Tom Roberts to Anton Shepelev:

> > The purpose of the fitting is to combine the eight
> > partial drift-sequences (from the eight combined
> > azimuths) into as smooth a function as possible, thus
> > removing any singnal that is a function of the azimuth.
>
> No. The fitting does not "remove any signal that is a
> function of the azimuth".

You quote my reply to David Jones, whereas I explained this
is detail in my earlier reply to you[1]. No, it does,
because a deliberately bad fit, e.g. when all the seven
parameters are zero, will result in huge signal when you
subtract it from the observations, which is why you need a
/good/ fit. In other words, the fit, on account of its
quadratic nature, tries to make the differences between
consequtive orientations as uniform as possible:
min( da^2 + db^2 ) => da = db,
removing any non-uniformity (or signal) from the drift
model.

> The removal of signal(orientation) was performed by
> subtracting the values of the first 1/2-turn.

As I explained in the reply mentioned earlier, and also in
my analytic interpretation[2], this subtraction is redunant
because it does not affect the form of any of the partial
error-difference curves, but only offsets them along the
ordinate axis. Since your fitting algorithm is invariant to
such offsets. It will end up with exactly the same quadratic
curve (+ constant), with the fit parameters representing
signal(orientation).

Perhaps a numerical illustration is in order, because
concrete calculations are unambiguous. Suppose for
simplcity -- but without loss of generality -- that we make
the observations at 3 orientations in 3 turns as follows:

Observations Error Fitted 1 2 3
T/O 1 2 3 diffs Fitting Subseqs Final model 123123123
----------- -------- ------- --------- -----------------------
1 0 2 2 1: 0 3 6 D1 = 0 0 3 6 Observations: 022355688
2 3 5 5 2: 0 3 6 D2 = 1 1 4 7 Sys. drift : 012345678
3 6 8 8 3: 0 3 6 D3 = 2 2 5 8 Pure signal : 010010010

Mark Fitted 1 2 3
drifts: Fitting Subseqs Final model 123123123
-------- ------- --------- -----------------------
1: 0 3 6 S1 = 0 0 3 6 Observations: 022355688
2: 2 5 8 S2 = -1 1 4 7 Sys. drift : 012345678
3: 2 5 8 S3 = 0 2 5 8 Pure signal : 010010010

In case your newsreader messes up the formatting, see

https://pastebin.com/raw/vKVpWqq3

The illustaration above shows calculation of the systematic
drift by two methods: via error differences (obtained by
subracting the first turn from the rest) and via mark drifts
(without subtractive the first turn). As you see, both
approaches give identical models of the systematic drift and
signal, but in your version, the fitted parameters Di represent
the drift at the first turn and in mine (Si) -- the pure
negative signal (0 -1 0), with same linearly increasing drift.

I hope this little example convices you that subtration
of the first turn from the rest is a redundant operation.

> Because Miller's setup is woefully inadequate -- far too
> much drift, the instrument has air in its optical paths,
> and quantizing the data at 0.1 fringe is bigger than the
> putative signal.

Miller assumed the noise to be random, in which case
oversampling improves the resolution by a factor sqrt(20).
____________________
1. <20230310010415.84c44e01e4811631afd46fe0@gmail.moc>
2. <20230308153302.2e74b7a62f096863323df7dd@gmail.moc>

Tom Roberts:

> Here is a read-only link to a directory containing 67 of
> Miller's runs:

Thank you very much, Tom. I have downloaded the files and
confirm they are perfectly legible. Great job transcibing
those records!

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Tom Roberts:
> Anton Shepelev:
> > RichD:
> > > Tom Roberts:
> > >
> > > > Worse than lack of statistical errorbars is Miller's
> > > > lack of knowledge of digital signal
> > > > processing -- his analysis is essentially a comb
> > > > filter that concentrates his systematic error into
> > > > the DFT bin corresponding to a real signal -- that's
> > > > a disaster, and explains why his data reduction
> > > > yields data that look like a sinusoid with period
> > > > 1/2 turn.
> > >
> > > Can you elaborate on this filter?
> >
> > Mr. Roberts is referring to the procedure of "folding"
> > the data of each 16-azimuth turn into an 8-azimuth half-
> > turn by summing up the observations at azimuths 180
> > degrees apart.
>
> No. I am referring to Miller's averaging the 20 turns.

Sorry for the misunderstanding, them. Yes, Miller averaged
his observrations over 20 or more (full) turns.

