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301) Colorado2 results must be revised
Ludwik Kowalski; 6/29/2006
Department of Mathematical Sciences
Montclair State University, Upper Montclair, NJ, 07043
As described in unit #300, I have been involved, for about one year, in an experiment, named Colorado2. It was similar to several glow
discharge plasma electrolysis (GDPE) experiments performed by other investigators in several countries (see references in unit #300). The purpose
was to convince myself, and others, that Mizuno-type excess heat is not an illusion due to experimental errors, or to some well known effects.
The conclusion we reached was that some unexplained source of energy was responsible for the excess heat measured. The draft of the manuscript
was nearly ready to be shared over the Internet when one interpretational error was discovered. Unit #300 shows my draft; as it was about two
weeks ago. The purpose of this unit is to follow new disturbing developments. I will assume that the reader is familiar with concepts and
terminology introduced in unit #300; this unit is a continuation of what was written there.
A question about invisible droplets of electrolyte escaping from cell has been raised but not answered in unit #300. Two experiments were
performed to answer that question, one based on titration of the electrolyte remaining in the cell, after an experiment, and another based on
the examination of the wet steam escaping from the boiling electrolyte. The result of the first approach is not clear to me; I hope it will
become clear after Appendix 2 is received. But the second approach is more simple. It was nothing more than a determination of exact masses
of four samples. The first three samples, at least one gram each, contained drops of steam condensed on a cold surface, the fourth sample was the
The method was introduced to us by Scott Little; here is his own description of it:
". . . I conducted a simple dissolved-solids test on the samples you [R.S.] sent. First I weighed 4 Al weighing cups. Then I
dispensed some of each sample into each cups. I used a new disposable pipette for each sample to prevent contamination. Then I
weighed the wet cups. Then I gently dried the samples in a 70C oven for 4 hours This gentle drying should leave the salt as
K2CO3+1.5H2O. I recorded the first set of
dry weights. Then I returned the samples to the 70C oven for another 8 hours. I recorded a 2nd set of dry weights.
Scotts net masses, for the first three samples turned out to be: 2.06, 1.15 and 1.84 mg, per cubic centimeter of the condensed liquid.
The mean and standard deviations are 1.68 and 0.47, respectively. For the sample #4 (the original electrolyte) the mass of the solid deposit
was 27.4 mg per cc. What does this mean? Under ideal conditions (no electrolyte escaping with the steam) the net solid masses, from the first
three samples would be zero. But the
measured mass, 1.68, was 6.1% of 27.4. That means that the amount of the electrolyte, in the escaping liquid, was about 6%. The mean COP,
determined when three samples were collected, was 1.15. But that was calculated by assuming that the escaping liquid is pure water. In other
words, our mass m, and Pv were overestimated by 6%. This leads a sizable correction, close to 0.05, in the value of COP. The correction would
be 0.06 is the Pc were zero. More specifically, the mean COP=1.15 becomes 1.10. That is too close to unity, considering the standard deviation
If this preliminary observation of Scott is confirmed then experimental COPs, reported in unit #300, are certainly exaggerated. A simple
reduction of the reported results by 0.05 would not be appropriate because percentages of the electrolyte in the escaping liquid were not
measured. Conditions under which experiments were performed to collect three samples were not the same as conditions under which the bulk of
Colorado2 data were collected. We are certainly not ready to write a paper that would be difficult to reject.
What is surprising is that researchers who performed similar experiments before us never mentioned, or tested, as far as one can say, a
possibility of a systematic error in m due to the escaping electrolyte. They all fell into the same trap as we. How can this be explained?
Appended on July 5, 2006
1) I am disturbed and disappointed. The following questions were asked, on June 29, at our CMNS list: Is Mizuno a member of this list? Is he
aware of new development, Jed? [I know that Jed, who if fluent in Japanese, if a friend of Mizuno] If not you should inform him by phone. Naudin and Iorio
are also on this list. I expected all three of them to be busy performing Little-type tests at this time. Four days later, I wrote that absence of
messages from them is very disturbing. Two more days passed and we do not hear from them. How can this be explained. How can authors of influential papers
remain silent after learning about Littles results? Having the necessary hardware I would simply condense the escaping liquid and measure the
percentage of the escaping electrolyte under two kinds of conditions: (a) boiling due to the ohmic heater and (b) boiling due to the current flowing through
the electrolyte. Perhaps nearly pure steam comes out in the first (usual) case and steam mixed with electrolyte comes in the second (not very usual) case.
