F&P HAD event
Kirk Shanahan
here is what I've found so far.
The 144.5W number Jed Rothwell has cited comes from ref 1. The section
Jed quoted comes from ref. 2, which was a response to ref. 3. Ref. 4
is the same paper as [1] printed in the Proceeding of ICCF3. It does
have a few more photos of the cells.
The 144.5W number comes from a computation where the amount of energy
transmitted outside the calorimeter is computed from the sum of radiated
heat per the calorimeter calibration equation and the vaporized liquid.
The vaporized liquid is assumed to be half the electrolyte volume (and
computes back to 50cc, 100cc total in cell at start). Input energy is
computed by (Ecell-Ethermoneutral)*(cell current). Power is then
computed based on a 600 sec time span, and the difference is 144.5W.
Radiated heat is only 6% of the total. Thus the most important
term is the heat lost by water vaporization.
Point 1.
Morrison [3] makes the point that the output computation is based on
visual estimates of how long it takes the last half of the electrolyte
to evaporate, but the system is loaded with bubbles and this could
reasonably make that point quite difficult to estimate (specfically,
determining when 50% is gone, and thus when to start timing, would be
difficult). In their rebuttal [2], F&P do not address this issue
amazingly enough. After all, if the estimated remaining volume of 50%
is actually 10%, then we have power balance {evaporating 50cc water
takes ~103 kJ, evaporating 10 cc takes ~21 kJ, input was 22.5 kJ}
So it should be clear that an accurate knowledge of the evaporated
volume of water is critical. In [4], F&P show a few more photos from
the videos, but I can't make out what is going on in my copies.
Again, being conservative, I would like to see the deatils on how the
evaporated volume is _accurately_ determined before accepting that
50cc was the number.
Point 2.
The input power is estimated as noted above, but the result was
expressed in joules. We all know that I*V gives Watts, so buried
in the estimate is a time integration. Subsequently F&P use
the 22.5 kJ and 600 sec to compute the power as 37.5 W. My
reading of the paper says the current was at 0.5A. That allows
one to backcalculate the cell voltage at about 76.5V. In Fig. 8
of [1], we can see that that is right in the middle of where the
voltage is shooting through the roof. (It normally ran at about
10V (pretty usual) but ended at almost 100V.) Accuracy again
comes to mind.
Point 3.
The other heat loss term due to radiation is computed with the
calibration constant determined from 'normal' operations. Again,
no check is done, so we can't be sure the value is right. The
computed heat lost is 6.7kJ, which is about 1/4 of the input.
So we need to remember that perhaps more or less heat is lost
in this pathway. Less lost of course would mean more available
to boil water. But we don't know without a calibration check.
Summary of points 1-3.
Between the various errors that might have occurred, we find
the power balance condition. Since that's what we expect when
we are a conservative, I suspect that's what happened. It will
take real data to change my opinion.
The questions to be answered:
- What amount of water evaporated during the 600 seconds?
- What was the actual input power (was it accurately measured)?
- What was the radiative heat loss (was the cal. const. correct)?
Point 4.
We haven't even talked about HAD yet. (HAD is apparent heat
after input power is discontinued.)
The HAD event occurred after this boil-off period, when the cell
remained hot for an additional 3 hours after the electrolyte was
gone. That time frame is entirely reasonable for the duration of
the Pd unloading period. Thus it is trivial to point out that the
released D2 could be reacting at the thermistor itself and causing
the apparent cell heat content. Or, the released D2 could be
reacting at the Pd, but with the thermistor right above the
Pd, it could be reading an artifically elevated temperature
(compared to what the whole cell is at). The error is in assuming
the thermistor is representative of the whole cell at that point.
Again the thermal homogeneity of the cell needs to be assessed,
which has always been recognized as the fundamental problem
of this type of calorimetry. There is about 5.3 kJ worth of D
available to keep hot spots hot.
Further to be complete, I would need to know what the heat loss
rate of the cell was, since the fully loaded Pd held about
5.3 kJ worth of D. However, the temperature drop off at the end of
the 3 hour period is reasonably rapid, and this may not be a
relevant point. But comparative data for a cell held at 100C
and then allowed to cool freely would be very interesting.
Conclusion.
1. As usual, more work needs to be done to provide a convincing
case of CF (during the 600 sec period and the HAD period).
2. Jed needs to reread the paper and realize the numbers he is
bandying about are not for a HAD event.
Refs.
1. "Calorimetry of the Pd-D2O System: from simplicity via complications
to simplicity" M. Fleischmann and S. Pons, Phys. Lett. A
176 (1993) 118-129
2. "Reply to the critique by Morrison entitled: 'Comments on claims of
excess enthalpy ny Fleischmann and Pons using simple cells made to
boil'", M. Fleischmann and S. Pons, Phys. Lett. A 187 (1994) 276-280
3. "Comments on claims of excess enthalpy ny Fleischmann and Pons using
simple cells made to boil", D. R. O. Morrison, Phys. Lett. A 185 (1994)
498-502
4. "Calorimetry of the Pd-D2O System: from simplicity via complications
to simplicity" M. Fleischmann and S. Pons, Proceeding of the ICCF3,
pg 47.
--
Posted via Mailgate.ORG Server - http://www.Mailgate.ORG
Kirk Shanahan
news:1b073177a47302a3910...@mygate.mailgate.org
{snip}
> Point 4.
{snip}
> There is about 5.3 kJ worth of D
> available to keep hot spots hot.
Correction: That should be 0.53 kJ or 530 J. This is less than the
number (650) that Jed and I agreed to elsewhere since in this case I
used the heat available from the reaction that forms gaseous water.
However, I did slip a digit here, and I repeated the erroneous number
right below.
> Further to be complete, I would need to know what the heat loss
> rate of the cell was, since the fully loaded Pd held about
> 5.3 kJ worth of D. However, the temperature drop off at the end of
> the 3 hour period is reasonably rapid, and this may not be a
> relevant point. But comparative data for a cell held at 100C
> and then allowed to cool freely would be very interesting.
Fortunately, the error above doesn't impact my point, it just
requires a larger response from the thermistor for the now correctly
reduced amount of heat. But since the effect is postulated anyway,
that would be a detail that would have had to have been determined
experimentally anyway.
---
Kirk Shanahan {My opinions...noone else's}
P.S. I also forgot my sig line in the previous message! Bad day I
guess...
James Salsman
>... a larger response from the thermistor for the now correctly
> reduced amount of heat....
Are you proposing a mismeasurement due to the heat capacity of a
thermistor?
If not, would you mind please re-stating the alternative hypothesis
in terms of calibration constant measurement that you've written
about in the past? If that doesn't apply, I withdraw the specific
request, but I still can't claim to have understood this thread's
critique at all, so any paraprase into simpler and/or more familiar
terms would be great.
