Posts by kirkshanahan

    IF the measured COP is real and not Calibration Constant Shift, then we can indeed inquire as to why they get more successes at a particular loading.


    That's the $64 billion question isn't it. Is that COP>1 real or not? And yes, if the COP>1 is real, than one would certainly want to investigate why.


    But you say it's a calorimetry error, and there was no actual excess heat. But what artifact of the calorimeter would know whether the loading was 0.94 or 0.92 ? Why weren't there as many false reports of success at 0.92 or 0.96? (The plot doesn't indicate how many FAILED runs there were at each loading for the SRI and ENEA data).


    I've gone through the basic process before, but to repeat... All F&P type cells have been designed to date with all penetrations for electrode and sensor leads through the top of the cell. Those penetrations are heat loss pathways. They allow calories to slip out undetected, which is why one has to calibrate. When you put 1W in, you don't actually measure directly 1W out. (Highly efficient calorimeters get quite close, and some people say that they therefore don't need to calibrate. But that just means they are assuming a particular value of the calibration constant.) To compensate for the loss, the calibration equation typically 'bumps up' the measured value to what it was supposed to be. Then that equation is applied to temperature data from a non-calibration run, i.e. an actual experiment.


    All F&P type cell calorimetry has assumed a single equation is all that is needed. A temperature or temperature difference or voltage (as in Seebeck cal.) is multiplied by a factor with perhaps an added offset value. More complicated equation forms have been used too, such as the McKubre transfer function approach. But because of the location of all residual heat loss pathways in one concentrated area, heat produced closer to that area will lose a slightly higher fraction out those paths. Heat produced further away has a better chance of being captured. So if you take some of the heat from near the loss points and move it to farther away, more of it will get registered as temperature rise, i.e. signal, and that extra fraction is then multiplied up and shows up as 'excess power'.


    So, to get apparent excess power, heat has to move from one location in the cell to another (we're talking closed cells here), or appear where it wasn't before at all (as in an open cell where the effluent gases recombine instead of exit the cell). That means (closed cell) that recombination has to start someplace in the area away from the loss paths to get 'overdetected', and that means that process has to start up and start operating. To do that the special active state has to form, which requires whatever it is it requires to happen to do that. Apparently, based on the data, in Pd systems that is facilitated by having a higher loading, which as I described previously would theoretically cause a more active surface to form the higher the loading. Specifically how high loading translates to more active surfaces, especially given the impact of additives, is the open research area. But it should be reasonably easy to envision that, with a fixed experimental profile. that would occur at a reasonably fixed place. Of course a little bit of 'noise' would be associated with that, which is why you would expect a spread and not an absolutely singular number for the initiation point.


    To fully understand the McKubre figure you need to know all the experimental operation details, which might be in his report, but I don't think so based on my vague recollections at this time. You would also need to compare the conditions used by MIT and Caltech as well. And of course the materials themselves can have an influence, it's chemistry after all.


    Regarding false reports...there are many more of those...all the 'failed' replications. The CFers are right in that the early replication attempts were not adequate in many cases, but the key is to recognize that means F&P were premature in their announcement. Normally, one does not announce 'ground-breaking' results via press conference until they are ready to be published by a journal. F&P were forced into it though because of University concerns over IP rights. But the onlookers didn't know that and expected that what they presented met the normal reproducibility requirements. Unfortunately they didn't, and F&P still had to play coy because of IP concerns, and that just ticked off a whole bunch of people, and we ended up where we are today.


    What we learned since then is that a there are a lot of F&P-type systems that can give apparent excess heat signals. What we haven't learned yet amazingly enough is whether they are real or not.

    You missed the point instead: I told, that most reproducible LENR is this one will palladium, you started to oppose it with some twaddling about platinum and another off topic things, so I ignored it. I'm just keeping the line of discussion strictly.


    And you missed all of my points. let me simplify for you:


    1.) Your statement mixes two separate types of experiments which have different issues involved.

    2.) Your numerics illustrate the problem of people refusing to acknowledge the CCS error may be the dominant error, and if so, the numbers you quote reflect 'working in the noise', which is an accepted sign of pathological science.

    3.) You incorrectly infer that Pd CF results are reproducible. They are not by the accepted definition of the term. CFers want to use the term loosely however in order to facilitate obtaining funding. In fact it was the _partial_ reproducibility of the FPHE (Fleischmann-Pons-Hawkins Effect) that led me to give serious consideration to the field instead of just blowing it off like most scientists do today.

    4.) The Pt results (and Ni to a lesser extent) negates any extensive relevance of loading level. Some significance may be present in Pd alone, but since those results are not very reproducible, it will be only marginally useful in understanding how the apparent excess heat signals can be made to appear.

    5.) The McKubre figure illustrates a biased point of view. Enough similar results at D/Pd<0.85 exist to again indicate loading level is of secondary importance.


    These points are offered as simple assertions here. I personally dislike it when people assert things without backing up their claims. But you didn't seem to follow when I did that, so I devolve to the assertion method here to clarify for you.

    I'm wondering why the calibration constant shift peaks at a maximum D/Pd loading of 0.94


    Short answer...no enough knowledge available to know.


    Long answer...speculating...


    First, the peak being at 0.94 may be a result of the sample size and the binning method used to make the histogram, i.e. a mathematical artifact. D/Pd = 1.0 is a 'magic number', since at that point all octahedral holes of the Pd lattice are filled with a D, so the max may actually be closer to 1.0. Need more data....


    Second, under the assumption that the absorption process creates a 'special active state' (SAS) precursor, and that that may require a certain number of dislocations + superabundant vacancies (or the probability of forming the SAS is proportional to the number of acceptable surface defects), the ~0.94 number may simply be the point where the probability of forming the SAS has now reached a high enough level to be noticeable in these experiments, but some random variation around that is to be expected, since the process is not being well-controlled at this time (otherwise the CFers would have the level of reproducibility needed to claim 'full' repro.). Also one needs to remember that attaining these high loadings is not an instantaneous process. It usually requires some cook time (i.e. an induction period). So the .94 number might change is a different loading protocol was used. McKubre did a very large study of this which he reported on in his 1998 EPRI report. It was called the 'Degree of Loading' experiments and consisted of about half of the reported effort (450+ page report). The use of a histogram to illustrate the results is perhaps not the best way for analysis, but is good for visual impact on the audience. In the end...need more data.


    That 'more data' would need to probe various hypotheses about what is going on, not just be 'more of the same', i.e. a little tinkering on methodology would be indicated.


    I also note that you've made a transition in your question that many haven't made yet. Associating CCS with that graphic requires connecting apparent excess heat to an ATER/CCS issue. Most refuse to even consider such.

    Zeph wrote: “IMO you're just poorly informed about subject.” {ROFL}


    and “Today the most replicated experiments are based on Palladium Deuterium, electrolysis and gas permeation. Production of heat have been proven above 50 sigma, and at COP above 2.”


    Then Zeph included a favorite figure used by McKubre.


    Zeph, you’ve just proven how uninformed you really are. Let’s start with what you wrote. So, COP>2. What do you mean by that? Do you mean COP=500 or 10 million or maybe just COP = 2.x where x=0-9? I’ll assume you mean the latter, and just call it COP=3. That means Pout/Pin =3 and then Pex = 2Pin. OK. So if that is ~50 sigma, that means 2Pin ~= 50 sigma, and sigma = .04Pin. Usually people talk about ~50 mW as being 1 sigma, so that means Pin was ~1.25W and Pex was ~2.5W. This is your best case, assuming COP=3 and sigma = .05W.


    Now, the data Ed Storms used to demonstrate excess heat signals from Pt used ~20W Pin values. The strongest signal he had was peaked at 780mW. My reanalysis of that same data showed that could be obtained by a 2-3% calibration constant shift, which is just a typical noise level on a well determined experimental number. IOW, the correct figure to use for the noise level of the experiment was not 50-80 mW but 500-800mW (roughly). Using that number, your Pex above is just 3-5 sigma, not 50.


    3 sigma is considered ‘in the noise’, but the LHC guys who found the Higgs boson use 5 sigma as a detection level in their work. IOW, your ‘best case that proves CF is real’ is potentially just noise. This of course assumes the method for getting your 2.5W Pex was calorimetric. If it wasn’t, the preceding may not directly apply. So you see, you shouldn’t just bandy numbers about, you should cite the specific refs.


    Additionally, electrolysis and gas permeation experiments are significantly different configurations, so I’m back to the point of proving each separately is valid before you lump them together.


    Now to the McKubre figure. First off, you recall I just mentioned the Storms data, determined on platinum (NOT palladium) cathodes? That proves ‘loading’ is not the generic controlling factor for generating apparent excess heat signals. (Note that CF signals from Ni-light water F&P systems also support this idea.) Hydride chemists have tried extensively to hydride Pt, but have never succeeded. Pt does not form a hydride. So McK’s plot is only applicable to Pd chemistry at best. Since we did see apparent excess heat from Pt, we can surmise it is a surface effect only. That suggests that the same could be said of Pd.


