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305) Science or Proto-science ?
Ludwik Kowalski; 7/28/2006
Department of Mathematical Sciences
Montclair State University, Upper Montclair, NJ, 07043
Results from interesting experiments were recently described in Physical Review Letters (PRL 96, 034301, January, 2006). The paper, Nuclear
Emissions During Self-Nucleated Acoustic Cavitation; was published by R. P. Taleyarkhan et al. The six authors, affiliated with four institutions,
observed nuclear particles emitted from a small jar with a liquid. They believe that what was observed was ordinary hot fusion; the main argument for
this was emission of 2.45 MeV neutrons, gamma rays and generation of tritium. The neutron emission rate is reported as between 5000 and 7000 per second.
That is indeed much more than in the normal background due to cosmic rays.
The fact that hot fusion can be induced in a small jar, as opposed to a large tokamac, is indeed remarkable. But the jar was not an electrolytic cell,
the authors do not claim that what they studied was cold fusion. They think that stellar temperatures are created in tiny cavitational bubbles
containing deuterons. The test cell -- height ~15 cm and diameter ~8 cm -- contained carefully selected mixtures of liquid, such as deuterated benzene
or deuterated acetone. A standing ultrasonic wave (maximum amplitude of 15 bars) was established in the jar by using a lead-zirconate-titanate
piezoelectric driver ring. A small amount of natural uranium nitrate was dissolved in the liquid to induce generation of desirable bubbles. Nuclear
products were observed in liquids containing deuterium but not in liquids containing common hydrogen.
Here is how this was described in the paper: Results of control experiments with a C6
6O-UN mixture indicated  that there was no statistically significant net change in counts between cavitation on
and off. In contrast, the results of experiments with a deuterated C6D6-C
2Cl4-C3D6O-UN mixture produced a
significant increase (400%) in neutron counts and 100% increase of ray counts as seen in Fig. 2 and in Table I. [UN stands for the uranium nitrate.]
Based on the calibrated detector efficiency, the neutron emission rate was estimated to be 50007000 per second. Experiments
with H2O and D2O liquids, containing UN, showed no sign of unexpected nuclear activity
under otherwise identical conditions.
Similar conclusion was reached by using the CR-39 detectors. One year ago, while working on the Oriani effect, I did place CR-39 detectors close to a
Pu-Be neutron source. And I saw smaller tracks due to recoiling protons and occasional two to three times larger tracks, probably due to alpha particles
from the (n,a) reactions in the CR-39. I also noticed that the number of tracks increased with etching time. My interpretation of
this effect was simple, most latent tracks due neutrons do not begin at the surface, as latent tracks due to external alpha particles. The longer one
etches, up to a limit, the more latent tracks are exposed to the etching fluid. That should rule out a possibility that tracks are due to a surface
contamination, for example, from fingers that were in contact with a liquid containing uranium nitrate.
Implosion of tiny spherical bubbles are accompanied by emission of intense pulses light; for that reason the phenomenon has been named sono-luminnecsence
(SL). How reproducible are SL experiments? That question was answered in another publication of Taleyarkhan et al. --
Supplement (E-PRLTAO-96-019605) to Nuclear Emissions During Self Nucleated Acoustic Cavitation). They wrote: "
Nuclear emissions with cavitation for a deuterated liquid can vary significantly and it is not uncommon to get null results on a given day if the test
cell produced non-spherical and comet-like bubble clusters. The precise reasons behind the absence of recorded nuclear emissions is unknown at present
but, as mentioned before, it appears to be closely tied with the behavior of the bubble clusters themselves. Spherical cluster implosions tend to result
in nuclear emissions, whereas, non-spherical clusters (especially those tending to comet-like shapes) do not. Nevertheless, nuclear emissions were never
noted for control experiments (i.e., with non-deuterated liquids) and also for experiments with water. For unsuccessful campaigns on any given day the test
cell operation would result in comet-like bubble streamer formations which would tend to persist despite operation for several hours. This required
dismantling of the test reactor to seal leakage pathways, and to filter the test liquid for impurities, or, for persistent problems it was necessary to
use a new batch of freshly-drawn test liquids.
That is another similarity between the SL and CMNS; the first similarity being generation of nuclear reactions in a small jar. The issue of reproducibility
in CMNS has often been addressed by Ed. Storms. He thinks that the so-called Nuclear Active Environment (NAE) has not yet been identified. Here
is how this was expressed a message Storms posted at the CMNS list (7/23/06). It was a reply to a message asking which CMNS is the most reproducible.
Ed. Storms wrote:
As I have been harping on for sometime, the method is not as important as being able to form the NAE on the cathode surface.