If so, those things are small. Please correct me if I am wrong, but
the least expensive weigh a few grams and have response curves smooth
at hundredths of a degree centigrade oscillations at thermal cycle
periods on the order of minutes. That seems way below the amplitude
of the signals plotted in Baudette's book, for instance. However, it
is true that they to have some heat capacity.
I should admit that although I feel as if I almost grasped it, I
still don't understand how such sources of error might affect the
calibration of mass flow measurements more (or less) than static
measurements, so I definetly should be asking for a resummarization
of Shanahan's earlier hypothesis at this point, too.
Best wishes,
James
Kirk L. Shanahan
:> Kirk Shanahan <...@srs.gov> wrote:
:>
:
:> ... a larger response from the thermistor for the now correctly
:> reduced amount of heat....
:
:Are you proposing a mismeasurement due to the heat capacity of a
:thermistor?
Technically, not a mismeasurement but a miscalibration. Although
I guess that's sort of a semantic game. I usually consider
'mismeasurement' to be primarily due to sensor malfunction. The
thermistor's time plot shows a sustained high temp during the time
when there should have been no current flowing. It even has a
slight increase evident. (Recall we are talking about Fig. 11 in
the 1993 Phys. Lett. A paper.) The subsequent rapid dropoff
indicates to me that the thermistor is functional. The problem is
in understanding what its reading means to the calorimeter as a
whole, which is what calibration establishes., thus 'mis-
calbration'.
During normal electrolysis conditions, the thermistor's reading has
been calibrated by known power inputs, and thus is 'translated'
by the calibration into a power value. During both the boiloff
and HAD phases, the original conditions that allow the thermistor
reading to be translated to power have changed. Thus we need a new
translation relationship to get power (different for each condition).
As to why the thermistor remains hot during the HAD period, the
suggestions is that the D2 from the Pd cathode is burning at the
thermistor. In that situation, the observed temperature would be
a function of how much D2 is burning and the heat loss function of
the thermistor.
What I meant by the sentence you quoted above is that if all the
heat that had previously been required to heat the cell to 100C was
applied just to the thermistor, which is now surrounded by gas
instead of liquid, it is likely that the observed temp would have
been much higher. So I presume that a smaller heat source is
sustaining the ~100C reading. That smaller heat source is likely
the heat deposited by the D2 reaction with O2 on the thermistor.
But without knowing the heat loss characteristics (i.e. without
calibration) I can't say exactly what heat quantity is required
to maintain the reading and whether my scenario is really valid.
However, the 3 hour observed duration of the event is not out
of line for a Pd unloading process. In fact if the cathode had
been as good as some people claim to have gotten subsequently, a
significantly longer period would not be unexpected either.
:
:If not, would you mind please re-stating the alternative hypothesis
:in terms of calibration constant measurement that you've written
:about in the past? If that doesn't apply, I withdraw the specific
:request, but I still can't claim to have understood this thread's
:critique at all, so any paraprase into simpler and/or more familiar
:terms would be great.
The calibration constant shift systematic error I have written about
before is applicable in a generic sense, in that the basic physical
condition required to shift the calibration constant the small
amount observed in the Ed Storms work is here in gargantuan
proportions. To explain the Storms' data I need only have a 2-3%
shift in the calibration constant value, induced by minor heat flow
pattern changes in a nominally similar configuration. The HAD event
is nowhere similar to the normal cell operation configuration, and
it is a trivial fact to recognize the calibration conditions have
changed (potentially, who knows, after it is checked you might find
it hasn't changed, but _that_ would be unexpected). In fact, F&P
do not attempt to relate the thermistor reading to a power,
because they realize this. They simply relate that their
thermistor registered ~100C for 3 hours after the cell was boiled
dry.
In the boiloff phase, their analysis appears to be dependent on the
thermistor reading only in about 6% of the total output. The rest
of the computed output is due to water evaporation. That power
requirement is calculated from the known heat of vaporization of
water and their estimate of how much water evaporated. The key
problem then is knowing how much water evaporated. They don't go
into details of how they decided this, but that claim they
measured the time required to evaporate the last half of the
electrolyte. Morrison questioned this measurement and I concur
that more reliable data is needed, especially in light of the
import of the claims.
Furthermore, the electrolysis current is used to compute input
power in the usual fashion, but the system readings (voltage esp.)
is changing rapidly during this time (10 minutes). I would like
some assurance they were _correctly_ computing input power.
Jed's comment on his observations of the videos suggested that
electrolysis had stopped because there were no bubbles at the
anode, which would imply that the computation used by F&P to
calculate Pin was wrong in that they subtract the thermoneutral
voltage. If no electrolysis was ongoing, that isn't correct.
However, that is only 1.54 V out of 75V average so that may not
be a large error in itself. Of more concern is whether their
electronics could keep up with the true voltages, etc. They
were designed for calorimetry with it's mutiple time constant
waiting periods after changes, and this whole stage lasted only
10 minutes.
Also, as the electrolyte boils away, the contact area between the
cathode and electrolyte decreases. This will concentrate the heat
deposition at that interface into a smaller area, making it hotter.
That in turn could lead to a transition to a different kind of
boiling process, which would really skew the power computation
through the water measurement numbers. (Morrison also discussed
this somewhat.)
Thus the 6% of output power computed from the calibration equation
determined under _normal_ operating conditions a) may not be
computed correctly because of a change in configuration, and b)
may be a much larger total fraction of the power output,
depending on the accuracy of the water loss estimates. The input
power may be computed incorrectly. And the primary output power
may also depend on faulty assumptions.
This leaves us asking for more data aimed at addressing the issues,
which we are unlikely to get since this work was reported in 1993
(meaning ot was probably done in the '91-'92 time frame).
:
:If so, those things are small. Please correct me if I am wrong, but
:the least expensive weigh a few grams and have response curves smooth
:at hundredths of a degree centigrade oscillations at thermal cycle
:periods on the order of minutes. That seems way below the amplitude
:of the signals plotted in Baudette's book, for instance. However, it
:is true that they to have some heat capacity.
At this point, you should realize that the issue is heat deposition
rate and heat loss rate at the thermistor in the new environment.
:
:I should admit that although I feel as if I almost grasped it, I
:still don't understand how such sources of error might affect the
:calibration of mass flow measurements more (or less) than static
:measurements, so I definetly should be asking for a resummarization
:of Shanahan's earlier hypothesis at this point, too.
:
:Best wishes,
:James
:
:
I showed in the thread on "D. Britz estimate..." recently how a
Seebeck calorimeter could suffer from the error. The simple bottom
line, understandable by anyone, is that if you call a number a
"constant", and use it like it is, it had better BE constant. In
my paper I show why the Storms' data suggests this is not the case
in his closed electrolysis cell. By analogy, that translates to
other cells, open or closed, and other calorimeters.
