47 Infinite Energy • ISSUE 24, 1999 • MIT Special Report Mark Wrighton Exhibit V Prof. Morrison’s Report to President Charles Vest October 14, 1991 Professor Morrison’s conclusion that the MIT PFC paper “does not mislead” is completely untenable. It does not square with the facts and it never will.—EFM MIT Department of Physics, Room 6-205 To: Charles Vest, President From: Philip Morrison, Institute Professor (emeritus) Assessing the Request for an Inquiry by Dr. Eugene Mallove, made August 18, 1991 I. My Standing in the Matter In the presence of clear concern for equity in treatment, I begin by stating my own qualifications and limitations as an assessor. A theorist with considerable experimental experience--though to be sure, most of it gained long ago—I think I am qualified as a referee of the overall methods and content of a paper on cold fusion, denoted Plasma Fusion Center PFC/JA-89-34, prepared and published by an MIT team from PFC and three other MIT departments, with sixteen co- authors ( Journal of Fusion Energy, 9, 133-148, 1990). It is this paper that is the focus of the substantive issues here, issues that grew in interest well after the summer of 1990. I shall not comment on the relationships between PFC research peo- ple and the media during the heated summer of 1989, though that is also part of the request for inquiry. Others may consider them. The topic crosses disciplines; indeed, that is one of the sources of trouble. My background in nuclear physics is strong, but I am not an electrochemist. Much of my general grasp of that specialty has been gathered during the cold fusion controversy itself within the last two years. I regard my task as that of an interested scientific reader, but not one who could propose detailed improvements in the entire experiment design. The editors who found referees for the paper would probably seek more than one referee. That understood, I shall support my opin- ions with inferences drawn from the paper and the criticism of it offered in Dr. Mallove’s submission. I know several of the participants in this dispute, none of them better than I know Dr. Mallove himself. His astronomical specialization and interest in science education and science journalism have brought us together over perhaps a decade, before and during his stay at MIT. Dr. R. Petrasso of the PFC, a nuclear experimenter, is the second person involved whom I know rather well. Our interaction extends over a few years, about a year longer than the cold fusion era. Of course I know the Provost and other more senior members of the team, but not with so much contact as with Mallove and Petrasso. I do not think I hold any sort of animus for any of these colleagues. Toward the idea of cold fusion itself I was rather more tolerant and optimistic than most physicists. I still believe that there may be a germ of novelty in some electrochemical phenomenon that is caught up in this complex system; it is very unlikely, though logi- cally possible, that new findings, if established, would turn out to have high economic importance. They would at most open some way to build a new battery, possibly a fuel cell. II. The Substantive Issues The papers before me are somewhat tangled. The core of the topic is the publication in the JFE. It is here, at least in part, in four distinct versions: the published paper, the MS finally submitted to the JFE and dated July 1990, and two partial drafts of that MS, both by S. Luckhardt of PFC, with signs of much comment by co-authors. The drafts are dated July 10 and July 13, 1989. With 16 authors, no paper will have a simple his- tory. This one shows that to be true; the published version itself is not the same as the MS submitted, but bears strong mark of editorial changes, in text and in figures. All of this is entirely to be expected. Two distinct experiments are reported. Phase I was “hastily assem- bled,” within days after the initial TV show from Utah. It sought both real-time nuclear radiation and excess electrochemical power. Phase II was more ambitious, designed as a much more sensitive test of all Utah claims by rough replication, and extended over a couple of months. All MIT results were negative: real-time radiations, atomic products of fusion within the cells, and excess electrochemical power. In addition, a telling technical criticism of the published Utah-gamma-ray data is included. I could find no claim by the MIT authors that was not well supported by the data they include. III. The Ground for Complaint What then is the ground of complaint? It is not without a logical basis. The sensitivity of the MIT tests for nuclear radiations is improved by two or three orders of magnitude over the Utah experiments. Even stronger limits follow from the search for certain fusion product atoms. In mid-1989 the Utah [people] claimed such products in ample amount, easy to find. For the most part by 1991 those side effects were no longer claimed, and the main evidence cited was excess power during elec- trolysis of heavy water. It is perceived that a new form of fusion might escape all side branches to deliver energy as lattice heat alone, making helium as the only product. Even this seems limited by this experiment to a power down from the Utah claim by a thousand or so. But the Utah investigators are electrochemists, and skilled in calorimetry. In that domain—if not in gamma-ray or neutron detec- tion—they worked closer to the state of the art. The MIT team claimed an intrinsic sensitivity of their own calorimetry no better than 10 mW, from the noise visible in all their power measurements. They claimed overall only a conservative 40 milliwatt sensitivity, about 3% of total power, allowing for cumulative systematic changes as the open cells ran for a week or more, losing water and gas. (Uncontrolled catalytic recom- bination of the oxygen and hydrogen produced gas is a source of possi- ble excess power in the right range.) The MIT estimate of the excess power expected using the scaling meth- ods of Utah applied to the MIT electrodes and current was 80 milliwatts. The point is clear: the expected nuclear products are excluded by the MIT paper at a level down from the Utah claims by several orders of magni- tude. But MIT could limit the excess calorimetric power only by less than one order of magnitude, a