All of the methods have produced heat on occasion. X1 has claimed co-deposition is completely reproducible, but I have not found this to be true. X2
claims use of a PdB alloy is very reproducible, but this alloy is not available. x3 claims palladium Type A is reproducible, but this is not
available and its characteristics are unknown. X4 claims his method is very reproducible, but it has not been described in enough detail to be
duplicated. X5 claims Ti is very reproducible, but I have not found this to be true. He also claims placing Ti in the electrolyte improves the behavior
of Pd, which I have not found to be true. I have found methods to form a NAE that work on occasion, but then fail to work for unknown reasons. In other
words, Scott, you are asking the wrong question. The proper question is, how can the NAE be formed with reproducible results? The answer is, we do no
yet know. Whatever you try will suffer the random consequences as experienced by everyone else. If any of us know the solution to this problem, we would
be running successful experiments, making demonstrations, and getting rich.
Ludwik Kowalski wrote:
In my opinion, a field of research that does not offer a single truly reproducible demonstration cannot be called scientific. That is why think that the
CMNS, and SL are examples of proto-science. My immediate reply to the above was In other words, CMNS should be replaced by CMNP, where P stands for
proto-science. Right or wrong? Then I added: Here is the excerpt from:
Proto-science is a word with two meanings. It may mean an unscientific field of study which later becomes a science (e.g.,
astrology becoming astronomy and alchemy becoming chemistry). Or, it may mean a field of study which appears to conform to the scientific method but is
either not falsifiable, or if it is, its predictions and principles have not yet been accepted as science or verified by a consensus of scientists.
By my own definition: an experimental field is proto-scientific when scientific methodology of validation is applied but reproducible experiments are
not available. I believe that a single reproducible-on-demand demo will turn CMNS into science. That is what Michel Jullian and Scott Little are asking
for. Right? And here is an excerpt about pseuo-science, from
What is pseudo-scince? Pseudoscience is a term applied to a body of knowledge, methodology, or practice that
diverges from the usual standards required for scientific work, or which is unsupported by sufficient, substantial or verifiable scientific evidence and
research . . . . The standards for determining whether a body of alleged knowledge, methodology, field, belief, or practice
is truly scientific can vary from field to field, but involve agreed-on principles including reproducibility and intersubjective verifiability. . . .
Scott Little wrote:
At this point, we would be delighted to simply have the cold fusion "experience". With one good, solid excess
heat experiment under our belt, it would change the whole landscape for us. We've been monitoring the cold fusion field every since its inception.
I had my first cold fusion experiment running within an month of the original F&P announcement. I attended the first cold fusion conference
held in Santa Fe NM and met Ed Storms there for the first time. Over the years, we've constructed a dozen different calorimeter systems for cold
fusion research. We've tried a variety of experiment including many of the newsworthy cold fusion ideas that have surfaced, like the Patterson beads,
the Case experiment, Stringham's sonofusion, Mizuno, etc. Proof is too much to
ask for right now. We just want to observe the excess heat effect.
Ed Storms wrote:
I want to make sure no one thinks I believe Szpak, Dash, etc. are untruthful and I'm amazed Swartz would come to this conclusion.
What I said was that I have not been able to duplicate the claims. This problem is universal in the field and is an accepted part of the experience
without hinting that someone did something wrong. We simply do not know enough to replicate the claims. . . .
Steven Krivit wrote:
We could eliminate many arguments and unfortunate misunderstandings within this community and external to this community if we can agree to,
and rigorously apply the distinction between REPEATABLE and REPRODUCIBLE.
REPEATABLE: Researcher A can obtain the expected result from his or her experiment every time he or she makes an attempt.
REPRODUCIBLE: Researcher B can obtain the same result from his or her replication of researcher A's experiment.
Ludwik Kowalski wrote:
To be useful an experiment must be reproducible; repeatability would not turn CMNS proto-science into science. A simple experiment cannot remain
repeatable-but-not-reproducible for a long time, unless secrecy is involved. Sooner or later A will teach B how to be successful, or B will convince A that
something is wrong. An author publishing experimental results tells others "do what I did and you will get similar results." Is this not the
main purpose of publishing?
My suggestion for Scott is to replicate excess heat in a Dash-type cell. It was demonstrated by John's students at ICCF10 and everyone could repeat the
experiment. Do you still believe that results are reproducible, John? Would you be willing to supply Scott with the recipe, or send him a ready-to-test
cell? Scott's MOAC seems to be ideal for measuring excess heat from your kind of cell. If I had such cell I would bring it to Texas and assist Scott -- to
be sure that all is done properly. The entire CMNS community would be interested in our result. John's cell was similar to that used by F&P. Therefore,
ruling out a prosaic effect would be much easier than in Mizuno-type cell, as emphasized by Ed. I am recommending this because Dash-type instrument was
the only low-voltage cell that I that saw delivering excess heat.
Ed Storms wrote:
[Ludwik wrote:] In other words, CMNS should be replaced by CMNP, where P stands for proto-science. Right or
The problem is one of ignorance. We do not yet know enough to make the effect work every time. This has nothing to do with science. Science is the
method by which ignorance is overcome. We are using science to gradually learn what it takes to solve this problem. Someone someday will discover what
the NAE looks like and will apply a layer of it to an inert metal substrate, and suddenly huge amounts of heat will be produced and the issue of
reproducibly will disappear.
John Dash wrote:
Ed, Thanks for trying to reproduce our results. Possible reasons why you were not successful may be caused by differences in the details of our
protocol vs. yours. In addition, We work at sea level and you work far above sea level. Does that make any difference?
