons emitted from Pd and Ti loaded with D2 by gas pressure. The cells and neutron detectors are in a thermostatically controlled bath. They find no neutrons at a level of one thousandth of those reported by Frascati and Fleischmann and Pons but about the same as Jones et al. An interesting point of their experiment was that with the BF3 counters they could get large signals when the leads were moist which disappeared when they dried out. Also when they turned on the sodium vapour lamps, they got 70 000 counts and this was a reproducible effect. With vibration they found hundreds of counts This confirmed the warnings of David Williams and Moshe Gai about the dangers of using BF3 counters.

Dr. Tanihasi from Korea loaded Pd electrodes to a D/Pd ratio of 0.8 +/- 0.1 The neutron spectra with D2O and H2O were the same after 20 hours.

Moshe Gai reported on the Yale - BNL results (given in an earlier note and now submitted to Nature). They have done a major and careful experiment and learnt by experience of the possible traps that give positive results. Pd and Ti rods were used as cathodes and Ti powder was loaded with D2 gas under pressure. They estimate a 3 std. dev. upper limit for d - d fusion giving neutrons to be 1 E-25 fusions/dd pair/sec. which is a factor of 50 to 100 times smaller than that reported by Jones et al.,(they noted that the Jones et al. rate is close to the rate expected for cosmic rays).

The Princeton Plasma Physics Lab used BF3 counters and found their background counting rate was highly variable from 5 to 30 counts/hour. With Pd cathodes and with gas-loaded Ti turnings, no neutrons were observed at a level of 1 n/s for both the d-d and p-d reactions, which is not lower than Jones et al. An unusual experiment, reported by a theorist, F. M. Mueller, was done at Los Alamos. Samples of Pd and Ti were loaded to D/Metal ratios of 0.7 and then were subjected to a shock pressure of greater than one megabar for a period of about 14 microsec. Neutron detectors were placed behind sandbags and Pb bricks nearby. A small instaneous pulse was observed. The authors conclude that less than 1 E4 neutrons were generated.

On the posters there were several negative results. R.I.Ewing of Sandia Nat. Labs, reported no neutrons giving a limit of < 100 n/ hour using 3He counters around Pd cells. LBL - UC Berkeley Collaboration said they found, for currents of 0.25 to 1.25 A, no neutrons corresponding to a limit of 1 E-22 fusions/dd pair per sec. Dr. C Ellegaard et al. of the Neils Bohr Institute, Copenhagen, used 10 rods of Pd with 500 mA current and 3 litre NE213 detector surrounding the cells and also Ti loaded with D2 gas under pressure and heated to 500 degrees and cooled to liquid nitrogen temperature then warmed to room temp. No neutrons were found. J. C. Hill of the Ames Lab at Iowa State reported no neutrons from cells with a Pd cathode at a lower rate than F&P. With Ti loaded with D2 gas absorbed at 110 degrees and up to 660 psia where the achieved a maximum loading of D/Ti of 1.9 [this is possible with Ti not Pd] no neutrons were observed above a counting rate of 6.5 counts per 10 min.


There are many groups who report upper limits of neutron production many orders of magnitude less than those of Fleischmann and Pons for cells with Pd cathodes and for those of Frascati for gas loaded Ti and it must be concluded that these results are excluded. The neutron rates of Jones et al. are appreciably higher than those of Frejus and of Yale - BNL but BYU used Ti and the others Pd which may provide a temporary loophole, but other experiments find no neutrons at the same level as Jones et al. Also the statistical accuracy of BYU has not yet been properly calculated yet. Thus the probability is that the BYU results are mistaken. This issue should be settled soon as Steve Jones took up the challenge from the floor of Moshe Gai to bring one of his working cells to Yale to test in their apparatus !


One of the striking results at the conference was the report by Kevin Wolf of abundant tritium production. 5 E12 tritium atoms were detected in the solution of the cell several days after the neutron production runs. The solution was also analysed by Sandia and General Motors who confirmed the presence of tritium, which therefore was not due to chemiluminescence. Prof. Appleby showed a graph with the tritium count, disintegrations per minute rising exponentially from 10 to a million in 10 hours [why such a short run compared to other runs of the same Texas teams?]. The tritium content of the cell before is not known. The energy spectrum of the betas looks reasonable (unlike Fleischmann and Pons). It is difficult to evaluate the fusion rate as one does not know in what time the tritium was produced, so the rate could vary between 1 E-3 to 1 E-8 Watts per cm3 of Pd. This is both a very low rate compared with the Watts reported by Fleischmann and Pons and is a very high rate compared with any other fusion product rate reported. Now in first approximation the fusion reactions
d + d ---> t + p
and d + d ---> 3He + n
have equal cross sections and hence one would expect the rates for n, p, t and 3He to be closely comparable. But this tritium rate is in contradiction with all neutron yield experiments and is in contradiction with the 3He yield of Texas itself! Perhaps Dick Garwin's comment is best - he believes there was tritium there but does not know where it came from! It was suggested that cathodes be analysed to look for tritium.