> As his final result for a single run is the plot at the
> bottom of my Fig. 1, with 8 points,

No, that plot is not the final result of his analysis, but a
digression made for the purposes of merely a "preliminary
study" -- quoth Miller:

For the purpose of a preliminary study of the
observations, it is convenient to obtain an
approximate graphic representation of the effect by
the following procedure. The second half of the line
of sixteen average readings is placed under the first
half and the mean of the two numbers in each column is
obtained;

These half-period plots were /not/ used in the final analysis
(see below).

> my discussion is of the fact that he averaged 40 values to
> get each point of the plot.

Yes, he did average the 40 values for that plot, that is
averaged the 20 turns /and/ then folded the result in two.
But no, he did not employ the last (half-turn) averaging in
his actual data analysis:

In the definitive study of the ether-drift effect,
this set of sixteen average readings for the position
of the interference fringes is plotted to a large
scale and is subjected to mechanical harmonic analysis
to evaluate precisely the second harmonic component,
which represents the second-order, half-period ether-
drift effect;
[...]
The twenty or more readings for each of the sixteen
observed azimuths are averaged and the averages are
compensated for the slow linear shift of the whole
interference system during the period of observation,
as explained previously in connection with Fig. 9. The
average readings for each set are then plotted on
coordinate paper, to a large scale, for the purpose of
harmonic analysis.
[...]
These charted "curves" of the actual observa-tions
contain not only the second-order, half- period ether-
drift effect, but also a first-order, full-period
effect, any possible effects of higher orders,
together with all instrumental and accidental errors
of observation.
[...]
In order to evaluate precisely the ether-drift effect,
each curve of observations has been analyzed with the
Henrici harmonic analyzer for the first five terms of
the Fourier series.

The quotations above provide compelling evidence that Miller
did not combine the half-turn observations in his analysis.
Your second comb-filter, which raises the lowest DFT bin up
to the half-turn frequency, is absent from Miller's procedure,
whereas your first comb-filter, which raises the lowest DFT
bin up to the fundamental full-turn frequency, is no doubt
present.

> But this still holds for his averaging of all 16
> orientations -- it is still a comb filter, and with a
> rapidly-falling noise spectrum it pushes most of the noise
> into the lowest DFT bin.

Yes, no good, but in that case the lowest DFT bin is the
fundamental, full-perdoid, full-turn frequency, not the
half-turn one.

> Averaging raw data is a VERY BAD analysis technique. But
> back in 1933 this was not understood; we understand it
> today.

Absolutely correct, even as any transoformation that reduces
the amount information in the data before that information
can be availed of.

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Tom Roberts to Anton Shepelev:

> > [with continuous least squares fitting],
> > you would have been able to avoid combining opposite
> > orientaions and analyse the entire turns, with 15
> > degrees of freedom. With the half-turns combined, the
> > error differences beween opposite orientations are
> > "baked" into the partial curves and uncapable of
> > smoothing out.
>
> Yes, my approach could not handle 15 parameters. I'm not
> so sure that a conventional fitting program would reliably
> converge with that many parameters.

The linear least-squares method has a global optimum, so
that with continuous parameters and partial derivatives
convergence is guarranteed, nor is overfitting an issue. In
your case -- the tighter a fit, the better.

> > > So look at my Fig. 2 and say with a straight face that
> > > you think a signal with amplitude ~ 0.1 fringe can be
> > > extracted from the data.
> >
> > I do not have that Oscilloscopic, Harmonic-analysing,
> > Fourier-transforming vision that you seem to take for
> > granted :-) Yes, it looks awful.
>
> I am skeptical of ANY analysis that claims to pull a
> signal out of noise that is so very much larger.

I persume your experience entitles you to this opinion,
whereas we laymen, lacking statistical intuition, must
content ourselves with formal analysis.

> > The phase would indicate the direction, and the
> > amplitude -- the velocity of the aether wind speed as
> > projected upon the plane of the interferometer.
>
> Sure. That was Miller's intent. But with errorbars so very
> much larger than the variation in the data (Fig. 5), the
> errorbars on velocity will be enormous (and include 0),
> and the errorbars on direction will be much greater than
> 360 degrees. In other words. Miller's approach cannot
> determine the speed or direction of the "aether wind" at
> all.