factor somewhere between two and five. That entails much closer scrutiny of the much less precise results of calorimetry. The hope of the optimists—Mallove is not the only one—is that the assumptions, plausible as they are, that fusion has to proceed at least in part along known channels, is somehow wrong. Heat is the most gen- eral (and desired) product. (Helium appears to me almost equally robust; if it is not made, the process is hardly fusion. It is possible that helium is lost from the cells.) IV. The Two Drafts Differ The focus of Mallove’s criticism is on a difference between the two partial MIT draft manuscripts. In the earlier one (Attachment 5) the excess power is corrected by a simple linear fit for long-term drift and plotted, with many points, both for heavy water and the light water control cell. I measured on the MS graphs the mean excess power over time for both cells, using for each the area of the region between the locus of zero power and the noisy data. The mean power excess: heavy water cell +15 milli- watts; light water cell + 4 milliwatts Neither result is significant, for the claimed power error is 40 mW, and even a less stringent definition would put the error at 20 or 30 mW. The 13 July draft fits a less simple, least square cor- rection to eliminate the drift, and ends up with a value I did not measure, but one visibly close to zero for both cells. The claimed error is not reduced; such small vari- ations in the mean are simply not significant, whether they turn out zero or not. The first hint of a small positive excess power in the heavy water cell is a source of encouragement for From Philip Morrison’s PBS Television Series

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48 Infinite Energy • ISSUE 24, 1999 • MIT Special Report those who expect power from fusion, and its disappearance between drafts is the burden of Mallove's concern. But it might well have been that the new correction would have shown the other sign. After all, the light water cell also indicated an excess power at first, if smaller still. These are matters of chance at this level of power. Objectively, one has to say that the published paper does not mislead; the change in power between drafts is rather smaller than the clearly stated and plausible overall error, at most a little outside of random error alone. The disappointment of a hopeful reader is understandable, but hard to defend in reason. The open possibility might support an effort to do experiments with more precise calorimetry; they have gone on apace since, though not at MIT or at PFC. V. My Recommendations I close with an explicit answer to your questions about options for action in your letter of 9 October 91. 1) I do not believe an inquiry needs to be conducted. 2) I do not believe any formal investigation is needed. Both of these recommendations apply only to the scientific paper, and not to the media interactions. 3) On the other hand, I recommend that PFC should spend a person-day or two of work to compute the mean excess power for all four cases, the light and heavy water cells under the two protocols of drift correction. They should also describe the two approaches to correction in more detail than the by-name-only account in the letter by Dr. Parker to Dr. Mallove of 8 August 1991. (Notice that in Figure 6 of the MS submitted from MIT, but not in the published version, one fit to the declining heater power curve is drawn.) The work need not even invoke much ado about old records; it can probably be done from the curves already published or at hand and the algorithms used. Making these few numbers publicly available, first of all to Dr. Mallove—they are probably not important enough to publish—would for me fairly and helpfully clear the record. Anyone is then free to make what use he can of data that are clearly below the level of significance, if possibly suggestive to the hopeful. Sincerely, Philip Morrison Exhibit W President Charles Vest’s Letter to Eugene Mallove October 17, 1991 President Vest tries to settle the matter with the Morrison memo. Nice try, but no cigar.—EFM Dr. Eugene F. Mallove, Bow, New Hampshire Dear Dr. Mallove: As you know from my letter of October 15, 1991, I have asked Insti- tute Professor Emeritus Philip Morrison to review the materials you sent me, in light of your concerns about the scientific content of investi- gations by MIT scientists into possible cold fusion phenomena. Profes- sor Morrison has now done so and has submitted to me a thoughtful memorandum stating the issues as he views them and presenting his recommendations regarding an appropriate response for the Institute. I am sure that you join me in appreciating Professor Morrison’s careful work in this regard. Enclosed is a copy of Professor Morrison’s memorandum, dated October 14, 1991. Before any further actions are taken by the Institute, I would like to have your reactions to his recommendations. Professor Morrison has kindly agreed to make himself available to discuss the content of his memorandum with you, if you so desire. I hope that this represents a constructive step toward resolving your concerns. Sincerely yours, Charles M. Vest Enclosure cc: Philip Morrison, Mary P. Rowe Exhibit X: Eugene Mallove’s Letter to President Charles Vest, October 24, 1991 I opposed the conclusions of the Morrison memo in very strong terms, asking again for a full-scale investigation. — EFM President Charles M. Vest MIT Room 3-208 Dear Dr. Vest: Thank you for sending me Professor Philip Morrison’s memoran- dum of 14 October to you regarding my 18 August request for an inquiry into scientific misconduct at MIT. First, let me say that I have the highest regard for Professor Morri- son as a gifted scientist and educator, a man of impeccable character, and one of the finest human beings I know. I also count him as a friend and a person who made an honest attempt to be fair to all sides in his letter to you. I deeply appreciate the time and effort he made on your and my behalf. With that said, I regret to tell you that I am in substan- tial disagreement with Dr. Morrison’s conclusions about the technical matters that he discussed. These disagreements I detail below. At your request, Professor Morrison did not concern himself with the substantial issues of motivation and dealings with the press