The question of what causes the shift is the most interesting. In
a strictly physical sense, the calibration procedure makes up for
the fact that some heat is always lost in any real calorimeter
system. Unfortunately we usually don't know where this happens
(or can't do anything about it), so we can't include this lost
heat in the model we use (called the calibration equation).
Instead we assume it remains unchanging, and try to compensate
for it through calibration. So if the lost heat quantity changes,
our calibration equation changes. I believe that is what is
happening with CF.
In a closed cell the best candidate for this is movement of some
of the heat generation from the recombination catalyst to another
point in the cell. Being near the cell top and usually supported
from it, the recombination catalyst represents a good heat loss
path, with heat flowing through the supports and out the lid.
Note that this is a small loss, not large. Now if some of the
heat generated there moves, say, to the surface of the cathode,
the heat generated at this new location will have a greater chance
of capture (maybe 99% vs. 95%), and that 'extra' heat captured will
show up as an excess heat. But it really isn't, it's just a
change in overall calorimeter efficiency because of a heat source
location change. The input power hasn't changed, and the true
output power still equals the input.
Now in an open cell, one normally loses a good bit of potential
heat with the gas flow out. Researchers try to compensate for
this mathematically, but any recombination of evolved gases in
the cell would also appear as an excess heat. Now realize that
this new recombinant heat might not have the same capture
efficiency (calibration equation) as the 'routine' heat, and the
stage is set for a misunderstanding about how much heat is really
there. In effect is it the same case as the thermistor problem
above in the HAD event.
My little paper demonstrates how all this can appear in real data,
and as you can see, it is not limited to any specific case, but is
generally applicable to any calorimeter system. Only the detailed
specifics will vary from calorimeter to calorimeter. Design A may
overestimate heat by 3%, while Design B may do so by 100%, it
depends totally on the specific calorimeter/cell in question.
That was a very long-winded response, but I hope it clarified
things for you. I'll try to answer any further questions you
might have as well.
(As an aside, there are additional reasons why one calibrates,
lost heat is not the _only_ reason.)
Kirk L. Shanahan
:>
:
:> ... a larger response from the thermistor for the now correctly
:> reduced amount of heat....
:
:Are you proposing a mismeasurement due to the heat capacity of a
:thermistor?
Technically, not a mismeasurement but a miscalibration. Although
:
:If not, would you mind please re-stating the alternative hypothesis
:in terms of calibration constant measurement that you've written
:about in the past? If that doesn't apply, I withdraw the specific
:request, but I still can't claim to have understood this thread's
:critique at all, so any paraprase into simpler and/or more familiar
:terms would be great.
The calibration constant shift systematic error I have written about
:
:If so, those things are small. Please correct me if I am wrong, but
:the least expensive weigh a few grams and have response curves smooth
:at hundredths of a degree centigrade oscillations at thermal cycle
:periods on the order of minutes. That seems way below the amplitude
:of the signals plotted in Baudette's book, for instance. However, it
:is true that they to have some heat capacity.
At this point, you should realize that the issue is heat deposition
rate and heat loss rate at the thermistor in the new environment.
:
:I should admit that although I feel as if I almost grasped it, I
:still don't understand how such sources of error might affect the
:calibration of mass flow measurements more (or less) than static
:measurements, so I definetly should be asking for a resummarization
:of Shanahan's earlier hypothesis at this point, too.
:
:Best wishes,
:James
:
:
---
Gordon D. Pusch
Another factor is that the calibration constant was determined by linear
regression, and as most statisticians know (and most physicists don't!),
there is an intrinsic trade-off between bias and variance in any quantity
determined by linear regression. Linear regression estimates made from
data-sets having a low variance will have a high bias, and vice versa.
Furthermore, it is impossible to find a linear regression estimator that
reduces the sum of the bias squared and the variance of the estimate below
a data-set dependent positive value.
-- Gordon D. Pusch
perl -e '$_ = "gdpusch\@NO.xnet.SPAM.com\n"; s/NO\.//; s/SPAM\.//; print;'
Kirk Shanahan
news:9acdab21.02062...@posting.google.com
..a long message that was posted twice by Google. I have no
idea why. I cancelled one.
---
Kirk Shanahan {My opinions...noone else's}
James Salsman
>...
> During normal electrolysis conditions, the thermistor's reading has
> and HAD phases, the original conditions that allow the thermistor
>
> As to why the thermistor remains hot during the HAD period, the
> suggestions is that the D2 from the Pd cathode is burning at the
Are there any other suggestions for changed conditions other than
combustion? "conditions" and "suggestions" are plural, but only one
root alternative hypothesis has been given. If I missed others, in
other threads or not, please reiterate all the changed conditions.
Furthermore, with what can deuterium combust under water?
I'm trying to regain my skepticism, and Shanahan's theories are
what I believe to be my best hope. When he and Gordon Pusch start
talking about regression residuals, I feel like I almost have a
chance of getting back up there on the fence with Britz, where I
spent most of the mid 1990s. However, the more I try, the more at
seems that there isn't any substance to the claim. On some data
sets (e.g., Storms), I just know there is something there, and I
HEARTILY commend Shanahan for culling that chaff.
But when I consider the amplitudes of the signals reproduced in
Baudette's book, I am totally unable to believe that false
regression residuals made during the calibration of mass-flow
measurements are to blame. Even if I were to ignore everything
Szpak, Bockris, et al., have published on codeposition, I think I
would be left with the same conclusion.
Beyond that, I think the boson field descriptions of S. Chubb, and
the classical angular momenta-based explanations of Swartz agree in
their essential characteristics, and explain the phenomena. Having
said that, I know of no sufficient explanations for HAD effects.
There are plenty of possibilities, but the effect seems less likely
to be useful other than for demonstration.
I have asked my congresswoman to ask the Dept. of Energy to
investigate fluidized bed electrodes with respect to the
codeposition process, and my advice to my fellow citizens is to
join me in that request.
Sincerely,
James Salsman
Kirk Shanahan
:>...
:> During normal electrolysis conditions, the thermistor's reading has
:> been calibrated by known power inputs.... During both the boiloff
:> and HAD phases, the original conditions that allow the thermistor
:> reading to be translated to power have changed....
:>
:> As to why the thermistor remains hot during the HAD period, the
:> suggestions is that the D2 from the Pd cathode is burning at the
:> thermistor....
:
:Are there any other suggestions for changed conditions other than
:combustion? "conditions" and "suggestions" are plural, but only one
:root alternative hypothesis has been given. If I missed others, in
:other threads or not, please reiterate all the changed conditions.