I for one have not tested Miller's astronomical calculations
yet. If they are as good as he says then it must be a
miracle or one-in-a-million coincidence that the an absent
signal and a strong systematic drift of the device should
have produced a galactially-oriented signal.

> A modern analysis can reduce those errorbars considerably,
> as mine did...

Yet technically, your statistical model and its fitting are
quite simple.

> > The only justification is in the first sentence. Mr.
> > Roberts thinks he should use quantised model parameters
> > because the input data is quantised, whereas I see no
> > logical connection between the premise and conclusion.
>
> My analysis is fitting to find the DRIFT, not the signal.
> The DRIFT is inherently quantized by Miller's data taking.

Quantised are the obsererfations (o) of finge shift (f),
comprising signal s and drift d:

o = quantise(f)
f = s + d

Physically, none of these values is quantised, but the
method of observation quantises f. What harm can be in
fitting the drift in continuous parameters? If you must,
quantise them after the fitting.

> But before you get all excited about a potential aether
> model, first you must consider how it could agree with all
> the experiments that display quantum effects. No aether
> model to date has done so, and IMHO it seems EXTREMELY
> unlikely that one will ever do so. Electrodynamics is A
> LOT more than light beams and interferometers....

My current purpose being to understand Miller's results and
your analysis of them, I have not considered other
experiments and their reconcillication with an aether
theory.

> > No sceptic has been able to answer how all his
> > measurements made at different times of day and of the
> > year might have conspired to point at a fixed direction
> > in the galaxy.
>
> Experimenter's bias. Miller could not possibly avoid
> imposing his personal opinions, hopes, and dreams into his
> data. Such experiments REQUIRE data taking in a way that
> the experimenter cannot do that, or they are useless.

But experimenter's bias is excluded by design:

An assistant records these readings in order, on a
prepared form, starting with the reading corresponding
to the north or other noted azimuth [...] The observer
gives no attention to the azimuth. The reading is
determined by instantaneous visual estimation; it is
quite impracticable to use any kind of a scale in the
field of view because the width of the fringes is
subject to slight variation.
[...]
While readings are being taken, neither the observer
nor the recorder can form the slightest opinion as to
whether any periodicity is present, much less as to
the amount or direction of any periodic effect; the
taking of observations is quite unprejudiced and is
simply mechanical.

The conjecture that the data from several seasons points to
a single galactical direction due to experimenter's bias
requires extraordinary evidence. The observer did not have a
harmonic analysier and an astronomical computer in his mind
instantenuously to adjust his observations at the time of
making them! I expected you would rather plead an error in
their calculations or, at least, a loose degree of
correspondence between seasons. I have not estimated it.

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Once again, I’ll start afresh to avoid any impression that I been
following all the treads in detail.

Someone seemed to question motives for reconsidering past literature.
While there are good-purpose investigations of what a “modern” analysis
of data might yield, to possibly exemplify the benefits of such
analysis, my main thoughts here are about the clarity of the
descriptions of what was done. Overall, the aim is to allow things in
the future to be done better than they might otherwise have been done.

I should say that I haven’t looked at the 1933 paper, or other related
papers, and I can’t access the Shankland paper of 1955 as it is behind
a pay-wall. A thorough of the overall topic would need to consider all
of these. My own comments are limited to the 2006 paper, taken on its
own. I did see a comment elsewhere on the web to the effect that this
paper provides convincing evidence of something. I think it falls
rather short of that.

On the topic of the clarity of this paper, we can obviously rule out
deliberate obfuscation which leaves both a general vagueness and an
over-reliance on “standard procedures” in either physics or statistics,
where its reliance may not be explicitly stated. I would classify all
of that lack of clarity as essentially relying on telepathy. We can
hope to help future writers to avoid placing too much reliance on
telepathy.

In general one might distinguish discussion of past works under two
headings: “was what was done good enough?” and “was the description of
what was done good enough?”. For this one can introduce the concepts of
“good enough for what purpose?”. I won’t try and discuss the whole of
the 2006 paper but will instead concentrate on one minor part where my
previous comments were followed by a request for expansion.