by Pro- fessors Parker and Ballinger. That was a significant part of my request for an inquiry and investigation. Not only is it absolutely clear to me that these individuals engaged in reprehensible conduct in the manner that I have described and documented, but their behavior significantly illuminates the handling and representation of the technical aspects of their experiments. The PFC cold fusion experiments of 1989 were by no means conducted in an intellectual vacuum. There was a clear rush to judgement by that group and a calculated attempt by at least two of its members to besmirch the scientific work of Drs. Fleischmann and Pons. I urge you to immediately turn over this aspect of my allegations of mis- conduct to a panel of individuals who will assess these concerns fairly and make recommendations. Now let me return to Professor Morrison’s memorandum to you. I do not agree with his conclusions that there is no need for an inquiry and no need for an investigation. I have read Professor Morrison’s com- ments carefully. With due respect for his prodigious scientific talent and respected judgement, I come to very different conclusions, for reasons that will become clear. First, let me begin by noting Professor Morrison’s initially stated bias, a term that I hasten to characterize precisely in imputing such to Dr. Morrison. It is certainly not a bias that arises from any animus, but it is a bias nonetheless. He writes, “I still believe that there may be a germ of novelty in some electrochemical phenomenon that is caught up in this complex system; it is very unlikely, though logically possible, that new findings, if established, would turn out to have high econom- ic importance. They would at most open some way to build a new bat- tery, possibly a fuel cell.” I suggest to you and to Dr. Morrison that this flies in the face of the work of hundreds of researchers around the world —many working right now and getting remarkable results—scientists who have done experiments that clearly reveal nuclear processes at work where none should be, by conventional reckoning. If Professor Morrison relies mainly on what he has read in Nature about cold fusion or what the people at the Plasma Fusion Center have told him, then that may explain his missing a host of phenomena that many observers, who did not reject cold fusion in the spring of 1989, see as firmly established. There are two classes of phenomena that in my view have been experimentally confirmed in deuterated metal systems: (1) Calorimetrically measured excess energies that exceed megajoules per mole (tens of MJ/mole has been reliably found) and (2) Nuclear anomalies that may well be linked to the excess heat, albeit not in naive or one-to-one correspondence to nuclear products that have been mea- sured (there may be others not yet measured). Among the byproducts that have been found are tritium, neutron emissions (both burst and continuous), helium-4, and charged particles with MeV energies. There is a steadily growing literature of such findings, both thermal and nuclear effects. This cannot be brushed away. It must be evaluated and studied carefully, without the preconceptions that have plagued this controversy. The phrase, “They would at most open some way to build a new battery . . .,” I have heard before. It was made by Dr. Frank Close, whose assessment of cold fusion deliberately did not include the vast bulk of supporting data. In evaluating the MIT experiment, Professor Morrison repeats the

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49 Infinite Energy • ISSUE 24, 1999 • MIT Special Report canard used by those who have tried to “wish away” many cases of experimentally determined excess heat: “Uncontrolled catalytic recom- bination of the oxygen and hydrogen produced gas is a source of possi- ble excess power in the right range.” A number of excellent experiments have thoroughly investigated this “explanation” and have rejected it. Recombination is not a significant factor in open cell work. (In closed- cell, deliberate recombination work, it is no factor at all, and there are excellent positive experiments of that kind too.) On the other hand and to his great credit, Professor Morrison correctly notes, “It is possible that helium is lost from the cells.” Indeed, this is precisely the result that researchers at the Naval Weapons Center have recently reported in con- nection with their calorimetric work. There is a significant omission in Professor Morrison’s critique. Nowhere do I find an assessment of the validity of subtracting a “some- what arbitrary linear function” from the raw heater power data to get net excess power. Dr. Morrison assumes a priori that the group employed a correct algorithm. But as my 18 August letter suggests, that methodology is completely incorrect. Professor Morrison accepts what I believe to be a gratuitous state- ment in Professor Parker’s hastily prepared letter to me of August 8, 1991—the one I received on the eve of the WBUR radio broadcast—in which he tries to explain the apparent curve shift between July 10 and July 13. Parker’s statement is: “In one, the drift was fitted with a some- what arbitrary linear function. . . in the other, the drift was fitted with a different linear function, this time a least squares fit, and the data appearing in the final version of the paper were produced.” I do not think it is possible to accept this statement on its face. The light water curve has not been moved down by any new form of mathematical adjustment, but the heavy water curve most certainly has been moved. In fact, I believe that this statement about two methods of fitting the drift to be a complete fabrication on the part of Parker, much as his statements about what he did or did not say to Nick Tate are completely false. Professor Morrison is certainly correct that the July 13 draft results in an excess heat that is “visibly close to zero for both cells.” I do not contest that, for that is precisely what this curve shift was apparently intended to bring about. So, I must strenuously disagree with Professor Morrison’s statement, “Objectively, one has to say that the published paper does not mislead.” I believe to the contrary. The paper misleads most egregiously. Professor Morrison’s polite recommendation #3 directly governs this matter: “They should also describe the two approaches to correction in more detail than the by-name-only account in the letter by Dr. Parker to Dr. Mallove of 8 August 1991.” In my view, there is very strong evidence that the alleged “two approaches” is real- ly only one method of fitting the data and performing the foremen- tioned inappropriate subtraction of the resulting fitted line. The second “approach” is merely data-averaging into one-hour samples and subse- quent shifting of the curve down to give the impression of a null result. More evidence for my contention: If there really had been two methods of analysis applied to the data that would instantly explain the curve shift, why would not Professor Parker et al. have immediately shown me the two computer source codes or the notebook-written algorithms. This would have immediately cleared up at least the matter of the ori- gin of the shift. Such was not done, I am quite certain, because two dis- tinct approaches to the data processing did not exist. I do not believe that Professor Parker et al. can be trusted at this time to give forth a complete account of how that curve adjustment occurred. If asked to do so, they might contrive some kind of algorithm with a convenient free parameter or parameters that will show how they processed the data to get the two sets of results. In conclusion, and in regretted disagreement with the recommen- dations of Professor Morrison, I must again ask you to convene an appropriate panel to thoroughly explore scientific misconduct on the part of the MIT research group. When this panel renders its opinion, I am confident that it will reach the very conclusion about this experi- ment that Professor Parker publicly announced on June 7, 1991, and later implicitly rejected, namely that it not “worth anything.” This is what he said and he will be held to his word that he believes the curves can be redrawn “anyway that you want”: “I’ll tell you what my opinion is of that work, because I was part of it. I don’t think it’s worth very much. Alright? And that’s why it’s just published in a tech report. I don’t think it’s worth very much. I think to do calorimetry is one of the hardest things I ever tried to do. I’d rather stick to plasma physics. . . When you have an open system is where you can make big errors, where you don’t know the overpotential, the elec- trode potential, and so on. These things are unknown. I mean it’s really tough and that’s why I don’t put any stock at all—you can redraw those curves anyway that you want. I don’t think that data is worth anything.” Rather than allow the PFC team members further opportunities to fiddle with their data, I recommend that all notebooks, computer files, and printed records relating to their experiment be immediately impounded and turned over to an investigative team for thorough analysis. I requested this inquiry in late August. It is now late October. Your letter to me in early September said that my material would be “appropriately reviewed during the coming several days.” Time enough has gone by in deliberations over what to do. It was a good, but not a sufficient course to ask Professor Morrison’s opinion, which he rendered the day after he received the material from you. However, it is now time to appoint a panel that will probe to the core of what I steadfastly believe to be evident scientific misconduct. Both you and others, especially Professor Morrison, should be under no illusion that my hope for cold fusion lies in extracting some evidence of excess heat from the PFC data. You should know that posi- tive conclusions about cold fusion are based on a preponderance of evi- dence from elsewhere. After the results that will likely be discussed at the third annual conference on cold fusion in Nagoya, Japan, in the fall of 1992, no one will need the PFC’s ancient and discredited data. It will be past history, and, indeed, a very sorry history for MIT. The case of the PFC data concerns scientific ethics: Is it permissible to massage data to one’s taste—to artificially present a strong negative impression rather than an ambiguous and possibly positive one? I think not. I do not deny the PFC group the right to discuss the sensitivity of their experimental measurement and then to suggest that because of that sensitivity their result should be read as null. But it was clearly inappro- priate to arbitrarily shift processed data to contrive a “desired appear- ance” and not let the viewers of their report form their own judgements. And do not forget my contention that the very basis for arriving at the original processed data (before the shift) is, in any event, not correct. At the very least, the paper requires substantial revision on that account. Until I am persuaded by strong technical arguments that deliberate curve-shifting has not occurred, and that an appropriate processing of the data has been applied, I will continue to believe in the need for a thorough investigation. I appreciate Professor Morrison’s offer to dis- cuss the content of his memorandum with me, however at this time I do not feel a need for that kind of discussion. The discussion I and several of my colleagues would respectfully like to have with him would be to discuss the overwhelming ancillary evidence for cold fusion, not the PFC paper. I understand his contentions about the PFC work very well and do not need clarification. I look forward to your reply about the next steps that you will take. Sincerely, Eugene F. Mallove Exhibit Y Eugene Mallove’s Letter to President Charles Vest December 31, 1991 Over two months have gone by and still no action has been taken on my request for a full investigation.—EFM President Charles M. Vest, MIT Room 3-208 Dear Dr. Vest: My last letter to you regarding the progress of the MIT misconduct investigation was on 24 October. With the exception of a subsequent telephone message from Ms. Laura Mersky stating that you considered the investigation to be a matter of high priority, which you would attend to upon returning from a foreign trip, I have received no com- munication from you. Would you kindly let me know what actions have been taken? I can assure you that in 1992 there will be many developments regarding cold fusion, both scientific and governmental. It will accord- ingly be imperative to resolve the MIT misconduct matter as soon as possible. I look forward to your early reply. Sincerely, Eugene F. Mallove