In order to reply correctly, I need to have the recipe which you used in your attempt to reproduce our results. I need to know every detail from the
beginning to the end of the experiment ( vendor of the cathode and anode materials and recombination catalyst and and the chemicals used to make the
electrolyte, including lot numbers and chemical analyses, thickness or diameter of the anode and cathode materials; also include composition of the cell
body and pH of the electrolyte). I need to know the initial condition of the cathode (cold rolled, including %reduction in thickness, annealed, including
temperature, time, and environment, etc.), temperature of the electrolyte at steady state, data from an experiment, and your analysis of the data. Was
there any deformation of the cathode during the experiment ? Was there any difference in the surface composition of the cathode after electrolysis
compared with the composition before electrolysis ? Please send me these details of your attempts to reproduce our results.
Ed. Storms wrote:
Dear John, Here is a summary of what I did to replicate the use of Ti to initiate CF using Pd and D2SO4. An electrolyte of 3 ml
D2SO4(concentrated) and 30 ml D2O was used. Titanium was used as the cathode and Pt as the anode. This was electrolyzed in a closed cell using the
Seebeck calorimeter as follows:
0.048A for 178 min
At the end of this treatment the Ti had lost about 3 mg and had turned black. The electrolyte had turned yellow. No excess energy was observed
during this time.
A palladium cathode was put in the cell. This was made by rolling a piece of palladium to a thickness of 0.082 mm and cleaning with acetone. No
further treatment was used. This was electrolyzed as follows:
0.047 A for 89 min
No excess energy was observed within Ī10 mW of zero. The sample surface was examined using the SEM and was found to contain no Ti. The absence of Ti
is consistent with Ti not plating from such a solution, as expected. If some aspect of this procedure is not right to make it work, please let me
know and I will try again - once I finish the book.
Akito Takahashi wrote:
[Mitch] Thank you for teaching your model. Maybe we need to read your papers which are not available in downloadable e-data, on lenr.canr site and your
sites. Where are downloadable ones available? One primitive comment back: We know that the biding energy (strong interaction) of deuteron is 2.22 MeV
against the breaking-up to neutron plus proton. How is the so high energy excited state as 21 MeV of deuteron possible?
Ed. Storms wrote:
It has come to my attention that a comment I made about being unable to replicate the claims if Szpak and Dash has been misrepresented.
I want it clearly known that my failure to make these replications in no way means that I believe Szpak or Dash are dishonest or in any way misrepresented
their work. I believe these gentleman are honest and are examples of the highest integrity in the profession. Failure to replicate claims is common in
this field and in no way indicates a lack of honesty or skill.
John Dash wrote:
Dear Ed, Thanks for the fast response. My comments are:
1. We use H2SO4, not D2SO4, in the electrolyte.
2. We also use a Seebeck calorimeter, and we detect excess heat from cells with Ti cathodes and also from cells using Pd cathodes.
3. The currents given are not meaningful. We need to know the current density.
4. Our Ti cathodes never turned black, nor did the electrolyte turn yellow.
4. We need to know the % reduction in thickness of the Pd.
5. I don't understand why you did not find Ti on a Ti cathode after electrolysis.
So, there are many differences in our experiments, compared with your attempts to replicate. When you finish your book, I will be pleased to work
with you in another attempt at replication.
Ed and John recognized that the disagreement resulted from not performing the same experiment. They decided to work together to either confirm or refute
reality of excess heat in John's setup. Is this not a good way of solving the controversy? What else should be done when mistakes are made in such
Let me return to protoscience. The concept of NAE -- nuclear active environment -- invented by Ed Storms (and by others, under different names?) -- is
very peculiar. Does it belong to theories or does it belong to experiments? Theories (models of reality) are invented to explain facts. Facts are discovered
via experiments activities. NAE is an unknown form of matter, it is something to be discovered in the future, perhaps a new nano structure or a new catalyst.
Things that may possibly be discovered in the future should not be counted as experimental facts.
Does it mean that the concept of NAE belongs to the realm of physical science theories? I do not think so. Theoretical predictions are made either on the
basis of deduction or on the basis of induction. Neither of these are part of NAE, as far as I know. Existence of NAE is based on faith in results of the
not-yet-reproducible experiments. Such experiments, performed by recognized experts, are too numerous to be dismissed. Should this kind of attitude be
called a physical science theory? I do not think so. NAE is not such theory. In my opinion it is an empty name, a placeholder for something that remains
to be discovered.
Unlike in mathematics, a theory in a physical science is validated by showing that it agrees with valid experimental findings, that it has predictive
ability, and that it is experimentally falsifiable. The NAE “theory” does not refer to particular findings, it does not have predictive abilities, and it
is not falsifiable. The only prediction of the NAE “theory” is that some experimental results will become reproducible, sooner or later. And what about
being falsifiable; how can the only NAE prediction shown to be wrong? Suppose that results remain irreproducible for another century. That would certainly
not be a proof that the "theory" is wrong. Next suppose that a claim, for example, excess heat accompanied by accumulation of 4He, becomes verifiable on
demand. That would possibly validate NAE. But that is not what is needed now, if one wants to elevate NAE to the level of a scientific theory. I cannot
think of an experiment capable to falsify validity of the only NAE prediction.