I’ll discuss the part of the paper concerning the graph present shows
some of the data divided up into short subsections in time, with lines
summarising each. The description of how this was done is almost
totally non-existent and seems to rely on what one might call standard
practice. Let’s assume, for now, that a reader can make an accurate
guess as to what was done. Then the question of whether what was done
was good enough can be considered in the context of two possible
purposes for the graph:
(a) to enable and assist an informal viewpoint to be taken of the
behaviour of the series;
(b) to enable strong conclusions to be drawn about the behaviour of the
series.
I think the paper’s position is somewhere between the two, since the
considerations here are only preliminary to later analyses, but perhaps
guided those analyses. My conclusion is that what was done would have
been good enough for purpose (a), provided that readers were told of an
important caveat about what is presented since an informal
consideration of the graphs can informally take the caveat into
account. As for purpose (b), what was done was not good enough because
of the same necessary caveat.

Now there is some wishy-washy-ness introduced by dividing the overall
series into subsections, but this would be obvious to everyone and so
is not of immediate concern. To derive the lines that appear on the
plot, certain assumptions have to be made. Making such assumptions may
be what is usually done for some standard data analyses, but they
remain assumptions and there seems to be no way of justifying them
here. The effect of these assumptions is that the error-bands presented
may be too wide or too narrow. This is the “caveat” mentioned above.
Essentially, the data-analysis seems to be derived along the lines of
“let’s proceed on the basis that the observations within a subsection
are homogeneous and statistically independent.” It is this assumption
of independence that leads to the caveat, since it is not immediately
justified or justifiable. A theoretical approach seems to be of
doubtful use, partly because it would involve adequately defining what
is meant by a “local mean” since this seems to be what is being
estimated. I think there may be some data-analytical way of assessing
the validity of the assumption, and this might even extend to producing
a better estimate of the uncertainty in the estimate of the “local
mean”. Any of this would have been an adventure too far for the paper
itself. However there may be benefits from a subsequent investigation
of this or similar datasets so that future work can be improved.

There remains the question of the ambiguity in the description of what
was done to create the graphs. There seem to be two ambiguities apart
from not providing or referencing explicit formulae. The first concerns
the error-bars or error-bands: are these plus or minus one standard
error, or plus or minus two standard errors, or approximate confidence
intervals at a levels of 50% or 90% say. Different scientific fields
will have various standard practices. The second ambiguity relates to
the calculation of the width of the bands: presumably this is via
dividing an estimated variance by a sample size: is this estimated
variance obtained only from observations within the given subsection of
data, or is it pooled across a number of subsections? Such pooling
across subsections would seem necessary if there were only 2 or 3
observations within a subsection. Note that I am not asking for a
response here to these questions, just raising them for consideration
to describe the ambiguity.

Let me turn to the question of the effects of quantisation of the data.
It may be that in previous comments I have assumed too much importance
for this but possibly Prof Roberts has also done this. For example, in
other thread there was the question “do you seriously think you can
extract a sinewave signal with amplitude ~ 0.1 fringe from that data?”,
and I think a similar thought is in the paper. Assuming this question
relates to an overall analysis of data, rather than trying to identify
the signal locally in time using only local data, the answer is “yes”,
provided that you have a long enough stretch of data and provided that
the data hasn’t been munged before you get to analyse it. This could be
posed simply as a question of sample-size-determination for detecting a
signal of a given frequency within an estimated spectrum. Presumably
there is literature on this question. So the remaining question is how
much effect does quantising the observations have on the spectrum that
would result. An underlying sinewave signal will not simply disappear
because of quantisation. Brief thoughts on the mathematics of this
suggest that the size of any effect will depend on how the
quantisation-bins are aligned to the mean of the underlying process, as
well as the width of the bins. It seems the mathematics would be
tedious but possible, but would also involve special functions and thus
mean computers to get results for example cases. Thus it might be best
to investigate the effects of quantisation by simply simulating
long-enough stretches of data and estimating spectra for these. Of
course you could do a sample-size determination on the basis that the
analysis to be done would be a simple ordinary-least-squares regression
analysis including sine and cosine terms. This would yield formulae
involving variances and covariances rather than spectra, but
essentially the same possibilities exist. In either case you would be
evaluating the effects of quantisation without assuming that your final
analysis technique would necessarily be designed to be optimal in the
presence of quantisation.

On a different topic, the question was raised as to whether or not you
should join the separate sections data together to form as single time
series for an analysis. My response to this is:
(a) you shouldn’t mung the data if you don’t have to;
(b) to ask what would be the effect of joining the sections in a
different order (i.e. Would you get a different answer?). Is there some
obvious reason that demands some “natural order”.
(c) we need to distinguish between getting an estimate, getting an
optimal estimate, and getting an estimated uncertainty for the
estimate. For the last two you would need to know or estimate the
dependence within the observations. Thinking in terms of serial
dependence, you would need to know how you would treat such dependence
across joins in the data: one possibility is that you would want data
in the originally-distinct sections to be treated as statistically
independent across sections.