    Now as I mentioned in response to your picture in post #14 in this thread, Pd swells when it absorbs H. In addition, there are several papers out there by Yuh Fukai that suggest the formation of ‘superabundant vacancies’ (or voids inside the Pd) at high loadings (H/Pd>~.85). Those vacancies are thought to form by ejecting the Pd atoms that were in the void and shifting them to the surface (by a domino like effect, the ejected Pd atom is probably not the one that gets pushed up onto the surface). Alternatively, they can lead to a higher degree of dislocation formation than usually observed when hydriding Pd (normal loading form dislocations). It is my opinion that those newly formed surface atoms serve as the basis for the ‘special active state’ that promotes ATER. The key point is that it is not how many H atoms are in the bulk that causes the effect, it is the ease of forming the special active surface state.


    So the McK figure is a pretty graphic used to promote a pet idea, which under scrutiny involving the whole field, just doesn’t hold up. Hmmm…where have we heard of an idea being ignored in favor of promoting a pet position…? There’s more I could say, but I expect it would be wasted, so I’ll stop here…

    I have responded to this post and others but my posts are moved to another thread without notice. I can see how that disrupts the narrative.


    I saw those responses today. My response: No, the CFers have not responded appropriately. In scientific discourse via the literature, it is expected that what is published will be digested by the readers. Then, they may comment back, either directly via Comments or indirectly in the body of related publications of new work. Storms did the former with his 2006 Comment, and Szpak, et al, did the latter in their 2004 paper. Then it's the original author's turn (actually anyone can chime in). I replied immediately to the Storms comment, and somewhat later to the Szpak, et al, paper (because I didn't see it right away). In those replies I gave reasons why what the commenters said was irrelevant or incorrect. Normally, the debate would continue, usually in subsequent publications but once in a while in a second layer of Comment and Reply, but that's where this drama goes off script. The CFers quit responding. Instead Storms published a book in 2007 where he mentions my objections and claims he addressed all concerns, referencing my 2002 paper and his 2006 response, but completely failing to mention my 2006 reply to his comment. IOW he implies the issue was settled by his pointing out my 'mistakes', and by not mentioning my rebuttal, he further implies to the reader that there was none, solidifying his implicit claim of 'putting me in my place'. That is inappropriate.


    There never was a response to the 2005 paper until Miles (one of the authors of the 2004 paper I commented on) published his recent 2017 article in Infinite Energy vol 132. There, Miles claims that the paper he is publishing was written primarily by Fleishmann and that it rebutted my objections. But Miles also failed to note my 2005 rebuttal, even admitting he had never read *any* of my papers on the subject. Also inappropriate behavior.


    Then there is the 10 author rebuttal of my 2010 comment on the 2009 Marwan and Krivit article, where they misrepresent what I write by attempting to convert the CCS abbreviation I use to CCSH, which stands for Calibration Constant Shift Hypothesis, followed by attempting to convince the reader that I discuss random errors when I clearly talk about systematic ones. (In case you or someone else is unfamiliar with the terms, random and systematic are diametrically opposed.) This is a clear case of the use of the strawman argument which is known as a fallacious logical tactic. Yet from that time they have proceeded to act as if they 'put the final nail in the coffin' regarding my ATER/CCS (at the electrode recombination/calibration constant shift) proposed mechanism for getting apparent excess heat signals. Also inappropriate behavior.


    Since I rebutted their objections to my proposals, and demonstrated that it worked in the case of the Szpak, et al, 2004 paper's results (plus several other cases via Internet forum discussions), the ball is in their court to continue scientific discourse. But they didn't. They labeled me a 'skeptopath', and thereby justified their ignoring me. Just look at how Hagelstein handled the question on my work from his audience in his 2015 'MIT' Cold Fusion course. First off, he doesn't know what the *only* publishing skeptic says about CF, he has to go and look it up. This is true even when he is quoting conclusions from my 2010 paper in his slides! When he comes back the next day, he restates my theses reasonably well, but then says nothing. But his body language does... Combine that with the fact that he was presenting my work in the section where he was warning the course attendees about the 'difficulties' they will face when and if they decide to do CF research, and you get a pretty good idea where he stands on the validity of my work. But I have to ask, on what basis does he make this decision? The erroneous "random Shanahan CCSH" strawman he and 9 others invented? Again, quite inappropriate.


    So, no, they have not even dealt with correctly evaluating my work, let alone the next phase where they respond to it.

    I must say I love how you mumble


    I'm mumbling? I GUESS I'LL HAVE TO SPEAK LOUDER THEN..


    do you have any idea how 'the good Doctore' salted his ash? Just speculation will do.


    No, not really. When I saw the analyses on this I didn't believe it. I assumed that a natural process was going to produce a mix, not a nearly pure sample. But I'm not a nuclear chemist, so I don't know if there is a nuclear reaction that could do that or not. And hey, it might be a LENR right? However, allowing Rossi to fiddle with the samples was a bad move. It makes it easy to suggest sleight-of-hand tricks, and given his rep, that is hard to fight off. If he really wanted to prove his process, he needed to step all the way away. That's just my opinions though, and they're no better than any of the ones presented all over this forum.


    I have avoided the Rossi stuff because it's all anecdotal information, and you can't do science from anecdotes. Maybe they can inspire you to do some work, but science requires reproduction, and Rossi never seems to do anything the same twice....

    kirkshanahan wrote: BTW (by the way), what’s tldr? (You should stop using undefined acronyms…)

    ***Hah hah, touche'. tldr is too long, didn't read. It's how you win an argument on the internet by generating so much bloviating that the other side stops reading it. You're pretty close to winning.


    Actually I should have know that but I forgot it. Sorry...


    But I hate to tell you, you're going to have a very hard time reaching any valid conclusions about CF if you don't read. I have read most papers in CF, excluding radiation detection by instruments, and that totes up to 1000's of pages. I started in 1995 and my first paper was written in 2000. I know it's daunting, and probably impossible for most.


    So what I like to do is boil it down to essentials. The biggest single factor is lack of full (detailed) reproducibility. Until that is obtained, the field is still open to alternative interpretations. But the CFers don't act that way. It must be LENR!


    Next, is the way the CFers have handled my work. It's actually pretty trivial what I did, and most of it was actually suggested by what others have said. I just did it though, and I found something interesting, a systematic trend in the calibration constant shifts (CCS) that correlated with what was done experimentally. That is very powerful evidence of real chemistry ongoing in the effect. The problem is that the CCS wipes out the apparent excess heat with trivial changes. That defines a very tough problem to study, they're working at the noise level, which is extremely difficult.


    Then look at the way they responded to my illustrating the problem to them. It's just math, but they invent scads of reasons why it can't happen. OK, so maybe my idea about why is wrong. What's their's - does it produce reproducibility and control? No. So maybe they should look at alternatives. Like an ATER/CCS situation. But they don't. That means they are pre-deciding the conclusions of their experiments, which is not good science.


    Several basic rules of how to do science are being violated by the CFers. That drops their credibility to near zero in my book. But you may have a different book. Its your time and your money, spend the, as you like. I just want you to understand what I'm saying.

    Oh, BTW, forgot this one...


    Kev wrote: "And your solution does nothing towards the findings of gamma rays, Helium, and nuclear ash."


    Yup, why would you expect a calorimetric math error to impact radiation or nuclear ash results?


    Actually though, the ATER process has some answers buried it in. Not on radiation detection by instrumental methods, which is an area I have always admitted I am not commenting on, but as for helium, tritium, CR39 results, X-ray film, heavy metal 'transmutation', well, that's falls right out. There's even a couple of other things that could be going on to give false results in those area.

    Replying to Kev’s recent post…


    kirkshanahan wrote: “Kevmolenr wrote a multitude of comments on my posts. Taking some of his points out of order…”

    Kev replied: “And out of context. Then you pile it all together into one tldr argumentation. I can see why you've been ignored. “


    Sorry you find my rearrangement offensive, but you expressed similar thoughts in several places that were scattered about. I simply tried to collect them in one place so I could avoid repeating myself multiple times. I will avoid that from now on for your benefit.


    BTW (by the way), what’s tldr? (You should stop using undefined acronyms…)


    kirkshanahan wrote: “Kevin misses the fact that I think there is NO TRUE EXCESS HEAT.”

    Kev replied: “You said "Note that I agree that there is something going on in F&P cells. I proposed a non-nuclear mechanism for what it could be."”


    Yes. And if you followed my theses you would realize that what that means is there is no beneficial source of unexpected energy in the cell. Likewise a COP ~=1 in the *calibrated* calorimeters is expected. It’s not like this is a study on an ICE. The researchers put 1 watt in, and they measure some fraction of a watt coming out due to losses. They then create a calibration equation to correct for those losses, and report the corrected Pout as 1 watt. COP = Pout/Pin = 1W/1W = 1.


    kirkshanahan wrote: “Kevin thinks it my job to correct prior workers mistakes and, apparently, republish their work for them.”

    Kev replied: “No, that isn't what I think. I have posted what I think and you can respond to those posts, or you can continue to use out of context straw argumentation. I don't think you accomplish much with your approach.”


    You repeatedly suggested that I redo the 150+ papers and then make a bundle by selling spaceheaters (or something similar). A.) I can’t do that because I don’t have either the original data or the equipment. And B.) That’s not the job of a critic in the scientific process. The critic points out possible mistakes. The researchers evaluate them and respond appropriately. CFers have NOT evaluated my criticisms appropriately and thus they have not responded. This means they still use the same lumped parameter approach to calorimetry, which in turn means the ATER/CCS mechanism is still possible (in F&P setups). The 150+ refs were primarily pre-2002, and that time frame was dominated by F&P setups. I repeat, I know of NO paper or presentation describing a CF calorimetric study that does not use the lumped parameter approach.


    kirkshanahan wrote: “Kevin thinks I want to make a ‘name’ for myself.

