Validity of LENR Science...[split]

Quote from JedRothwell

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

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).

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Jed, the problem is that the different experiments all have different potential issues. You are saying that in this case if enough people come up with positives we should trust them, because they are experts. That is not good enough, because there can be systematic errors, and because of selective reporting at different levels. I'm happy, for example, that you quote one high quality paper such as, you say, McKubre. But this is a summary paper - appropriate for when a phenomena is generally accepted. Much more care with details is required when a new phenomena is not accepted - particularly when we do not seem to have contemporary high quality replications.

On the specifics I take your point about salt but that has errors. The issue is when you carefully add all these errors what are they. I'd expect all this work to be done in a high quality paper making the case for an extraordinary new effect. It would convince other people to replicate. But without such work mentioned there are loopholes and people will reckon loopholes are more likely than an extraordinary new effect. Rightly so - even if in fact the extraordinary phenomena does exist.

Is there material from McKubre which covers these experiments in a more detailed form? I find it difficult to reach a conclusion with only the summary data.

"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."

Yet looking at those thousands of experiments(*), one finds they all used essentially the same cell configurations and roughly the same data interpretation methods. Can you spell "systematic error"?

(*) Don't mix F&P electrolysis with Rossi Hi-temp gas loading with ...not correct procedure to do that.

So - of these thousands of experiments. You'd expect earlier ones (for example F&P) to have more issues. Certainly open cells here would have significant issues that closed cells avoid, or reduce. You'd expect that with so many experiments the various error mechanisms can be very well understood and all considered in the writeups - which would become ever more detailed in the quest to gain more bullet-proof results.

In this situation what is needed is these detailed write-ups with all bases covered. McKubre would appear to be quite careful in that he is using high quality calorimetry, but I'd like to see very detailed results from him which would, for example, provide ammunition against critics like Kirk.

Kirk, have you seen detailed results from McKubre's stuff? I notice this is isoperibolic and therefore a prime candidate for CCS? Presumably it cannot have the nice qualities that an absolute method such as mass flow calorimetry with very well insulated closed cell systems and 99% efficiency as noted by Mallove et al. I'm wondering what are the LENR results done with such equipment?

Jed: Mallove et al quoted 99% efficient (that is total losses <1%0 mass flow calorimetry as ome reason why CCS(H) is not relevant. Do you have from your 1000s of papers results using such a system? That would be the simplest way to argue that at least in some setups CCS(H) does not apply, if we have absolute excess power beyond the absolute accuracy.

Regards, THH

"So - of these thousands of experiments. You'd expect earlier ones (for example F&P) to have more issues."

Not necessarily. Only if there was an effort to eliminate error. So far, my suggested error hasn't been dealt with, so I see a consistent problem in all the experiments.

"Certainly open cells here would have significant issues that closed cells avoid, or reduce."

Actually I don't know that I agree with that statement. They both have similar but slightly different issues. That's why the CFers need to publish equations, constants, and at least some check data, so we can evaluate the actual error.

"You'd expect that with so many experiments the various error mechanisms can be very well understood and all considered in the writeups - which would become ever more detailed in the quest to gain more bullet-proof results."

That's the supposed norm, but not in the CF field.

"In this situation what is needed is these detailed write-ups with all bases covered. McKubre would appear to be quite careful in that he is using high quality calorimetry, but I'd like to see very detailed results from him which would, for example, provide ammunition against critics like Kirk.

Kirk, have you seen detailed results from McKubre's stuff?"

Yes, I believe I've described this here before, but here's a thumbnail again. In 1998 McK published a 400+ page EPRI report on his work of the 1993-1994 timeframe. This covered his "Degree-of-Loading" experiments, which is where he derived the >0.9 criterion he and others favor today. That was about half the report, the other half was a description of a large number of calorimetry experiments with modified, and even totally new, calorimeters. This is where the infamous "M4" run comes from. Along with the text, which was a few pages for each type, was a CD with 250 Mb data files on it. I read the report and noted he only saw significant excess heat signals in a couple of cases, and only the M4 was very large relatively speaking with a peak excess heat signal of 360 mW. (This was about 4-5X lower than his prior report and publications from the 1991-1193 time period.)