David Jones <dajhawkxx@nowherel.com> wrote:
[new aspects, so crosspost left in place, for once]

> Once again, I'll start afresh to avoid any impression that I been
> following all the treads in detail.
>
> Someone seemed to question motives for reconsidering past literature.
> While there are good-purpose investigations of what a "modern" analysis
> of data might yield, to possibly exemplify the benefits of such
> analysis, my main thoughts here are about the clarity of the
> descriptions of what was done. Overall, the aim is to allow things in
> the future to be done better than they might otherwise have been done.

You may have been refering to me.
Again for clarity: It seems to me that you and Mr. Roberts
are doomed to be talking past each other in some respects.
(precisely because your motives may be different)

You, as a data analyst, will want to look at the data, (so I guess)
to see what conclusions can be drawn from it. (if any)

Mr. Roberts otoh knows beforehand, from other (physical) arguments,
that the whole Miller experiment must be deeply flawed, in some way.

The aim of a reanalysis of it must therefore different.
The question is not what information there is in it, (none)
but instead: 'can we understand what went wrong?'.

In other words, Roberts was trying to do forensics.
It seems to me that he has done a credible job on it.
To come to an agrement you should not try to reanalyse the data,
once again, but you should instead try to see whether or not
the forensics by Roberts is a plausible explanation.

In forensic terms, the aim cannot be to establish
that the victim is dead, because there is no doubt about that.
The aim must be to find out how and why he came to be in that state,

Jan

J. J. Lodder wrote:

> David Jones <dajhawkxx@nowherel.com> wrote:
> [new aspects, so crosspost left in place, for once]
>
> > Once again, I'll start afresh to avoid any impression that I been
> > following all the treads in detail.
> >
> > Someone seemed to question motives for reconsidering past
> > literature. While there are good-purpose investigations of what a
> > "modern" analysis of data might yield, to possibly exemplify the
> > benefits of such analysis, my main thoughts here are about the
> > clarity of the descriptions of what was done. Overall, the aim is
> > to allow things in the future to be done better than they might
> > otherwise have been done.
>
> You may have been refering to me.
> Again for clarity: It seems to me that you and Mr. Roberts
> are doomed to be talking past each other in some respects.
> (precisely because your motives may be different)
>
> You, as a data analyst, will want to look at the data, (so I guess)
> to see what conclusions can be drawn from it. (if any)
>
> Mr. Roberts otoh knows beforehand, from other (physical) arguments,
> that the whole Miller experiment must be deeply flawed, in some way.
>
> The aim of a reanalysis of it must therefore different.
> The question is not what information there is in it, (none)
> but instead: 'can we understand what went wrong?'.
>
> In other words, Roberts was trying to do forensics.
> It seems to me that he has done a credible job on it.
> To come to an agrement you should not try to reanalyse the data,
> once again, but you should instead try to see whether or not
> the forensics by Roberts is a plausible explanation.
>
> In forensic terms, the aim cannot be to establish
> that the victim is dead, because there is no doubt about that.
> The aim must be to find out how and why he came to be in that state,
>
> Jan

You seem to have ignored everything I said in this post, which is that
the aim here is to discuss here whether what was in the 2006 paper
clear enoudgh to describe what he had done to reach his conclusions...
not to croiticise those conclusions or to reanalyse whatever data there
might have been or what might be available now.

"David Jones" <dajhawk18xx@@nowhere.com> wrote:

