Validity of LENR Science...[split]

Quote from JedRothwell

Heat from recombination or other events inside the cell cannot be distinguished from other chemical heat or nuclear heat.

However, it is very easy to determine that recombination is occurring, or that that it is not occurring. You do not measure the heat from it; you measure the electrolyte left in an open cell.

In a closed cells there is always recombination, and it never shows up as apparent excess heat. Shanahan's claim that heat sources shift in cells and cause spurious excess heat are wrong. That never happens.

Along similar lines, you can also measure the total amount of hydrogen absorbed in the cathode by measuring the "orphaned oxygen" left in the head space of a closed cell. There cannot be much, because the hydrogen to palladium ratio never reaches 1:1. Also because most cells are made of glass, and they would break if a lot of oxygen pressure built up. There is only a little orphaned oxygen, and therefore only a little absorbed hydrogen.

As I mentioned above, at the power levels observed in heat after death, if all of the hydrogen magically emerged from the cathode instantaneously, and if oxygen magically entered the cell, the power would be sustained for about 5 seconds before the fuel was used up. Since the cells remain hot for hours or days, that cannot explain the heat. As I said, this is impossible because there is no oxygen, only water vapor, and because it takes weeks for all of the hydrogen to come out.

Quote from JedRothwell

The maximum apparent heat from recombination is easy to compute, and it is always far less than a cold fusion reaction. Thousands of times less, in some cases.

It is thousands of times less because only insignificant levels of recombination are observed. As I said, you can be 100% sure there is (or is not) recombination. In any open cell made by a professional electrochemist there will be none. The methods of avoiding it have been common knowledge since Faraday first described it.

IO: clearly hostile questioning just gets the backs up of people who believe (rightly, I'd guess) you have made up your mind and are not interested in contrary evidence.

Jed: the trouble is that what (indeed) some mainstream scientists have said about LENR people is just what you have said about people like Shanahan or (possibly) me. Equally dismissive.

Your reason for this, I guess again based on your answers here, is that you trust various LENR people who are experienced and knowledgable, and who disagree with Shanahan. You've said that you consider none of us competent - which may be true. But when given the contrary opinions of people all of who have published in the area you dismiss one set and endorse another.

That is exactly what the mainstream scientists you quote do - except they have different views and dismiss arguments of people on a different side of this argument.

Shanahan, in his white paper, which I suspect from some of you comments you may not yet have read, and which unlike your claims Shanahan has says has not received a proper reply, makes some salient points about the symmetry with which both sides in this debate are inclined to cling to their prejudices and therefore not examine contrary evidence. For example, in the argument about CCS(H) you strongly quote things that you believe prove LENR as an effect exists, and yet do not allow the possibility that his ideas might well apply to some F&P style experiments.

A good scientist would not be dismissive in the way the Marwan authors were. They would examine the contrary arguments each one carefully working out its possible domain of application, noting where it appeared not to apply, rather than ignoring them as the Marwan authors did. There is real scientific interest in the engagement - nothing of interest in the dismissal. No doubt you have reasons, based on the other people not sharing your views when the evidence seems clear, to be so dismissive. Has it occurred to you that the mainstream scientists you quote may have been equally frustrated?

Science requires more from both sides in such a debate. And dismissive attitudes to wards criticism from the LENR community will simply reinforce the view of most mainstream scientists that there is not likely to be any nuclear effect involved, and therefore the lacunae of these experiments are errors and weird phenomena of no great commercial of scientific interest. Having said that there is always some scientific interest in weird phenomena: but maybe not enough to get people following an area that does not seem to progress.

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In a closed cells there is always recombination, and it never shows up as apparent excess heat. Shanahan's claim that heat sources shift in cells and cause spurious excess heat are wrong. That never happens.

Jed, I'd be interested what type of evidence you (or the other people you trust more expert than you) would provide to back up that claim. It is always difficult to prove a negative - especially for something that would be noticed only as second order changes in apparent heat balance. As far as I can see the only experiments susceptible (on theoretical grounds) to this hypothesised recombination would be LENR ones? And just as LENR is a sporadic phenomena, for almost identical reasons (presence of absence of active environments which depend on details of physical structure) Shanahan hypothesises that this type of recombination is sporadic. Therefore a few cases where such recombination is been shown not to exist does not dent his hypothesis - no more than a few negative LENR experiments dent the LENR hypothesis.