M. L. Muga et al. of Florida Univ., Gainsville find no tritium in contradiction to a report from another Gainsville group - it is thought that the latter's room was heavily contaminated.

R. Crooks et al. of MIT looked for tritium but did not find any - do not have a note of any limit being given.


Six groups whose experiment is described above, reported that they had searched for gammas and had not found them. They were; Dr. Scott et al. of ORNL, R. Crooks et al. of MIT, Dr. Tanihasi of Korea, N. Lewis et al. of Cal Tech, all reported null results, but do not have limits. Dr. M. Gai of Yale-BNL Collaboration gave a rate of < 1 E-22 fusions/dd pair/s The Princeton group gave a limit of < 3 gammas per sec.

What was very worrying was the discussion of the Fleischmann and Pons result by Dr. Crooks. He showed plots of their result together with his, which is very different as the peak at 2.2 meV is twice as wide and also on the low energy side the rate rises due to the Compton edge and other effects. The mystery is how Fleischmann and Pons could produce such a plot? It is also worrying that they showed an earlier plot of a different shape and even indicated that the peak was at 2.5 MeV (the value you would expect if the neutrons were not slowed down) and not at 2.2 (as expected when the neutrons are captured at rest. This is troubling.


R. Fleming et al. of Michigan Univ. looked for the 21 KeV characteristic X-rays from Pd. The background rate was 3 counts/hour and no increase was seen during 2 days running of a Pd cell.

The observation of 3He or 4He in the cathode after electrolysis is considered a major test of fusion since the only possible explanation of the observation of Watts of heat but of fusion products only at many order of magnitude lower rates, would be that one had
d + d ---> 4He + energy
and possibly p + d ---> 3He + energy
and this energy is somehow absorbed by the lattice instead of emitting a gamma as it would normally [this is pretty far-fetched as timing is wrong by many orders of magnitude, but it is useful to check anyway]. One result has already been reported in section 2 and was;

Appleby et al. gave upper limits of 3 E9 and 0.3 E9 atoms per cm3 for 3He and 4He resp.

Crooks et al. of MIT said they had examined a small sample of Pd and found no 4He giving an upper limit of < 0.1 E9 atoms per cm3 of Pd.

This confirms that if there is excess power, it does not come from fusion.


It has been suggested that fusion might be triggered by muons from Cosmic Rays. This has already been tested at Bugey by a French-Swiss Collaboration where there was a layer of scintillator to detect muons, inside the Pb, water and boron layers. 2% of the time there was the signal of the passage of muons, and separate counts were made of neutrons, but no effect was seen.

More direct experiments were made by firing beams of muons into an electrolytic cell. M. Gaudreau of MIT reported passing 80 KeV/c muons into Pd and Ti targets at a rate of 1000 muons/sec/cm2. The authors are still interpreting the results but indicate no dramatic effects were observed. At KEK, K. Nagamine et al. passed muons into Pd samples loaded to a ratio of D/Pd = 0.6, and unloaded. They observed no differences. They deduced a neutron production rate of < 0.012 n per muon. It was concluded that the rate of producing neutrons from cosmic ray muons was < 1.3 E-6 per sec. The Colarado School of Mines reported that they had implanted D ions of 95 KeV in 1.5 micron thick foils of Pd giving D/Pd ratios of 1.0 or above. No significant effect was found giving a limit of < 0.2 n/dd pair/sec or < 5E-10 Watts/cm3 of Pd.

S. M. Myers of Sandia Nat. Labs. gave a talk about ion implantation which will be discused below. They also did an experiment where D ions of 10 KeV, were implanted into Pd at 40 degrees K. Clear signals of 1 MeV tritons and of 3 MeV protons were observed from the reaction d + d = t + p and this allowed the loading ratio D/Pd to be measured. After the beam was turned off no significant rate of fusion was observed despite the loading being much higher than can be obtained by electrolytic or gas pressure methods. An upper limit of 2 E-22 fusions/dd pair/sec was estimated. Ti and Zr were also tried with null results.