That would be much easier to do than measuring the COP.
2) It is only a matter of time before the mystery of tiny droplets is solved. I know, from private messages, that the Little-type test
is now being conducted in Boulder by Richard Slaughter. Similar tests are planned during the upcoming Paris3 experiment, probably in a month or two. But
what about the second main issue? Would I be able to say, referring to the appendix, that known chemical reactions cannot possibly be responsible for
the main part of excess heat? The first draft of the appendix, written by Jean Francois Fauvarque, did not allow me to say so. But some progress in that
direction was made yesterday. It came after I posted the following problem on the restricted list for CMNS researchers.
A cell contains one liter of the 0.2 M K2CO3 electrolyte. The cathode is tungsten and the anode is platinum. The temperature
is already 100 C. How much heat is generated when a constant potential of 30 V is applied for 100 seconds? Assume that a constant current of two amperes
is flowing through the cell. Part of the answer is obvious, the thermal energy is 30*2*100 + X = 6,000 + X joules, where X is the energy released
(positive or negative) via anticipated chemical reactions. What is the value of X?
Note that 30 V was chosen to avoid complications associated with the glow discharge plasma electrolysis (GDPE) that is ignited above 100 V. The outside
temperature of 100 C was chosen to make sure that the cell temperature remains constant. The idea was to establish the value of X in a simple situation
before trying to establish it for a much more complicated situation. Two Ph.D. chemists on the CMNS discussion list wrote that the dominant
reactions, are: decomposition
(electrolysis) of water and production of CO2 from the K2CO3. Not being a chemist I am happy to take this for granted.
3) I will return to this topic a little later below. My impression was that contributions of chemical reactions to excess heat from Fleischmann-type
cells have been discussed extensively in papers written by Fleischmann and Pons. Statements that chemical heat was negligible are easy to find but not in
F&P papers. The only one that I found today, after browsing through their papers (downloaded from the library at www.lenr-canr.org), is shown below.
The title of the paper was Calorimetry of the palladium-deuterium-heavy water system; it was published in J. Electroanal. Chem, 1990.
". . . The total specific energy output during the bursts as well as the total specific energy output of fully charged electrodes
subjected to prolonged polarization (5-50 MJ cm^3) is 100 - 1000 times larger than the enthalpy of reaction of chemical processes."
Two or three orders of magnitude is impressive. But specific energies are in J/cm^3. Did they divide the total excess heat by the total volume
of the cathode or by the volume of a thin layer at the surface of the cathode? The same question can be asked about chemical processes. Are these all
conceivable reactions in the cell or only reactions conceivable inside the cathode? It would certainly make no sense to compare MJ/cm
3 with MJ. Furthermore, the bursts to which the 1990 paper referred were of very short duration, as illustrated in
several figures. Did they produce less ambiguous statements in later publications? I do not know. My search for a better reference will continue; the
quote will be inserted here, if found.
4) It is well known that the electrolysis of water is an endothermic reaction. In other words it absorbs heat instead of releasing it. If the
current is 2A, as in my illustration above, then the contribution of the electrolysis is -295 J. The negative sign is used to indicate the endothermic
nature of the dominate reaction. And what about consumption of K2CO3, I asked. That reaction is also endothermic but the energy absorbed depends on
how much of the potassium carbonate is consumed. For each gram of consumed salt the contribution to X is -82 J. Let me assume, to be specific, that
only five grams of the K2CO3 is consumed. In that case the contribution of the two reactions to X becomes -295 - 5*82 = -705 J.
Yes, you might say, but what is the purpose of discussing a 30 V experiment when real experiments (Paris1 and Colorado2) were performed at 300 volts?
