On Tue, Feb 22, 2011 at 3:04 PM, Abd ul-Rahman Lomax
<a...@lomaxdesign.com>wrote:
> At 04:31 PM 2/21/2011, Joshua Cude wrote:
>
> You are arguing with a straw man, Joshua.
>
You're call yourself a straw man?
It's obvious that "many scientists" do not "accept" cold fusion. So people
> write to explain it. That's somehow unusual or suspicious?
>
No. It's usual and expected. You said they weren't, though; that CF had
passed that stage. I was just trying to demonstrate that it hadn't. And now
you agree.
>
> The reviews do not outnumber the primary research publications. If we look
> at recent publications, they are anomalously high, that's true, but the
> reviews are covering a vast body of literature, not just peer-reviewed work,
> they cover, as well, conference papers. I don't have a count for the primary
> papers, but mainstream peer-reviewed publication for the period of the 19
> reviews is about 50 papers, using the Britz database.
>
>
I counted 23 last time I looked a few months back. So yea, reviews don't
outnumber them, but 5 were negative and 9 theoretical. That leaves 9 papers
with new positive experimental data, less than half the number of reviews.
(I excluded hydrino papers, and the Sourcebook papers, since the Sourcebook
is not a legitimately peer-reviewed journal. Maybe that's the difference.)
But even 19 reviews and 50 papers signals a dying field.
>
> 1/3 is plenty for correlation studies. You, and others like you, have
> invented an non-existent standard that scientific research should meet. If
> there is a drug that will cure a disease one-third of the time, there will
> be great excitement! You are now stating the low end of reproduction
> (without specific reference) and neglecting the high end. I don't have much
> data on the Energetics Techologies primary work, but it was replicated by
> McKubre and ENEA, reported in the American Chemical Society Low Energy
> Nuclear Reactions Sourcebook, 2008.
>
Even within the Energetics work, reproducibility is abysmal. The summary of
their results from 2008 I think claims 80%, but when you look at the
results, no two experiments give the same answer. Only in CF is an
experiment considered reproducible when it gives the same sign of a result.
> 23 cells were run and reported by McKubre. Excess power as a percentage of
> input power was given. They only gave specific excess power results if they
> reacjed 5% of input power, though their calorimetry has, I think,
> substantially better resolution than that. Of the 23 cells, 14 showed excess
> power at or above 5%. Two were at 5%, two were above 100% (200% and 300%),
> and the rest were intermediate.
>
>
That's what I'm talkin about.
> I look at Table 1 in this paper and wish that it had simply presented the
> actual results, instead of filtering it and summarizing part. I'd want, for
> every cell, the actual measured or estimated "excess energy." The chart
> presents excess power, but filters out *most* data below 5% of input power
> (presumably steady state input power at the times of the appearance of
> excess power). Filtering out the low end disallows understanding how the
> phenomenon operates under marginal conditions.
>
> Preaching to the choir.
>
>
>
> Indeed, your whole thesis here has been that there is a solid scientific
> consensus, in place for twenty years, that cold fusion is bogus. Now comes a
> review that clearly backs off from that, as to some substantial fraction of
> experts, and you manage to reframe it as "all more of the same since 1989."
>
>
Actually, it's how the summary of the review itself framed it.
>
> And do you realize that Pons and Fleischmann, per Fleischmann's account
> published something like 2003, was expecting to find nothing? Do you know
> what he was researching?
>
> Hint: it wasn't a technique for generating energy. He was doing pure
> science, attempting to falisfy a theory that he thought was correct, but
> that he also thought was incomplete. Indeed, it was necessarily incomplete,
> because it was an approximation.
>
>
I'm not sure how that bears on any of this, but that's not what he said to
Macneil Lehrer in 1989:
"It is this enormous compression of the species in the lattice [which he
earlier said was 10^27 atmospheres] which made us think that it might be
feasible to create conditions for fusion in such a simple reactor."
>
> I would assume that you'd have solid theoretical grounds for that
> assumption, some theory that is well-established, with excellent predictive
> power, that would be overturned if the experimental results are valid. Okay,
> what is that theory? How does it predict the results of cold fusion
> experiments. Please be specific!
>
> That seems backward to me. I'm not interested in developing a theory for
why something doesn't work. If the results collectively showed evidence of
something new going on, then it would be worth trying to understand them,
but in my judgement, they don't.
The fact remains, progress, experimental or theoretical, has been
>> completely consistent with pathological science. None to speak of.
>>
>
> You have now denied facts that you are aware of. That does not bode well.
> Replication percentage has improved. New techniques are known and are being
> tested. The necessary conditions for the F-P effect are far better known.
> Helium was identified as the ash and demonstrated conclusively.