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50 Infinite Energy • ISSUE 24, 1999 • MIT Special Report Exhibit Z President Charles Vest’s Letter to Eugene Mallove January 6, 1992 President Vest’s penultimate brush-off letter, which suggests no need to do anything further. He checked with his legal counsel regarding the matter of unethical press deception, which he calls “bias in dealing with the media.”—EFM CHARLES M. VEST, PRESIDENT, Room 3-208 Dr. Eugene F. Mallove, Bow, New Dear Dr. Mallove: In your letter of October 24, 1991 commenting upon Professor Philip Morrison's report on his inquiry into your concern about possible sci- entific misconduct in the paper by Albagli et al., you acknowledge Pro- fessor Morrison as: a gifted scientist and educator, a man of impeccable character and one of the finest human beings I know. I also count him as a friend and a person who made an honest attempt to be fair to all sides in his letter to you. I deeply appreciate the time and effort he made on your and my behalf. With that said, I regret to tell you that I am in substantial disagreement with Dr. Morrison's conclusions about the technical matters that he discussed. I agree with all you have to say about Professor Morrison and am left with the question of whether I should ignore his conclusions and order the additional investigation which you requested in your October 24 let- ter. Since receiving your letter, I have sought an additional independent review by Professor J. David Litster, our interim Associate Provost and Vice President for Research, and he has confirmed Professor Morrison’s conclusion that there is no basis for further investigation of the charges of scientific misconduct. I have also considered, and sought advice from legal counsel, on whether it was necessary or appropriate for me to investigate your charges of bias in dealing with the media, and I have concluded that is neither necessary nor appropriate for me to do so. You will recall that Professor Morrison did recommend “that PFC should spend a personal day or two of work to compute the mean excess power for all four cases, the light and heavy water cells under the two protocols of drift correction.” However, your letter of October 24, 1991 rejects this suggestion, so I am not requesting that it be done. In closing, I do wish to express my regret for the length of time that it has taken to respond to your letter of October 24. Because the Provost had participated in the Albagli paper, I thought it best if I dealt with your concerns personally, and between a long trip in November and the holidays, this is the first opportunity I have had to respond. Sincerely yours, Charles M. Vest CMV:cbb Exhibit Z-1 Eugene Mallove’s Letter to President Charles Vest February 9, 1992 New evidence in the form of Dr. Mitchell R. Swartz’s analysis of the MIT PFC data manipulation had come to my attention. My request for a thorough investigation became more emphatic.—EFM President Charles M. Vest, MIT Room 3-208 Dear Dr. Vest: I had intended to reply promptly to your letter of 6 January 1992, but new information was unexpectedly brought to my attention, which delayed my response. I am referring to the substance of the draft report, “Semiquantitative Analysis and Examination of MIT PFC Phase-II Cold Fusion Data,” which MIT graduate Dr. Mitchell R. Swartz submitted to you on 28 January after a lengthy period of very careful consideration. He has discussed his analysis with me and given me a copy of the report that he submitted to you and to Professor Ronald R. Parker. Let me assure you that Dr. Swartz initiated his investigation independent- ly. I was surprised—shocked would be a better word—to see what he found. I was given a copy of his report to verify the accuracy of Dr. Swartz's use of quotations from correspondence that I had allowed him to see. Later, I requested and received a copy of his draft report. In your one-page letter of 6 January, you mention consultations with your colleagues, Professor J. David Litster and legal counsel. Based on these consultations and the previous memorandum submitted to you by Professor Philip Morrison, you presumed that you had dealt appropri- ately with my request for a misconduct investigation. I am sure that it will not surprise you to hear now that I emphatically disagree. I am extreme- ly disappointed that you chose to sweep this serious matter under the rug with what I consider to be a totally inadequate response. I trust, howev- er, that what Dr. Swartz’s analysis has revealed about the MIT PFC “Phase-II” data will have dismayed you and your colleagues and will lead you to quickly reverse your dismissal of my charges. It seems that Dr. Swartz has performed a major part of the investigation that I believe should have been your business to require, but which you did not. To summarize what I understand Dr. Swartz has discovered about the PFC data from his computer processing of the electro-optically scanned published and unpublished PFC results: (1) Extra data points have been arbitrarily and inexplicably added to the published heavy water curve. These may amount to between 10 and 20 percent of the data points. (2) The addition of two more “data points” at the portion of the curve, which in the July 10 pre-publication data exists as a time-calibration mark. These points were clearly arbitrarily placed in their vertical positions. They should not have been published as data points if they were mere time-calibration points. (This is not a small matter, see comment below.) (3) Conclusive evidence that the light water data and the heavy water data were “processed” differently. The light water data that was final- ized on July 13, 1989 is a direct and appropriate hourly average of the July 10th pre-publication data. By contrast, the finalized heavy water data of July 13 cannot be obtained from the July 10 prepublication data in a similar manner. Furthermore, Dr. Swartz has shown that no linear transformation exists that successfully maps the July 10 heavy water data into the final published data. This means that whatever technique was used to create the final published data set was highly contrived, that is, was manipulated to give the curve its