I see nothing wrong with believing in NAE; but importance of this attitude should not be overemphasized. Our rules of validation are not different from
those used by mainstream scientists. Like all of them, we know that being patient is a virtue. We should emphasize what our protoscience has in common
with science, not what makes it unique. Overemphasizing NAE can hurt our reputation.
In principle, CMNS can remain protoscience for another century or longer. But in practice it will not survive without injection of new resources (young
scientists and some financial support). It might disappear in ten or twenty years and reappear naturally much later. In that respect CMNS is not different
from other protosciences.
Jim Giles discusses reproducibility in the most recent issue of Nature (July 27, 2006). But that is about science, not protoscience. Here is his
opening statement: The idea that readers should be able to replicate published scientific results is seen as the bedrock
of modern science. But what if replication proves difficult or impossible? How should editors of leading journals, and referees,
deal with undesirable consequences of irreproducibility? That was followed by an explanation of why failures to replicate are unavoidable,
even in physical sciences. Several suggestions for dealing with this problem are made by the author. Unfortunately, due to discrimination,
CMNS publications are deprived the scrutiny of the refereed journals.
Edmund Storms wrote:
The NAE is neither a theory nor an experiment, but the recognition that for the CF reactions to occur, a novel structure
is required. This fact has been supported by every attempt to produce CF. This same concept is applied to many phenomenon, such as superconductivity.
For a material to be a superconductor, a special structure is required. This idea says nothing about what that structure must be. The idea is
important in discussing the phenomenon because without this concept, many theories have been applied to the normal structure of PdD. Naturally t
hese theories have no value because the normal PdD structure can not support nuclear reactions, as the skeptics are quick to point out. The concept
forces people to look at special structures to find an environment that can support CF.
Ludwik Kowalski (not posted):
If NAE is neither a theory nor an experiment then what is it? In our present situation it seems to be a substitution for a recognized theory. How can
a recognized theory emerge when not a single CMNS demo is reproducible on demand? Most researchers are aware that what they know is always a small
fraction of what can possibly be known. That is part of general philosophy. It goes together with believes that laws of nature exist, that physical
science theories are idealized models of reality, and that models should be validated by empirical evidence.
In my opinion NAE is a substitution for a recognized theory. The role of theories in science and technology is essential. We want to understand
nature; collecting unrelated empirical facts is not sufficient. Several CMNS theories have been suggested but, as far as I know, none of them was
declared to be a winner. So when someone asks for an explanation of a particular CMNS effect; we say it is due to a hidden effect (HE), such as NAE
that must be discovered. Our protoscience will become science what its HE, such as NAE, new chemistry, etc. is discovered.
In static electricity, for example, the HE was humidity. In humid air dielectric surfaces are often covered with thin conducing layers through which
discharging is much more rapid than it is when the layers are not present. Physics teachers are advised to keep electrostatic demonstration apparatus
in dry environments (hotboxes). In that way they can be sure of high reproducibility. Hot air from a blow-dryer is often used to remove undesirable
layers on dielectric surfaces.
On a list for physics teachers I posted this message: When was the the effect of humidity recognized as a factor influencing electrostatic
demonstrations? I suspect that Ben Franklin was already familiar with the effect of humidity. But I am not sure. Who was the first to write about
this? Here is a reply from one teacher: Probably Desaguliers [1683=> 1744]. However, Wm. Watson [1715=>1787],
... explained more clearly than Desaguliers had done, that atmospheric moisture destroyed electricity by conduction " I couldn't find the
reference, only the quote above. The leak derives primarily through surface conductivity promoted by the moisture, not from loss to the air,
a point not understood until the end of the 19th century. Ref: Conduction of Electricity through Gasses I", the Thomsons, Cambridge 1928.
Quoted: Electricity in the 17th and 18th Centuries, Heilbron, J. L. UC Press (1979)
Another teacher responded: I believe this [see above] quote is from: A Collection of the Electrical Expeririments Communicated
to the Royal Society by Wm. Watson, F. R. S. Read at Several Meetings between October 29. 1747. and Jan. 21. Following William Watson Philosophical
Transactions (1683-1775), Vol. 45. (1748), pp. 49-120.
Ed. Storms wrote (referring to Giles article in Nature):
This is a very interesting article, but it does not address the situation we face in the CF field. The CF or LENR phenomenon has
been replicated many times by laboratories all over the world. By the standards described in the article, CF should have been accepted years ago. The
problem we have is the difficulty in making the effect work every time and in a predictable way. This is entirely different from the problem of
replication. By continuing to describe the problem as being one of replication, we keep the skeptical attitude alive by using their vocabulary. We
should call the problem what it is, i.e. a difficulty in making the effect easy to produce.