The problem was that he did not include any calibration data in that 250 Mb, only experimental runs were included. And, he used a very unusual calibration method on the M4 runs, namely transfer functions. As usual, his descriptions were superficial, with no details. I wrote him twice asking for the equations and constants, but he claimed he was too busy to reply each time. I then tried a 'Hail Mary' move, and asked a group of people discussing CF via a mailing list whether anyone knew what he did. McK was a participant on that list. He got incensed at my action, labeled me a 'grandstander', and broke off communications. Shortly thereafter Ed Storms posted his data.

I did do one 'tricky' thing with McK's data. Since there were 4 runs in the M series, and M1 and M3 (as I recall) had no excess heat, I used those data streams to construct a typical "y=mx+b" cal curve for the M calorimeter, and I applied it to the M4 run. I observed the excess heat peak, but I also noted it was in a baseline shifted section of the run. Apparently the transfer function approach somehow removed baseline shifts! I then played with the cal constants a bit, and of course everything shifted around a little as expected, but given the lack of cooperation I really couldn't make any claims based on this. The Storms case was significantly better in that regard.

The upshot is that McK's data can be shown to have similar problems using similar methods, and without the full info on his method, I can't decide if his signal is real or not. I suspect though it's not, since even transfer functions have coefficients (which are the cal constants).

" I notice this is isoperibolic and therefore a prime candidate for CCS? Presumably it cannot have the nice qualities that an absolute method such as mass flow calorimetry with very well insulated closed cell systems and 99% efficiency as noted by Mallove et al. I'm wondering what are the LENR results done with such equipment?"

Doesn't matter what they type of calorimetry is. If the cell design concentrates het losses in one area, a 'lumped parameter' approach to the calibration is susceptible to the CCS.

"Jed: Mallove et al quoted 99% efficient (that is total losses <1%0 mass flow calorimetry as ome reason why CCS(H) is not relevant. Do you have from your 1000s of papers results using such a system? That would be the simplest way to argue that at least in some setups CCS(H) does not apply, if we have absolute excess power beyond the absolute accuracy."

Storms' calorimeter was 98% efficient. McK's M series calorimeter was also, maybe even 99%. Being 99% efficient does NOT exclude the possibility of a CCS. It may make the maximum possible signal smaller than in less efficient calorimeters.

Quote from JedRothwell

Perhaps you misunderstand. As Fleischmann said, heat is the principal signature of the reaction. If there is no heat, then the cold fusion reaction did not occur

Fleischmann was not a nuclear scientist and he never identified the reaction, so to claim that the principal signature is heat is mere conjecture. The fact is, and I think this is quite undisputed, that nuclear measurements can be up to a trillion times more sensitive than crude calorimetry. So it is a fallacy to claim that "the cold fusion reaction didn't occur" merely because you weren't using the appropriate instruments.

Quote from kirkshanahan

Storms' calorimeter was 98% efficient. McK's M series calorimeter was also, maybe even 99%. Being 99% efficient does NOT exclude the possibility of a CCS. It may make the maximum possible signal smaller than in less efficient calorimeters.

Lack of detailed write-ups makes McKubre's work of less use for people who are not a priori convinced that this effect exists and is nuclear in origin. Jed would be well advised not to use it as his "this is so good you don't need other stuff" example. Especially when, without details, there is a possible CCS error mechanism.

However I don't understand this. If a calorimeter has efficiency of 99% then it means that without calibration at all it will be accurate to within 1% (subject to additional errors from flow and deltaT and imperfect mixing). Of those only imperfect mixing could carry a CCS like signature - since there is no calibration needed. And (subject to imperfect mixing being controlled) a signal >> 1% would be difficult to explain other than through excess heat.

Quote from THHuxleynew

However I don't understand this. If a calorimeter has efficiency of 99% then it means that without calibration at all it will be accurate to within 1% (subject to additional errors from flow and deltaT and imperfect mixing). Of those only imperfect mixing could carry a CCS like signature - since there is no calibration needed. And (subject to imperfect mixing being controlled) a signal >> 1% would be difficult to explain other than through excess heat.