That is certainly a valid concern. My two chemists wanted me to be aware that a large number of unknown reactions become possible under the GDPE. One
of them wrote: what happens at the anode for high voltage electrolysis- is interesting and important. And in great part, new- a place for
discoveries. My 30 V illustration is an instrument for thinking; call it a gedanken-ing tool. I will use it to subdividing all possible reactions,
chemical and non-chemical, into two categories: (a) well known to chemists and (b) all others. I am aware that the term "well-known to chemists"
is not very precise. But this term must be defined if one wants to make a claim that "the excess heat we measured cannot possibly be attributed to
well known chemical reactions."
As indicated before, our Colorado2 report would not be worth publishing without a credible statement of that kind. Perhaps such statement will appear
in the new version of the appendix written by Fauvarque. For the time being I am defining well known reactions as those for which the excess heat
contribution (X in my illustration) can be estimated. Suppose that someone makes a claim that thermal energy released, during a 30 V experiment,
exceeds the electric energy supplied by 4000 J. How large is the unexplained excess heat? My answer would be 4000 + 705 = 4705 J.
The 705 J is the heat absorbed by the two well known reactions (for the current of 2 A and for 5 grams of K2CO3 consumed).
Note that 2A can be treated as a measured quantity. But 5 grams was only a guess. So what should the error bar be to account for the uncertainness
in the guess? The smallest possible amount of K2CO3 lost was zero grams. In that case the contribution of the second reaction to X would be zero and
the unexplained excess heat would be 4000 + 295 =4295 J. The other extreme (highly unlikely) would be that all the K2CO3 present, about 25 grams,
was consumed to produce the CO2. In that case the value of X would be -(295+5*410) = -2345 and the unexplained heat would be 6345 J. The well known
reactions underestimate excess heat because they are endothermic. Being able to say that excess heat is between 4295 and 6345 joules is due to
unknown processes, chemical or non-chemical, would be a great step forward. Note that even under the lower limit the rate of generating excess heat
would be close to 43 W.
What is wrong with that kind of speculation? It is based on my own definition of well known reactions. Other knowledgeable chemists might be able
to extend the range of well known reactions by calculating their contribution to X. In that case the value of X would have to be modified.
We cannot exclude a possibility of exothermic reactions under conditions of plasma electrolysis. Suppose that X turns out to be close to +4000 J. In that
case we would say that the entire excess heat is due to well known chemical reactions. My main point is that excess, as measured in Colorado2 experiments,
cannot be attributed to non-chemical reactions unless contributions of chemical reactions is ruled out by chemists.
A much more convincing approach would be to show that the amount of non-chemical byproducts is directly proportional the amount of excess heat generated.
No experimental evidence of that nature exists, as far as I know, for Mizuno-type experiments. Presence of products of nuclear reactions has been
discovered by Mizuno but the amounts were extremely low. Will these amounts be shown to be correlated with amounts of excess heat measured? That remains
to be seen.
5) I like coincidences. After composing the above I received this junk-mail message:
A Genuine University Degree in 4-6 weeks! Have you ever thought that the only thing stopping you from a great job and better pay was a few letters
behind you name? Well now you can get them! Well I am certain that my chemical consultants did not graduate from the Genuine University. Only highly
knowledgeable experts can estimate X from exotic chemical GDPE reactions.
Appended on July 7, 2006
Let me show extracts from some recent messages posted on the CMNS list. They show interactions among the CMNS investigators.
How do these interactions differ from those in other areas of physical sciences? Keep in mind, however, that this is a multi-discipline list;
backgrounds of contributors are very different.
Scott Little wrote:
. . . I agree that your scenario above does not violate the 1st Law and I distinctly recall challenging you that it was instead a violation of
the 2nd Law. My reasoning was that the heat absorbed from the environment was, in effect, "free air-conditioning" (very valuable
here in Texas) and that for a "price" of 1.23V*Q in input energy you were getting out of the cell 1.48*Q in output energy (in the
form of H2 and O2 "fuel" gas).