Replication percentage was claimed to be high in the mid-nineties, the
necessary conditions for FP cells were spelled out in the early 90s, helium
was "identified" as the ash in 91, and if you claim later unpublished work
was better, even that was 11 years ago. So, even if these are considered
progress, it seems to have stopped more than a decade ago.
But the reported excess power has gotten smaller. The table published by
Storms in his Science of LENR book shows the excess power for dozens of
experiments, and in the 90s there are 4 years where it exceeds 100W, and up
to 1 kW in one experiment. Since 2000, there are none, and only 2 years
where it exceeds 12 W. It doesn't go beyond 2005, but I'm not aware of any
higher power results than the Dardik 2004 results since then (Rossi
notwithstanding). Within Dardik's own results, the excess power has
decreased over time.
New techniques have been developed over the years (gas-loading, glow
discharge, sonic, superwave, standing on head while reading the meter), but
even those were mostly tried in the 90s (superwave is newer). And
the results are not better, and more importantly, some are in conflict with
the electrolysis results. For example, electrolysis established the need for
a loading ratio of 0.9 or so, whereas gas-loading doesn't come anywhere near
that, and yet reactions happen anyway. D-Pd experiments used H-1 as a
control, but H-Ni experiments claim LENR without deuterium. These would seem
to be contradictions, and therefore the opposite of progress.
This sort of scattershot approach with no consistent picture emerging is
consistent with the absence of a effect, and screams pathos.
>
>>
>> If the helium-heat correlation is so significant, why is there so little
>> work on it.
>>
>
> Because the work that has been done is conclusive. Helium is still being
> measured, work continues, because helium has become the corroborating
> confirmation of excess heat.
>
>
Conclusive? Have you ever followed any other scientific field. Scientists
are obsessive about nailing down the details, reducing error. In relativity,
they are still doing experiments to test time-dilation, and have observed it
in clocks moving as slow as 10 m/s. That's something like a part in 10^15.
They wear results like these as a badge of honor.
And what about heat-helium? Well you've got Miles from the early 90s, in
crude experiments in which peaks are eyeballed as small, medium, and large,
the small taken as equal to the detection limit (which seemed to change by
orders of magnitude over the years). Even in the best of Miles results, the
energy per helium varies by more than a factor of 3.
Miles results were severely criticized by Jones in peer-reviewed literature.
And although there was considerable back and forth on the results, and in
Storms view (of course) Miles successfully defended his claims, that kind of
disagreement and large variation simply cries out for new and better
experiments. So what have we got since?
The only results that Storms has deemed worthwhile to calculate energy come
from conference proceedings, and the most recent of them from year 2000.
Nothing that Storms considers adequate quality in this critically important
experimen has met the standard of peer review. And they're not good enough
that Miles results can be ignored; Storms still uses some of Miles results,
one assumes because it improves the average. The error in the result, even
if you accept Storms' cherry-picked, dubious analysis is still 20%. On an
experiment that removes the dependence on material quality. Heat, it is
claimed, can be measured to mW, the helium, it is claimed, is orders of
magnitude above the detection limit, and yet the errors are huge.
This is what passes for conclusive in the field of cold fusion. This is good
enough that no measurements of helium-heat in the last decade entered
Storms' calculations.
>
> And why is the work that has been reported, (since Miles 1993 work) not
>> been published in peer-reviewed journals?
>>
>
> Aoki (1994), Miles (1994, two papers),
I'll give you these. They don't change the point though. Change my date to
1994.
> Miles (2000),
I wonder why you don't list the journal. Because there isn't one. I presume
this is the Trans Am Nucl Soc which "publishes summaries of all papers
presented at the ANS Annual and Winter Meetings, which are reviewed by the
National Program Committee and ANS Division representatives." Not a
peer-reviewed journal.
> Arata (1997, 1999),
Arata published some helium results, but they did not make the cut into
Storms' calculations of energy per atom.
> Gozzi (1998),
Gozzi concludes that the helium results are too weak to be definitive. And
oddly, after this paper he got out of the field. Coincidence?
> De Ninno (2008, ACS Sourcebook),
ACS Sourcebook is a volume of cold fusion papers edited by cold fusion
advocates. They're gonna reject cold fusion papers? Next?
McKubre (2000)
>
Storms lists 3: 2 are from the 8th ICCF conference, one from Trans Am Nucl
Soc, also conf proc.
>
> Helium is the only nuclear reaction product from fusion that is present in
>> the background at levels *above* that required to explain the heat. Is it a
>> coincidence that it is also the only one that is found to be correlated to
>> the heat.
>>
>
> No, that's a gross oversimplification.