Irregardless of the amount of heat lost, whether it is 1%, 10% or 99.999%, there is a steady state established. Doing no calibration effectively assumes a value for the calibration constant instead of measuring it. Now, if the heat distribution changes, and if that can affect the calibration equation, the original assumed calibration constant is no longer accurate. The only question in that case is "Is the change big enough to be notable?" In the CF case, excess heat is a "small difference between two large numbers" so the only way to answer the question is to examine it mathematically, and see if it gives an apparent excess heat signal that exceeds baseline fluctuation. In the Storms' case, baseline fluctuation was on the order of 50-80 mW. The peak excess heat signal was 780mW (~10sigma by normal terminology which uses baseline noise as the only important noise). The input power at that point was ~21W, so the excess was ~4%. But that was 'zeroed out' by a 2-3% change in calibration constant. There's no reason to believe that result can't be translated to any other calorimeter, even high efficiency ones.

In reality, my contribution to this field is to alert practitioners that things at less that 5% are very important. Most people just ignore that kind of thinking out of habit.

Quote from interested observer

I have read McKubre's paper.

I do not have any better answers than that paper. If you are not satisfied, I cannot help you.

Quote from interested observer

So there has been no progress in the field since 2009?

Not much. Most researchers are dead. There is no funding and there is tremendous opposition. It is remarkable that the research survived at all. As Hagelstein said:

"The advances in our understanding of nature resulting from science

generally might be seen as a much greater accomplishment in light of how imperfect humans sometimes are, especially in connection with science."

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

Quote from THHuxleynew

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.

Yes, I know that. In part, I am being ironic. But my larger point is what Martin Fleischmann said: "We are painfully conventional people." This is conventional science, grounded in 19th century physics such as thermodynamics. The opposition to it is irrational. It is not based on any facts, analysis or science. There is not a single valid paper showing errors these experiments. That is not hyperbole; it is a fact. There are only a handful of papers that even try to show errors.

If this were any field other than cold fusion, by 1990, every scientist on earth would have been convinced by Fritz Will, Storms and McKubre. There would no opposition.

Shanahan is making up unprecedented physics that depend on deus ex machina magic factors that pop into existence just when you need them to extinguish the excess heat, and that can never be observed, confirmed or falsified by normal science, such as by calibrations. This is the epitome of pseudoscience. It has all the hallmarks.

By any objective standard, the cold fusion researchers are mainstream, and the people opposed to the research are fanatical anti-science, anti-intellectual fruitcakes.

Frankly, if you disagree, you are deluded, or you are pretending to be impartial in a political fight between scientists and barbarians. Schwinger was right! "The replacement of impartial reviewing by censorship will be the death of science."

Quote from THHuxleynew

Lack of detailed write-ups makes McKubre's work . . .

Is that supposed to be joke? He has published hundreds of pages, available at LENR-CANR.org.

You also need to know electrochemistry before you start, as McKubre points out. Every mistake I know of in replicating was made in textbook electrochemistry, not in cold fusion per se. For example, in one famous experiment that the skeptics all point to, they mixed up the anode and the cathode. (They put the positive wire on the Pd, and the negative on the Pt.)

Quote from THHuxleynew

Especially when, without details, there is a possible CCS error mechanism.

That mechanism does not exist. It is impossible. It is a figment of Shanahan's imagination. If it did exist, it would be obvious to the researchers and it would show up in calibrations and null runs.

You need to look at actual science, not fruitcake science. Look at his preposterous assertions about recombination in heat after death. Look at the list of reasons I posted showing why that is wrong, such as the fact that there is no oxygen in the cell during heat after death. Do you not see the point of that? Morrison made the very same claims, and Fleischmann corrected them. Have you even read that? You should have seen this years ago.

If you do not see that Shanahan is wrong about heat after death, then frankly you are a hopeless case, incapable of understanding even the simplest aspects of this -- such as the fact that you cannot have combustion with hydrogen only and no oxygen. The point is, Shanahan is not only flat out wrong about this, he is equally wrong about all of his other claims as well.