But now that I have the accepted the concept that dG is the maximum amount of work a reaction can perform, it is beginning to look like there
is no 2nd Law violation here at all....maybe. Can you suggest a reference that discusses these concepts, particularly thermoneutral potential,
electrolysis of water, etc. in detail? All my Pchem (e.g. Moore) and thermo (e.g. Sears, Sonntag) books just seem to graze the surface and don't
really discuss this very issue.
Mel Miles wrote (responding to a question about two electrolytes):
Fleischmann and Pons selected LiOD as their electrolyte to avoid the possibility of other cell reactions. If we assume that K2CO3 is oxidized to
form CO2 and O2 at the anode and that water is reduced to form H2 at the cathode, then the cell reaction becomes
2 H2O + K2CO3 = H2 + CO2 + 0.5 O2 + 2 KOH
At standard conditions, Delta H =+395311 J for this reaction. Thus . . .
If I had to start another Mizuno-type experiment I would use fresh electrolyte for each test. Then the amount of the K2CO3 reacted would be
measured for each test. Little-type test would be used on samples of the electrolyte. Suppose a sample of the electrolyte, extracted moments
before a test, shows that each cm3 contains 26 mg of the solid deposit (after 1 cm3
of water is evaporated). Suppose the sample extracted after the experiment has only 22 mg of deposit per cubic centimeter. Then one would probably
say that no more that 4 grams of the K2CO3 (from the total of 26 g initially added to one liter of distilled water) was consumed. The
"no more" is appropriate because one cannot exclude a possibility that some tungsten, lost by the cathode during a test, is also
present in the solid deposit. The amount of tungsten lost during a test would be measured by comparing the weight of the cathode before and after.
If I worked with a chemist I would insist on measuring the amount of tungsten in the solid deposit and in the electrolyte. A complete chemical
analysis of the sample would be preferable. But focusing on tungsten would be a big step forward. Knowing the result, a competent chemist would be
in a much better position to estimate X due to formation of CO2, and probably due to other chemical reactions. I guess that was the essence of
what Peter wrote two days ago.
And here is another suggestion, it was made by Pierre Clauzon, in a private message yesterday. Measure temperatures very accurately and do not
start collecting excess heat data before thermal equilibrium has been established in the cell. He was probably thinking about power differences.
Excess heat must be measured after thermal equilibrium is established inside the cell. The temperature must be constant and the rate of
evaporation must be constant. Fortunately, a fast electronic data acquisition system can be used to make sure that this precondition is met. That
is how data were collected during Texas1 experiments. Colorado1, and Colorado2 data were collected without using the fast data acquisition system.
But we usually waited several minutes before starting a new run. The rates of evaporation, from run to run fluctuated randomly. A systematic trend
would probably be noticed but that is far from being certain. Recent Paris2 measurements were made under the thermal equilibrium. The results were
more or less the same as in Paris1 and Colorado2 experiments. Is this correct, Pierre? As you can see, what I write is an extrapolation from what
you mentioned yesterday. I am sure that what we learned from previous experiments will be taken under consideration in future experiments, such
as Paris3 and Marseilles1.
Peter Gluck wrote:
This is not the essence of what I wrote 2 days and more days ago. The results of this experiment -- as described above cannot be interpreted
univoqually -- what's more (less) they are not interpretable:
a) because a part of water is evaporated the concentration of solid salts are increased and because a part of K2CO3 is decomposed, the
concentration of solid is increased. Which wins? Who knows? [actually, fresh water was added constantly to replace what
was evaporated in Paris1. In Colorado2 we did this periodically, to keep the total volume more or less constant.]
b) only CO2 is lost via decomposition/decarbonation, K remains in the solution or is lost via droplets entrainment and it is not possible to
distinguish between all these facts- how much of the residue is carbonate, how much is hydroxide;
c) tungsten gives heavy, bulky, granular precipitate that is absolutely non-uniformly distributed in the reaction vessel. It stays at the bottom.
You will not find a representative quantity of W in one cubic cm of sample extracted aleatory from the solution.