    Kev replied: “Ok, now we gather that you don't. You proposed a theory that doesn't fit the facts and the experimentalists dismissed your theory. So you can leave it at that. “


    No, my ‘theory’ does fit the facts quite well. That only makes sense. If it didn’t fit the facts, it wouldn’t be a threat to them, and they wouldn’t have to resort to a strawman method to try to dismiss it. As you have noted in other cases, a strawman approach is illegitimate.


    kirkshanahan wrote: “Kevin thinks I haven’t taken ownership of my theory/hypothesis/proposal.”

    Kev replied: “Yes I do.”


    Doesn’t seem so. You seem to think I need to do lots more work in the area. I think I am about done.


    kirkshanahan wrote: “Given that I think there is no true excess heat,”

    Kev replied: “And yet, you say you think there's something going on. If that is recombination, then getting such a cell to work for months is a solid source of energy. You apparently are claiming to know what causes calculations in error but it appears your hypothesis doesn't account for how these recombinations and appearance of excess heat can go on for months. If it's chemical and COP<1, it is still efficient.”


    Injecting energy into water to break it into H2 + O2 and then recombining them doesn’t seem too efficient to me. Everyone in the energy field recognizes this. That’s why we are still burning oil or coal. The only problem with that is the greenhouse gas problem, which water doesn’t have because the water absorption band for solar energy is already saturated. The big problem in converting to a hydrogen economy is the added cost of production, i.e. the net lower efficiency in turning water into fuel as opposed to oil into fuel.

    kirkshanahan wrote: “I certainly am not going to make space heaters or any amount of money from this. I could care less about making a ‘name’ in this field.”

    Kev replied: “Well then, see ya later, alligator. Don't be surprised if someone else takes up your mantle and not only makes a name for himself but makes good money at the same time. “


    I won’t be, don’t worry.

    kirkshanahan wrote: “Ungrateful little ‘sot’ aren’t you.

    Kev replied: “Again, I can see why you've been ignored in the field.”


    No, the sad thing is you can’t.


    kirkshanahan wrote: “I point out to you that 148 of 153 references precede my 1st publication, meaning that their results were incorporated into my proposals,

    Kev replied: “You're just handwaving. I posted what you could do to correct the whole field but you're not interested. So your effort will become an asterisk in the field.”


    Less than that actually. But that’s fine, it looks like psuedoscience so far.


    kirkshanahan wrote: “I think the applicable term is ‘cheeky’ (Alan?).”

    Kev replied: “Posting stuff out of context is cheeky. “


    Yes, would be if I actually did that.


    kirkshanahan wrote: “Read them again.”

    Kev replied: “No thank you.”


    Your loss. You’ll never understand why F&P didn’t win the Nobel Prize then.


    kirkshanahan wrote: “Kevmo: “It was basically ignored, as far as I can tell. That makes him not too bright, because if he has the SOLUTION to this LENR thing, he could have generated tons of data, material, money, and interest by selling chemically based space heaters. I would buy one, just to be able to play with it.”

    kirkshanahan wrote: “As noted above, I find it highly unlikely that any true excess heat source has been discovered.

    Kev replied: “You're not getting it. Assume there is no "true" excess heat but this is just a nicely efficient chemical burning process. It would make a great water heater. “


    No, you’re not getting it. See comment above on this topic.


    kirkshanahan wrote: “So your “SOLUTION” doesn’t exist to my mind. Yes I was ignored, and as THH kindly points out that’s disappointing. I have said it more strongly. I believe it is the primary signature of pathological science.”

    Kev replied: “It is not my solution, it is your solution. You honestly seem to think you have the solution to why all these top notch electrochemists are making some kind of calculation error. Now you are the one retreating and calling them pathalogical scientists. And your solution does nothing towards the findings of gamma rays, Helium, and nuclear ash.”


    (The “SOLUTION” term refers back to Kev’s quote of my quote of his words in the prior comment above.)


    This is one of those repeating theme comments Kev. You think I have some solution about how to generate excess energy that could turn me into a billionaire. What I have is a hard reason why their numbers are wrong and mislead them into thinking they have an excess energy source when they don’t. Why would I ever pursue experimentation on that? To prove Pout always equals Pin when you do the calorimetry right? Don’t think so.

    kirkshanahan wrote: “The Cfers have withdrawn from the normal publish-critique-refine cycle that defines modern science.

    Kev replied: “It's like what Reagan said about the democrat party: I didn't leave them, they left me. Cold Fusioneers tried to publish their reports in the "normal" cycle and were dismissed.”


    They weren’t ‘dismissed’, they failed to pass the minimum quality standards of the peer-review system, OR they tried to publish in high impact journals whose focus was hot topic research (Nature, Science). As soon as the irreproducibility of the field became apparent, CF dropped off those journal’s radar. Of course they would be rejected by them at that point. In fact there were many peer-reviewed CF publications in the years following the loss of impact, so the system worked fine. But after a while, the submissions were just ‘more-of-the-same’ and added no clarity or novelty to the situation. That is a prime requirement of publications (novelty, which includes work that clarifies prior difficulties). So they got rejected. Yes, sometimes reviewers used the rationale “CF is junk science”, which I agree was inappropriate, but when the CFers used that logic on me, I argued, modified, submitted elsewhere, etc. to get published. It was a lot of work. They just gave up trying to conform to minimum standards.


    kirkshanahan wrote: “Actually, I don’t talk about COPs usually. I talk about apparent excess power signals,”

    Kev replied: “Right there I need to simply call bullshit.“


    And why would that be? I’ll grant you that ‘here’ people always talk about COP, but in the pre-2002 CF literature, it’s not common. My papers don’t use the term. But if you talk about it and I answer without using the term, that just creates difficulty in understanding.


    kirkshanahan wrote: “What’cha been smokin’ dude? “

    Kev replied: “Apparently not as good as the stuff you are.”


    OK so you don’t like my humor. I should have said: “You haven’t shown any understanding of what my work means to the CF field, or about how real scientific progress is made.” Better?

    Kevmolenr wrote a multitude of comments on my posts. Taking some of his points out of order…


    Kirk wrote 1 paper, right?


    If that were only true… That’s what I wanted to do. Just a little paper telling the CFers “Hey, you guys missed this…” Then they’d initially say “No way”, but after some serious consideration, they’d say “Hmmm, maybe so. We’d better look into this…” But that’s not what happened. Instead in 2004 (two years after my 1st paper was published) Szpak, Mosier-Boss, Miles, and Fleischmann called my stuff ‘difficult to understand’. So I wrote another try at it in reply. Then in 2006 (6 years after Storms first saw my objections) Storms wrote a rebuttal claiming what I proposed could never happen. So I wrote another reply explaining why his reasons were wrong or irrelevant. Then in 2009 Marwan and Krivit published this article that I responded to with criticisms in 2010, and a group of 10 CF authors (including Marwan, Storms, Miles, McKubre, Hagelstein, Mosier-Boss) said this “random Shanahan CCSH” thing was ridiculous. Problem was that “Shanahan” never said “random”, the group of 10 did. (That’s known as a strawman.) Now I would have written another reply to that, but I asked the editor first, and he refused to publish anymore (reasons unspecified). He wouldn’t request an Erratum to disassociate my name from the “random CCSH” thing either. I did submit a manuscript to Phys. Lett. A, which was rejected because they didn’t want to publish more “CF” papers. So, I gave up on publishing as it took up too much time, and wrote the whitepaper I referred to instead.


    Several related comments:

    "That's 153 replications he's trying to undo. That's quite the tall order. I doubt his finding is significant enough to do it, or otherwise we would have been hearing more about it these last 15 years.”

    “You came out with your hypothesis after all those papers so the onus should be on you to back-apply your approach.”

    “It's your theory so you should take ownership of it.   Back-apply your hypothesis to a few of the best replications and someone will take notice.”   


    Shanahan wrote: “The upshot is that they don’t rebut my ATER/CCS mechanism.”


    Kev: “Then set up your own website where you take down every replication using your mechanism. And sell space heaters & electrocalorimeters. There's thousand dollar bills on the ground, just pick them up.”

    Some of the points I note from the above comments (and others I haven't quoted):

    • Kevin misses the fact that I think there is NO TRUE EXCESS HEAT.

    • Kevin thinks it my job to correct prior workers mistakes and, apparently, republish their work for them.

    • Kevin thinks I want to make a ‘name’ for myself.

    • Kevin thinks I haven’t taken ownership of my theory/hypothesis/proposal.

    Given that I think there is no true excess heat, I certainly am not going to make space heaters or any amount of money from this. I could care less about making a ‘name’ in this field. I of course would like to attain some recognition in my field, which I think I have done to a small extent VIA MY OTHER PUBLICATIONS. In fact, my CF field pubs detract from my 'name'. And Kevin, defending my ideas IS taking ownership.


    “And yet there are 153 papers that seem to disagree with his stance.   Perhaps Kirk should prove how brilliant he is and write his own retort to those 153 papers.  There are other papers too, ones that aren't peer reviewed, etc.“

    “Kirk should have been a busy man these past 15 years but instead he wants guys like us to do his busywork.”