During the conference a press release was received saying that a group of Mexican scientists had achieved cold fusion producing more energy than any other experiment reported to date. "With this success, they have increased the (prospects) in our country for the use of fusion to produce energy". The team of M. Fernandez et al. at the National Institute for Nuclear Reasearch, had discharged electrodes one of steel and the other of titanium and magnesium in an atmosphere of enriched deuterium. "A considerable number of neutrons per second" were produced. Such press releases illustrate the importance of responsible workers in the field explaining clearly what is happening to all countries in the world.


The major conclusion is that all the measurements of fusion products agree that any possible fusion rate is many orders of magnitude less than would be needed to account for any positive measurement of excess power that is claimed.

There is the question "is there any experiment which has been carefully performed and all the checks and controls made, which has statistics that everyone agrees are significant, which shows a positive result?". This is tough and for some an emotional issue. Many would not like to answer this question yet. But the best and most careful experiments with the most controls, (e.g. Frejus, Yale-BNL) find nothing. One would still like to check further for the possibility of bursts as suggested by the data of Menlove et al., but first these need to have basic checks done.

Inevitably in trying to report many papers, there must be some mistakes. Please accept my apologies and send me corections or additions


On the last morning there were some interesting talks on the fundamentals of hydrogen in palladium by long-term experts in the field.

G. S. Collins of Washington State University studied ions in lattices by perturbed gamma-gamma angular correlations, PAC techniques - essentially observing waves of various frequencies. For example as H ions diffuse into Ni, the waves change as the Ni is annealed at various temperatures. It was observed that Li ions can diffuse into platinium as its radius is small, 0.7 A.

F. Besenbacher of Aarhus in Denmark gave a major talk. He compared their results with the Effective Medium Theory (Morskov, PRL 35 (1987) 7433) which he showed fitted the data very well. He showed drawings of the effective electron density in palladium lattices. He described trapping, channeling, the depth of ion implantation, annealing effects. I asked him 2 questions;

Q; What is the chance of having two deuterons in the same site?
A; Zero
Q; What do you think of the chances of d-d fusion in Palladium?
A; (after a long pause - for politeness?) I am sceptical.
Other answers were equally illuminating.
Q; Is palladium the best metal to use?
A; I would not chose palladium. Aluminium or copper would be better.
Q; Normally people reach D/Pd ratios of 0.7 to 0.8, but it is said that to succeed with fusion, you need > 0.8
A; Alice in Wonderland
(later he said that for > 0.8, one needs ion implantation).

S. M. Myers of Sandia Nat. Labs. said that normally by electrolysis or by gas pressure one can fill the octahedral sites, but to bring the deuteron ions closer together, one needs to fill all octahedral sites first which means going beyond the stoichiometric condition to superstoichiometric palladium hydrides, i.e. D/Pd ratios of above one. D-implantation is found to give D/Pd ratios up to 1.3 at 35 degrees K. Graphs were shown of the D/Pd ratio as a function of depth as more and more D was implanted. As the temperature was raised, the ratio fell to 0.8 but then stayed there from 100 to 130 degrees K, then fell again, indicating that there is a stable condition at 80 K (it means that 80% of the octahedral sites are filled). He said the error on 1.3 was 0.1.

J. Bigelstein of SUNY discussed enrichment of tritium during electrolysis and gave a table of enrichment ratios as a function of the fraction of electrolyte used - the ratio goes from about 1.4 at 0.6 electrolysised to 5.1 at most for 100% electrolysis. He said he would look with suspicion at any experiment that did not find an enrichment. On the other hand this did not explain the very large tritium yield claimed by Wolf et al. of Texas A&M Another point brought out in the discussion was that there is tight control over the amount of tritium in liquid D2O for radioactive safety reasons (must be safe to drink), but not for D2 gas - so D2 gas can sometimes contain high amounts of tritium and experimenters should measure the initial amount of tritium before measuring tritium afterwards.


In compiling results reported on cold fusion, I found that the ratio of positive to null results varied greatly from region to region of the world. There was a strong correlation with the information available in the region. Also the results within a region varied with time. These results are statistically very significant. As this survey was not presented in detail at the Santa Fe workshop, these results from 83 different labs will be given in a separate note.