What I am trying to tell is that the material balance has to be performed for the integral quantities of all the participants: water, K, CO2,
W- before and after the test.
Thanks for good suggestions, Peter. The bottom line is that a well equipped analytical chemist must be part of a better team of researchers. Let
me make another suggestion for Paris3 and Marseilles1 experiments. It is based on what Pierre and Richard wrote to me in private messages.
Ideally one wants to operate under thermal equilibrium, that is when the dm/dt (rate of evaporation) remain constant. The way to accomplish this,
in an open beaker during the electrolysis, is to use two power supplies, one feeding the electrolysis and another feeding the ohmic heater,
immersed in the electrolyte. I am assuming one can measure the electric energy delivered to the cell by each power supply. One would have to add
these energies to calculate the COP.
Suppose the mean dm/dt is evaluated every 3 seconds and the values are plotted versus time when an experiment is in progress. To keep the dm/dt
constant one simply changes the voltage feeding the ohmic heater. If the dm/dt starts going up the voltage is decreased; if the dm/dt starts
going down the voltage is increased. I think that keeping the dm/dt constant, within 2 or 3% would not be too difficult.
The temperature-versus-time plot could be useful below the boiling point. Stirring of the electrolyte is probably worth having in all cases. I
thing that the last container in Colorado2 was too big for the power of 300-400 W, especially without stirring. One can probably work without
stirring, at such wattages, when the beaker is much smaller, for example, one liter. Under such conditions boiling is sufficiently uniform to get
a constant temperature within the cell.
Peter Gluck wrote:
All I want is to contribute to the success of this important experiment and I don't like to be kind of negativist critic. But you wrote:
"Ideally one wants to operate under thermal equilibrium..." I think this is both useless and impossible:
- useless - CF/CMNS is created by dynamic dis- or non-equilibrium conditions; and it is not good to sacrifice the intensity of the process
for the sake of the precision of the measurement (unfortunately this happens in many CF/CMNS experiments!!! and this is what I call, unpolitely
enough, metrologomania- focus on measurement instead of intensification.)
- impossible due to the huge inherent temperature gradient- 3000 degrees Celsius in the plasma and maximum 100 degrees Celsius in the water, the
released gases-hydrogen, oxygen, carbon dioxide at some unknown intermediary temperatures It is such a mess that you need a bunch of angels in
order to make some equilibrium. There is no symmetry in this cells, with our without stirring. The unique way to kind of equilibrium -- dynamic
is a flow-through cell a la Philip KANAREV but this is an other way; let's keep us in our limits.
REMARK+ - an shortcut, absolutely independent from our troubles with droplets is the examination is the separation and careful examination of
the W based residue -- what the devil is it? And the suggestion of our colleague HENRI LEHN has to be treated with priority -- it shows
immediately if some nuclear phenomena takes place in the system. [Henri's suggestion was to perform isotopic analysis if
iron presumably produced from another element during the electrolysis. That would certainly be an interesting experiment. But our goal was
to accomplish something much less spectacular.]
Our goal in Colorado2 was to either to confirm or to refute Paris1 results. And we confirmed them. We showed that by performing a similar
experiment one gets similar results, more or less. That was important. But now we are addressing a different issue. How do we know that the
excess heat measured was not an illusion due to a prosaic effect, such as well known chemical reactions? That issue has not been answered
satisfactory. Will it be answered in the new version of the appendix to our anticipated paper? I hope so. If not then we must wait for results
from better-designed experiments. Colorado3, Paris3 and Marseilles1 experiments will probably be designed
to show that excess heat is not an illusion. Those who are planning these experiments are probably paying attention to various suggestions made
on this list. Are Colorado2 results publishable? I tend to be more and more pessimistc about this. But suppose Little-type tests, or titration
tests, or some other test based on a setup similar to that used in Paris1 and Colorado2 show that the percentage of droplets of the electrolyte
in the liquid was about 10%. That would be the answer to our question. It would mean that the probability of an illusion due to a prosaic
effect is very high. We would have to rewrite the paper and publish it.