    Ungrateful little ‘sot’ aren’t you. I point out to you that 148 of 153 references precede my 1st publication, meaning that their results were incorporated into my proposals, and aren’t likely to change that. And then I go on to show why 4 more are also likely to be unhelpful. And I end with pointing out I critiqued that last one left, and you say *I* want *You* to do *MY* homework??? I think the applicable term is ‘cheeky’ (Alan?).


    “My impression from reading a bunch of the papers in LENR-CANR library (and asking for more) is that Kirk's hypothesis doesn't stand up.”


    Read them again. Start with a good understanding of what I propose is the problem.


    “It was basically ignored, as far as I can tell.   That makes him not too bright, because if he has the SOLUTION to this LENR thing, he could have generated tons of data, material, money, and interest by selling chemically based space heaters.   I would buy one, just to be able to play with it.”


    As noted above, I find it highly unlikely that any true excess heat source has been discovered. So your “SOLUTION” doesn’t exist to my mind. Yes I was ignored, and as THH kindly points out that’s disappointing. I have said it more strongly. I believe it is the primary signature of pathological science. The Cfers have withdrawn from the normal publish-critique-refine cycle that defines modern science.


    "but Shanahan claims to know why these experimentalists see such high COP in their cells. If it's purely chemical and can generate an appearance of a COP>6, it would make a fantastic new addition to our energy ecosystem. If what he's saying is true, he is sitting on a gold mine.”


    Actually, I don’t talk about COPs usually. I talk about apparent excess power signals, which are often discussed somewhat inaccurately as ‘excess heat’. And once more, they are artifacts of the data analysis methodology. No true excess energy source present as far as I can see.


    “That is kinda one indication that this effect is real, if it shows up in other experimental cells than just PdD calorimeters.  I gather your hypothesis of error does not apply to the other mixed cells.”


    The fact that multiple researchers got ‘bumps’ in their excess power curves is what led me to want to consider the possibility that they were real. It was only partial replication, but it held the promise of someday being fully reproducible (still unrealized). If true, it represented a safety problem for me and my coworkers. My specific ATER/CCS proposal is for F&P-type electrolysis cells, and thus does not apply to other experimental apparati. I recall you mentioned the Patterson Power Cell previously. That is a modified F&P setup, but I believe the modifications induced a new set of errors that dominated. If those could be eliminated there might be a residual CCS problem as well. Calibration constant shifts, if they occur, will induce apparent excess heat in other apparati. There, the excess could be positive or negative, depending on what causes the shift. In F&P cells, calibration is always done with an ‘inactive’ electrode, which means that anything that causes heat to shift to the electrode area will give positive excess heat signals. Thus the calibration methodology gives only positive excess heat signals. And all of this never negates other error mechanisms, such as for example, thermocouple degradation in the Rossi case.


    “Would it be something you could state categorically that the larger the COP, the larger the error and the more expectation we should have had of these experimenters to see their error?”


    As THH has noted, the ATER/CCS problem has some built in limitations. This is why it should have been easy to disprove, especially for “high COP” cases. The CFers should still have all the data from all their prior work, with some reasonable exceptions allowed of course. All they need to do is trot out the case that shows the CCS problem is not relevant to their results. We’re still waiting for that to happen.


    Instead they have attempted to discredit the ATER part of my proposal, usually with very weak argumentation and no real data. They even resorted to the “random Shanahan CCSH” fallacious argument to try to do so. What that seems to show of course is a.) they have no data that can’t be explained away by CCS, and b.) they refuse to accept the idea they might be wrong in invoking “LENRs”.


    KLS wrote: “That is a typical CFer (cold fusion researcher or cold fusion engineer (the last as per Gene Mallove)) illegitimate tactic. The idea that LENRs are present is about the only thing that links these divergent experimental setups, and they shouldn’t be linked like this until they are actually shown separately to have LENRs present. That has not been done.”

    And Kevin responded:

    “That is valuable scientific data that you should publish to the community as a whole.”


    What’cha been smokin’ dude? That’s just basic science. If some guy waves a magic wand around and says I just did xxx, are you going to fold that into your thinking about xxx? No, you’re going to say “That didn’t measure up to normal scientific standards and I can’t use it.” Substitute “LENR in an arc” as well as “LENR in a chicken” for xxx. The conclusion remains the same. No incorporating any experiment until it has been shown to be valid.


    KLS wrote: “An interesting side note from the discussion we had (email) was that Miles admitted he has never read my papers. I have to wonder how he can know they are ‘wrong’ when he hasn’t.”

    Kev wrote: “Interestingly enough, I believe it was hyper-critical Jones who said the same thing about LENR papers.”


    Jones? Not Steve Jones, originator of the ‘other CF claim’. Parks has been quoted saying something to that effect, and it is obvious many of the people involved in critiquing the CF field early on didn’t keep up after the first DOE review. So yes, in their cases, the same applies which is part of why I decided to take a look at it starting in 1995.


    A couple of others wrote:


    AlainCo: “My advice to Kirk Shanahan, is that like all people who work on LENR because their have observed it and think it is a nuclear phenomenon, he try to amplify the phenomenon, characterize it, and why not make money with it.”


    Do you think I hadn’t thought of this? Silly boy! I just can’t think of a way to capitalize on a hydrogen/oxygen recombiner configured as an F&P cell. I mean you split the water and then immediately reform it? Why?


    There have been proposals for example to place Pt wire in the top of nuclear reactor containment structures to recombine any released hydrogen before it blows up and ruins the containment, and while that makes sense and is a very passive way to do it, I can’t see putting an F&P cell up there and keeping it running would be of benefit…


    Zephir_AWT: “Results with palladium are way more reliable.”

    Not really…

    kirkshanahan wrote: 

    Once he recognized I was skeptical, he broke it off.

    There is nothing worst for a Scientist of that level to lose his time with a skeptical who will not accept any argument.

    Is quite nice to see that a Scientist of that level can study LENR without giving up his career because of pathoskeptical bloggers.

    4 or 5 emails does not a discussion make. It is impossible to tell from 2 or 3 emails if a person is pathologically holding onto a belief or not. Every scientist who thinks he/she is onto something is reluctant to give it up, and it takes a reasonable amount of discussion to change that. Claytor used a Femtotech ionization detector to supposedly detect tritium he was forming by a gas plasma. That process also spits out other stuff that gets blasted off the surfaces of the apparatus. Claytor knew this because he said he made sure it wasn't water (one of the typical contaminants from this activity), but his assertion was not as well defended as I'd like, so I asked for clarification. He replied with very little new info, so I pointed that out and asked for more details of his procedures. He never replied. (Disclaimer: this is how I remember it happening...) That's not 'pathological skepticism', that's normal skepticism. This kind of request happens millions of times a day. But I'd bet Claytor checked with his buddies (probably Storms) who told him all about me, and he trusted their assessment instead of checking it himself (just like Melvin Miles recently admitted he'd done by admitting he hadn't even read my papers (while signing off on the strawman "random Shanahan CCSH" thing)).

    keV


    In order to help you a bit I have looked over the list of 153 references that Jed claims are ‘excess heat papers’.


    First off, out of the 153 papers (you dropped 153 from your post BTW) only 5 were published after my 2002 paper on the systematic calorimetric error I detected, so none of the other 148 papers is likely to have enough information on their method to tell if their calorimetry is correct or not because they weren’t aware of the problem. One of the 5 post-2002 papers is the one by Szpak, et al (ref#144) that I replied to with my second publication in 2005. There I showed that their results were consistent with a CCS being present.


    Since the reception I have received from the CF community has been universally negative, I feel safe in saying that you won’t find any studies to date that contain enough information relevant to the calorimetric method to evaluate the CCS potential. I’d love to be proven wrong on that statement.


    Further, there is a classic problem present in the list, namely the mixing of experimental types, many are not even based in calorimetry. For example, my papers deal specifically with F&P-type electrolysis cells, but this list mixes those in with plasma discharge experiments and arcs in water experiments and possibly others. That is a typical CFer (cold fusion researcher or cold fusion engineer (the last as per Gene Mallove)) illegitimate tactic. The idea that LENRs are present is about the only thing that links these divergent experimental setups, and they shouldn’t be linked like this until they are actually shown separately to have LENRs present. That has not been done.


    The calorimetric experiments in F&P-type cells is the largest block of related experiments, and that is what my papers address. I point out that in all cases known to me the calorimetric method used the lumped parameter approach that is susceptible to the calibration constant shift (CCS) problem I outline in my papers. It is usually impossible to tell if that problem is relevant, since the CFer authors never give sufficient calibration details and results to allow testing its relevance. Miles is about the only author who does anything along these lines in that he often quotes the standard deviation of his determinations of the ‘heat transfer coefficients’ (which are just the calibration constants of his calibration equation). They typically are about 1% relative standard deviations. I found approximately the same was all that was required to zero out Ed Storms’ 780 mW excess heat signals in his data I reanalyzed. In Storms’ ICCF8 paper on that data, he shows calibration constants obtained by two methods, electrolytic heating and Joule heating, and they differ. He also says he gets different electrolytic calibration results over time, which is consistent with Miles.


    So, to eliminate the CCS problem from consideration, a paper should list the calibration equation and specify the variation of the calibration constants over time and/or method and/or anything else that might be relevant. This is universally missing to my knowledge. If they don’t give that info, you can’t tell if their excess heat signals are real or an artifact of the math.


