[I am the author of the arxiv paper 0608238v2.pdf, from 1986.
I have just started reading sci.stat.math. I will respond in this post
to all of the posts in this thread that exist right now, consolidating
them; I will respond to the thread as long as it makes sense to do so. I
will not read the unrelated alt.usage.english, and after this post will
not include it. I am cross-posting to sci.physics.relativity.]

On 2/27/23 3:00 PM, Rich Ulrich wrote:
> [Roberts' new] analysis itself occupies about two pages in Section
> IV of this article:
> https://arxiv.org/vc/physics/papers/0608/0608238v2.pdf

That is the paper I wrote, back in 1986.

> Modern statistical analyses and design sophistication for statistics
> were barely being born in 1933, when the Miller experiment was
> published. [...]

Yes. I mentioned that in the paper. 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. In short, this is every
experimenter's nightmare: he was unknowingly looking at statistically
insignificant patterns in his systematic drift that mimicked the
appearance of a real signal.

See sections II and III of the paper.

> Also, 'messy data' (with big sources of random error) remains a
> problem with solutions that are mainly ad-hoc (such as, when Roberts
> offers analyses that drop large fractions of the data).

I did not "drop large fractions of the data", except that I analyzed
only 67 of his data runs, out of more than 1,000 runs. As my analysis
requires a computer, it is necessary to type the data from copies of
Miller's data sheets into the computer. I do not apologize for doing
that for only a small fraction of the runs (I had help from Mr. Deen).
The 67 runs in section IV of the paper are every run that I had.

> Roberts shows me that these data are so messy that it is hard to
> imagine Miller retrieveing a tiny signal from the noise, if Miller
> did nothing more than remove linear trends from each cycle.

Yes. See figures 2,3,4 of the paper. A glance at Fig. 2 shows how
terrible the drift actually is (almost 6 fringes over 20 turns, more
than 50 times larger than the "signal" Miller plotted in Fig. 1). The
fact that the dots do not lie on the lines of Fig. 3 shows how
inadequate it is to assume a linear drift, by an amount as much as
10 times larger than the "signal" he plotted.

Had Miller displayed his actual data plots, like my Fig. 2, or the
nonlinearities as in my Fig. 3, nobody would have believed he could
extract a signal with a peak-to-peak amplitude <0.1 fringe. Both of
those are well within his capabilities.

> I would want to know how the DEVICE made all those errors possible,

It is drifting, often by large amounts -- so large that in most runs
Miller actually changed the interferometer alignment DURING THE RUN by
adding weights to one of the arms (three times in the run of Fig. 1).
Even so, there are often jumps between adjacent data points of a whole
fringe or more -- that is unphysical, and can only be due to an
instrumentation instability.

Modern interferometers are ENORMOUSLY more stable. In the precision
optics lab I manage, we have a Michelson interferometer that is ~ 10,000
times more stable than Miller's. We use it to stabilize lasers, not
search for an aether. That stability includes a lack of 12-hour
variations, with a sensitivity of ~ 0.00002 fringe (~ 10,000 times
better than Miller's).

> If you are wondering about how he fit his model, I can say a little
> bit. The usual fitting in clinical research (my area) is with
> least-squares multiple regression, which minimizes the squared
> residuals of a fit. The main alternative is Maximum Likelihood,
> which finds the maximum likelihood from a Likelihood equation. That
> is evaluated by chi-squared ( chisquared= -2*log(likelihood) ).
> Roberts seems to be using some version of that, though I didn't yet
> figure out what he is fitting.

See Section IV of the paper. As described, the analysis starts by
modeling the data as
data = signal(orientation) + systematic(time)
The challenge is to separate these two components. By taking advantage
of the 180-degree symmetry of the instrument, only 8 orientations are
used. Since signal(orientation) is the same for every 1/2 turn, by
subtracting the data of the first 1/2-turn from the data for every 1/2
turn, signal(orientation) is canceled and the result contains just
systematic(time), with each orientation individually set to 0 at the
first point (of 40). The time dependence of each orientation is
preserved. Here "time" is represented by data points taken successively
at each of 16 markers for each of 20 turns, so there are 16*20=320
"time" points; my plots are labeled "Turn" (not "time").