Michel Jullian wrote:
Peter I think on the contrary that Pierre's idea of operating the cell at constant thermal power, ensuring a more constant temperature
distribution, is excellent. It will not hamper short term plasma instabilities in the least, and it will make sure that no thermal capacitance
effects will interfere. Such effects can be responsible for illusion of non-unity COPs, don't you agree?
The scheme will also automatically maintain the vapor barrier I proposed to prevent ingress of possible atmospheric fuels such as N2 (forgotten
in recent discussions it seems): stopping the discharge e.g. to replace the eroded cathode will make the ohmic heater step in automatically.
Here are some nitrogen and oxygen based compounds which could form in a GDPE cell, together with their formation enthalpies [the units are
kJ per mole of the product.]. Some of the formation enthalpies are negative, which tells us that the corresponding compound's formation from
N2(g) and O2(g) from air (null formation enthalpies) dissolving into the solution and being processed in the plasma would be exothermic.
NO3 -(aq) -205
As I said many times before, it would be presumptuous for anybody to state that no chemical reaction involving gases from air (including common
impurities such as ethanol, benzene, silicones etc...) can be responsible for the excess heat in a GDPE cell and it's plasma furnace. Hence my
idea to block atmospheric ingress by maintaining a vapor barrier (less dangerous than a lid).
Peter Gluck wrote:
. . . N2 is in some air solved in water at the start. But ingress of air from outside is not possible- it has to go counterstream to the gases
released from the cell.
Mitch Swartz wrote:
First, carbonates cannot be removed from the experiments unless the experiment is not exposed to the atmosphere. They enter the water as CO2
in hours no matter how many times the water has been distilled. Second, including for reasons of which we spoke briefly, it might be more important
to determine your input electrical power with some accuracy and precision, by careful measurement of V and I, faster than the Nyquist threshold,
before focusing on the chemistry at this point. Once you obtain excess energy of sufficient magnitude, then optimizing the chemistry could then
be done on an active working system.
1) Is it not true that the concentration of the CO2, entering the LiOH electrolyte, could be estimated by a chemist? I also expect reaction rates
to be estimable. That would allow to anticipate chemical contributions to excess heat. My expectation was that this was done and that estimated
contributions were found to be orders of magnitude below what was actually measured. But I am no longer certain that this was the case. Please
provide references in which impossibility of chemical contributions to excess heat was convincingly ruled by either Fleischmann or Mizuno.
2) Do not assume that everyone on this list knows what the "Nyquist threshold" is. My recollection is that in order to overcome this
threshold the sampling rate should be several times higher than the highest frequency of the signal. As I wrote in unit #300 (at my CF website) the
frequency of sampling does not have to be very high, when fluctuations are random. The only thing that counts is a sufficiently large total number
of samples. One thousand would probably produce sufficiently reliable mean values of V and I. Do you agree with this, Mitch?
Mitch Swartz wrote:
We sample applied voltage, and the voltage across both the cell and the control, and the electrical current, between 100 Hz and a lower limit of,
at least, 1 Hertz, for at least 70,000 samples per day, with most runs lasting several days. For some experiments involving specialized studies
the sampling rate is much higher.
1) That seems to be perfect when fluctuations of V and I are random. By the way, imposing some randomness on the sampling frequency would extend
the reliability of electric measurements to situations in which fluctuations of I and V are not random. I believe that the expensive instrument
used by Scott Little, in Texas1 experiments, had the built in randomness of sampling. He will probably correct me if I am wrong.
2) What is the overall situation with excess heat from Mizuno-type experiments? The claim is clear -- excess heat is believed to be due to something
unknown. That claim is being challenged on this list. It appears that not sufficient amount of information is available to exclude prosaic effects.
The number of prosaic effects is large. In principle one should deal with them one after another. That can take a long time. Showing that one or
two trivial sources of excess heat are impossible does not guarantee that another trivial source is not going to be suggested by a skeptic. But
even a single acceptable evidence against the claim is sufficient to negate it.