So you say, but you don't contradict it. You go back to the correlation with
heat. But the fact remains that the only ash that is observed at
commensurate levels is the one that is in the background. Funny how all
those usual products of nuclear reactions that can be detected and
identified at ridiculously low levels are absent.
> The possibility of coincidence was analyzed by Miles. He found that, with
> his experimental series, the probability of chance correlation was
> 1:750,000. Care to challenge that?
That dubious calculation is based on unsupportable assumptions that errors
would cause a 50/50 chance of excess heat and or excess He, and that the
artifacts that might produce the errors are uncorrelated. And anyway, the
opposite of random errors is not fusion.
> Remember, Miles has been confirmed, by much more accurate measurements of
> helium, by McKubre. And there are many other confirmations of heat/helium.
>
Again, very few that Storms considers "quality", and none of those in
peer-reviewed journals.
>
> Given that the experiments are working close to detection limits for
>> helium, a little cognitive bias could explain the correlation.
>>
>
> That is simply not true, again. They are not working close to detection
> limits, what made you think that?
In the Miles results, they use the detection limit (crudely guessed and
adjusted as needed) to estimate the level of helium. Some of the data points
("small peaks") are taken to be at the detection limit. Medium and large
peaks are taken as 1 and 2 orders of magnitude above. Who does this? They
seemed to improve this in later experiments, but that's the origin of my
comment.
> And you are now asserting "cognitive bias," neglecting that the Miles work
> was blind. Miles was using a lab which did not know which cells showed
> excess heat and which did not.
But still, things got adjusted after the fact, and Jones offers reasons why
artifacts might be correlated. But you're right, I really don't want to get
into analyzing the details of 20-year old experiments. (I'm too far into it
already.) The simple reality is that in any other field, results you have
admitted are crude, wouldn't enter the picture 20 years later. There would
be new and better *publications* to use.
>
> The idea that work with helium is not going on is just ignorance.
Maybe, but if it's going on and not getting used in Storms' calculations of
energy per atom, that's kind of worse for the field.
> Scientists in the field are *so over* proving the reality.
So you say, but I don't believe it. First because every paper, esp reviews,
seems to dwell on the proof of the phenomenon, and second, because everyone
wants money, and proving the reality would get them money.
>
> But reading the paper, I don't see why anyone should be convinced by that
> picture, because ... the details are missing, not explained. What is being
> seen? How often did this kind of result appear? What was the normal response
> to a current excursion that is shown? What kinds of controls are involved?
>
> The caption is partly accurate and partly misleading. And, for sure, any
> skeptic is going to pick up on the misleading part!
>
>
So the problem with the field is not the results or the experiments, but the
fact that the researchers are too incompetent to report the results lucidly.
I don't think that argument's gonna win a lot of converts.
> [ A lot of stuff about possible artifacts and why they're invalid.]
>
>
I know you're trying to drag me into detailed arguments about the various
experiments, but I've already told you, I don't have the patience for it. To
me, if the heat is real, show it to me in an isolated, unpowered cell. If
Arata can produce heat from deuterated Pd to give 2C above ambient in a big
machine, then make some deuterated Pd pellets under pressure, remove them
from his device and drop them in a Rothwell beaker, and see if it gets
palpably warm. If electrolysis experiments produce heat after the power is
turned off, disconnect it, take out the Pd electrode and put it in an
isolated beaker and see if it gets hotter.
People will go back and forth forever on excess heat and artifacts and
differential equations and controls and whatnot. But an experiment without
input, and continuous, unambiguous heat, removes any need for discussion
about artifacts.
> Nobody has controverted *any* of the testimony from Pons and Fleischmann,
> to my knowledge. There was an artifact regarding their conclusion that
> neutrons had been seen.
Artifact? That was a mistake. Plain and simple. And coincidentally, it
supported their theory. That's the thing about radiation, it's hard to fake.
But heat? Calorimetry is a well-known magnet for artifact. And they're much
harder to find and identify.
>
> One of the biggest errors on the P/F side was in allowing the experiment to
> be seen as a simple one. It looked simple and it sounded simple, but,
> obviously!, it was not simple. They had been working on it for five years
> with still quite limited success and a low rate of occurrence of excess
> heat.
>
>
The experiment is simple. I get that the preparing the material can be
tricky, but when someone figures it out, they can supply it to anyone to get
the same results, or at least the same success rate, but that's not been
done.
The fact that many people fail to see heat does not mean it's difficult like
playing a piano, it's much more consistent with the absence of an effect,
and the occasional occurrence of an artifact. What's difficult. Preparing
the electrolyte? Connecting the power supply? Reading the thermometer. You
can't just keep saying the results are spotty because it's difficult,
without saying what's difficult about it.
>
> The evidence for cold fusion is stronger than a great deal that is accepted
> routinely in science.
Examples please?