Once the systematic has been isolated for each orientation (see Fig.
10), the idea is to restore the time dependence of the systematic and
then subtract it from the data. Because the first 1/2 turn was
subtracted everywhere, each of the 8 orientations starts at 0. So to put
them together into a single time sequence I introduced 8 parameters,
each representing the systematic value for one orientation in the first
1/2 turn. Because the ChiSq is a sum of differences, it is necessary to
fix the overall normalization, which I did by holding the parameter for
markers 1 and 9 fixed at 0. So the fit varies 7 parameters with the goal
of making the time series as smooth as possible. The ChiSq is the sum of
319 terms corresponding to the differences between successive points of
the time series for the systematic (a difference for each dot in Fig. 10
except the first). Note each entry is subtracting values for two
successive orientations, because that is how the data were collected;
this is clearly a measure of the smoothness of the overall time
sequence. The errorbar for computing the ChiSq was set at 0.1 fringe,
because that is the quantization of the data; similarly the parameters
were quantized at 0.1 fringe. Conventional fitting programs don't work
with quantized parameters (they need derivatives), so I just performed
an exhaustive search of sets of the 7 parameters, looking for minimum ChiSq.

Note I did NOT do the simple and obvious thing: use the data for the
first 1/2 turn as the values of the parameters. That would reintroduce
signal(orientation) and make the analysis invalid.

Once the full time sequence of the systematic drift has been determined,
it is subtracted from the raw data to obtain signal(orientation). For
most of the runs (53 out of 67, closed circles in Fig. 11), the
systematic model reproduces the data exactly. The other 14 runs exhibit
gross instability (see section IV of the paper).

> I thought it /was/ appropriate that he took the consecutive
> differences as the main unit of analysis, given how much noise there
> was in general. From what I understood of the apparatus, those are
> the numbers that are apt to be somewhat usable.
>
> Ending up with a chi-squared value of around 300 for around 300 d.f.
> is appropriate for showing a suitably fitted model -- the expected
> value of X2 by chance for large d.f. is the d.f. A value much
> larger indicates poor fit; much smaller indicates over-fit.

Yes. In this case it means my guess of 0.1 fringe for the errorbars was
appropriate.

David Jones wrote:
> I have heard some non-statistical experts in other fields just using
> "chi-squared" to mean a sum of squared errors.

I used the term as it is commonly used in physics. It is a sum of
squared differences each divided by its squared errorbar. Having no
actual errorbars, I approximated them by using a constant 0.1 fringe,
which is the quantization Miller used in recording the data.

> My guess is that some of the stuff in this paper is throwing-out
> some information about variability in whatever "errors" are here.

Within each run, no data were "thrown out"; from the set of 67 runs I
had, no runs were "thrown out". But criticism about using just 67 runs
out of >1,000 is valid. But realistically, since these 67 runs show no
significant signal, and display such enormous drift of the instrument,
does anybody really expect the other runs to behave differently?

> If this were a simple time series, one mainstream approach from
> "time-series analysis" would be to present a spectral analysis of a
> detrended and prefiltered version of the complete timeseries, to try
> to highlight any remaining periodicities.

Fig. 6 is a DFT of the data considered as a single time series 320
samples long, for the run in Fig. 1. Here "time" is sample number, 0 to 320.

> There would seem to be a possibility of extending this to remove
> other systematic effects.

What "other systematic effects"? -- all of them are contained in
Miller's data, which were used to model systematic(time).

Tom Roberts <tjoberts137@sbcglobal.net> wrote:

> [I am the author of the arxiv paper 0608238v2.pdf, from 1986.
> I have just started reading sci.stat.math. I will respond in this post
> to all of the posts in this thread that exist right now, consolidating
> them; I will respond to the thread as long as it makes sense to do so. I
> will not read the unrelated alt.usage.english, and after this post will
> not include it. I am cross-posting to sci.physics.relativity.]

But you forgot to set the Follow-up To:
Now done.
[-]
> Miller's experiment is "seminal" only to cranks and people who don't
> understand basic experimental technique. The interferometer is so very
> unstable that his measurements are not worth anything --
[-] Yes.
> In the precision optics lab I manage, we have a Michelson interferometer
> that is ~ 10,000 times more stable than Miller's. We use it to stabilize
> lasers, not search for an aether. That stability includes a lack of
> 12-hour variations, with a sensitivity of ~ 0.00002 fringe.

Yes, but your interferometer is no doubt in a stable environment.
Dayton Miller, following Michelson,
would explain your stable results with complete aether drag.
This was already a fringe idea in the time of Michelson.
Nowadays it is a downright crackpot explanation,
because it directly contradicts many other established physical results.
Dayton Miller thought that doing his experiment on a mountain top,
and not enclosed by walls was a physical precondition
for obtaining non-zero results. [see below]

I repost what I said in AUE on the physics background
for the benefit of SPR and SSM, where it didn't appear,

Jan

[reposted material]
=========================================================================
There is a good physics reason for that.
Michelson had tried to explain his null result
by postulating complete aether drag.
(caused by the building he was in, and the solid earth beneath) [1]
He insisted that his experiment should be repeated on a mountain top,
and as much as possible in the open air. (so no solid walls)
Dayton Miller compromised by having a tent-like structure
to shield his interferometer as much as possible
from the worst of the temperature fluctuations.