final appearance. This is in contrast to the impression that Professor Parker has given all along, that the two data sets were treated either identically or in some kind of equivalent manner. Dr. Swartz uses “polite language” to characterize these findings. He writes, “There appear to be the possibility that some of the data points in the published heavy water curves are most likely artifact, rather than a result of the original experimental data.” He states, “. .there does appear to have been an asymmetric algorithm used when the July manuscripts are examined. The light water curve was published essentially intact, whereas the heavy water does appear shifted without any clear explana- tion for the difference.” He writes of the heavy water data, “. . .the possi- bility of additional superimposed components cannot be excluded. . .” and “. . .much would be clarified by the marking of incidental, questionable, or less clearly derived data points.” I will not be so polite. To be blunt: Dr. Swartz’s findings mean that it is absolutely certain that the heavy water experiment data have been manipulated, adulterated, and presented in a way that is completely misleading. I no longer characterize as scientific misconduct what I for- merly believed to be an unwarranted shifting down of a data curve, which was a serious enough charge itself. I now consider that an indi- vidual or individuals responsible for the preparation of that data are guilty of scientific fraud. I am using the term fraud, which connotes in my mind a deliberate attempt to mislead, to correspond with the defin- ition of “misconduct” in “Section 50.102 Definitions of Sub-Part A, Sec- tion 493 of the Public Health Service Act.” Furthermore, I would con- sider any significant delay in dealing appropriately and severely with these findings to be an attempt to cover up scientific fraud. Some further conclusions that one can reasonably infer from Dr. Swartz’s findings: The artifactual time-calibration mark is alluded to in the PFC Journal of Fusion Energy paper in Figure 6— in the context of the description of the declining heater power curve. There is no such description in the previous figure in which the data is presented, Figure 5, nor could there have been, since it would obviously have been ludi- crous to insert points that look like data and then say, “by the way, they are not really data, they are calibration points.” I suggest that these points seem to enhance the impression of a wider y-axis data spread—

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51 Infinite Energy • ISSUE 24, 1999 • MIT Special Report a useful impression to give if one is trying to show that any possible excess power is within error bounds. It is inconceivable to me that these points were “inadvertently” put in. The only way that could have hap- pened would have been if the time-calibration “data” were included erroneously in the purported algorithm that processed this data (which would then invalidate the entire purported “least squares” fit that Pro- fessor Parker has mentioned in one of his letters). These are dramatic outlying points that I believe may have been intentionally introduced. I hope that in view of the seriousness of Dr. Swartz’s findings, my assertions about them, and in the context of other major faults that I and others have alleged about the MIT PFC publication, you will now act immediately. You could put in place a formal investigation of the entire matter with a panel of experts from both inside and outside MIT, which should include people both favorably disposed to cold fusion, and those either not so disposed or neutral. But let me suggest that based on the facts that now appear so crystal clear, you should ask Professors Parker and Wrighton, who were the leaders of the research in question, to formally withdraw the entire “Phase-II” part of the Journal of Fusion Energy published paper, and the corresponding part of the PFC/JA-89- 34 report, and all conclusions that derive therefrom. I note that in the January 1992 issue of Physics Today , there is a news item (see attached) about the Council of the American Physical Society voting last November to adopt a set of guidelines “outlining profes- sional conduct by physicists.” The text of the guidelines is printed and contains several statements that I think are very pertinent to the PFC matter. One statement is: “Following publication the data should be retained for a reasonable period in order to be available promptly and completely to responsible scientists. Exceptions may be appropriate in certain circumstances in order to preserve privacy, to assure patent pro- tection, or for similar reasons.” The response of Professor Parker throughout this affair egregiously violates this guideline. For example, he has deliberately determined not to reveal the method of generating the heavy water curve of the “Phase-II” results. In my 24 October 1991 letter to you I specifically suggested that obtaining the algorithms that processed the data would be important. So did Professor Morrison in his 14 October 1991 memo to you: “They should also describe the two approaches to correction in more detail than the by-name-only account in the letter by Dr. Parker to Dr. Mallove of 8 August 1991.” In your 6 January letter to me you did not mention this key suggestion by Dr. Morrison, which I most certainly did not reject. Nor, as you stated in that letter, did I reject Professor Morrison’s suggestion “that [the] PFC should spend a personal day or two of work to compute the mean excess power for all four cases...” I must say, you have inadvertently twisted the interpretation of one brief phrase that I wrote, “..in regretted disagreement with the recommendations of Pro- fessor Morrison..”, which was made in the context of a request for a much more complete investigation, to imply that I did not want to see those alleged PFC algorithms or have the means computed. Another guideline that the APS Council put forth also has direct application to the matter at hand: “Fabrication of data or selective reporting of data with the intent to mislead or deceive is an egregious departure from the expected norms of scientific conduct, as is the theft of data or research results from others.” In the issue of Tech Talk dated 5 February 1992 is published the MIT procedures