Ludwik Kowalski (not posted):
How does the problem of replication differ from the difficulty in making the effect easy to produce? According to the
article, problems of replications result from the limited ability to describe experimental protocols in refereed journals. Our difficulty in making
the effect easy to produce, on the other hand, is due to not having the protocol. That is how I understand the last message of Ed (see above). I do
not share his opinion that avoiding the term replication, in favor of difficultiy, will help us. Replication -- the bedrock of science, is expected
from us and we should keep trying to deliver it. Nobody is asking at high precision at this stage.
The underlying assumption of science is that macroscopic phenomena are reproducible, under identical conditions. But conditions are never exactly the
same. That is why very precise replications are impossible. The best one can do to overcome precision limitations, in any laboratory, is to calculate
averages and to assume that they are close enough to true values. Limited precision did not interfere with scientific progress, or with technological
applications of science. The problem has to do with unpredictable, and large, fluctuations of accuracy, not precision. By the way, the term accuracy
usually refers to systematic errors while the term precision refers to random errors. I am imagining an instrument whose calibration constant is
significantly influenced by solar flares or by coincidences of other rare events. Using such instrument would be like trying to win in a game designed
to tease losers. Expecting reproducibility of CMNS effects would not be consistent with chaotic fluctuations of essential parameters.
Michel Jullian wrote:
Michael, if the difficulty of replication is too many unknown unknowns, which makes sense, couldn't the _complete_ original
working cell, or at least one replicated by researcher A himself, be lent to researcher B to save time?
Mike McKubre wrote (7/29/06):
That is how we usually begin; the original equipment set up and operated by the original experimenter(s). In this first Phase
we just provide technical and plumbing support. When the experiment is running to the satisfaction of the originator - and we believe we understand
what is being done - we invite the originator to leave operation to us. Even at this stage it is quite usual for us to seek further help. Only when
the experiment is running for us in the same way as for the originator do we allow ourselves to succumb to the siren urge to "improve".
In terms of unknown unknowns it is interesting that recent discussion in this thread has centered on Huggins and Mengoli. At the time of their
successes both of these men were at the top of their respective professions (material science and electrochemistry). They knew more than (I would
timidly suggest) anyone who attempted their replication - that is, fewer things were unknown to them. At least one of these things might have been
As an example look at Huggins repeat melting that Charles started us with, and the issue of lithium (and beating). Ed assumed in his attempt that
Huggins' repeat melting was to remove Li. This is not what I recall from my discussions with Bob at the time, but who knows? My point is that we
don't know what we don't know. This applies to the originator as well. So you must start with the same equipment, the same procedures in the same
hands. This is the beginning of replication.
Ed. Storms wrote:
What was your understanding, Mike, about what Huggins intended to do? My understanding was that the crucible was the only
piece if Pd Huggins had easily available. They arc melted it to get it into a form they could use and to purify it. Arc melting will remove any
volatile such as Li, C and O. He pounded the button onto a flat sheet because an arc melted button does no have much area and is hard to use, as
we discovered. At that time, I don't believe anyone knew what would work best. As you and others discovered, annealing is beneficial, but Huggins
did not do this.
As for replicating exactly what a person has done, I find that replicating exactly what I have done in the past does not always result in success.
Obviously variables are present about which we have no knowledge and over which we have no control. On the other hand, when I successfully
replicated the Letts laser experiment, I prepared my Pd in an entirely different way. It turns out that the nature of the Pd is not important.
What is important is the nature of the gold plate. It turns out gold can plate in many different ways depending on subtle conditions, most of which
Dennis did not control or even know about. Consequently, he and I were both lucky to make the effect work at all, something neither of us has been
able to do again. We are chasing ghosts until someone identifies the important variables and the important conditions that must be present.
Ludwik Kowalski (not posted):
The debate started in 1989 is going on. On what basis are the authors of these messages accused of being pseudo-scientists? They are addressing a
difficult problem. In my opinion their methods of validation are 100% scientific. They perform experiments, they discuss results and they develop
theories, like in other areas of physical science. But our scientific establishment is practicing an unfair discrimination against the CMNS field.
When will this end? Yes, it is not the first time that I am asking this question. Discrimination against honest and dedicated scientists is
Ludwik Kowalski (7/30/06 in a thread about systematic errors):
1) I agree with a possibility of that kind of error. One way to check the reliability of the sampling method would be to use a bomb calorimeter, as
suggested by Jed. Instead of a Mizuno-type cell (which is expected to produce excess heat) one could use a sparking current interrupter, as in an old
door bell, or in a Tesla coil. This setup is not expected to generate excess energy and electrical power is expected to be exactly the same as thermal
Suppose the heat capacity of the calorimeter is 1000 J/deg. Suppose the experiment lasted 300 s and the calorimeter temperature increased by 30 C.
Then we would know that thermal energy was 1000*30=30000 J, and that the mean thermal power was 30000/300=100 W. The sampling method, used at the same
time, should confirm this result. But suppose that the sampling method gives 50 W, instead of 100W, as speculated by Michel. That would show that he is
correct; the electric power obtained by sampling would be declared to be strongly underestimated (by the factor of two in this illustration). . . .