So in a sense he was on a mission impossible of his own making.
If he had a null result, nothing special.
If he did find a non-zero result nobody would believe
that he could have controlled the circumstances adequately.

The reanalysis of Shankland and Roberts confirm just that.
The results of Dayton Miller are compatible with a null result,

Jan

[1] Aether drag is also ruled out by a number of other experiments,
such as stellar aberation, Sagnac, and several others.

On Sun, 5 Mar 2023 12:48:31 -0600, Tom Roberts
<tjoberts137@sbcglobal.net> wrote:

Thanks for the responses here. Interesting.

me >
>> Also, 'messy data' (with big sources of random error) remains a
>> problem with solutions that are mainly ad-hoc (such as, when Roberts
>> offers analyses that drop large fractions of the data).
>
>I did not "drop large fractions of the data", except that I analyzed
>only 67 of his data runs, out of more than 1,000 runs.

It was someone else who was concerned with the 1000 runs.

I wish I had been clearer -- I was pleased that you paid attention
to badness of scores, as you indicated later in this response:

> For
>most of the runs (53 out of 67, closed circles in Fig. 11), the
>systematic model reproduces the data exactly. The other 14 runs exhibit
>gross instability (see section IV of the paper).

In my data universe, dropping 14 of 67 runs is a large fraction of
the data. However: Doing that is preferable to lumping those
high-variance runs ("gross instability"), with their impossible data,
together with the runs that are (most of them) not impossible.
Thank you for the long explanations. Unfortunately, I still don't
understand the device or the measurements or their errors.
My physics ended before I learned about interferometers, and
the little I picked up doesn't tell me about this experiment.

Given my further gap in understanding the method of analysis,
and my conviction that you have shown there is nothing there,
I remain not-interested in studying the question.

As a data analyst, what satisfied me is what you showed in
the figure as the results of runs. I take the results for 67
(or 53) runs as replications of the main parameter. There are
53 values of zero (if I understand correctly); plus 14 values that
are non-zero from the 'unstable' runs.

The good runs, identical at zero, show there is zero effect.

It is conceivable that the unstable runs are similar enough that
the pooled (67) runs would test as 'significantly different from
zero' by a t-test against zero. If so, the proper conclusion, all
in all, would be that the unstable runs carry systematic error.

--
Rich Ulrich

Hello, Tom:

> I am the author of the arxiv paper 0608238v2.pdf, from
> 1986.

I find your statistical procedure in section IV described
somewhat hurriedly so that I, as well as some other readers,
had trouble understanding it. Below I describe in detail and
with equations, yet with maximum concision, my best
understanding of your transformations of the raw Miller
data. Please, let me know whether I interpolate them
correctly. I hope it will enable statisticians to see your
procedure with better clarity.

The raw data is a series of 20 runs, or interferometer
revolusions (r), with fringe shift observations (S) taken at
sixteen equidistant azimuths (a): S[r,a], where 1<=r<=20 and
1<=a<=16. You propose a model expressing the observations as
a combination of aether drift D and systematic error E:

S[r,a] = D[a] + E[t] ,

where the drift is a function of orientation and the error a
function of time. Time, in turn, may be considered equal to
the observation number within the entire run, expressed in
the number of revolutions:

t[r,a] = r + (a-1)/16 ,

so that a function of (r,a) is also a function of time, and:

E[r,a] = E(t) = E[r + (a-1)/16] .

You then observe that the signal D[a] may be cancelled out
by subtracting the first run form the rest for each azimuth.
Taking advantage, however, of the half-periodic symmetry in
the predicted effect, you combine the observations half a
cycle apart, defining eight interleaved sequences Ed[a] of
systematic-error differences:

Ed[r,a] = E[r,a] - E[1,a]
Ed[a](r + (a-1)/16) = S[r,a] - S[1,a] ,

each of which evaluates twice per revolution. From now on,
the azimuth of the folded data is in [1,8]. These eight
Ed[a]'s are plotted in your figure 10.

Whereas Ed[a] are interlevaed in time, it is reasonable to
assume they should combine into a single smooth function of
systematic-error difference Edc(t) with 8*2*20 = 320
equidistant samples:

Edc(t) = Ed[a](t) + B[a], 1 <= a <= 8 .