for dealing with “Academic Fraud in Research and Scholar- ship.” The statement is made: “In addition, the Provost has the author- ity to mitigate the effects of the fraud by withdrawing MIT’s name and sponsorship from pending abstracts and papers and by notifying per- sons known to have relied upon any work affected by fraud.” I expect that this will be carried out for the matter at hand once the final deter- mination has been made. I note further in the MIT-published statement: “An inquiry must be initiated immediately after an allegation has been made and must be completed within 60 calendar days of its initiation unless circumstances clearly warrant a longer period. If the inquiry takes longer than 60 days, the record of the inquiry shall include documentation of the reasons for exceeding the 60 day period.” My initial request for an inquiry and pos- sible investigation was submitted on 18 August 1991. There have been a number of written exchanges between us, including my 31 December 1991 letter in which I asked about the status of your inquiry, following my earlier letter of 24 October. Your letter of 8 January 1992 seemed to terminate the matter as far as you were concerned. Thus, more than 140 days have gone by in which only one MIT faculty member, Professor Morrison, spent part of October 13 and October 14 reviewing (incom- pletely) my requests. After October 24, but perhaps as late as the first week of January 1992, Professor Litster, the Associate Provost to Provost Mark Wrighton (one of the authors of the questioned research) “inde- pendently” reviewed the matter and “confirmed Professor Morrison’s conclusion that there is no basis for further investigation of the charges of scientific misconduct.” In your 8 January 1992 letter you wrote, “I have considered, and sought advice from legal counsel, on whether it was necessary or appro- priate for me to investigate your charges of bias in dealing with the media, and I have concluded that it is neither necessary nor appropriate for me to do so.” Please go back and read my 18 August request for an investigation, because you have again inadvertently twisted my posi- tion. I was not and am not concerned about “bias in dealing with the media.” Bias in dealing with the news media (such as selecting which newspaper one wants to favor with an interview) is precisely the objec- tive and accepted (if not altogether proper!) role of a news office; I have no objection to such “bias.” What I was talking about in my request was the investigation of giving false information in matters that are not small—giving false information to me to prepare an erroneous new release, giving false information to others in the News Office, and giv- ing false information to the greater world about what was said to a reporter. In other words, a calculated attempt to discredit that reporter and newspaper by giving false information. Moreover, a denial of giv- ing this false information persists. Do you not think it is time to do something about that? Is this level of expected personal integrity no longer important at MIT? In summary, I consider that the inordinately extended inquiry up to this point has not met MIT’s own proclaimed standards. I hope that in light of the newly developed information, this time you will understand my points quite clearly. This is a very grave matter which has in my view, I regret to say, already damaged MIT. You cannot sweep research fraud under the rug -- even if it is in the context of a claimed phenome- non with which you, Provost Wrighton, and several others at MIT have little patience. If you do not do the necessary investigative job yourself, I am convinced that others inevitably will. I am also sending a copy of this letter to my former associate, Ken- neth Campbell of the MIT News Office, because I know he is familiar with the ramifications of this type of situation, having witnessed, as did I, another well-known controversy that did not help the image of MIT. Sincerely, Eugene F. Mallove cc: Kenneth Campbell Exhibit Z-2 Eugene Mallove’s Letter to President Charles Vest February 21, 1992 President Charles M. Vest, MIT Room 3-208 Dear Dr. Vest: On February 10 you received a letter from me that discussed a seri- ous issue connected with research at MIT. Have you initiated any actions on this matter? When might I expect a reply from your office? Sincerely, Eugene F. Mallove cc: Kenneth Campbell [MIT News Office] Exhibit Z-3 Dr. Stanley Luckhardt’s Letter to Professor Mor- rison March 10, 1992 While President Vest continues to stonewall, a con- genial memo is passed between Dr. Luckhardt (who still has control of the contested data) and Prof. Mor- rison—some “investigation”! Of course, this con- cerns the “discredited” cold fusion, so it is not impor- tant for MIT to observe the usual standards.—EFM Plasma Fusion Center Massachusetts Institute of Technology MEMO Dr. Luckhardt MIT News Photo

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52 Infinite Energy • ISSUE 24, 1999 • MIT Special Report TO: Prof. Phil Morrison FROM: Dr. Stan Luckhardt MIT Plasma Fusion Center, NW16-266 DATE: 3/10/92 SUBJECT: ANALYSIS OF CALORIMETRY DATA IN THE PAPER: D. Albagii et al. , Journal of Fusion Energy , 9, 133, (1990). In this memo, I will go through the analysis of the calorimeter data from our 1989 experiment, and show how we arrived at the reduced data presented in our paper. As explained in our paper, the calorimeter used a feedback controlled heating element to maintain a constant temperature in the electrolytic cells. Any production of “excess heat” would show up as a reduction in the heater power level. The heater power level could be accurately measured by monitoring the current and voltage applied to the resistive heating element. The signal of interest is then the heater power (P h = I h x V h ). The level of excess heat claimed by Fleischmann & Pons for our conditions is ~79 mW, this excess was claimed to appear after an initial “loading period” of some hours or days. Thus, to repro- duce the claimed effect, we would expect the heater power to undergo a change of the claimed magnitude after some days of “loading.” In our experiments, and those of others using the open cell type calorimeters, the heater power undergoes a steady drift caused by the loss of solvent from the