I actually can't come up with any other scenario that I consider
viable. The cool down rate after the three hour period suggests
that it requires a true heat source to maintain the thermistor
reading at 100C for that time frame. You can always say 'sensor
malfunction' but I don't think that's viable in this case. I
suppose one could contruct a scenario where the last bit of
electrolyte boils off due to residual heat in the cell, and the
gas from that keeps the thermistor hot too, but again, that's
really stretching credibility. The bottom line is that with a
single point temperature measurement, there is enormous room to
propose alternatives. What is needed is a better experiment,
most likely with redundant and different thermistors to confirm
or deny the magnitude of the proposed heat source.
:Furthermore, with what can deuterium combust under water?
:
The usual, oxygen, from the electrolysis. In the HAD
configuration, the O2 would be remnants from the electrolysis,
plus any that came into the cell by back flow through the vent
that the boiloff gases escaped through.
:I'm trying to regain my skepticism, and Shanahan's theories are
:what I believe to be my best hope. When he and Gordon Pusch start
:talking about regression residuals, I feel like I almost have a
:chance of getting back up there on the fence with Britz, where I
:spent most of the mid 1990s. However, the more I try, the more at
:seems that there isn't any substance to the claim. On some data
:sets (e.g., Storms), I just know there is something there, and I
:HEARTILY commend Shanahan for culling that chaff.
:
:But when I consider the amplitudes of the signals reproduced in
:Baudette's book, I am totally unable to believe that false
:regression residuals made during the calibration of mass-flow
:measurements are to blame. Even if I were to ignore everything
:Szpak, Bockris, et al., have published on codeposition, I think I
:would be left with the same conclusion.
:
I am not a statistican by training, but I have a lot of practical
on-the-job training from staticians, and the main thing I learned
from them (and quality control technolgists) is that a cause of
variation should be assumed to be a real thing, that can be
isolated and identified by appropriate experimentation. I also
believe there is something there, but that thing's primary effect
is to ruin the numerical accuracy of calorimetry. The fact that
the largest numbers of experiments discover no excess heat is an
indication that the FPH effect is not easy to obtain. I believe
there is a real chemical state/configuration of the cell
components that has to be 'grown in' by appropriate treatments.
But that state has nothing to do with nuclear fusion. Instead
it causes a heat flow redistribution in the cell, that
invalidates the calorimeter calibration as a side effect.
I've read Beaudette's book, and I found nothing new in it, he
basically just 'popularizes' the results of the field, meaning
that if you worked through the literature, his book presents no
new information. Of course that means his book doesn't change
my opinion. What specifically were you referring to that seems
so compelling to you? Or does my (re)statement that I believe
there is something real going on clarify things for you?
:Beyond that, I think the boson field descriptions of S. Chubb, and
:the classical angular momenta-based explanations of Swartz agree in
:their essential characteristics, and explain the phenomena. Having
:said that, I know of no sufficient explanations for HAD effects.
:There are plenty of possibilities, but the effect seems less likely
:to be useful other than for demonstration.
:
Which phenomena are you referring to? The incorrect calorimetric
measurements or the bad mass spectral analyses? The point is that
all theories are nothing more than sytematization of our
experimentally determined knowledge. If the experimental 'knowledge'
is false, the theory derived to explain it will be false too. In
developing their theories, the theorists pick what data to include
and which to reject. If they condsider my contentions regarding
calorimetry, there will be no observations to explain by theory.
That then means their theories are simply exercises in
mathematics. Thinking along these lines gives one a different
appreciation for theory and how it is developed.
:I have asked my congresswoman to ask the Dept. of Energy to
:investigate fluidized bed electrodes with respect to the
:codeposition process, and my advice to my fellow citizens is to
:join me in that request.
:
Before I ask the government to spend more money on the field, I'd
ask the primary CF researchers to fairly address the issues I and
others raise. We have seen the following criticisms: bad
calorimeter calibration leading to apparent excess heat, bad mass
spectrum interpretation leading to claims of transmutation, bad
analytical chemistry leading to He detections, superficial
responses to concerns of recombination, etc. No scientist is
required to accept the 'assertions' of another scientist without
significant evidence to support those assertions. In the questions
above, the evidence has not been presented. Once it is, and has
been evaluated favorably towards CF, then we can go looking for
what causes it. But first we have to establish that it is really
there. Then we can go hunting the world's energy solution.
James Salsman
>: Are there any other suggestions for changed conditions other than
>: combustion? "conditions" and "suggestions" are plural, but only one
>: root alternative hypothesis has been given. If I missed others, in
>: other threads or not, please reiterate all the changed conditions.
>
> I actually can't come up with any other scenario that I consider
> viable.... What is needed is a better experiment,
> most likely with redundant and different thermistors to confirm
> or deny the magnitude of the proposed heat source.
Okay so far.
>: Furthermore, with what can deuterium combust under water?
>
> The usual, oxygen, from the electrolysis. In the HAD
> configuration, the O2 would be remnants from the electrolysis,
> plus any that came into the cell by back flow through the vent
> that the boiloff gases escaped through.
How could that much O2 remain dissolved or engress?
Best wishes,
James
Kirk Shanahan
news:%asU8.12868$T_.2...@iad-read.news.verio.net
> Kirk Shanahan wrote, in response to:
{snip}
> >: Furthermore, with what can deuterium combust under water?
> >
> > The usual, oxygen, from the electrolysis. In the HAD
> > configuration, the O2 would be remnants from the electrolysis,
> > plus any that came into the cell by back flow through the vent
> > that the boiloff gases escaped through.
>
> How could that much O2 remain dissolved or engress?
>
First you'll have to tell me how much 'that much' is. Be careful!
If you think about it, you'll realize that you have a presupposition
here, namely that the O2 requirement to produce the observed
temperature signal is 'large'. However, without a valid calibration,
you can't make any such quantitative judgements. First you need to
calibrate the system and test the thesis I present of D2+O2 reacting
at the thermistor itself. Then you could compute how much combustion
was required to get the signal observed.
One could attempt a theoretical computation based on standard heat
transfer properties to try to make an educated guess at how much
D2+O2 would be needed, given the heat loss rates from the thermistor.
But that is a lot of work too. Lots of assumptions that would have
to be explored to check how sensitive the computation was to the
underlying assumptions. I think it's more realistic to get an
experimentalist to do more experiments than to do a sophisticated
heat transfer comp, but who knows? Maybe there is a volunteer out
there.