> J. J. Lodder wrote:
>
> > David Jones <dajhawkxx@nowherel.com> wrote:
> > [new aspects, so crosspost left in place, for once]
> >
> > > Once again, I'll start afresh to avoid any impression that I been
> > > following all the treads in detail.
> > >
> > > Someone seemed to question motives for reconsidering past
> > > literature. While there are good-purpose investigations of what a
> > > "modern" analysis of data might yield, to possibly exemplify the
> > > benefits of such analysis, my main thoughts here are about the
> > > clarity of the descriptions of what was done. Overall, the aim is
> > > to allow things in the future to be done better than they might
> > > otherwise have been done.
> >
> > You may have been refering to me.
> > Again for clarity: It seems to me that you and Mr. Roberts
> > are doomed to be talking past each other in some respects.
> > (precisely because your motives may be different)
> >
> > You, as a data analyst, will want to look at the data, (so I guess)
> > to see what conclusions can be drawn from it. (if any)
> >
> > Mr. Roberts otoh knows beforehand, from other (physical) arguments,
> > that the whole Miller experiment must be deeply flawed, in some way.
> >
> > The aim of a reanalysis of it must therefore different.
> > The question is not what information there is in it, (none)
> > but instead: 'can we understand what went wrong?'.
> >
> > In other words, Roberts was trying to do forensics.
> > It seems to me that he has done a credible job on it.
> > To come to an agrement you should not try to reanalyse the data,
> > once again, but you should instead try to see whether or not
> > the forensics by Roberts is a plausible explanation.
> >
> > In forensic terms, the aim cannot be to establish
> > that the victim is dead, because there is no doubt about that.
> > The aim must be to find out how and why he came to be in that state,
> >
> > Jan
>
> You seem to have ignored everything I said in this post, which is that
> the aim here is to discuss here whether what was in the 2006 paper
> clear enoudgh to describe what he had done to reach his conclusions...
> not to croiticise those conclusions or to reanalyse whatever data there
> might have been or what might be available now.

There may have been a conclusion in your lengthy discourse,
but, if so, I freely confess to having missed it,

Jan

On 3/12/23 6:25 AM, Anton Shepelev wrote:
> Tom Roberts to Anton Shepelev:
>> Yes, my approach could not handle 15 parameters. I'm not so sure
>> that a conventional fitting program would reliably converge with
>> that many parameters.
>
> The linear least-squares method has a global optimum, so that with
> continuous parameters and partial derivatives convergence is
> guarranteed, nor is overfitting an issue.

You OBVIOUSLY have never done this in practice. While in a mathematical
sense convergence is guaranteed, in the real world, with too many
parameters it is easy to "converge" to a nonsense result.

>> I am skeptical of ANY analysis that claims to pull a signal out of
>> noise that is so very much larger.
>
> I persume your experience entitles you to this opinion, whereas we
> laymen, lacking statistical intuition, must content ourselves with
> formal analysis.

This ought to be obvious -- just LOOK at the data from Miller's Fig. 1.

> I for one have not tested Miller's astronomical calculations yet. If
> they are as good as he says then it must be a miracle or
> one-in-a-million coincidence that the an absent signal and a strong
> systematic drift of the device should have produced a
> galactially-oriented signal.

As I said before, computing an average ALWAYS yields a result. In this
case, it is quite clear that experimenter's bias played a part -- Miller
"knew" what result he wanted, and by George he obtained it.

> But experimenter's bias is excluded by design: [...]

By Miller's account, sure. But modern knowledge supersedes that, and it
is quite clear that experimenter's bias was present. In particular, no
"blinding" was used, and we now know that is the only way to eliminate
experimenter's bias.

> The conjecture that the data from several seasons points to a single
> galactical direction due to experimenter's bias requires
> extraordinary evidence.

When none of his runs [#] determine a speed that excludes zero, and none
of his runs determine a phase (direction) with resolution less than 360
degrees, it is clear that the measurements cannot actually determine
such speed and direction, no matter how many runs are included. But
computing an average will yield an answer. Given his methods,
experimenter's bias cannot be ruled out.

[#] in my sample of 67 runs.

None of the old measurements will stand up to modern scrutiny, including
MIller's; to "find the aether" you need a new experiment with modern
resolutions and controls. But, of course, that (or equivalent) has
already been done many times, with negative results.

You are searching for a very specific needle, not in a haystack but in a
large box of identical needles -- hopeless (you cannot distinguish the
one you want from all the others).

Tom Roberts

Tom Roberts to Anton Shepelev:

> > The linear least-squares method has a global optimum, so
> > that with continuous parameters and partial derivatives
> > convergence is guarranteed, nor is overfitting an issue.
>
> You OBVIOUSLY have never done this in practice. While in a
> mathematical sense convergence is guaranteed, in the real
> world, with too many parameters it is easy to "converge"
> to a nonsense result.

Generally, LSM can overfit, but in your model it cannot: a
combination of the eight error-difference sequences cannot
be /too/ smooth.