Suppose that Little-type tests are independently performed in several laboratories. Presumably, the outcome of each tests gives the percentage of
the electrolyte in the steam escaping from the open cell. Knowing that percentage one can calculate a correction for the COP measured. Suppose
that corrected COPs turn out to be close to 1.0, in several laboratories. That would definitely negate the initial claim. The only way to rescue
the claim would be to show that experimental or logical errors were made in evaluations of COP corrections. In other words, we are in a situation
in which confirmation of a claim is much more difficult than showing the the claim is not valid. Justifying our positive (extraordinary origin of
excess heat) is much more difficult than justifying our negative (prosaic origin of excess heat).
That reminds me of two kinds of reasoning: inductive (from more specific to more general) and deductive (from more general to more specific).
Conclusions drawn on the basis of inductive reasoning are often questionable. Observing 1000 white swans, and concluding that all swans are white,
would be an example of inductive reasoning. Deductive reasoning, like in mathematics, is said to be more convincing; its reliability depends only
on the reliability of the already accepted propositions, and on the absence of derivational mistakes.
Sorry for a philosophical digression. What we are after is not philosophy. We want to find the answer to a simple question, can Mizuno-type excess
heat, as measured in Colorado2 experiments, be explained by a prosaic effect? At least one such effect has been identified on the CMNS list -- escaping
of the electrolyte during electrolysis. Is it reasonable to assume that the COP=1.24 we reported was a mistake resulting from not taking that effect
under consideration? The question will probably be answered in coming weeks.
Appended on 12/17/06
In preparing myself for another exciting electrochemical experiment I found this brief description of chromium electroplating:
Electroplating involves immersing the metal parts to be plated in a bath of chromium trioxide (CrO3),
typically prepared by dissolving crystalline CrO3 in a mix of distilled water and sulfuric acid. A direct current is passed through
the solution, and the resulting reaction leaves a deposit of chromium on the piece being plated. One problem in this process is the production of
hydrogen and oxygen at the electrodes. The gas bubbles to the surface, creating a mist of the plating solution (which contains hexavalent chromium)
that must be controlled. Additionally, mechanical agitation of the bath (used to improve plating quality) can also result in the release of this
hazardous mist. . . The fact that bubble of gas remove chemicals dissolved in the electrolyte is probably known to chemists. In the
same way bubbles of steam remove some liquid electrolyte creating wet mist in air. Why were Mizonos and Naudins results not explained by
chemists familiar with wet mist?
I suspect that several CF researchers were aware of the possible explanation and decided to stay away from the Mizuno type effect. I would not do this;
I would criticize conclusions based on erroneous assumptions. If Favaurque was aware of the trivial explanation of the apparent excess heat
then why didnt he address the issue in the paper presented at ICCF12? The CNAM team was going to conduct tests similar to those of Scott Little.
I suppose that this was done several months ago, considering the simplicity of the task. Do they still believe that the claim of Mizuno-type excess
heat was real? I do not know; no one wrote to me about the outcome of investigations. What would I do if after presenting a paper at an international
conference I later found that the claim was wrong? I would certainly try to correct the conclusion and explained why I no longer believe in it. That
is why I am puzzled by the absence of messages. The appendix professor Fauvarque promised will probably not materialize. Something is not right. What
a waste of time and money it was! But I did enjoy the adventure. We did our best but the paper cannot be submitted without valid chemical arguments
supporting the claim of excess heat.
Appended on 2/12/07
Pierre Clauzon sent me the description of their new reproducible results from a better experiment; Perhaps this will be presented at the
CCF13 (Sochi, Russia). Here is my reply: . Hi Pierre, I am glad you continue
working and this topic. Did you convince Fauvarque to address the issue of chemical origin of excess heat? You paper would be more convincing if it
contained a section devoted to possible chemical reactions and the amount of heat they generate. Is it less than 1% of what you measure? Is it less
than 10%? Is it only 50%? Such numbers, justified by an electrochemist, are essential at this stage of research. I would be very interested to read
I WILL WRITE MORE ABOUT THIS WHEN ADDITIONAL TESTS ARE PERFORMED.
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