Edc(t) is specified with eight degrees of freedom,
corresponding to the baselines B[a] of the error-differences
for individual combined orientations. Since the whole model
is invariant to a constant additive, you fixed the baseline
of the first sequence at zero:

B[1] = 0

ending up with seven degrees of freedom, wich you fitted on
a computer to obtain as smooth a Edc(t) as possible.
Knowing B[a], the systematic error can be restored:

E[r,a ] = S[r,a ] - S[1,a ] + B[a]
E[r,a+8] = S[r,a+8] - S[1,a+8] + B[a] .

And the ether-drift is calculated by subtracting the error
from the raw data:

D[a] = S[r,a] - E[r,a] .
--
() ascii ribbon campaign -- against html e-mail
/\ www.asciiribbon.org -- against proprietary attachments

Tom Roberts:
> David Jones:
>
> > Also, 'messy data' (with big sources of random error)
> > remains a problem with solutions that are mainly ad-hoc
> > (such as, when Roberts offers analyses that drop large
> > fractions of the data).
>
> I did not "drop large fractions of the data", except that
> I analyzed only 67 of his data runs, out of more than
> 1,000 runs.

So you did not include 93% of data, for the reason stated
below:

> As my analysis requires a computer, it is necessary to
> type the data from copies of Miller's data sheets into the
> computer. I do not apologize for doing that for only a
> small fraction of the runs (I had help from Mr. Deen).
> The 67 runs in section IV of the paper are every run that
> I had.

What I regret is that you selected the 67 runs from
disparate experiments, instead of from the ones Miller
considered his best (and might prove his
worst!) -- performed on Mt. Wilson. Are you certain you did
not pick some of the sheets recording laboratory tests of
the interferometer, including those to determine the effect
of temperature irregularities, rather than actual ether-
drift measurements?

> It is drifting, often by large amounts -- so large that in
> most runs Miller actually changed the interferometer
> alignment DURING THE RUN by adding weights to one of the
> arms (three times in the run of Fig. 1).

To avoid the wrong imporession, he /never/ readjusted the
interferometer mid-turn, but always during a special
calibaration turn, when no observations were being made. In
other words, those adjustments took place /between/ complete
full-turn series of observations and no doubt contribute
large and sudden discontinuitites into your error-difference
functions, for I think you did not sew-together the
observation turns separated by such calibration turns, prior
to fitting the model of systematic drift. These
calibration-caused irregularities may have a negative effect
upon the fitting of combined systematic drift.

> Even so, there are often jumps between adjacent data
> points of a whole fringe or more -- that is unphysical,
> and can only be due to an instrumentation instability.

Not all the errors are systematic, as Miller himself noticed
the action of sound in disturbing the air in the
interferometer light path, let alone those due to the
hypothetical aether wind, which, if partially entrained,
will be affected by atmospheric turbulances, as well as show
the typical instabilities occuring when a laminar flow meets
with obstacles.

> Modern interferometers are ENORMOUSLY more stable. In the
> precision optics lab I manage, we have a Michelson
> interferometer that is ~ 10,000 times more stable than
> Miller's. We use it to stabilize lasers, not search for an
> aether. That stability includes a lack of 12-hour
> variations, with a sensitivity of ~ 0.00002 fringe (~
> 10,000 times better than Miller's).

How interesting. Is it installed in a basement and/or
screened off from the hyphothetical aether by metal? I
should like to see it installed in a triple-glass casement
on Mt. Wilson and left for an entire year. Hardly possible,
of course...

> By taking advantage of the 180-degree symmetry of the
> instrument, only 8 orientations are used.

No, I think you are taking advantage of the 180-degree
symmetry of the hypothesised effect rather than of the
instrument, which itself may be asymmetrical due to many
factors, including an asymmetrical air flow and temperature
in the aether house.

> Note I did NOT do the simple and obvious thing: use the
> data for the first 1/2 turn as the values of the
> parameters. That would reintroduce signal(orientation) and
> make the analysis invalid.

The subtraction of the first turn has but one effect -- that
of offsetting each of the eight error-difference curves by a
constant value, equal to the observation in the first turn
at the corresponding azimuth. It has /no/ effect on the
forms of those curves. Since your fitting consists in
finding the seven relative vertical offsets between these
curves, it may safely be applied to the raw drifts at each
combined mark, in which case the seven fit parameters will
represent the pure signal, if any!

Tom Roberts:
> David Jones:
>
> > I have heard some non-statistical experts in other
> > fields just using "chi-squared" to mean a sum of squared
> > errors.
>
> I used the term as it is commonly used in physics. It is a
> sum of squared differences each divided by its squared
> errorbar.