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However, it is very easy to determine that recombination is occurring, or that that it is not occurring. You do not measure the heat from it; you measure the electrolyte left in an open cell.

I don't quite understand that. In an open cell you would also need an accurate measure of the gasses evolved and how much D2 / O2 they contained. and then the subtraction leaves the wanted quantity together with errors in other larger numbers, a classic case where errors get amplified. I know it can be done, but I would not call it easy to do accurately.

Quote from interested observer

Jed, I gave you a one-sentence phenomenological definition of superconductivity. I asked for the equivalent for LENR and you told me to go read two books by Storms. Doesn't that strike you as peculiar?

No, I suggested you read the paper by McKubre. If you want more detail, read the books by Storms. The paper by McKubre is 15 pages long. If you will not make the effort to read a 15-page paper, you are not serious.

Superconductivity is better understood than cold fusion, so it is easier to summarize it briefly. Cold fusion an experimental observation with no theoretical explanation that has been widely agreed upon.

Quote from interested observer

You spend half your life spreading the gospel of LENR to the world but when anyone asks you a specific question, you respond by telling them to look at hundreds of papers or read books.

No, I responded here repeatedly by pointing to McKubre's review and to two other pages, by Fleischmann and McKubre. The review is featured on the front page at LENR-CANR.org.

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And my comment about 90 efforts was just a quote from IH Fanboy. Argue with him about it.

I do not know what he is talking about. I have no knowledge of his sources. There are, of course, many researchers, but they are working on a shoestring. You can see a large fraction of them in this photo:

http://lenr-canr.org/wordpress…oads/ICCF18groupphoto.jpg

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I am mostly looking to understand why people are so convinced about something that in the big picture seems so nebulous. But when I ask such questions, I am told to go read 1,000 papers. There is most assuredly no other area of science where this is the standard response.

I share your annoyance at being told to read 1000 papers when asked for clear evidence that LENR exists. A more honest answer to me would seem to be to admit that there is no such clear evidence, but note that many experts who have read 1000s of papers, many of which document difficult to explain phenomena, have become convinced which is undeniably true.

A lot of the difference in judgement here comes from how people process this plethora of suggestive but inconclusive bits of evidence. Those who are convinced by it reckon it is independent enough, and therefore so many different recorded anomalies must add up to something which they call LENR. Those not convinced reckon that selection effects undermine any independence and that if there were a real effect of the type suggested that delivered reproducible near error evidence in so many different experiments, it would be bound to deliver reproducible clear evidence in some by now. That is what normally happens when elusive phenomena are studied over decades, although you can point out to novel phenomena that went unrecognised (or at least not understood) for a very long time. So making that argument stick would require much more precision and careful analysis.

Quote from interested observer

So I have been told that there are hundreds or thousands of observations of LENR, a hitherto unknown nuclear process. Can someone present a phenomenological description of LENR? What are its defining characteristics?

As far as I'm concerned the definition of LENR is in the name - Low-Energy Nuclear Reactions, e.g. the observation and/or production of nuclear reactions using (as input) much lower energies than would be normally expected based on theories and experiments which only correspond to (in the case of experiments) or take into account (in the case of theory) two-body reactions along with the effects of the long-range Coulomb repulsion between nuclei and the short range of the nuclear force. Presumably, many-body effects, and/or screening play an important role, but there could be many other processes going on as well. I note that some (such as Storms) have given other defining characteristics (such as it does not follow the expected pathways for nuclear fusion, or does not produce significant radiation) but I consider the much broader definition implied by the term LENR to be more scientifically useful and interesting.

Quote from THHuxleynew

In an open cell you would also need an accurate measure of the gasses evolved and how much D2 / O2 they contained. and then the subtraction leaves the wanted quantity together with errors in other larger numbers, a classic case where errors get amplified.

Nope. The method works quite well. It is more accurate than trying to measure the heat from recombination directly, because that heat is a few milliwatts at most. Also because measuring gas flow can be tricky. I will discuss that below.

You measure the electrolyte left over in the cell, and compare this to the amount that would have left the cell with zero recombination. Water also leaves the cell from evaporation, but that amount can be estimated with precision. Here's the thing: you measure the water left in the cell once a day, or once every week, when you replenish the water. This is usually done with a syringe to avoid contamination from air. So it is a cumulative amount of water that corresponds to a cumulative amount of energy. Every joule of heat from recombination is accounted for. To measure the instantaneous power of recombination, you need a calorimeter than can detect 0.1 mW, which costs tens of thousands of dollars. To measure the joules that add up over a week in water, you need a hypodermic syringe that measures liquid volume to nearest 0.1 ml, which costs $0.10.