After many protests, the Wednesday evening was given to discussion with no presentations allowed except that Dick Garwin was given at the start, 5 minutes for comments - this was rather brief as he made major comments on all the positive results. He started by saying that of the original results of BYU and Fleischmann and Pons, they were all gone except for some evidence of excess heat, but not fusion. Huggins had found more heat and one might believe that but not necessarily energy. The power in is not just IV but is twice that in a realistic calculation. His result if fusion, would imply 3 E5 neutrons per sec while the Texas result would imply 3 E9 neutrons per sec - which should have observable effects. As for the tritium result, Garwin said he believed there was tritium, but did not know its origin. For the subject of neutron bursts - as one counts thermal neutrons, they take time to diffuse and hence there cannot be sharp bursts in times less than these diffusion times which are exponential decays. He also discussed briefly what was happening inside the palladium lattice explaining how difficult it was to have two deuterons close to one another. Pyroelectrics can give large fields but not fusion.

Near the close of the discussion, D. R. O. Morrison said that Dick Garwin had given a major talk hinting that many results had other explanations, but no one had commented on it. Dick Feynman had offered a solution to the situation that we face today where;

(1) we cannot find a theory that fits all the data, or as Peter Hagelstein had asked "does anyone have a theory that will allow two deuterons to come close enough together that they have a good chance of fusing?"

(2) experiments seem to be in contradiction with one another. Feynman's solution was to say that sometimes one has to assume that an experiment is wrong. Now this is not something that one likes, but everyone makes mistakes. Now have been interested in Wrong Results in Science for many years and after reading the famous chemist, Irving Langmuir's paper on Pathological Science, I have extended it to more subjects and have been giving lectures on it for the past 13 years. After analysing 83 experiments on cold fusion reported so far, there is strong statistical evidence that cold fusion is a case. In view of the great interest and importance attached to the subject, no serious explanation, evem if disappointing, can be neglected.

In his balanced and kindly summary talk, Bob Schreiffer said something that made me ask him afterwards if he had been reading Langmuir's "Pathological Science" article - he said , yes he had.

In a previous note, I had repeated a public statement that Peter Hagelstein of MIT had withdrawn his explanations of cold fusion. At Santa Fe he has told me that he has not withdrawn them.

Am told there are 6 patents applied for by U of U, one by BYU and two by U. St. U. (who are working away busily without drawing attention to themselves). Someone seems to be mailing anonomously tapes of what is said to be a patent application by Pons and Fleischmann - one person who looked said it did not contain anything special or magical.

There are quite a number of companies which have been set up to exploit cold fusion, at least six in Utah and I gather they are not short of investors. Of the $5 million that has been set aside for cold fusion by the State of Utah, it is said that one million has already been released - to pay the lawyers!

While in Santa Fe, I heard that the DOE Cold Fusion Panel which had wanted to visit the labs quickly, had been refused permission to visit Pons's lab at U of U. and they did not want DOE funding. This rather unscientific decision surprised some, but the Deseret News of SLC (Salt Lake City) explains the other point of view. On 28 May there was an article entitled "US Fusion Panel cancels plans to view U research". "The visit scheduled Wednesday, was cancelled after fusion researcher B. Stanley Pons told the panel co-chairman, John Huizenga,... to change the make-up of the "negatively biased" committee or stay out of his U. laboratory."

"I have refused to entertain this committee for several reasons" Pons told the Deseret News, "I see this visit as a waste of valuable time, since many of the panel members have already clearly stated their positions. I feel there is very little one can say to a hostile person that will change his mind". ... "It is disappointing that the committee is composed of so many members who have previously stated their very negative position in the press regarding this research" he said. "the most notable of these are Richard Garwin, Steve Koonin, and Mark Wrighton.

He said they "have only allowed reputable sincere scientific collaborators into their labs and will continue to do so"

"He was very understanding and sensitive to these points; he admitted that my perceptions regarding the composition of the panel were correct: some very open-minded individuals such as ......., some very negatively biased individuals, and no positively biased individuals".

"Pons said he proposed a visit could be arranged if the committee would agree to either of the following conditions; dismiss the negatively biassed people or add an equal number of positively biassed individuals". "He recommended adding..............Or Pons or Fleischmann himself". He was notified Friday the committee's visit had been cancelled.

A committee member, X, said he is sympathetic to Pons' concerns. "He is certainly taking a lot of flak and I can certainly understand that he would feel this way" "Personally I know the people on the board and they wanted to go there (the U.) to learn. I don't think the other committee members have made up their minds, but there is a lot of scepticism"... "It is still possible that he is right and people do not realise what it takes to make the experiment work"

Pons said "The newest results are very strong and indeed confirm and surpass our earlier results. These data and their analysis will be published later this summer in scientific literature. In addition, we are developing collaborations with reputable scientists who will help us with the rapid development of the fundamental aspects of and practical applications of this work".