But in a rough attempt to answer 'how much', remember that when the
HAD conditions are in effect, there is essentially no liquid in the
cell, and that means no outgoing gas flow from boiloff. Instead
there will be a smaller flow from the postulated slow unload of the
Pd. But that may be overcome by the inflow of air driven by the
combustion. Remember 2D2 + O2 = 2 D2O, so 3 molecules of gas converts
to two, and there should be a pressure drop that would have to be
equalized by inflow. Add to that the possibility of some
condensation, which would cause even more pressure drop and inflow.
The maximum 'how much' would be determined by assuming 100% of the
D in the Pd burns. Then you need to know the overall efficiency of
the reaction to decide how close to that you come.
So how could that much O2 engress? Simple flow from the atmosphere,
just enough to produce the observed signal.
James Salsman
>... So how could that much O2 engress? Simple flow from the atmosphere,
> just enough to produce the observed signal.
Perhaps I don't have all the parameters, but even for a very small
amount of very hot solution, the extent to which additional O2 is
dissolved from standing with a surface next to the atmosphere is not
large enough to produce a signal larger than the short-time
electrolysis input, which would describe the maximum dissolved gasses
in such solutions anyway. Not only does your theory not hold water,
it doesn't even hold gas. If I am mistaken, please tell me the
parameters of which I seem to be least cognizant.
Best wishes,
James
Kirk L. Shanahan
James, your biggest problem is you are lumping the heat-after-death claim
in with the regular PF effect claim. Separate them. HAD occurs when the
cell is dry, no electrolyte. The 'death' refers to the cessation of
electolysis current due to a loss of the conductive pathway between the
electrodes. So you see your comments above do not refer to HAD, right? My
quoted comment above refers to the HAD period, not the pre-boiloff period.
Your comments instead refer to how the PF effect could occur, which only
happens in an electrolytic cell. That means electrolyte present and current
flowing. In that situation, the O2 comes from the electrolysis. And in
fact I favor the 'recombination at the cathode' explanation of why the
calibration constants would shift.
In the transition region of the F&P cell being boiled dry and then showing
HAD, the exposure of the Pd cathode as the electrolyte boils away makes
this even _more_ likely. Now we are just talking about a simple gas phase
D2 + O2 reaction at the exposed cathode surface. Mass transport and access
to a metal surface for ignition is trivially easy, not to mention the
presence of grossly changing heat transfer pathways that would contribute
to a further calibration constant shifting.
James Salsman
> James, your biggest problem is you are lumping the heat-after-death claim
> in with the regular PF effect claim. Separate them. HAD occurs when the
> cell is dry, no electrolyte. The 'death' refers to the cessation of
> electolysis current due to a loss of the conductive pathway between the
> electrodes....
Kirk, In the third sentence you claim the cell is dry, and in the forth
you claim the input power is merely switched off.
What narrative description of which event are you going by? A published
version or something you've patched together for multiple reports?
>... in fact I favor the 'recombination at the cathode' explanation of why
> the calibration constants would shift.
So you're saying that an increase in heat during calibration is going to
increase the heat signal during measurement? That makes no sense.
> In the transition region of the F&P cell being boiled dry and then showing
> HAD, the exposure of the Pd cathode as the electrolyte boils away makes
> this even _more_ likely. Now we are just talking about a simple gas phase
> D2 + O2 reaction at the exposed cathode surface....
I'm not sure about P&F, but Szpak and Mosier-Boss used cell designs
with no nonsubmerged cathodes. Letting one boil dry could lead to very
dangerous results.
Best wishes,
James
Kirk Shanahan
> Kirk L. Shanahan wrote:
>
> > James, your biggest problem is you are lumping the heat-after-death claim
> > in with the regular PF effect claim. Separate them. HAD occurs when the
> > cell is dry, no electrolyte. The 'death' refers to the cessation of
> > electolysis current due to a loss of the conductive pathway between the
> > electrodes....
>
> Kirk, In the third sentence you claim the cell is dry, and in the forth
> you claim the input power is merely switched off.
>
C'mon James! In the electrolysis circuit, the electrolyte is a current
carrier. Think of it as a liquid wire. When the electrolyte stops
making contact with the cathode, the circuit breaks, and current stops.
No current, no electrolysis. If apparent heat output continues at that
point, you have 'heat-after-death'. And I don't claim the input power
was physically switched off by some human action at a switch. As you
can see from above, I say the same thing as I just did.
> What narrative description of which event are you going by? A published
> version or something you've patched together for multiple reports?
F&P's paper in Phys Lett A, 176 (1993) 118. What are you using?
>
> >... in fact I favor the 'recombination at the cathode' explanation of why
> > the calibration constants would shift.
>
> So you're saying that an increase in heat during calibration is going to
> increase the heat signal during measurement? That makes no sense.
>
No, I'm saying a) a calibration constant shift (CCS) seems capable of
explaining just about every calorimetry-based CF claim made to date,
b) a CCS requires a redistribution of heat flow in a cell to cause the
CCS, and c) one good way to get a redistribution is to move some of the
recombination from the recombination catalyst to the cathode (in the
case of closed cells certainly, but the F&P open cells also show small
but similar effects, coupled with 'bursts' which I suspect are an
additional onset of recombination in the cell).
Note that this shift _is_ the 'CF' event, so it clearly does not occur
in calibration runs, otherwise they would have been labeled 'CF
displaying' runs. And as we all know, CF displaying runs are hard to
come by. Most of the time, including calibrations, Pout=Pin, and
no apparent excess heat source is observed.
In fact, that subtlety about how the runs are labeled (i.e. cal or CF)
is important to note, as it represents a 'bias' that can explain
Storms' Pt CF results. Normally Pt is considered inert to CF, and
is used for calibrations. But in some cases, excess heat is observed.
So Pt then gets the label 'CF producer' too. Yet, the chemistry of
D on Pt (it doesn't go in!) is radically different from Pd, and thus
invalidates most of the 'requirements' people have developed from
Pd studies. I always thought that was very important, but the CFers
don't seem to catch on.
> > In the transition region of the F&P cell being boiled dry and then showing
> > HAD, the exposure of the Pd cathode as the electrolyte boils away makes
> > this even _more_ likely. Now we are just talking about a simple gas phase
> > D2 + O2 reaction at the exposed cathode surface....
>
> I'm not sure about P&F, but Szpak and Mosier-Boss used cell designs
> with no nonsubmerged cathodes. Letting one boil dry could lead to very
> dangerous results.
>
> Best wishes,
> James
I haven't considered anything but the F&P event explicitly here. I
also haven't examined any Szpak claims to HAD. What reference has
those claims in it?
---
Kirk Shanahan {My opinions...noone else's}
James Salsman
>>>... in fact I favor the 'recombination at the cathode' explanation of why
>>> the calibration constants would shift.
>>
>> So you're saying that an increase in heat during calibration is going to
>> increase the heat signal during measurement? That makes no sense.