Gas flow meters are tricky and expensive. You can measure the instantaneous flow with an inverted test tube under water (outside the cell). This is cheap and reliable. It tells you there is (or is not) recombination during the hour you do this procedure, but the flow rate might change when you are not measuring it. So you should use this method but mainly rely on the water level in the cell.

Quote from THHuxleynew

I know it can be done, but I would not call it easy to do accuratel

It is quite accurate but somewhat imprecise. If there is a 10% error (let us say) it is 10% after 1 day and 10% for the whole week. It does not get any larger, because there are only two ways for the water to leave the cell: electrolysis and evaporation.

If the water leaves the cell by any other path, you can tell after the experiment because amount of electrolyte salt left over is not how much you put in at the beginning. This is carefully measured after an experiment.

Fleischmann described all of this in the paper I pointed to, and elsewhere. Miles discusses recombination.

THH made some comments I’d like to address to enhance the discussion:

“(1) Marwan et al make some general remarks about Shanahan's hypothesis which are not backed with detailed argument and as Shanahan points out inaccurate - his proposal is for a systematic, not random, error in these F&P style experiments. These remarks are just not convincing at all.”

Thank you for noticing. Definite proof you’ve read and/or listened.

“(2) Marwan et al give as evidence that different types of calorimeter show the effect. That is not in itself an argument against Shanahan, since some systematic effect might be present for this type of reaction in multiple calorimetry setups - more is required here. However, it might become this with more detail.”

The systematic effect I describe arises because of cell construction details. The calorimeter type does not affect that at all. The only difference between calorimeters that seems to be relevant is the extent to which they capture the heat from the cell. Less efficient calorimeters allow for larger apparent heat signals (which conforms to one of the Langmuir pathological science requirements).

“(3) Marwan et al point out that high efficiency mass flow calorimetry does not require calibration and therefore is immune to CCS(H). This is a valid point.”

In the purest sense, the only way that statement can be correct is if you have a perfect calorimeter. Of course, no such thing exists. What you have is differing extents of approach to this ideal, expressed as the percent of input power detected. Calibration adjusts the detected output to match the input, i.e. it compensates for heat losses. The idea of ‘no calibration required’ is just saying that assuming a value for the calibration constants is “good enough”. However, that is one of the points of my original study in 2000-2002. Storms had a 98% efficient calorimeter. That seems to be able to produce a peak 780mW excess heat signal. I don’t think anyone else’s calorimeter is going to do much better than that. Another 1% perhaps, but that would be about it. Yet in that 2% lost heat lies the whole of ‘CF’.

To my knowledge, no one has ever tested out my ‘hypothesis’, so saying it isn’t important and/or can’t happen to them is just wishful thinking. CFers seem to maximize that problem.

“They then quote specific calorimetry from SRI:

4. M. R. Swartz, Survey of the Observed Excess Energy and Emissions In Lattice Assisted Nuclear Reactions, Journal of Scientific Exploration, 2009, 23(4), 419–436.
5. M. H. Miles, B. F. Bush and K. B. Johnson, “Anomalous Effects in Deuterated Systems”, NAWCWPNS TP 8302, September 1996.”

Off the top of my head, I don’t recall what Swartz said. I do know that all of Miles’ work is incorporated into my thinking, so the Miles reference does not invalidate the CCS/ATER proposal. I strongly suspect Swartz’s paper adds nothing to this debate.

“This needs further investigation, since they do not quite join up the dots by quoting calorimetric efficiency for the results that they quote. In any case, while this is a possibly (I have not investigated it) valid point that there may be other good evidence for FPHE, it is not a critique of Shanahan's ideas which could nevertheless apply to any similar experiments in lower efficiency mass flow calorimeters. Shanahan does not address this point (as far as I can see, maybe I missed it).”

Further investigation will run into the same brick wall I found, namely that the CFers never give enough information about how they work up their data to be sure. Some mention techniques, some equations, a few give cal constants (Miles esp.), and some information can be tentatively derived in a few other cases, but on the whole, no one fully describes their calorimetry methods and results. A case in point is my second publication of 2005 that commented on a 2004 paper by Flesichmann, Miles, Szpak, and Mosier-Boss. Guestimates from their paper suggest their data would fit the CCS/ATER scenario.