Pons is displeased that the commitee cancelled its visit rather than negotiate with Fleischmann and him. "It appears that the people who would benefit most by this work being discredited, have again taken the initiative to cause us great difficulty" he said."I am pleased to tell you that they might cause us difficulty, but they will not stop the science" X "believes Pons is right on this point". "A recommendation -- pro or con-- by the government committee won't faze private industry"

In a related article entitled "U. backs decision", it is written "While the University of Utah would welcome a visit by the Department of Energy's panel on cold fusion, a U. official said Saturday that he respects the decision made B. Stanley Pons and Martin Fleischmann not to allow the committee in their lab". "When we were asked if the committee could come, we said 'of course' said James J. Brophy, Vice-president for research.


At the end of the Santa Fe Workshop, it was suggested that there should be another workshop sometime, perhaps in the autumn. The basic idea of a workshop is excellent as it succeeds in allowing scientists working in different fields to discuss together instead of having meetings where only certain people are invited (e.g. only those with positive results). Also it allows people who are investing commercially in the field, and there are millions of dollars engaged, to evaluate the practicalities of the subject. Some of the features of the Santa Fe workshop were excellent, others could be modified. Some comments;

1. The workshop should be announced as early as possible and those concerned targetted so that people from all parts of the world can attend.

2. It is not enough that most people get a chance to present their work or ideas it is necessary to avoid that the discussions are so dispersed that no one has any idea what the conclusions might be. Normally this is done by having a series of survey talks on each sub-topic as well as broad topics, early in the workshop which can focus the discussion (often by being a target for the workers in the field). This prevents also undue repetition and sometimes wilder ideas (some people said they had never heard so much bad science at a conference).

3. With 450 people in a room, it is difficult to have a profitable discussion; it is better to have many separate working groups with fewer people.

4. An innovation at the conference was to have badges with a small number on them. It was also hard to write on the glossy surface. It was very effective in convincing people that there is an advantage in having badges with their name and affiliation on them. I realised that of the 450 persons present, that two months ago, there were only three whom I had previously met occasionally, but the subject is so intense and interesting on different levels, that I now feel as if I had known many of them for years.

5. The registration fee of $400 was a surprise to many and jokes were heard that Los Alamos was the first to make money out of Cold Fusion (wrong - the lawyers were first - or someone who played the palladium futures). Normally we arrange that for a sponsored conference, the sponsors contribute and for $400 one has 5 nights accomodation, 5 breakfasts, 5 lunches and 5 dinners plus the conference hall and proceedings. So it was a surprise to find only two lunches and the conference hall plus proceedings were included. On the other hand the conference hall was very big which had the advantage that coffee could be served at the back without disturbing the proceedings and those having a discussion there could still hear the speakers and decide if they wished to return to their seats - small point but good organisation. The library service and the copying service were excellent a great help to the distribution of knowledge in a very fast moving field. So finally the $400 was almost justified even if it probably discouraged some who would otherwise have attended.


The conference will clearly be judged a very useful step when the history of Cold Fusion comes to be written. It was the first time that a large proportion of those interested could meet together, electrochemists, chemists, particle physicists, nuclear physicists, material scientists, venture capitalists, power organisations, government officials and the DOE panel, etc.

Nothing too dramatic happened. But many people may have gotten a first taste of evidence and opinions that they had not been exposed to before and this can only be valuable in the long term.

Finally society must make a judgement on this subject that has excited such great interest and raised such wonderful hopes. Although most, though not all, workers in the field realise that cold fusion will never be of any practical use for power production, this is still not the popular perception of it. Most people still hope that maybe something will come of it. There seems to be a tendancy amongst some to let the bad news leak out slowly. This is often good politics and PR, but not all scientists feel this way - they want to avoid people getting into false positions because of lack of knowledge of the facts.

There is a second question which is of purely academic interest - does there exist cold fusion at some very low level (a billionth or a trillionth or a billion-billionth of a Watt). Clearly the Fleischmann and Pons level is excluded by the data, but some hope it might occur at the BYU level, but again there are good experiments which find no counts at much lower levels. So one cannot avoid asking the difficult question of whether all the positive results are mistaken. Scientists do not want this to be correct, but can one exclude it?

The consequence will be that for many we are not yet in phase 3 and the debate and experiments will continue for some time more.

Douglas R. O. Morrison.