>
> No, I'm saying a) a calibration constant shift (CCS) seems capable of
> explaining just about every calorimetry-based CF claim made to date,
> b) a CCS requires a redistribution of heat flow in a cell to cause the
> CCS, and c) one good way to get a redistribution is to move some of the
> recombination from the recombination catalyst to the cathode (in the
> case of closed cells certainly, but the F&P open cells also show small
> but similar effects, coupled with 'bursts' which I suspect are an
> additional onset of recombination in the cell).
How can moving heat production (of any kind) from the anode to the cathode,
whether during calibration or trial runs, support your stated hypothesis
that no extrachemical events are responsible for the measured heat?
>... D on Pt (it doesn't go in!) is radically different from Pd, and thus
> invalidates most of the 'requirements' people have developed from
> Pd studies. I always thought that was very important, but the CFers
> don't seem to catch on.
I think you have half of a good argument, but the other half seems false
so the whole thing is no good. However, having said that, I have to admit
that it is nice to see someone referring to the actual calibration and
measurements instead of arguing on more sophistic, rhetoric-only grounds,
as we have had to endure before you joined this group.
>> I'm not sure about P&F, but Szpak and Mosier-Boss used cell designs
>> with no nonsubmerged cathodes. Letting one boil dry could lead to very
>> dangerous results.
>
> I haven't considered anything but the F&P event explicitly here. I
> also haven't examined any Szpak claims to HAD. What reference has
> those claims in it?
The Szpak paper where tritium was assayed (and found at very low
quantities.) Please let me know if you can't find the cell and
large surface recombiner diagrams from that late-1990s paper.
Best wishes,
James
James Salsman
>... What reference has [submerged-only electrodes] in it?
The reference I was trying to remember from my post of some hours ago is:
Szpak S, Mosier-Boss PA, Boss RD, Smith JJ; Fusion Technol. 33 (1998) 38.
"On the behavior of the Pd/D system: Evidence for tritium production".
I hope that's the one I'm remembering. I bet the diagram in question is
in one of those three big .pdf files in www.bovik.org/codeposition/.
Best wishes,
James
Kirk L. Shanahan
> Kirk Shanahan wrote:
>
{snip}
> > and c) one good way to get a redistribution is to move some of the
> > recombination from the recombination catalyst to the cathode (in the
> > case of closed cells certainly, but the F&P open cells also show small
> > but similar effects, coupled with 'bursts' which I suspect are an
> > additional onset of recombination in the cell).
>
> How can moving heat production (of any kind) from the anode to the cathode,
> whether during calibration or trial runs, support your stated hypothesis
> that no extrachemical events are responsible for the measured heat?
>
The same way as moving it as I suggested would work? However, because of
the similarity in thermal pathways for the two electodes, I would guess that
your suggestion would not be noticed in excess heat. In fact, the anode is
usually longer (at least in wire wound basket type configurations), so there
would be more opportunity for heat transfer to the electrolyte, and so I
would guess at a negative excess for a jump from the anode to the cathode,
assuming it was detectable at all.
I also realize that your question could really be: Why does a moving heat
source mean no cold fusion? The answer is that if you can show the heat
sources moved, and that it caused a change in the calibration constant,
and that that change accounts for the apparent excess heat (as I surmise
in my rework of Ed Storms' data), then you have shown the apparent excess
is due to the CCS. That logic chain starts with a moved heat source. That
never completely excludes CF, but it does say you have no evidence for it
in that experiment.
> >... D on Pt (it doesn't go in!) is radically different from Pd, and thus
> > invalidates most of the 'requirements' people have developed from
> > Pd studies. I always thought that was very important, but the CFers
> > don't seem to catch on.
>
> I think you have half of a good argument, but the other half seems false
> so the whole thing is no good.
Before you reject the other half, make sure you understand it. You're
comment above suggests you have an inaccurate picture of a closed cell,
as you seem to be equating a heat source shift from the anode to the
cathode as equivalent to one from the recombination catalyst to the cathode.
They aren't even close. Yes, a redistribution of any kind could have an
impact, but the facts are that the effect is small, so I suspect one needs
a significant change in heat flow pattern to get the FPH effect. Significant
means one where the heat leaving the cell would see 'radically' different
environments.
> However, having said that, I have to admit
> that it is nice to see someone referring to the actual calibration and
> measurements instead of arguing on more sophistic, rhetoric-only grounds,
> as we have had to endure before you joined this group.
>
Thanks. I always prefer to argue from the data as well. Usually, my
disagreements with CF researchers is with their interpretations.
> >> I'm not sure about P&F, but Szpak and Mosier-Boss used cell designs
> >> with no nonsubmerged cathodes. Letting one boil dry could lead to very
> >> dangerous results.
> >
> > I haven't considered anything but the F&P event explicitly here. I
> > also haven't examined any Szpak claims to HAD. What reference has
> > those claims in it?
>
> The Szpak paper where tritium was assayed (and found at very low
> quantities.) Please let me know if you can't find the cell and
> large surface recombiner diagrams from that late-1990s paper.
>
> Best wishes,
> James
I will check. But, even before that I would like to 'warn' you that most
of the tritium results reported to date that I have seen are near the
detection limit of the technique. That makes the problem 10X more
difficult, and in general I've not seen statistically adequate data sets.
So, recognizing that I am likely to say that Szpak's calorimetry has the
same problem as everyone else's, the follow up to that with respect to
tritium measurements is that there is some other systematic error in those
analyses. Remember that to establish X is correlated to Y, you need to
believe both X and Y are accurate, and precise enough.
Kirk L. Shanahan
> Kirk Shanahan wrote:
>
{snip}
> > recombination from the recombination catalyst to the cathode (in the
> > case of closed cells certainly, but the F&P open cells also show small
> > but similar effects, coupled with 'bursts' which I suspect are an
> > additional onset of recombination in the cell).
>
> How can moving heat production (of any kind) from the anode to the cathode,
> whether during calibration or trial runs, support your stated hypothesis
> that no extrachemical events are responsible for the measured heat?
>
The same way as moving it as I suggested would work? However, because of
the similarity in thermal pathways for the two electodes, I would guess that
your suggestion would not be noticed in excess heat. In fact, the anode is
usually longer (at least in wire wound basket type configurations), so there
would be more opportunity for heat transfer to the electrolyte, and so I
would guess at a negative excess for a jump from the anode to the cathode,
assuming it was detectable at all.
I also realize that your question could really be: Why does a moving heat
source mean no cold fusion? The answer is that if you can show the heat
sources moved, and that it caused a change in the calibration constant,
and that that change accounts for the apparent excess heat (as I surmise
in my rework of Ed Storms' data), then you have shown the apparent excess
is due to the CCS. That logic chain starts with a moved heat source. That
never completely excludes CF, but it does say you have no evidence for it
in that experiment.