Quote from THHuxleynew

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. [that moving heat sources in cells produces spurious excess heat] It is always difficult to prove a negative - especially for something that would be noticed only as second order changes in apparent heat balance.

Oh come now. That's easy to test. Researchers usually end up testing that whether they plan to or not. It is inherent in the equipment. Many cells have three sources of heat:

1. The anode-cathode combination.

2. A joule heater for calibration.

2. The recombiner in the head space.

They have to be in different places. 1 and 2 cannot fit in the same spot, and 3 has to be in the head space. So they produce point-source heat in different parts of the cell.

The power is switched from 1 to 2. 3 will vary in output depending on the power level of electrolysis. In other words, heat flows within the cell will vary, and the point of origin of the heat will vary. But this never, ever causes spurious excess heat. It never causes a spurious endothermic reaction either. The latter is yet another thing Shanahan ignores. All of his hypotheses should produce a deficit as often as a surplus, but no one has ever reported a deficit.

This never causes spurious heat or cold for many reasons. You can see most of the reasons looking at the calorimeter. With most calorimeters, the heat is measured outside the cell, usually some distance away, as with a Seebeck. There is air between the walls of the Seebeck calorimeter and the cell, and the air inside the chamber is stirred with a fan. How could a changing point source of heat in the cell affect what happens several centimeters away at the walls? That would be magic. In other cells, multiple sensors are attached to a copper sheet which envelopes the cell. The copper would conduct a point source of heat everywhere, to all sensors. And indeed, the sensors all agree to within 0.01 deg C. Even when you calibrate with #2, a joule heater only, turning off 1 and 3, you get exactly the same response as with the same combined power from 1, 2 and 3.

In principle, Shanahan's hypothesis might apply to cell with the sensors in the electrolyte, inside the cell. However it never happens even with that configuration, because the fluid is well mixed by electrolysis, and often with a magnetic stirrer. And because researchers use an array of censors about 1 cm long, which gets a sample from different parts of the electrolyte.

Finally, as I said, if it did happen, it would happen as readily with a calibration as a test run, and as readily with Pt and light water as it does with Pd and heavy water. It would as readily be negative (endothermic) as positive. NONE of these things are observed.

Quote

why does anybody continue to think this is a real phenomenon at all

If you take a look at the impressive pile of Jed's Rothwell's links, it must be immediately evident for everyone, that this effect is real and everyone who is doubting is is ignorant crackpot instead. The controversy is rather in very diversified nature of LENR effects, which defies its description with single theory (this aspect many new physics phenomena have in common, being of extradimensional nature). Picture bellow illustrates the thermonuclear sparks at the surface of palladium mesh during codeposition of palladium and deuterium. How such an effect could be faked?

Quote from AlainCo

One good start is Beaudette book : Excess Heat

http://www.amazon.com/Excess-H…h-Prevailed/dp/0967854830

Hmmm . . . We brought out a Kindle edition of this. I do not understand why it is not linked to this edition.

See:

https://www.amazon.com/Excess-…/dp/B06VTH3TTF/ref=sr_1_1

Quote from THHuxleynew

Lack of detailed write-ups makes McKubre's work of less use for people who are not a priori convinced that this effect exists and is nuclear in origin.

See TR-107843-V1 for detailed descriptions of some of SRI's calorimetry and helium measurement work under McKubre's direction, c. 1998 (there is also a TR-107843-V2, looking at nuclear signatures, which I haven't read; both PDFs can be downloaded for free, without providing any information). In the TR-107843-V1 studies they use mass flow calorimetry. According to the report, the calorimetric results were not as impressive as were seen in earlier work. But the report gives a sense of the methodology and cross checks that were used by McKubre et al.

Quote from Alan Smith

That reminds me of a song...

Nice song, but about 3 minutes too long.

Quote from Eric Walker

See TR-107843-V1 for detailed descriptions of some of SRI's calorimetry and helium measurement work under McKubre's direction, c. 1998 (there is also a TR-107843-V2, looking at nuclear signatures, which I haven't read; both PDFs can be downloaded for free, without providing any information). In the TR-107843-V1 studies they use mass flow calorimetry. According to the report, the calorimetric results were not as impressive as were seen in earlier work. But the report gives a sense of the methodology and cross checks that were used by McKubre et al.