2)Scott's attempts to replicate Mizuno's GDPE results are significant in the context of this discussion. His COPs were consistently very close to 1.00.
That can be explained by saying that Scott's cells had no NAE in them. Are his results not indicative that the method of sampling is reliable for
Mizuno-type cell frequencies? Yes, I know that the COP=1.00 can be purely coincidental. For example, a little bit of NAE perfectly masked by a systematic
error in measuring electric energy. But i do not believe that this was the case.
Ed. Storms wrote:
May I suggest you all are beating a dead horse. Eliminating errors in measuring applied power is easy and can be solved three different
ways. The first, as observed by Ludwik, if some cells produce a COP of 1.0, this is a good indication that applied power is correct. Although not all
cells are identical, they won't be different in this regard if the same power supply and detection equipment are used. Second, if you sample using a low
rate, then use a high rate and see no difference, the values can be taken as correct. This can be checked at any time. Third, if calibration is made
using a dead cathode, the sampling errors will cancel out and be eliminated as an issue. With too much emphases on trivial issues, the real issues are
overlooked. The real question is, what does it take to form the NAE?
1) I like the idea of using dead cathodes in control experiments. But this does not apply in Mizuno-type experiments. In these experiments
cathodes are destroyed. Solid tungsten rods are turned into tiny metallic particles or compounds (?).
2) I do not think we are beating a dead horse. If submitted, the Colorado2 paper will be scrutinized in terms of possibilities of experimental errors,
not in terms something that might possibly be discovered later. We do not speculate about the mechanism by which excess heat is generated in a Mizuno-type
cell. We only argue that the COP>1 is not due to a systematic error, or to a well known effect. Even this seems to be more difficult than I expected.
3) May I suggest that the term Nuclear Active Environment be replaced by something more acceptable to mainstream scientists. Suppose we say that NAE stands
for New Active Environment or Not Anticipated Environment (or something like this but better -- please suggest better alternatives). Such replacement would
be needed for Mizuno-type cells; we have no evidence that their excess heat is due to a nuclear process. A paragraph about NAE (but without the
word nuclear) is worth adding at the end of our paper.
Ed. Storms wrote:
. . . .You [Ludwik] are playing into the attitude of the skeptics here. We need to stop doing this. Cold fusion is based on initiating
nuclear reactions. This fact can not be hidden. If the Mizuno cell does not make nuclear energy, then it is not cold fusion and it does not involve
the NAE. Why confuse the issue just to satisfy a few skeptics who will not be influenced no matter what you call the effect.
Ludwik Kowalski (7/31/06, not posted):
This website contains other cold fusion items.
Ed wrote: Cold fusion is based on initiating nuclear reactions. This fact can not be hidden. It is not a fact;
it is a statment what cold fusion is. The rest of the message is also not acceptable. The main point is that Mizuno does seem to produce excess enegy. But
we have no evidence that a nuclear process is involved. It can be something else very interesting. That is why the word nuclear is not
appropriate, at least at this time. And I do not believe that all skeptics are dishonest.
Several short messages about NAE were posted today (8/10/06) on the CMNS list. I think they are worth adding. The concept of NAE is interesting but
strange. Nobody knows what NAE is but the concept is used as if reality of NAE has already been established. When something unexplained is discovered
we know that it can be explained, sooner or later, in terms of something else. That something else is a cause of the event. In my opinion NAE (Nuclear
Active Environment) is nothing else but a synonym for the word cause. Believing that NAE exists is like believing that a cause exists for
an unexplained phenomenon.
The secret of NAE is -- probably -- in such studies:
What is the basis for such expectation? Is it because distances between ions become shorter? Is it because screening is expected to be much stronger?
My understanding is that NAE is a word invented in anticipation of something totally different from what is known.
I agree, the features of nanostructures and their subtle methods of formation would fit the experience of trying to make CF work. As for NAE, the
concept is only used to describe a general condition, both known and unknown. This is used just like the word "tree" is used as a general
concept, which is applied to many different items of the same general type.
I think that Les Case's method- was the most promising CMNS achievement- in a form very adequate for a real energy technology, but it was not studied
and developed with sufficient forces and ideas. It was poisoned and forgotten. Nanotechnology is the key- but this is only a slogan
today. CMNS is a special form of catalysis- I bet, therefore this paper is valuable.
I worked very hard trying to duplicate the Case method. I understand even Case can not replicate what he had done. Formation of the naoometer-sized
particles on carbon is the problem. This was done using the conventional methods for making chemical catalysts. We need methods to achieve the same
end, but without the many variables associated with the catalytic method. Some day money and interest will be available to allow a marriage between
CF and the many methods now being developed to apply small particles. The child of such a marriage will save the world.
Well Peter, I have identified 9 possible candidates for the NAE. With sufficient money, these possibilities could be easily explored and the real NAE
identified. The tools and knowledge are available. All that is lacking is the will and the money.