> >... D on Pt (it doesn't go in!) is radically different from Pd, and thus
> > invalidates most of the 'requirements' people have developed from
> > Pd studies. I always thought that was very important, but the CFers
> > don't seem to catch on.
>
> I think you have half of a good argument, but the other half seems false
> so the whole thing is no good.
Before you reject the other half, make sure you understand it. You're
comment above suggests you have an inaccurate picture of a closed cell,
as you seem to be equating a heat source shift from the anode to the
cathode as equivalent to one from the recombination catalyst to the cathode.
They aren't even close. Yes, a redistribution of any kind could have an
impact, but the facts are that the effect is small, so I suspect one needs
a significant change in heat flow pattern to get the FPH effect. Significant
means one where the heat leaving the cell would see 'radically' different
environments.
> However, having said that, I have to admit
> that it is nice to see someone referring to the actual calibration and
> measurements instead of arguing on more sophistic, rhetoric-only grounds,
> as we have had to endure before you joined this group.
>
Thanks. I always prefer to argue from the data as well. Usually, my
disagreements with CF researchers is with their interpretations.
> >> I'm not sure about P&F, but Szpak and Mosier-Boss used cell designs
> >> with no nonsubmerged cathodes. Letting one boil dry could lead to very
> >> dangerous results.
> >
> > I haven't considered anything but the F&P event explicitly here. I
> > also haven't examined any Szpak claims to HAD. What reference has
> > those claims in it?
>
> The Szpak paper where tritium was assayed (and found at very low
> quantities.) Please let me know if you can't find the cell and
> large surface recombiner diagrams from that late-1990s paper.
>
> Best wishes,
> James
I will check. But, even before that I would like to 'warn' you that most
of the tritium results reported to date that I have seen are near the
detection limit of the technique. That makes the problem 10X more
difficult, and in general I've not seen statistically adequate data sets.
So, recognizing that I am likely to say that Szpak's calorimetry has the
same problem as everyone else's, the follow up to that with respect to
tritium measurements is that there is some other systematic error in those
analyses. Remember that to establish X is correlated to Y, you need to
believe both X and Y are accurate, and precise enough.
---
Kirk L. Shanahan
Well James,
I've had an opportunity to look at your suggested Szpak paper,
(FT 33(1998)38), and as expected, the pathological skeptic Shanahan has
some problems. Let me keep this short and hopefully logical, and see if
it shows you why I have problems.
In the Conclusions, Szpak, et al, state:
"The evidence for tritium production is based on the difference between the
computed and observed concentration of tritium, the nonequilibrium
distribution of tritium, and the total mass balance."
OK, so if we had no evidence for T (tritium) production, we'd have no paper,
right? And the evidence is based equally on the three things noted above,
right? So all I have to do is find a rational reason or set of reasons not
to believe one of the three 'legs' of the stand the conclusions rest on,
right?
OK, let's look at the first leg, the comparison of computed and observed.
Let's focus on the computed (major problems in either kills the comparison,
right?).
What is being computed is the expected tritium concentration in gas and
liquid phases of the electrolysis cell. Figures 3 through 6 show the
comparative data. The first sentance of section III.B says:
"we assume the constancy of the isotopic separation factor"
in computing the T distributions.
At the top of that column are listed 3 "restrictive conditions" on the
separation factor. Number 3 is:
"3. The system operates in a stationary state; i.e. equilibria between
various species are established, resulting in d(theta_sub_m)/dt=0 (Ref.
12)."
Theta_sub_m is not explicitly defined here, but the sub_m refers to
species undergoing reduction such as D2O or DTO. Ref. 12 is a 1964
Bockris publication I don't have, but I expect theta relates to
concentration, probably in the double layer. The point is that it is
time invariant.
So the logic goes, if we can show "3" above is not held to, then
the constancy of the separation factor is called into question and thus
the computed T distributions will be suspect. That will invalidate the
use of those computed values in any comparison. If we can show that,
we cannot conclude excess T was produced. Make sure you follow that.
I call it a chain of confidence. If the base link is broken, the whole
chain falls away.
What indicates a nonstationary state? Significantly changing
concentrations. What is significant? It really depends, but I think
a typical number might be a 10-20% change is bad. More would be very
bad.
In Figure 2, Szpak describes the sampling protocol. I noted he does
a good thing, he samples right after an electrolyte top off. In fact,
he (they) seem to be very careful about that, defining Va (the volume
added) as 2*Vs + Ve. Vs is the volume they remove for sampling (2
because they sample before and after addition), and Ve is the volume
electrolyzed away. This is designed to bring the cell volume, Vc,
back to the same starting point every time.
In the Appendixes, the data behind the Figures is listed, along with
computation parameters. Included are Vc. Va and Vs values. Thus we
can compute Ve values and compare to Vc values. Guess what, I compute
that the varied Ve volumes range from 10 to 84% of the Vc values. Now,
that means the electrolyte concentration is varying wildly (a 50% Ve
means a 100% increase in electrolyte concentration). Do you think the
system "operates in a stationary state"? I don't.
QED
P.S. This isn't a paper about a HAD event.
James Salsman
>...
> I also realize that your question could really be: Why does a moving heat
> source mean no cold fusion? The answer is that if you can show the heat
> sources moved, and that it caused a change in the calibration constant,
Granted, if the heat source moved closer to the thermocouple(s) subsequent
to calibration. I need to look up the F&P HAD cite you gave (thank you)
before I have a hope of contributing any further to that thread.
Look, Kirk, you've done lots of emperical experiments in electrochem,
right? What would it take for you to try the kind of codeposition
experiment in http://www.bovik.org/codeposition/best.gif and let us all
know what happens?
Given the prestige of your lab, this ought to be something that you and
your colleagues could put together without much hastle, isn't it? You've
got the best shot at a result with controversy-settling significance, as
everyone knows your reputation in the field is squarely based on your
demolition of Storms' analysis. I agree you caught Storms asleep at the
switch (or thermometer, as it were) and nobody can take that away from you.
I'm predicting you get the same results that Szpak and Bockris get, and I
think you have the integrity to say so if you do.
When we went through the review of the bibliography papers, I think you
got the same impression I did (if for no other reason that we were looking
at the same citations.) Whether you agree with the theory involving the
implications of conservation of angular momenta of deuterons, I know you
know enough of the idea that, from my perspective, since you have the
integrity to look at Storms' data with the correct critical eye, then you
ought to be curious enough to try what has been designed to be the least
expensive and most conclusive of any possible confirmatory experiment.
What do you say?
Best wishes,
James
Kirk L. Shanahan
{snip}
Well, I find I need to back off a bit from my conclusion of my last post.