    Note that I agree that there is something going on in F&P cells. I proposed a non-nuclear mechanism for what it could be. That has been was attacked by Storms in 2006, but I rebutted his points. The Szpak, et al derogatory comments were non-specific or irrelevant, as were the ones in the Fleischmann version published by Miles in Infinite Energy vol. 132 (2017). I responded to Szpak, et al in 2005, and posted a few comments here about the recent Miles IE132 publication. The upshot is that they don’t rebut my ATER/CCS mechanism.


    The other 4 post-2002 papers are Ararta, ref 19; Li, ref 64; Mizuno, ref 95; and Szpak, ref 145. The Arata paper is on the Pd/ZrO2 system, which was replicated by Kitamura, et al, in Phys Lett A, 373 (2009) 3109. That paper was one I attempted to rebut, since it had enough details presented to be able to analyze them, but was not allowed to publish. The manuscript for that rebuttal is in the whitepaper I have previously mentioned. (The whitepaper is supposed to be here: https://docs.google.com/open?id=0B3d7yWtb1doPc3otVGFUNDZKUDQ) My thesis there is that the observations are consistent with known Pd/Zr/ZrO2/H2 chemistry. That would apply to Arata’s paper as well, if enough information had been presented to do so. The Li, et al paper is on D2 permeation through a Pd tube and gives nothing but a single figure claiming abnormal heat flow observation. No details at all to allow one to assess errors, plus it isn’t an F&P-type electrolysis. The Mizuno paper is on plasma electrolysis with a W cathode, also not an F&P type cell. The Szpak 2005 paper seems to have no information in it regarding excess heat except a mention of ‘hot spots’, so I fail to see why it is on the list at all. It only presents SEM/EDX data.

    do you believe in the reality of any of the hundreds of reported LENR phenomena at all? Not just Pd/D, but any?


    The problem with answering your question is that the field has become so inclusive of anomalous results that a 'reported LENR phenomena' could be anything. So let me answer you this way - I do not automatically reject LENR claims, but I am very skeptical. This is based on my interaction with the field since 1995. I usually find LTA efforts to define what could be causing the anomalous results, and I usually find aggressively dismissive consideration of skeptical commentary.


    As I've said before, I work with almost all the materials people talk about in the LENR field, and if LENR is true, I need to know. It involves my and my coworkers safety. That's why I studied the F&P-type studies. There was enough crude reproduction of results to suggest something real was going on, and I wanted to know what it might be. I believe I figured it out, but it ain't nuclear, and that has led to mass rejection out-of-hand of my views by those who think it is. That's fine I guess. I just hate it when a newb gets caught up in the fantasy of an free energy world, *and* I am dumb enough to believe scientists try to find the truth, so I keep plugging away. My interactions with the field have gone a long way towards disabusing me of the latter belief in fact.


    Bring me something that shows at least a little reproducibility and I'll look at it...

    @kevm

    Since Alain mentioned me, but seems a bit confused in what he said, let me try to clarify.


    As background, at this point I have published 4 papers relating to CF. The first was about the reanalysis of cold fusion data collected by Dr. Edmund Storms that was posted to the Internet in Feb. 2000. He subsequently presented his interpretation at ICCF8 as showing excess heat. The exciting point in it was that the cathode and anode both were platinum (i.e. no palladium in the system). He obtained excess power signals most of the time when he applied a stepwise increasing to maximum then decreasing to 0 input current. I obtained the data and examined the question of how one could assume there was no excess power actually present, yet obtain the published results. What I found was that a trivial (2-3%) change in calibration constants zeroed out the excess power signals (the maximum size claimed by Storms was 780 mW). My paper was published in 2002. In it I also gave a proposed explanation of what was going on that required no LENRs.


    In 2004 Szpak, Mosier-Boss, Miles, and Fleischmann published a paper claiming what I said was in error and made no sense. I rebutted that in 2005. In 2006, Ed Storms published a Comment on my 2002 paper, and I rebutted that in a paper published immediately following Storms’ paper. In 2009, Jan Marwan and Steven Krivit published a pro-CF article, which I published a Comment on in 2010. A group of 10 CF authors published an attempted rebuttal of my comments/proposals, but they screwed it up so badly it’s embarrassing. However, I was not allowed to publish a reply to their comment. I eventually released a whitepaper that contained what I would have written, plus a comment on the calorimetric method F&P used, plus another manuscript that wasn’t allowed to be published responding to some claims by Kitamura, et al, in Phys. Lett A.


    I have also been active on the Internet ‘promoting’ my views, including trying to edit the Wikipedia page on CF.


    Recently, Krivit misrepresented an email I sent him in answer to a question he asked me. Also, Miles published an article in vol 132 of Infinite Energy, wherein he says he is publishing a paper written primarily by Fleischmann in 2003 but not published because of the Szpak 2004 paper, which is extremely similar. Miles precedes the paper with a 1 page note, claiming that Fleishmann rebutted my work, but I responded in this forum showing that no, he didn’t. In fact he makes the same mistakes that he made in the Szpak 2004 version. See Miles-Fleischmann-Szpak-Mossier-Boss Article in IE132 An interesting side note from the discussion we had (email) was that Miles admitted he has never read my papers. I have to wonder how he can know they are ‘wrong’ when he hasn’t. Storms also recently published a new paper that I comment on here: Edmund Storms publish a paper in "Environmental Science: An Indian Journal" : A New Source of Energy using Low-Energy Fusion of Hydrogen


    Perhaps the easiest thing to do to catch up is just click on my name and get the list of posts I made. There are only 330 or so of them, and they are grouped into just a few threads so it should be easy to ‘catch up’ (compared to Jed, Alain, etc.).


    With respect to excess heat and LENR, I have found no examples of any published calorimetric work that does not have the same basic flaws in it that I noted in my 2002 paper. Therefore, the question of whether excess heat has really been detected or not remains unanswered to this day. The key flaw is that everyone treats the calorimeter/cell as a homogeneous unit when it doesn’t appear to be. This induces an artificial apparent excess power signal via a mathematical problem with how they interpret their temperature data. You can read the original manuscript version of my first paper here: http://lenr-canr.org/acrobat/ShanahanKapossiblec.pdf


    This is a thread that goes into a little detail on these issues as well:

    [Split] Reconsidering F&P with CCS....

    I don’t believe I make any of the mistakes Alain accuses others of, but he seems unable to grasp that. You can read what I write and decide for yourself though.

    I think MFMP thought they had some minor excess heat levels. Regardless, researchers at SKINR demonstrated through some very well done studies using Celani provided wires that it didn't work. I'll look up a reference if there is interest.

    The only problem with what you say Jack is that one can always just say they did the experiment wrong, and that's why they saw nothing. As the saying goes "lack of evidence is not evidence of lack". What would be more useful is if they had seen something and then offered an alternative explanation that accounted well for it.

    The only other "objections" were published by Shanahan, who is a member of tin-foil-hat school of cloud-cuckoo-land physics, where anything goes, and anything might be true. See:

    http://lenr-canr.org/acrobat/MarwanJanewlookat.pdf

    Why do you insist on ignoring reality Jed? Your ref "MarwanJanewlookat.pdf" is more correctly written as:

    J. Environ. Monit.
    , 2010,12, 1765-1770


    which is the paper you continuously cite as somehow refuting what I wrote in:


    J. Environ. Monit., 2010,12, 1756-1764


    But the Marwan, et al paper is the one that talks about the "random Shanahan CCSH", whatever that is.


    But I never brought up a random effect. For ex., my very first paper was:

    A systematic error in mass flow calorimetry demonstrated, Thermochimica Acta, Volume 387, Issue 2, 23 May 2002, Pages 95-100, Kirk L. Shanahan

    Note the word "systematic" - NOT "random"


    Get with the program Jed, if you can't read the literature (and do your homework), you ought to keep quiet. It only makes sense.

    P.S.

    No one has discovered any errors in any of the major experiments, which were published by scientists in 180 mainstream laboratories, in peer-reviewed literature.


    My first paper delineates the major error you fail to note....

    Wyttenbach - I am not specifically interested in LENR and Helium. I am interested in proposed LENR reactions that occur in metal hydrides (and specifically metal deuterides and tritides) that can supposedly generate heat and radiation, as these products represent a safety hazard for me personally and for my coworkers. The patent you refer to doesn't fall in this bailiwick, so I'm not very interested. I suppose if there was a LENR that produced significant tritium, I'd be interested in that also as an alternative T production method. (I support the DOE's tritium processing facility at the Savannah River Site, and I personally work with most of the metals claimed to do cold fusion.)


    This thread is about the idea that there is a heat-helium correlation 'proving' CF exists (Abd's favorite idea), and about the new Storms' article showing his failure to incorporate any of my criticisms, starting with my 2002 publication,

    Just noticed something with the Storms' Figure 2 data we've been discussing. The count of experiments in the histogram bins goes like this 0, 2,3,7,3,1,0,0,0 and maybe one more zero. That totals to 16 on my calculator. The Figure caption says 'Summary of 17'. Wonder where the other point is? If you look, you can see that adding that extra point in somewhere is going to hurt the supposed Gaussian fit to the data. I guess in the 'Dictionary of Graduate Research Terminology' 'Summary of 17' means '16'.