That is very helpful Eric, thank you. These electrolytic systems are fascinating, and deliver much interesting data. I'm impressed by the detail in these reports - though without doing a very careful analysis i can't yet say whether they have all the information I need. I need to drill down because at the moment there is a gap between the summary conclusions (claiming what would normally be indisputable excess power fractions) and the detailed data. My plan, unless anyone has a better suggestion, is to take the isoperibolic data summarised in Jed's paper:

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

Look at the source material (which I hope will be in the report) and check carefully Jed's and Kirk's comments about the plausibility of errors in this specific experiment. I find it is unhelpful to anything other than to concentrate on just one experiment, because they are all different, and we need a complete analysis to understand the ways in which these results are (or are not) irrefutable as Jed suggests. Or, perhaps a better way to look at it is, what are the aspects of these results, if any, that have the capacity to generate errors comparable in magnitude to the results.

I realise that others (for example perhaps Kirk, or Jed) will have done this with more resources than me: but sometimes the process of doing something for oneself can be enlightening.

Some points:

• I'm not motivated to do this with the F&P data which seems to me to have too many uncontrolled variables.
• I'm not clear that these isoperibolic results are the best that can be found from McKubre's data. Clearly he wanted to highlight them - but that may be because of the large magnitude of the calculated excess. I'm looking for something different - a calculated excess which is significantly larger than the various possible error mechanisms. I'm going to do my best to include CCS(H) in this analysis ab initio - not assuming that it does or does not apply. So before I do this here, does anyone think my choice of these experiments, rather than the mass flow ones, is good? The mass flow series would be more difficult to critique in terms of calibration errors, but also show smaller magnitude of results, so it sort of balances out.

I take it as read that Jed's statements here include a certain amount of hyperbole (sorry Jed) but nevertheless I defer to his knowledge of the literature so whatever he says is most convincing I'll be happy to look at - with the exception of F&P which I've previously spent some time with, and found various issues that could not be resolved because of the paucity of published data.

Before I hear "he is a pseudoskeptic" alarm bells ringing. I would lilke transparency and clarity in these headline statements "there is no evidence", "there is irrefutable evidence". My current expectation - only that - is that none of the well-conducted experiments - McKubre's would appear to be that - are likely alone to show irrefutable evidence. Mainly because if they did more people would be interested in replication of them. The question would then be whether one is convinced by "weight of evidence" as Zephir indicates. This is more philosophical than anything else. Personally I can't quantify the effect of selection and systematic error in these data, and therefore aggregating many non-irrefutable pieces of evidence does not help me. Looking at it the other way round: were these electrolytic systems, for example, to indicate clear signs of excess heat you would expect that in a long sequence of experiments such as McKubre's that there would be some irrefutable results.

So: bottom line; should I go for the experiments summarised in the paper above, or some different series?

Quote from AlainCo

of course He4/Heat correlation is best evidence, because errors on so different subject cannot correlate, especially accros different experiment at similar ratio...

http://www.currentscience.ac.in/Volumes/108/04/0574.pdf

I'm looking forward eagerly to the new work being done on He4/XS heat correlations. It should be interesting. I disagree with you about correlation being impossible however for the following rather subtle reason:

(1) in all these experiments those that do not generate He can be removed from consideration as no LENR - after all LENR is a variable effect

(2) in all of these experiments He values too high can be noted as leaky apparatus and again removed from consideration, with apparatus repaired.

(3) measuring lab He, and taking this as a bound, is problematic because in lab conditions He levels can vary greatly with time and space. There are ways round this, e.g. a nearly airtight jacket with stirring and He levels measured inside. But they require a lot of care and extra work, as far as I know few of these experiments do that.

These two selection mechanisms can in principle make random error correlations obey the expected ratio quite well. To get round this, you need to have a clear non-selective protocol and not amalgamate results with others from less clear protocols. I'd expect the new experiments to deal with this problem.