The problem is that the change in sample cell electrolyte volume may NOT
be as severe as I explained, not because it doesn't change as I reported,
but because the concentration of import is the _water_ concentration,
which won't change that much. Thus the steady state approximation may
actually be OK. So, that means while the modeling assumptions would still
need to be checked, it isn't immediately apparent they are wrong.
Therefore I would have to progress to other problems I've seen with the
paper. Another potential problem with the model is the disagreement
between Szpak, et al, and Boucher, et al, (FT 24(1993)200) on separation
factor values. Recognizing that Szpak defines his sep. factor as the
inverse of Boucher, there is an ~20-25% difference. (Szpak averages
1.5 and Bocher ~2.0). Since the sep. factor comes in as an exponent,
I haven't worked out how important that is, but the point is that there
are disagreements with the literature here on the model parameters, and as
we all know, it's the parameters that make or break the model. (I've even
heard that F&P claim sep. factors of 4 or so, but I haven't checked that.)
One of my biggest problems in that arena is the old saw, replication.
There is no indication this data is replicated, and that always means
that the observed variation may not be an 'effect' but an error. Only
replicating the effect proves that it is replicatable. Szpak, et al,
present 4 sets of data (gas & liquid phase T measures) for 4 different
electrolyte combinations, and observe different behavior in each. Ok, so
now replicate it.
Of further concern is that they are working with a signal that is only
about 2x the background levels. This is always a concern point for
analytical chemists. In that experimental regieme, statistics is very
important, and there isn't enough data to address the issue in this paper.
Secondarily, they use Will's method of distilling a tritiated water sample
and then measuring with LSC. I have noticed that Will's method only gave
about 80% or so 'recovery' of their T (in other words, they published a
calibration curve whose counts for a given amount of T in solution was
about 20% low.) In their prior paper where they dissolve T-containing Pd
and run that direct, they had to quench correct the LSC numbers to get
back to a 100% recovery number. But the distillation technique is not
supposed to need that as there is only pure water there. So where does
the other 20% of the counts go? Will, et al do not address the issue at
all. Presumably they notice it, but thought it unimportant. But I'd
like to know why.
So if we recall Szpak, et al's conclusion:
"The evidence for tritium production is based on the difference between the
computed and observed concentration of tritium, the nonequilibrium
distribution of tritium, and the total mass balance."
I am still not convinced the computation is trustworthy at the level they
are trying to use it, and I don't necessarily believe their data has the
small error bars they claim. These two general concerns attack all
three parts of the conclusion. So I now state my overall conclusion
regarding this paper as: "Intriguing but not compelling, replication
required."
Kirk L. Shanahan
:Kirk L. Shanahan wrote:
:>...
:> I also realize that your question could really be: Why does a moving heat
:> source mean no cold fusion? The answer is that if you can show the heat
:> sources moved, and that it caused a change in the calibration constant,
:> and that that change accounts for the apparent excess heat....
:
:Granted, if the heat source moved closer to the thermocouple(s) subsequent
:to calibration.
OK! So now you've understood my point. A moving heat source in the cell
can be a problem. Now you need to realize that the few CFers who have
addressed my paper refuse to accept this as even possible. However, you
and I know it's not.
:
:I need to look up the F&P HAD cite you gave (thank you)
:before I have a hope of contributing any further to that thread.
:
Don't worry about it James. I'm tapped out on CF and I think I'm
going to try to exit the scene as gracefully as Steve Jones did a few
years back.
:Look, Kirk, you've done lots of emperical experiments in electrochem,
:right?
Nope, I could try to learn how to do it if I felt there was a reason
(which is why I have been looking at CF so hard for so long), but it
represents a change in direction for me. I basically do gas loading
experiments with metal hydrides, and particularly with tritium.
:What would it take for you to try the kind of codeposition
:experiment in http://www.bovik.org/codeposition/best.gif and let us all
:know what happens?
:
The biggest thing it would take is a belief that I was going to be able
to do any better than the current crop of CF researchers. You have to
understand that I give them (mostly) a lot of credit for _doing_ the
experiments, I just disagree with how they interpret their data.
I would love to se the CF question 'resolved', and I have been trying
to assist in that by defining minimum acceptable quality levels for
CF research (i.e. calorimetry must be shown to NOT have the CCS,
anomalous masses in MS must be shown to NOT be multiple atom/ionization
peaks, etc.), but I have been compeltely unsucessful in getting anyone
to listen. At this point, it's a waste of my time to do so, so I am
left with the choice between dropping it or doing it. Since my belief
at this point is that there is no CF, I choose to get on with the rest
of my research.
:Given the prestige of your lab, this ought to be something that you and
:your colleagues could put together without much hastle, isn't it?
Yes, we could put it together with a little effort and some help. But
should we spend gov't money to do so? That's the relevant question.
:You've
:got the best shot at a result with controversy-settling significance,
Not really, any current CFer could do it if they would just do good
analytical chemistry and not jump to conclusions.
:as everyone knows your reputation in the field is squarely based on your
:demolition of Storms' analysis. I agree you caught Storms asleep at the
:switch (or thermometer, as it were) and nobody can take that away from you.
:
Thanks. So far he doesn't agree though....even though he recently wrote
something to me that proved to me that he understood my points. I had
been assuming I wan't communicating well, and kept trying to explain more.
In fact, he understood but simply won't accept. I can't do anything about
that.
:I'm predicting you get the same results that Szpak and Bockris get, and I
:think you have the integrity to say so if you do.
:
Thanks for trusting me to that extent. I doubt Jed would agree with you.
:When we went through the review of the bibliography papers, I think you
:got the same impression I did (if for no other reason that we were looking
:at the same citations.) Whether you agree with the theory involving the
:implications of conservation of angular momenta of deuterons, I know you
:know enough of the idea that, from my perspective, since you have the
:integrity to look at Storms' data with the correct critical eye, then you
:ought to be curious enough to try what has been designed to be the least
:expensive and most conclusive of any possible confirmatory experiment.
:
:What do you say?
:
:Best wishes,
:James
Of all the issues in the CF field, the only thing I'm not that sure of today
(which is just an expression of my opinion) is low level tritum monitoring.
But until that impacts me directly, I am going to leave it alone, since it
is work at the trace level, and that is _always_ enormously difficult. I
believe that all the positive excess heat events reported so far are variants
on recombination, and I don't see an economic incentive to pursue that in
favor of what I am doing now. I'm sorry James, but any proposed research has
to meet the researcher's economic objectives as well.
In any case, I am going to try to say farewell here, since I do have a lot
of work to do in the immediate future, and I hope to stay that busy.
To everyone who remains: "Have fun if you can!"
Bye,
Kirk Shanahan