    But Abd wrote:

    "This newer histogram I think is from data in Storms book (2014), The Explanation of Low Energy Nuclear Reaction. Table 9 (p. 42) is a summary of values. There are 19 values. It looks like Storms has omitted one value (2.4 x 10^11 He/W-sec) as “sonic” (Stringham), one as an outlier (4.4), and maybe one as “gas loading,” (McKubre, Case), then perhaps has added one. Or maybe he left in the Case value (2.0)."


    So 'Summary of 17' might even mean 'Summary of 19'??? Putting that 4.4 in will really bollix the fit.

    Abd said I should read his paper, so I did. Nothing but recitation of what others say. He referenced a Powerpoint presentation by a group of authors whose primary CFer is McKubre that details some positive CF experiments (http://www.lenr-canr.org/acrobat/ApicellaMreproducib.pdf) that I'd like to comment on.


    At the end in the background material there is a slide that actually has a calibration equation on it for their isoperibolic calorimeter. It gives electrolyte temp as a function of input power. The equation is: Telec = -0.1649 * Pin^2 + 5.3636*Pin + 24.337, and it has a multiple R^2 value of 1, implying it is a very highly precise equation. This can be reversed to predict Pin given the Telec values. I did it by computing Telec for Pin values of 1, 2, 3, 4, 5, and 6W, and then using the Excel fitting routine for a quadratic. I got this equation: Pin = .0022001*Telec^2 +.0060493*Telec -2.6978, with an R^2 = .99997 (I’m not sure why it didn’t give 1.0, probably round off error). Of course excess power (Pex) is given by Pex = Pout – Pin, and in calibration we set Pout = Pin.


    The question is what a small change in calibration constants would do to apparent excess heat. So I started with the McK equation to compute Telec for the Pin’s given above, then changed the linear and quadratic term constants in the reversed equation by +1%, and recomputed the ‘new’ expected Telec. Then I went back to the original McK equation and computed the Pout values for those new Telec’s. At 6W Pin, the shifted equation gives an apparent excess heat of ~78 mW. In my Storms’ reanalysis, I found a +/- 2.5% shift, which translates here to a 195 mW 1 sigma value (for 2.5% shift). Thus the 3-sigma band is +/- 585 mW, which can be rounded up to 600 mW band. Thus theoretically the excess power signal needs to exceed 600 mW to be ‘out of the noise’ if a 1% CCS has occurred.


    McK, et al have several slides claiming excess power. For example, their 3rd slide shows an excess power peak from a flow calorimeter of ~90 mW in a spike, smoothed I say more like 70 mW. This is approximately the same magnitude as the 1% CCS effect.


    Slide 6 show “Excess Power at SRI”. They seem to plot an excess power (very noisy) and a smoothed version that apparently uses the right Y-axis based on the figure legend across the top of the graph. Those plots show peak values of ~55 mW (guessing at the units, since they stated ‘Total Power = 214mW’), which is within the 1% CCS 1 sigma.


    Their 8th slide shows more calorimetric results for laser triggered experiments. They plot energy and power on the same graph. Of note is at the start the output power slightly exceeds input power (i.e. positive small excess power signal) but it basically tracks the input power, which is a good indication that the calibration is off or there is something else going on (Storms' first data set for Pt-Pt F&P cell work showed negative input power feedback due to ground loops). Later on, they get spiky output power when input power is constant. The spikes are about 190 mW peak values (~2.5 times the 1% CCS effect (or just a 2.5% CCS as found in Storms' results)).


    So my point is that the apparent excess power/energy values shown in these slides could *easily* be a very small CCS. It seems important to me that the reality of these signals need to be determined and not just assumed to be real excess energy.



    Since I am looking at the Apicella, et al, slides - some other points:


    In Slide 7, they state some conclusions which I find contradictory. In the first line they say: “(D/Pd > 0.9 in some cases also with less loading) have been observed at ENEA.” Then in the 2nd line they say: “We can conclude that high D loading is a necessary condition for excess of power production during loading of Pd with D.” But if one can get apparent excess power at <D/Pd=0.9, then it is incorrect to conclude that that is a requirement. Of course they don’t specifically say right there that >0.9 is the requirement, but in Slide 12 they do. These slides were presented in 2005, and today in 2017 the mantra is still “>0.9”. I disagree, it simply takes a little more work to get the effect when the Pd loading is <0.9.


    In slide 10 they show some 4He results for laser-triggered experiments. I note that the indicated background level is ~0.55e16 and the strongest result is 1.05e16, i.e., less than 2X background. I find that to be ‘working in the noise’, and I require much more replication to be convinced this plot shows anything of value. There’s also no way to evaluate if these signals come from leaks or not.


    Slide 11 shows results from the SRI “M4” experiment. I’ve noted elsewhere that I have looked at the calorimetry of this run, and determined that it could well be affected by a CCS. However, there is some *very* fancy data workup going on here, and I require a full explanation of that to be able to evaluate the data’s validity. I asked McK twice for that info and never got it. The He values plotted here never exceed the usual outside air value of 5.22 ppm, and there is no report of what the 4He concentration was in the lab at the time the experiments were run, so we can’t honestly reject leaks once again.


    Their 4th slide shows excess power from the Energetics lab that uses the “Superwave” on the input, and they don’t explain the calorimetric method. The excess is about 2.5W on an input of 4W. This clearly needs to be explained further, and the accuracy and precision clearly established, especially when the “Superwave” is being used. Ditto on the 5th slide, which is another Energetics lab results slide showing even greater apparent excess power.

    Wow…I thought we had dispensed with Abd’s garbage on this forum. Oh well…one more time…


    ABD quoted me and wrote:

    KS wrote: There are 38 references listed. 3 of them refer to the ‘general rejection’ of LENR by mainstream science (they refer to the books by Huizenga, Taubes, and Park).

    ABD: The books are references for the statement: “The special condition required to cause the LENR reaction is difficult to create. This difficulty has encouraged general rejection by conventional science [13-15] and has slowed understanding."


    My response: What’s yer point???


    ABD quoted me and wrote:

    KS wrote: If you look closely at Figure 2, you will see the He/Heat values exceed the theoretical amount in some cases.

    ABD: No. In one case, the value is on the theoretical amount, but something must be understood about this data. If what is being calculated is the heat/helium ratio, and if the actual ratio is a constant, experimental error will cause greater deviation from the actual ratio if the produced heat (or helium) are at low values. I have never seen the data presented with careful consideration of error bars as they affect the ratio.


    My response: As I put in my original disclaimer, I did this review quickly, and Abd has found a minor error I have made. Let me correct that now. What is funny is that once again, correcting my error places Storms in an even worse light.


    Storms’ Figure 2 is an alternative presentation of the ‘heat/helium correlation’ idea. He plots the number of experiments obtaining a value for the number of He atoms/watt-sec that lies within a specified range versus the mid-range value for that ‘bin’, in a typical histogram approach. He overlays a Gaussian fit to the data as a curve on the graph. The number of experiments obtaining a He/heat value in the selected range is indicated by a pink box on the plot. Storms also adds a vertical black line on the plot, and labels it “D+D=He”. I observed pink boxes at larger values than the black line. My mistake was to imagine Storms was using the data from his book’s Figure 47, which does show 1 point above the theoretical line and to assume he’d added a couple more (which would be expected based on prior data characteristics). In fact there are several pink boxes at zero values and most are above the black line. Only 1 lies below. So, my mistake, Storms does NOT show any positive values above the theoretical line.


    So, I have to ask, what happened to the data point from Figure 47 that was well above the theoretical line? Apparently, without telling anyone, Storms has rejected that datum. But that radically alters the interpretation of Figure 2. As I noted in other comments, that one datum alters the estimated standard deviation such that the 3 sigma spread encompasses the 0 line as well as going well over the theoretical line. It also swings the average up a bit. If you clip it out, you get a radically different picture, i.e. supposedly ‘all’ data points are now below theoretical (and we (meaning Storms and other CFers) have an ‘explanation’ for that). In my prior comments on Figure 47 from Storms’ book, I discussed why clipping out that high value was an illegitimate thing to do.

    The functional difference is that including it leads to the conclusion the experiments are too imprecise to use in making the ‘desired’ conclusion. Excluding it means you can use the data to support the LENR idea. But which of these is forcing the data to a predefined conclusion do you think?


    Abd said: “I have never seen the data presented with careful consideration of error bars as they affect the ratio.” – Perhaps, but I have discussed just that before, and now again in summary. Obviously Abd reads what I write, but apparently very selectively (which is typical of people looking to discredit something but not seeking to understand).


    ABD quoted me and wrote:

    KS wrote: I have previously commented in this forum on the related Figure from Storms book, which only had 13 numbers on it rather than 17, where I noted that the spread in the data indicates the precision of this measurement is too poor to allow one to make the conclusions Storms does. This hasn’t changed by the addition of 4 points.

    ABD: Shanahan doesn’t know what he’s looking at. The “Storms book” he is referring to is Storms (2007). Figure 47 in that book is a plot of helium/heat vs excess power, for 13 measurements from two sources: Miles and Bush & Lagowski. The Miles data is more scattered than the Bush data. Miles includes one value with the lowest heat (20 mW). The associated helium measurement generates a helium/heat value that is an obvious outlier.


    This newer histogram I think is from data in Storms book (2014), The Explanation of Low Energy Nuclear Reaction. Table 9 (p. 42) is a summary of values. There are 19 values. It looks like Storms has omitted one value (2.4 x 10^11 He/W-sec) as “sonic” (Stringham), one as an outlier (4.4), and maybe one as “gas loading,” (McKubre, Case), then perhaps has added one. Or maybe he left in the Case value (2.0).