> > I for one have not tested Miller's astronomical
> > calculations yet. If they are as good as he says then it
> > must be a miracle or one-in-a-million coincidence that
> > the an absent signal and a strong systematic drift of
> > the device should have produced a galactially-oriented
> > signal.
>
> As I said before, computing an average ALWAYS yields a
> result. In this case, it is quite clear that
> experimenter's bias played a part -- Miller "knew" what
> result he wanted, and by George he obtained it.

Do you believe in miracles, mind-matter interations, or
strongly emergent[1] properties? If you don't, pray explain
how Miller's desire can have affected the result.

> > But experimenter's bias is excluded by design: [...]
>
> By Miller's account, sure.

You snipped Miller's explanation why the experimenter's bias
had no effect on the result. Can you find a flaw in his
reasoning there?

> In particular, no "blinding" was used, and we now know
> that is the only way to eliminate experimenter's bias.

No, it is not the only one. Another is to decouple actual
observations from the final expected result, which depends
on the galactic orientation of the interferometer, totally
unknown to the operator.

> > The conjecture that the data from several seasons points
> > to a single galactical direction due to experimenter's
> > bias requires extraordinary evidence.
>
> When none of his runs [#] determine a speed that excludes
> zero,

It is true only in your statistical model and your method of
errorbar calculation.

> and none of his runs determine a phase (direction) with
> resolution less than 360 degrees,

Only in your model.

> it is clear that the measurements cannot actually
> determine such speed and direction, no matter how many
> runs are included.

But if, ignoring your error estimates, they do determine a
certain galactic velocity and direction, you will have to
explain this miraculous coincidence across the ~360 Mt.
Wilson observations. Instrumental error and noise cannot be
galactially oriented, and would result in largely varying
velelocity and random orientation, which is not the case.

> But computing an average will yield an answer.

Yes, but not one in which the phrase and amplitude agree
with a specific galactic direction in the undulations during
the day and across seasons of the year.
____________________
1. https://en.wikipedia.org/wiki/Emergence#Strong_and_weak_emergence

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On 3/15/23 12:10 PM, David Jones wrote:
> [...]

My paper was written for an audience of physicists. My three colleagues,
to whom I sent the paper for comments before putting it up on the arXiv,
had none of these issues or confusions.

Tom Roberts

On 3/18/23 4:32 PM, Anton Shepelev wrote:
> Tom Roberts to Anton Shepelev:
>> As I said before, computing an average ALWAYS yields a result. In
>> this case, it is quite clear that experimenter's bias played a
>> part -- Miller "knew" what result he wanted, and by George he
>> obtained it.
>
> Do you believe in miracles, mind-matter interations, or strongly
> emergent[1] properties? If you don't, pray explain how Miller's
> desire can have affected the result.

It is not I, it is psychologists and physiologists who have studied
"experimenter's bias". There is a large literature on this, and the
conclusion is that personal bias can influence results even when no
obvious mechanism can be identified -- "good intentions" are simply not
sufficient to eliminate bias in humans.

> No, it is not the only one. Another is to decouple actual
> observations from the final expected result, which depends on the
> galactic orientation of the interferometer, totally unknown to the
> operator.

At the top of every data sheet, Miller recorded the sidereal time. So he
knew much about the galactic orientation while taking data. That's
enough to support my claim of experimenter's bias.

[This was also not known in his day.]

>> When none of his runs [#] determine a speed that excludes zero,
>
> It is true only in your statistical model and your method of
> errorbar calculation.

And in Miller's -- he averaged 40 readings to make his final plot for
each run. The simple calculation of sigma/sqrt(40) is unassailable as
the minimum statistical errorbar on each point. For many if not most of
his runs these are larger than the variation of those averages.
Moreover, these errorbars are clearly dominated by the systematic drift,
so the readings are not independent and one probably should not divide
by sqrt(40)....

>> and none of his runs determine a phase (direction) with resolution
>> less than 360 degrees,
>
> Only in your model.

And in Miller's (he just did not realize it because he did not display
the errorbars).

The coincidence that several epoch's of his data result in similar
galactic orientations comes back to experimenter's bias. You cannot
eliminate it from Miller's data; that requires a whole new experiment
using modern techniques and data-analysis algorithms.