cell. This loss is caused mainly by electrolytic decomposition and evaporation. As solvent is lost, the level of solvent in the cell drops, this causes the thermal conduction path from the sol- vent to the top of the cell to increase, thus increasing the thermal “resis- tance” of the cell and reducing the rate of heat flow out of the cell. To maintain constant cell temperature, the heater power must also decrease slowly. This base line drift trend can be seen in the raw heater power plots attached. To analyze our heater power data, we first subtract the baseline drift, then any onset of anomalous heating would appear as an excursion from zero. In particular, in the attached Figs. 2&3 I show the raw heater power data P H for the D 2 0 cell and the linear regression fit y H to the raw data. In Fig. 4 the difference P X = Y H - P H is shown. To remove the high frequency fluctuations, the data is time averaged, Fig. 5. We believe these rapid fluctuations are caused by the trapping and escape of gas bubbles from under the Teflon supports for the cell electrodes, (see drawing of the cell in our paper) and by condensation in the cell which causes water droplets to occasionally fall back into the cell. These effects cause fluctuations in the level of liq- uid and as explained above result in heater power fluctuations. The time averaged data has one main feature, a slow variation hav- ing a 24 hour period. We believe this is caused by daily room tempera- ture variations and/or some sunlight hitting the cells. Both the D 2 O and H 2 O cells exhibit this feature. Aside from this 24 hour period variation, the data is quite close to zero with some residual fluctuations of order 10-20mW. There does not appear to be any evidence of the claimed anomalous heating event of magnitude 79mW in Fig. 5. This conclusion was stated in our paper. Sampling rate: As noted in the caption of Fig. 6 in our paper, the data sampling rate for the D 2 O cell power was reduced at t=30hours. This was done to save disk space on the data acquisition computer. The regression analysis described above tends to weight the initial data more heavily because of its higher sampling rate. In the attached pages, I show a further analysis in which a uniform sampling rate is used throughout. In the attached Figs. 6-9 the data analysis is carried out again using the uniform sampling rate data and the final time averaged signal is plotted in Fig. 9. This signal is almost indistinguishable from the results of the original analysis shown in Fig. 5. So our conclu- sion from this analysis is the same as before. The analysis of the H 2 O cell data is shown in Figs. 10-14. Note the in Fig. 14 there is a residual, 24 hour period variation in the heater power. As dis- cussed above we believe this is an error signal caused by the daily varia- tion of the room temperature and/or variation in sunlight hitting the cells. I hope this brief summary is of use to you, please feel free to contact me at 3-8606 if you need further information. Exhibit Z-4 Dr. Charles McCutchen’s Letter to MIT President Dr. Charles Vest March 19, 1992 DEPARTMENT OF HEALTH, EDUCATION, AND WELFARE PUBLIC HEALTH SERVICE, NATIONAL INSTITUTES OF HEALTH BETHESDA, MARYLAND 20892 Bldg. 8, Room 403 I had asked NIH physicist Dr. Charles McCutchen to give me his opinion of the MIT PFC experiment and my interchanges with MIT. Dr. McCutchen, who with MIT Professor Robert Mann had had his own battles with unethical establishments, obliged and wrote to President Vest supporting my position.—EFM Charles M. Vest, Massachusetts Institute of Technology Dear Dr. Vest, Eugene Mallove has sent me material about the MIT cold fusion experiment. Mallove contends that calorimeter data were manipulated to suppress experimental evidence that excess heat was generated when heavy water was electrolyzed. I can see why he is disturbed. The experiment was not a gem. Of the 1.8 to 2.1 watts that went into each electrolysis cell, 1.25 to 1.55 watts were supplied by the heater. Over two thirds of the power entering the cell did not go into electrolysis. Any signal from excess power would have been diluted by more than a factor three. Worse was the variability of the total power input. Over an inter- val of 80 hours, the heater power declined progressively by almost 20%. The experimenters ascribe this to the steady fall in level of the solution ln the cell. This reduced the working area of the heat-loss path through the insulation surrounding the cell, and lowered the power needed to keep the cell at constant temperature. Power generation by cold fusion, if lt happened, would like- wise be revealed by a reduction in heater power. The potential for confusion is obvious. In his letter of August 8, 1991 to Eugene Mallove, Ronald Parker wrote, “The implicit assumption was that we were look- ing for a fast turnon of the anomalous heat production and so it was legitimate to subtract out a slow baseline drift caused by depletion of the electrolyte.” This would have been a reason- able position, had the experimenters stated it in the paper. They did not do so. The ordinates of their figures are labeled P x , else- where defined as unknown ( i.e. excess) power, zero is marked on the ordinates, and nowhere is it stated that the height and slope of the curves mean nothing. Had they wanted to be able to detect constant or slowly vary- ing excess power the experimenters should have improved their calorimeters to get rid of the baseline slope. Their calorimeter depends on the constancy of the thermal conduc- tance of its insulation, and steps should have been taken to make it constant. They could have put a thermally conductive sleeve between the cell and its insulation so as to keep the area of the heat path constant. They could have kept the solution at a constant level in the cell. Better, they could have done both. They did neither. Instead, they say they subtracted a linear ramp from the data for apparent excess power in each cell. How they picked the height and slope of the ramp is not stated. Because I took their graphs of excess power to mean what they said, I assumed that they thought their procedure would not have concealed constant or slowly varying excess power, had such occurred. Dr. Charles McCutchen MIT Photo

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