Ludwik Kowalski (referring to Ed.s first message above):
"Tree" is probably not the best analogy for the "NAE." What about the "EOL" (Elixer of Life). It also was a word reserved
for something to be discovered much later. I am thinking about antibiotics and other effective drugs. Ancients believed that such substance will be
found, sooner or later.
I agree, EOL is a better analogy. However, we already know a NAE exists. We just don't know what it looks like.
The ideal solution would be a palladiumless NAE, made from cheap and abundant materials, delivering "high currency" energy -- hot steam and
not warm water.
Jean Paul Biberian:
NAE is very similar to catalysis where people talk about "active sites". After years and years of research with many scientists and lot of money
we still don't know exactly what it is. We know how to manufacture catalysts that work, but without knowing precisely how they work.
Cold fusion is very similar to catalysis, in both cases thermodynamics is favorable, the only obstacle is the energy barrier. The only difference
is the many orders of magnitude larger barrier height for cold fusion. In catalysis as well as in Cold Fusion we don't know if the active site
is localized or de-localized? What is the role of impurities? What kills the catalyst? I am pretty sure that soon enough we'll discover ways to
have a reliable device, however, the understanding of the phenomenon might take lot longer.
By the way, Arata's system: a mixture of nano-particles of palladium embedded in zirconium oxide seems promising and reproducible. SRI has
duplicated the experiment years ago with the double cathode system. His new design with gas loading alone is even more convincing.
Do you think that we still do not have sufficient experimental and theoretical data in order to develop a strategy for trying to discover the secret
of NAE? If yes, what is actually missing?
I think EOL is a "metaphor too far" NAE describes the new function -- triggering nuclear reactions via a special electronic environment.
Simple logic says this is possible only via neutral entities- not by forcing nuclei through the Coulomb Barrier but this is the job of theorists. I
am convinced that (excuse me for using the old name of our field): "Hot Fusion is force brute, while Cold Fusion is a very smart nuclear
ju-jitsu" It seems tooooo smart!
I fully agree with you. I worked on catalysts for ten years and I can tell you that the basic principles on how a catalyst works are perfectly well
known. What is still a kind of an art is : how can you design a multifunction catalytic system (for instance find an hydrogenation catalyst
that can at the same time withdraw nitrogen compounds while standing unaffected in the presence of sulfur (I worked 4 year on that kind of system!).
The only problem is that these systems involve too many parameters to be correctly modelized and trial and error experiments are needed. Moreover
the detailed reaction paths of certain systems would be too long to be studied scientifically and an empiric approach is more efficient
from an industrial point of view.I also worked during my carrier in ore separation by flottation and the situation is exactly the
same.In both domains the relevant phenomena underlying the industrial realisation are perfectly known and understood.
Ludwik, I suggest a new acronym for NAE. I propose NYUP for Not Yet Uncovered Phenomenon. As long as this new phenomenon is not indentified
and scientifically studied, all the rest is just mondaine discussion (not to use the term bla-bla !). Trying to persuade people, that making so
call CF work, is only a question of money and number of people working in the field, is not far from being borderline to intellectual
I find this debate about what to call the environment in which CF occurs a distraction from the important idea. It makes no difference what
the environment is called. The only idea of importance is the recognition that such a special environment exists. This idea is in contrast
to the original thought of F&P that the entire palladium cathode was involved, being limited only by the amount of deuterium present.
The word does not imply any thing about the environment, either known or unknown. It does not imply that the effect occurs on the surface or
in the bulk. It does not imply that the mechanism involves resonance or magic. You are free to say that the NAE is unknown, unexplored,
unknowable and anything you like. The word only allows a person to speak about a concept, just like the word "tree" allows a person
to speak about a concept without saying anything about the kind of tree. As for my suggestion that more money and people are needed to solve
the problem, I ask Jacques what he thinks is needed that would not be dishonest?
Jacques Dufour (8/13/06):
The name is very important and not distraction. When you say NAE (standing, as I understand for Nuclear Active Environment), you say, with no possible
discussion, contradiction, confrontation, that the phenomenon is nuclear. As far as I am concerned, the certitudes I have are :
1/ there is something in the field and the main phenomenon is thermal (anomalous enthalpy of reaction in certain systems metal/hydrides)
2/ some very weak nuclear signatures are observed (tritium, neutrons, helium4)
but they don't explain the bulk of the phenomenon
Hence, the strategy for me is to present an experiment that a physicist will accept (small, with minimum matter, using the more robust equipment you
can imagine, eliminating all energy storage problems, measurement problems and so on). In short a really irrefutable experiments (by the way, this
was suggested by some reviwer of the DOE survey). At that stage a potential industrial application is of no interrest .It is better to have
Pout/Pin=110% with an irrefutable experiment and a few mg of matter, than Pout/pin = 130% with hundred watts, that a physicist can easily prove
doubtfull. A working hypothesis can also be presented, with the objective of being confronted to experiments and to all theoretical knowledge available
to day (I am speaking of theoretical knowledge of the main stream physicists, not of those who completely mis-interpret something as basic as the
Then I came to intellectual dishonesty. My reaction was triggered by what Jean-Paul [Biberian] wrote about catalysis. Having worked for some 15 years
in the field (see my answer to Ludwik), I can tell you that the basic principles are fully understood. Trying to establish a parallel between what
is presented as an empirical art only i.e catalysis (which is far from being the case) and the need for money an manpower to generate NAE based on a
very controversial interpretation of what I think is a real phenomenon, is not only really exagerated but also very likely to be counterproductive,
in terms of getting this new phenomenon accepted and its research financed (which I hope is our common goal).