Tom Roberts

Tom Roberts:

> Here is a read-only link to a directory containing 67 of
> Miller's runs:
> https://www.dropbox.com/sh/8z5svuenaabegoq/AAAPrjK9AOqP-
> yyPRr5wNBwra?dl=0

Whoever is interested is welcome to study this data
converted into simpler, machine-readable formats:

http://freeshell.de/~antonius/file_host/RobertsMillerData.7z

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Tom Roberts wrote:

> On 3/15/23 12:10 PM, David Jones wrote:
> > [...]
>
> My paper was written for an audience of physicists. My three
> colleagues, to whom I sent the paper for comments before putting it
> up on the arXiv, had none of these issues or confusions.
>
> Tom Roberts

Well yes. Your other comments have noted via types of bias. You might
want to consider reviewers' bias.

David Jones to Tom Roberts:

> Your other comments have noted via types of
> bias. You might want to consider reviewers' bias.

Or the reviwer's lazyness. Knowing Thomas to be a reputable
physicist, they might choose not to dig into the finest
details of his paper. Futhermore, this paper being
concerned with statistics much more than with physics, it
may have been outside their primary line of interest and
expertise, which is another reason I brought it up here in
sci.stat.math (via Rich Ulrich).

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On 3/20/23 12:12 PM, RichD wrote:
> It's unclear what Miller's intent was. Did he believe Michelson's
> apparatus or observations were faulty? Did he revise those methods,
> an upgrade, so to speak?

Miller wanted to reproduce Michelson and Morley's results, with more
sensitivity. Remember that Miller was working at the institution that
has become CWRU, in the same building where the MMX was performed
(initially; he moved the interferometer elsewhere as well). He
refurbished the mercury pool and float that they used to permit the
interferometer to rotate smoothly, and added steel arms to give a much
longer optical path length. In doing so, he also made it significantly
more sensitive to temperature variations.

Unfortunately, Miller used the same analysis method, which is seriously
flawed -- this was not known until several decades after Miller
published, and until my paper nobody applied a modern analysis to
Miller's data.

Shankland et al (in 1955) performed a basic statistical analysis, and
concluded there are significant systematic errors in the data. But in
their paper they never actually plotted any data with errorbars. They
concluded that the second harmonic that Miller found was due to
temperature effects, but they did not apply the DSP algorithm to show
WHY the noise/drift appears as a second harmonic (the comb filter of the
analysis concentrates a noise spectrum that falls with frequency into
that specific frequency bin of a DFT).

Tom Roberts

Tom Roberts:

> Miller wanted to reproduce Michelson and Morley's results,
> with more sensitivity. Remember that Miller was working at
> the institution that has become CWRU, in the same building
> where the MMX was performed (initially; he moved the
> interferometer elsewhere as well). He refurbished the
> mercury pool and float that they used to permit the
> interferometer to rotate smoothly, and added steel arms to
> give a much longer optical path length. In doing so, he
> also made it significantly more sensitive to temperature
> variations.

Indeed, but then he insulated them and verified the result
with radiant parabolic heaters.

> Unfortunately, Miller used the same analysis method, which
> is seriously flawed -- this was not known until several
> decades after Miller published, and until my paper nobody
> applied a modern analysis to Miller's data.

Yes, and he also wrote that complete analysis of his data
would require a year's work of a "professional computer."

> Shankland et al (in 1955) performed a basic statistical
> analysis, and concluded there are significant systematic
> errors in the data. But in their paper they never actually
> plotted any data with errorbars. They concluded that the
> second harmonic that Miller found was due to temperature
> effects,

And of course they assumed it could not have been due to
aether, and ignored Miller's exteniive control experiments
and laboratory tests including measuremenents of temperature
sensitifity. I write this from second-hand sources, not
having Shankland's papaer on hand, because it does not seem
available for free download.

Yes, a temperature variation would produce a half-period
effect, but would it also produce a full-period effect, as
predicted by Hicks?

> but they did not apply the DSP algorithm to show WHY the
> noise/drift appears as a second harmonic (the comb filter
> of the analysis concentrates a noise spectrum that falls
> with frequency into that specific frequency bin of a DFT).

I have already explained that this statement of your is
inaccurate, because the second comb-filter, which would move
the signal into the lowest DFT bin, was absent from Miller's
actual procedure. See my post:

From : Anton Shepelev <anton.txt@gmail.moc>
Date : Sun, 12 Mar 2023 01:51:41 +0300
Subject: Re: statistics in Roberts' paper on Miller
URL : http://al.howardknight.net/?ID=167939199000

You are welcome to answer that article.

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