    My response: “Shanahan doesn’t know what he’s looking at.” – Really? Really??


    “I think”? Yes, Abd is right, you have to guess at where it comes from. As I noted in my initial review, the referencing on this paper stinks. Where the data comes from is actually not specified, so you can’t check it. Abd makes some interesting guesses about where it comes from, and most importantly, he notes that Storms’ is picking and choosing what to look at. A clear recipe for making the data say what you want it to say, instead of what it actually says.


    ABD quoted me and wrote:

    KS wrote:

    This newer histogram I think is from data in Storms book (2014), The Explanation of Low Energy Nuclear Reaction. Table 9 (p. 42) is a summary of values. There are 19 values. It looks like Storms has omitted one value (2.4 x 10^11 He/W-sec) as “sonic” (Stringham), one as an outlier (4.4), and maybe one as “gas loading,” (McKubre, Case), then perhaps has added one. Or maybe he left in the Case value (2.0).

    ABD: It’s been confirmed. Maybe Shanahan should actually read my paper. After all, I cited his JEM Letter. It is not a “hand-waving” argument, but, obviously, this cried out for more extensive confirmation with increased precision. And so, I’m happy to say, that work has been funded and is under way. And they will do anodic erosion, I’m told, to test what is apparent from the two studies that did it (McKubre and Apicella et al, see my paper for references). These are the two studies where dissolving the surface of the cathode took the helium level up to the full theoretical value, within experimental error. Two other Apicella (Violante) measurements did not use anodic erosion, and results were at about 60% of the theoretical.


    My response: The quote attributed to me is just what Abd wrote immediately above. Cut-and-paste malfunction. If Abd will actually use my quote I might be able to respond.


    ABD quoted me and wrote:

    KS wrote: Exactly so. So one shouldn’t try to work with these numbers until they are shown to be free of the errors Storms points out, which hasn’t happened.

    ABD: Shanahan ignores that correlation can show relationships in noisy data. (This is routine in medicine!) Leakage, quite simply, doesn’t explain the experimental evidence. It could have had an effect on some individual measurements. No, we were not going to wait for “error-free” measurements, but rather how to proceed was obvious: the data shows quite adequate evidence to justify funding further research to confirm these results, and this is a replicable experiment, even if heat, by itself, is not reliable. The variability creates natural experimental controls.


    My response: “Shanahan ignores…” No, I don’t. But Abd ignores the point that correlations derived from fictitious data (excess heat is likely not real) are worthless. For the record, I have been using statistics for many years, and Abd has added nothing to my knowledge base.


    “Leakage, quite simply, doesn’t explain the experimental evidence. It could have had an effect on some individual measurements.” – And it certainly does. But in the ATER/CCS proposed mechanism there is a way to get increasing He signals in cells that show apparent excess heat. You all will also note that Abd does not respond to my specification that lab He concentrations need to be reported. Another thing he conveniently ignores.


    “the data shows quite adequate evidence” – As I noted, that is true only if you start dropping out data that causes that conclusion to not be true. That’s bad science.


    “The variability creates natural experimental controls.” – What? That makes no sense.


    ABD quoted me and wrote:

    KS wrote: I published a consistent, non-nuclear explanation of apparent excess energy signals, but of course Storms refuses to recognize this.

    ABD: Shanahan expects Storms to “recognize” Shanahan’s explanation as “consistent” with the evidence Storms knows well, when Shanahan, with obviously less experience, does not recognize Storms’ opinions, and merely asserts his own as valid?


    My response: Read carefully here folks. Abd is pulling a fast one. He implies I ignore Storms’ opinions/conclusions. I don’t, I provide an alternative. I do not assert it is valid, I assert it has the potential to be valid. Like all proposed mechanisms, it must be confirmed experimentally, but that will never happen when the people who can do so refuse to accept it and instead resort to falsified representations of it to justify ignoring it. Abd’s response above is a veiled ‘call to authority’ (“Storms is the authority and Shanahan isn’t, so believe Storms”) which is recognized as an invalid logical technique, often used to intimidate others into silence. It has no inherent truth value.


    At this point I can’t tell if this is Abd or Zeus46 writing, but whoever it is wrote:

    “Shanahan’s views are idiosyncratic and isolated, and he has neither undertaken experimental work himself, nor managed to convince any experimentalist to test his ideas. To the electrochemists involved with LENR, his views are preposterous, his mechanism radically unexpected.


    Yes, I’m sure that response is frustrating. After all, LENR is anomalous, unexpected. However … Shanahan’s explanations are, generally, a pile of alternate assumptions, chosen ad hoc, and his claim is that they have been inadequately considered, but who decides what is adequate and what is not? Shanahan?”


    But these paragraphs are nothing but CF fanatic fantasies. There’s nothing in them worth responding to.

    Some comments on the paper after a quick read…


    There are 38 references listed. 3 of them refer to the ‘general rejection’ of LENR by mainstream science (they refer to the books by Huizenga, Taubes, and Park). Yet Storms makes the comment:


    “real and imagined error have distracted from the importance of these studies”


    *without* giving any references. This is a technical flaw that should have not made it through peer review. If the ‘error’(s) is/are significant enough to distract, they are significant to reference. And yes, some of those would be my publications.


    Storms present two figures to bolster his arguments. They are a figure of number of reports of tritium (T) and neutron (n) detection plotted as a function of T/n ratio (Fig.1) and a figure of number of reports of the heat-to-helium ratio that Abd has presented extensively in this forum and elsewhere, and which I have in turn claimed proves nothing.


    From the Figure captions:

    “FIG. 1. Histogram of independent studies that measured both tritium and neutron emission [32],”

    “FIG. 2. Summary of 17 measurements of both helium and energy production during the same study [32].”


    Ref. 32 is: “32. Storms E. Explaining cold fusion. J Cond Matter Nucl Sci. 2015;15:295-304. “

    The initial problem is that reading ref. 32 does not tell you what or where the data is. As far as I can tell, the only way one could track this down is via ref. 1 in the JCNMS paper:


    From [32]: “The unambiguous nature of the detection of tritium shows that nuclear reactions can occur in deuterated palladium, a remarkable proof of the possibility of nuclear reactions in this system (see papers by F.Will et al. and T. Claytor et al. in [1]).


    References

    [1] Papers by M. Fleischmann, S. Pons, M. McKubre, E. Storms, Y. Arata, Y. Zhang, D. Gozzi, A. De Ninno, V. Violante, A. El Boher, X.Z. Li, S. Szpak, M. Swartz, A. Takahashi, D. Cravens, J. Dash, M. Miles, D. Letts, P. Mossier-Boss, G. Miley and F. Celani, Downloadable from among _4000 papers at lenr-canr.org.”


    but that is not adequate referencing. For the interested reader, that means he/she has to read *all* the papers in the lenr-canr database to find the one or two that Storms uses to make his figures. References are supposed to be clear and point directly to the source data for these kinds of reference.


    Storms says: “This ratio has been measured 17 times by four independent laboratories, the result of which is plotted in FIG. 2. This collection shows a range of values with an expected amount of random scatter. Of considerable importance, the average value is equal to about 50% of the value expected to result from d-d fusion. This difference is thought to result because some helium would be retained by the palladium in which the LENR reaction occurred. When efforts were made to remove all the trapped helium from the palladium, the expected value for d-d fusion was obtained [33].”


    If you look closely at Figure 2, you will see the He/Heat values exceed the theoretical amount in some cases. I have previously commented in this forum on the related Figure from Storms book, which only had 13 numbers on it rather than 17, where I noted that the spread in the data indicates the precision of this measurement is too poor to allow one to make the conclusions Storms does. This hasn’t changed by the addition of 4 points.


    The work by McKubre, et al, referenced as [33], provides a convenient hand-waving argument to explain why the mean of these values fall near 60% of the theoretical value, but certainly is not definitive. For one reason, it would need to be replicated several times before it can be incorporated into other studies as a mathematical fact, which it hasn’t. If it actually does explain the variation adequately, that needs to be referenced or directly documented, which it isn’t.


    Storms says:

    “The claim for helium production is easy to ignore because a significant amount is present in the normal atmosphere, which makes the sought-for helium easy to mistake for helium from this source. When this error is combined with the normal error in a calorimeter measurement, reasons to ignore the claim based on heat or helium alone can become overwhelming.“


    Exactly so. So one shouldn’t try to work with these numbers until they are shown to be free of the errors Storms points out, which hasn’t happened.


    He goes on to say:

    “On the other hand, the energy/helium ratio does not have this problem. The independent errors in the He and power measurements are unlikely to combine and create a consistent value for this ratio unless the helium and energy both resulted from the same nuclear reaction.”


    As I have noted the value is not consistent, thus the quoted statement is nonsense. Furthermore, until one defines the causes of the errors, one cannot just conveniently conclude they are independent. My CCS/ATER proposal has the potential of correlating the numbers for example.


    Back to the new paper. Storms says: “Nevertheless, this commonly observed extra energy is consistent only with a novel nuclear process because the amount of energy frequently far exceeds any known chemical source as well as the expected error in its measurement.”


    This is incorrect. I published a consistent, non-nuclear explanation of apparent excess energy signals, but of course Storms refuses to recognize this.