“(4) Marwan et al say that heat production correlates with D/Pd ratio, and this excludes a CCS(H) like artifact. That would need much more careful analysis to make good, since there could easily be such a correlation within Dhanahan's proposed effect (which is not random) and which relies on some type of recombination of other mechanism that would be influenced by local chemistry.”

This is a big bugaboo of McKubre’s. The fact remains that early work supposedly showed excess heat and supposedly was at less than his optimal loading. That means his critical loading number is bogus. The problem is he did a lot of work on this, as detailed in his 1998 EPRI report, and thus he has become emotionally invested in the idea, just like all CFers seem to be in the ‘obvious’ nuclear nature of the effect.

More importantly, Pt does not hydride at all, yet showed ‘780 mW excess heat signals’. Loading level was 0 there, so how important can it be.

In the specific case of Pd, high loading is likely to induce more surface structure due to dislocation loop punching and superabundant vacancy formation. A more corrugated surface will hold bubbles better, which is what I believe the Special Active State does in some instances to promote the occurrence of ATER. Other ways to do that include contaminants on the surface (additives) or a massively increased surface area such as you get in dendritic deposits (codepostion process). All consistent with CCS/ATER.

“(5) Marwan et al note compelling HAD (Heat After Death) evidence. Shanahan strongly disputes this, with what seem detailed reasons. I have not checked this (how accurate the claims - which of them does Shanahan rebut, etc).”

This is an interesting phenomenon. CFers report single event excess heat/transmutation product events all the time, with no detailed explanation of how this occurs and very little chance of replicating it again. Case in point, Marwan and Krivit’s mention of the F&P HAD from their 1993 paper in the 2009 JEM paper. I respond to that case in my 2010 Comment, and then the ‘group of 10’ castigate me for not explaining every single report of HAD, even when the information available is extremely limited. Typical. The CFers would scream till they were blue in the face (and do) about that if done to them, but, hey, it’s OK for them to do to others.

The HAD events, per the Marwan, et al, definition, all involve radically altered operating conditions. Different operating conditions means a different steady state. A CCS is an induced calibration constant shift caused by a change in steady state conditions. So, what’s the reasonable thing to do under HAD conditions? Recalibrate. Does _anyone_ do this? No. Ergo, since heat measurements during a HAD event based on non-HAD conditions are useless, any attempt to interpret what is going on are bogus.

Further, as I mentioned yesterday, the HAD brought up by M&K in 2009 was F&P’s HAD from 1993 based on the video Jed posted. I show in my whitepaper that a cell that reportedly did NOT have a HAD event gave an almost identical temperature profile to the cell that supposedly was undergoing HAD. This illustrates that the criterion F&P used was not correct. I _suggest_ similar problems are present in all HADs claimed. But it is NOT my job to check every claim out there, as the group of 10 imply. It is THEIR job to recheck THEIR work in light of the new information I added.

Quote from THHuxleynew

A more honest answer to me would seem to be to admit that there is no such clear evidence,

No, that is not an honest answer. That is bullshit. There is clear evidence. Not just clear, it is 100% irrefutable. No skeptic has ever published any reason to doubt any the major studies by Fleischmann, Storms, McKubre, Miles and many others. * As I said, these two are good starting point, but there are indeed about 100 others:

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

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

This is iron-clad proof, based on the laws of thermodynamics and methods of calorimetry that have been in use for 180 years. If you were to claim that calorimetry does not work when applied to some other field of research, scientists would say you are crazy. It is one of the most well established methods in science.

Questioning this is as crazy as Morrison was when he claimed that it is impossible to know how much energy it takes to vaporize water at 1 atm. The answer is 2257 J/g. That textbook value is well established, to say the least.

No skeptic has ever challenged any of the major studies showing tritium production, or the helium studies either. In some cases tritium has been 50 times background, and in others millions of times background. It is not possible that researchers in several hundred labs measured this incorrectly. It is proof that there is a nuclear effect.

* I realize that Morrison and Shanahan published papers that they believed revealed doubts, but those papers have no merit. Read them and judge for yourself. I suggest you start with the claim that heat after death is caused by recombination. Look at the list of reasons I presented showing why that is impossible. That list was not compiled by me, by the way. It came from Fleischmann, the National Plasma Fusion Inst. in Nagoya, BARC and the French Atomic Energy Commission.