So, sorry Ed, but I think it very important to name NYUP [not yet uncovered phenomenon] what we are studying, even if the phenomenon occurs as you
think (and I think you are right) not in the bulk but in special sites. And we have to fight on the ground of anomalous enthalpies of reaction and
not on the ground of very hypothetical nuclear reactions.
I hope we can discuss all that soon and pardon me to have use the term dishonesty (but we clearly have to challenge each other in this community and
accept all contradictions : otherwise we shall be worse than what we criticize in the main scientific community ...)
Jacques DUFOUR wrote: “The name is very important and not distraction. When you say NAE . . . but they don't explain the bulk of the phenomenon” Here
we have a difference of opinion. My opinion is based on my complete study of the literature and the arguments I have made in the past and will make in
greater detail in my book. Consequently, I'm looking for a NAE. If you are looking for something else, then you will have to call it something else and
justify the name as I have done with the NAE.
[He also wrote] “Hence, the strategy for me is . . . as the Mossbauer effect).” I agree this is needed. However, from my reading of the literature such
experiments have been done as well as they can be done using the tools presently available. Nevertheless, I wish you success.
[He also wrote] “Then I came to intellectual dishonesty. . . . our common goal)” Please do not confuse your personal opinion about what is happening
with universal reality. I agree, you are seeing a real behavior. The issue is whether it has any relationship to what other people are seeing, which
is called cold fusion. Please try to avoid making your experience apply to every other observation. You may be observing an entirely different effect.
[He also wrote] “So, sorry Ed, but I think . . . hypothetical nuclear reactions.“ This conclusion would only be true if nuclear reactions were not
occurring. However, a huge collection of evidence shows that they are. They may not be occurring in your work, but they do occur in other studies. My
definition applies only to conditions where they do occur. You are free to define your studies however you see fit.
[He also wrote] “I hope we can discuss all . . . the main scientific community ...)” No problem. However, we all need to make a clear distinction
between dishonesty and a difference of opinion.
My recollection is that only Mizuno reported on presence of transmutation products in GDPE cells. Is this correct? How large would the energy/atom be if
the excess energy he measured were due to transmutations he reported? My guess is that it would exceed millions of MeV/atom. Note that that 23 MeV/atom
was reported for the F&P-type cells. Unfortunately, I do not have information on the number of atoms produced while excess energy was measured by Mizuno*.
I think that N -- in NAE -- is not yet justified, as far as Mizuno-type cells are concerned. Why don't we hear from Mizuno? Is he OK? I know that he was
scheduled for an important operation after the ICCF12. Did someone communicate with him this year? I am worrying.
*below 0.00001 MeV/reaction --> chemical
up to 200 MeV/reaction --> known nuclear
above 200 MeV/ reaction --> totally unknown
Biberian writes, "By the way, Arata's system . . . “ : I call Arata and Zhang's ZrO2 + nano-palladium powder an "oxide-coated nano-metal composite".
The NAE in this process would seem to be either the nano-metal Pd crystals or the interface layers between ZrO2 crystal and the Pd metal.
A-Z have shown that oxide-coated ZrO2, nano-Pd composites absorb hydrogen so as to create the remarkably hydrogen rich hydride PdH3, using what appears
to be equilibrium chemistry at 100 bar. Their 2002 electrolysis test run produced ~ 10 W of excess heat continuously for over 20 days using a few
grams of Pd. This technology seems to solve the damaging problem of nano-crystal growth, which occurs when metal nano-crystals make contact with each
other. The A-Z ICCF12 paper suggests cold fusion heat production at 200 deg C without electrolysis.
Scott Little (8/16/06):
Is it possible to formulate the hypothesis for cold fusion as a falsifiable one? The concept of falsifiable hypotheses was emphasized by Karl Popper
who claimed that unless a hypothesis was falsifiable, it was not a scientific hypothesis. Not everyone shares his viewpoint (see Criticism section
in this article)
but, as an experimentalist, I find it rather attractive. The simple hypothesis I have been assuming for cold fusion goes something like this:
"Nuclear reactions can occur in an electrolysis cell." Clearly this hypothesis is not falsifiable. Only an infinite number of null experiments
will falsify it. Can anyone formulate the cold fusion hypothesis so that it is falsifiable?
It is important to emphasize that the concept of falsifiability was develop for theories. The corresponding concept for experimental data is
reproducibility. [A hypothesis is often the first step toward a theory. The statement formulated by Scott would become falsifiable if conditions
under which a specific nuclear reaction, such as production of alpaha particles, were said to take place under specified conditions in a clearly
described kind of cell. But ths is possible only when experiments are reproducible.]
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