    Storms mentions:

    “Besides helium and tritium being produced, a complex collection of transmutation products is also occasionally reported. These nuclear products result from the nuclei of a hydrogen isotope entering the nucleus of a heavy element, such as palladium, and producing either a fragment of the target or a still heavier element [27-31]. Such nuclear products are very hard to justify when conventional understanding is applied. Nevertheless, many well-done studies report similar transmutation products.”


    Heavy metal transmutation claims are based on the detection of heavy metals. This is relatively certain. What is not certain are the isotopic distributions, which always come from SIMS, since there is never any proof given that they spectra are correctly interpreted. SIMS of metal hydrides gives many MHx species signals, which could be incorrectly interpreted as isotopes instead of multi-atom species. Until an adequate description of these studies is presented, these transmutation claims remain unlikely. Contamination concentration is much more probable.


    Overall, Storms continues to paint a rosy picture of the possibility of LENRs, while blithely ignoring relevant criticisms, further confirming the pathological science trait of not participating in the scientific process of critical review.


    Disclaimer: As always these are my opinions, and are based on a quick read (by a person who has followed the field since 1995). If you see something wrong, say something. I can be corrected by good, rational arguments.

    When journals stop publishing them?


    Depends on which journals. When CF was first announced in '89, major journals like Science and Nature published several papers on the subject, but when it devolved into an irreproducible phenomenon they quit publishing them. That is exactly what was to be expected though as Science and Nature are 'hot topic' publishers, and while a controversy is interesting, it isn't what 'hot topic' journals are looking for. (Yes, the editor of Nature made some poorly chosen remarks at the time, but that doesn't alter the fact that the controversy made them unfit subjects for Science and Nature.) Publication them moved to journals whose topical fields were consistent with the CF work, i.e. Fusion Technology (renamed later to Fusion Science and Tech.), J. of Electroanalytical Chemistry, Physics Letters, etc.). Then those journals started to cut back, primarily because there was no resolution to the conflict and lack of reproducibility occurring. So then the CFers started up their own publishing sub-network (Proc. of ICCFxx, J. Cond. Nuc. Mat. Sci., etc.). So technically, to date they haven't stopped being published, so I believe your criterion is not adequate. And besides, the CFers just claim 'establishment suppression' anyways.


    Personally, I don't think you should ever stop listening completely, but when a field has persisted in producing non-reproducible results for many years, and when the prime researchers in the field clearly ignore critics and make gross errors in their response when they don't, others are at least justified in requiring some semblance of good scientific practice from the researchers before they are given any significant attention. That's just my opinion though. I was wondering what Epi thought was the criteria. Maybe I can be convinced I *can* ignore them...

    @Epi


    So...having a clear agenda and beliefs about partially defined things means one can safely be ignored...interesting logic there Epi...


    Don't you think a scientist working in *any* field needs to listen to his/her critics? (And I infer 'listening' has occurred when appropriate responses have been made, not when someone simply says "I heard.")

    THHuxleynew - I will comment on your comments in an out-of-order fashion.


    “I'm never sure why in this case people claiming excess heat as they do jump on nuclear, unless for example the He4 evidence were to become real.”


    When apparent excess heat signals are integrated over the extended times that they have been seen to persist, the total ‘energy’ supposedly released exceeds what could rationally be obtained via chemical reactions computed using generous assumptions. That means that only nuclear energies have sufficient size to account for the observed signals, assuming they are accurate. But if they are not accurate, then the CF researchers are just integrating error, and the numbers are meaningless. This is what the CCS idea strikes at. It shows us how we can get an apparent excess energy signal (that can be integrated as above) when none is actually present. Once the pattern was established initially by F&P, others have just followed their lead.


    “I feel when there is such an attempt at science it should be treated with respect even if totally misguided, and badly done, as long as participants themselves behave properly.”


    I agree, and assert this is what I have done over the years, but the CF community has reacted inappropriately as I’ve explained elsewhere in this thread and forum as well as other places, i.e., they have NOT behaved properly. (In fact, I assert that their failure to participate in the normal scientific process of critical review qualifies them as pathological scientists.) So what do you think the rest of us should do when they behave improperly?


    “The lack of substance in the refutal [refutation] of your ideas as shown in the ten author paper is clear: they have not followed up on detailed points, and made a number of serious mistakes in characterising your argument. That this continues informally is a shame.“


    That this continues informally (and formally) is also the prime indicator of pathological science.


    “I can't say that your argument covers all or even most of the claimed electrolytic cell excess heat results. But, I can't say it does not cover these either.”


    To my knowledge there are no examples of a CF researcher properly considering the impact of calibration constant variation on their results (via, for example, error propagation) and I have followed this field since 1995. When it is possible to estimate calibration equation parameters and operating conditions from the publications, I have found no case that contradicts my theses. It is now 2017, and they are still doing the same thing. Again, this is a pathological science indicator. Once I showed how a ‘trivial’ CCS could wipe out a 780mW ‘excess heat’ signal, it became incumbent upon researchers to evaluate that possibility in their experiments, including revisiting the ones that predated my 2002 publication (which was actually known to the field in late 2000). That that has not happened illustrates pathological denial of criticisms. That conclusion is reinforced by the abortive attempt by the 10 authors to ‘pull a fast one’ on the rest of the science community.


    Discovering a systematic error that applies to a whole field of research is always a painful thing. But pretending there is no error doesn’t make it go away.


    “Were I an LENR researcher placing any reliance on these claims the first thing I'd want to do would be to examine your arguments carefully and see what they apply to.”


    That would be ‘normal’ science at work.


    “Your extending this to a polemic on not trusting LENR researchers is uncalled-for. Though I guess normal on this Forum!”


    As I have stated above, I have found no LENR researcher who is appropriately participating in the scientific process. I have observed lots of results and reports that could well be explained by ‘mundane chemistry and physics’, but never are. It seems to me that the people publishing in this field have given up the ideal promoted by Feynman in his famous quote:


    “You should not fool the laymen when you're talking as a scientist... . I'm talking about a specific, extra type of integrity that is not lying, but bending over backwards to show how you're maybe wrong, [an integrity] that you ought to have when acting as a scientist. And this is our responsibility as scientists, certainly to other scientists, and I think to laymen.”


    If you have a case where you think we should trust some particular CF researcher, would you share the example please? (Also, note that I am speaking about published authors who claim to have found excess heat or other evidence of CF. There are many people who have attempted replications of those claims but have failed to do so. Excluding the initial work of the 1989-1992(ish) time frame, I believe those researchers to have done good work, but of course failing to replicate can always mean you just did the experiments wrong. The early work was hampered by lack of details and a belief that replication could be done ‘quick and easy’.)


    “Whether anyone is right, or wrong, the only proper approach here is to evaluate specific actions of specific people, not to generalise. After a lot of such evaluation you might come to a conclusion that the whole collection of anomalies on which a set of LENR people depend has been well explained in ways that those people refuse to consider. The best way to show LENR ideas right or wrong would be to continue to take them seriously and be interested in them, and follow through the evidence.”


    One generalizes when one has sufficient detailed data to do so. To my knowledge to date, all CF research involving calorimetry assumes a one dimensional model (i.e. homogeneous) of the system is adequate, even when it is _known_ that the system is non-uniform. Further, to date there are extremely limited numbers of cases where those claiming to have detected 4He as a reaction product will cite the laboratory air 4He concentration. In the few cases where they do, the room and experiment numbers are disconnected and can’t be used to decide if leaks were present. Beyond heat and helium, there is usually an insufficient body of information available for drawing solid conclusions. But even there one can find logic errors that have been promulgated trough the field. A specific example: Ed Storms did a study to try to discount the idea promoted by Gary Taubes that tritium was spiked into some samples and then reported as CF proof. Ed claims in his paper that he disproved the spike idea, when in fact he disproved only one possible spiking method, the simplest imaginable, a single one-time spike. It is a logical error to imply that _all_ spiking was disproven. I could go on with more specific examples, but my point is that I believe I have done what you say, and I now feel I have a body of information sufficient to accurately generalize.


    It really can be summed up quite simply by saying that there is insufficient consideration of final error levels, which leads the CF researchers to conclude noise is signal. As I said, if you have a case where this is not true, let me know. Maybe I missed something, and I’d like to try to live up to the expectation expressed in the Feynman quote above.


    “You have to some extent done this, and to some extent been stopped by those making claims refusing to consider the arguments against: so a shame to fall at the last hurdle. “


    I believe I have done so to a major extent. I have established or adopted basic criteria to judge the quality of the reported work, and I’ve found none that meet the standard. And this standard is not some ‘pathological’ bar that can never be jumped. It is simply evaluating the error in a reasonable way. Claiming that recombination is not a problem by measuring an ~10% _excess_ of collected water in an F&P-type experiment when a 2-3% error in calibration constants can zero out the signal is not acceptable error analysis. Refusing to provide calibration equations and operating conditions used in the power calculations is not an acceptable way to claim excess heat. Etc. ,etc.


    The argument is never finished in science, and tomorrow, someone may show a true, unexpected excess heat. But if so, they must meet the objective criteria established to judge the validity of their claim. Being ‘out of the noise’ is one of them, and so far, no one has done this after 28 years.


    I don’t think I am ‘falling at the last hurdle’. I think I have simply pointed out the hurdles the CFers are running around instead of jumping.