A few pointed comments about more of Jed’s inaccuracies:

“Furthermore, even if there were recombination, as Fleischmann pointed out, the maximum power from recombination in this system would be 5 mW. “

The 5 mW number comes from assuming ELECTROLYTIC recombination. As such it is irrelevant to the whole CCS/ATER discussion.

“There is no oxygen in the cell during heat after death, as I said. There is a small amount during electrolysis in the headspace, but there cannot be much. It either leaves an open cell, or recombines in a closed cell, or the cell explodes.”

Of course the CCS/ATER scenario may or may not depend on residual recombination occurring after the electrolysis stops. I think the more likely problem is that the non-HAD calibration equation is invalid at that point.

“That is not possible. The heat is measured externally to the cell in many cases, such as with Miles, or with any flow, Seebeck or ice calorimeter. Heat from recombination or other events inside the cell cannot be distinguished from other chemical heat or nuclear heat. It is not possible to determine the location of the heat release, “

This is the CF community’s party line, and it is where they make their mistake.

“and moving the location, for example with a joule heater, has no measurable effect.”

This has actually been done? Where is it reported? (Plus, note that moving around in the electrolyte is likely NOT going to show the effect since we all agree mixing is good in these cells.)

“Yet we know this is nuclear heat because:

1. It exceeds the limits of chemistry by factors ranging from 1000 to 100,000.”

So does an integrated error.

“2. It is correlated with helium, tritium and transmutations.” - no it isn’t.

“3. There is no chemical fuel in the cell.” - of course there is, it’s called hydrogen.

“4. There are no net chemical changes in the cell. (Or, if there are, the cold fusion effect never happens.)”

Of course there are. Hydride levels change, gas composition changes, things dissolve and deposit elsewhere…

“5. The heat balance with null experiments is zero. There is no excess and no deficit.”

Null experiments do not prove ‘non-null’ ones are nuclear-based.

“6. The maximum apparent heat from recombination is easy to compute, and it is always far less than a cold fusion reaction. Thousands of times less, in some cases.”

I suspect Jed is invoking ELECTROCHEMICAL recombination again to justify this statement. That’s not what we’re talking about Jed. So far to my knowledge, no one has investigated whether a CCS/ATER phenomenon could produce apparent excess heat signals except in the one case I presented in my 2002 paper.

“7. In a closed cell, recombination always occurs (or the cell explodes) but it never produces spurious excess heat.”

Agreed. No spurious “excess heat” ever. (Did you realize that’s what you said Jed?) Just apparent excess heat signals.

“All of this is explained in the literature.” - and countered in my papers.

“I suggest you read it more carefully before commenting. You don't really need me to tell you these things. Needless to say, I and others have told Shanahan all of this countless times, but he ignores it.”

Yup. After having told YOU countless times that your heroes have made some mistakes, and then watching you ignore what I say and write, I do pretty much ignore you. At least I realize you’ll likely never change. I’m just worried about the people who seem to think you have something valuable to say.

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Water also leaves the cell from evaporation, but that amount can be estimated with precision.

That is what I was thinking might be difficult in all of these experiments. I'm not saying it can't be done, but it needs care, because you need to include any liquid phase water leaving the cell as well. Do you want me to check F&P's paper for how they did this? If you know the answer it is not needed...

THH

Quote from interested observer

Jed said that "Cold fusion an experimental observation with no theoretical explanation that has been widely agreed upon." All I am asking is what that experimental observation is

Shut up and read McKubre's paper and you will see! Stop whining and demanding that Daddy spoon-feed you. I gave you a link. I put the paper on the front page at LENR-CANR.org. If you will not read it, there is nothing more anyone can do to enlighten you. We cannot magically give you knowledge by ESP. You must read and work to understand these things yourself.

No one answers your questions better than McKubre. Although I have to say, Mallove and I did a pretty good job in the 14-page summary here, pp. 8-22:

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

@Kirk,

The HAD issue is only relevant for these anecdotal reports of cells that melt, etc. I guess I'd need to get Jed to give more precise evidence about these. Otherwise I agree that instrumented HAD may just be calibration issues - or at least these would remain a candidate until ruled out, Jed's arguments against this are not yet strong.

Jed claims that recombination is easy to bound from measurement of liquid mass change in cell, and liquid lost through evaporation (or - he did not include - but it is needed - splashing and liquid phase mist). He has a point there if the errors in this calculation can be got low enough - they certainly would allow recombination to be bounded.

@Jed - can you point me to someone who has bounded recombination in the manner you suggest? Perhaps F&P? Then I can check.

It is important to go carefully through each of these points: some I agree with Kirk, some I agree (but with caveats due to assumptions) with Jed, some I think would need further investigation to argue either way.

There is of course a world of difference between "CCS never happens" and "CCS accounts for all claimed anomalous heat in F&P type cells". I'd expect Jed to agree that, and am pretty sure Kirk would. It is helpful to explore this continuum rather than arguing as though a given class of cases settles the matter either way. In fact the strongest evidence that in this area Jed's "heroes" are not doing a good job is the lack of such attention.

Quote from THHuxleynew

That is what I was thinking might be difficult in all of these experiments.

I couldn't do it. You probably couldn't do it. But someone with a PhD in electrochemistry finds it easy because they spend year after year doing stuff like that, and other stuff way more difficult. (I have spent a month or so looking over their shoulders, and I have read electrochem. textbooks, which is how I know this.) It takes 5 or 10 years to a PdD in electrochem., for good reason.

This is like saying that surgery is hard, or that understanding the intricate details of Japanese grammar is hard. Yes, it is. I have Martin's Reference Grammar of Japanese which is 1198 pages long, crammed full of details. So there is a lot to learn. But you know what? I studied that subject for years, and read and translated many books and saw hundreds of hours of TV in Japanese, so it is not so hard for me. It just takes practice.

The point is, just because something is difficult for ordinary folks, that does not mean we should assume that several hundred world-class experts in electrochemistry did several thousand experiments from 1989 to 2000, using many different instrument types, and every single one of them botched it. That is not a rational assumption. That is not how the world works.

The calorimetry is actually the easy part of cold fusion. Other aspects of it are more challenging, as you see from papers by Storms and Fritz Will. Richard Oriani, who was one the best in the world by any measure, said that in his 50-year career this was one of the most difficult experiments he did. There is a long list of mistakes that a person not trained in electrochemistry will make, which will preclude any chance of success. As I wrote, experiments done by people with no experience in electrochemistry resembled "people trying to tune a piano with a sledgehammer." I published a fairly hilarious description of one such experiment. It would be a laff riot except that it cost a ton of money and skeptics always point to it as proof that cold fusion does not exist:

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

Quote from THHuxleynew

I'm not saying it can't be done, but it needs care, because you need to include any liquid phase water leaving the cell as well.

As I said, any path other than electrolysis or evaporation would change the amount of salt left in the cell. This is common knowledge, and it has been proved many times in cold fusion and other electrochemistry with blank experiments. Evaporation is estimated from first principles and also measured accurately with a joule heater only (no electrolysis).

@THH

In their 2004 paper, Szpak, Mosier-Boss, Miles and Fleischmann attempt to measure the extent of recombination by externally reacting the offgasses to reform water. The cell also showed excess heat signals. They obtain a number about 5-7% larger than they should have seen, based on zero recombination in the cell. I.e. we are forced to assume CF also creates a little excess water as well as excess heat. Actually, no one has claimed that. When I wrote my comment on their paper in 2005 I pointed this out. The review comments was "that's just the noise" or something to that effect. That illustrates the problem in a nutshell. The CFers ignore things I don't. I saw fake excess heat signals in Storms' work arising from a +/- 2.5% change in calibration constant (=1.5%RSD). It produced a 780 mW peak signal. Miles reports variations in cal constants of the same size. Storms' original paper on his data also demonstrates this type of variation. The CFers ignore this because "It's just the noise." Ignoring it alllows them to claim "LENR! LENR!". I on the other hand calculate it out and show that it means that their excess heat signals "are just the noise", but I find systematic effects buried in it too.

Yes you can measure recombination extent in principle, but if ignore the impact of the variation on your results, you needn't have bothered.

(Note: Don't miss the subtle point from the 5-7% error. It was obtained during 'excess heat'. If the CCS/ATER is correct, that was to due to in-cell recombination, which means that the amount of water observed should have been lower than what they used as baseline. I.e. The error in water volume measurement was worse than 5-7%.)