So you used a weighted form the of least-squares. But then
a complete enumeration is unnecessary, becuase least-squares
is designed to be an analitical method with linear
complexity: you simply write the smoothness function as a
sum of weighted squared differences over the tabulated data
and optimise it the usual way via partial derivatives.
Notice, however, that large discontinuitites between runs
due to interferomenter calibration are likely to dominate
the fitting.

> But criticism about using just 67 runs out of >1,000 is
> valid.

That critisicm is mine, Tom, and I would clarify that the
entire set of the Mt. Wilson experimenets, consisting of
some 350 runs, would make happy.

Tom Roberts:
> David Jones:
>
> > If this were a simple time series, one mainstream
> > approach from "time-series analysis" would be to present
> > a spectral analysis of a detrended and prefiltered
> > version of the complete timeseries, to try to highlight
> > any remaining periodicities.
>
> Fig. 6 is a DFT of the data considered as a single time
> series 320 samples long, for the run in Fig. 1.

Unfortunatly, this is affected by the discontinuities due to
the several calibration turns, which is why I recommended
that you sew them together beforehand.

> Similar experiments with much more stable interferometers
> have detected no significant signal.

Were they performed according to Michelson's and Miller's
emphatic instructions not to obstruct the light path and the
aether flow, which includes raising the device as well as
possible above any terrestrial features?

> Arxiv says it was last revised 15 Oct 2006; the initial
> submission year and month are enshrined in the first four
> digits of the filename.

Which is why I thought it was published in 2006 rather than
in 1986. The earlier dates explains a lot.

> > Anton Shepelev wrote: there are no time readings in
> > Miller's data.
>
> Yes, but that doesn't matter, as time is not relevant;
> orientation is relevant, and that is represented by
> successive data points, 16 orientations for each of 20
> turns.

It is of some relevance where you consider it continuous
between turns, ignoring the unrecorded calibration turns,
are observing instabilities of high rate and magnitude at
points where two observations turns were interrupted by a
calibration turn.

> Note that Miller never presented plots of his data (as I
> did in Fig. 2).

I see that has the adjustments included, as I am sure you
had to do for the statiscical reanalysis in section IV as
well. Did you do it?

> Had he displayed such plots, nobody would have believed he
> could extract a signal with a peak-to-peak amplitude < 0.1
> fringe.

Why not? Assuming, as Miller did, the plot to consist of
signal, linear drift, and random noise, they would well
believe that oversampling would help rescue the signal,
produducing the nice smooth curves that Miller had.

What is your opinion regarding the claimed galactic
orientation of the measured drift, as plotted in fig. 22 of
the 1933 paper? Can an instumental error have a concistent
half-periodic dependency on 1) time of day and 2) the season
of the year so as to point into a fixed direction in the
galaxy?

> > [further analysis is] impossible without Miller's
> > original data
>
> Miller's original data sheets are available from the CWRU
> archives. They charge a nominal fee for making copies.
> IIRC there are > 1,000 data sheets. Transcribing them into
> computer-readable form is a daunting

I believe doing even the 67 was tiring. Do you know anyone
who could help me in obtaining the 350 sheets from the Mt.
Wilson experiements if I cannnot travel to CWRU in person?
I will pay the costs, of course.

Tom Roberts:
> Anton Shepelev:
>
> > Exactly, and I bet it is symbolic parametrised funtions
> > that you fit, and that your models include the random
> > error (noise) with perhaps assumtions about its
> > distribution.
>
> I don't know what you are trying to say here, nor who
> "you" is.

This is because you have chosen to reply to everybody in one
huge message. It was Rich Ulrich I was addressing.

> But yes, my model has no explicit noise term because it is
> piecing together the systematic error from the data with
> the first 1/2 turn subtracted; any noise is already in
> that data. Virtually all of the variation is a systematic
> drift, not noise, and I made no attempt to separate them.

On 3/5/23 12:48 PM, Tom Roberts wrote:
> [I am the author of the arxiv paper 0608238v2.pdf, from 1986...]

My mistake, it was 2006.

Tom Roberts

On 3/5/23 2:47 PM, J. J. Lodder wrote:
> Tom Roberts <tjoberts137@sbcglobal.net> wrote:
>> In the precision optics lab I manage, we have a Michelson
>> interferometer that is ~ 10,000 times more stable than Miller's.
>> We use it to stabilize lasers, not search for an aether. That
>> stability includes a lack of 12-hour variations, with a
>> sensitivity of ~ 0.00002 fringe.
>
> Yes, but your interferometer is no doubt in a stable environment.

Absolutely. Our lab is amazingly stable, as we see no trace of the
elevated and Metra trains a block away, nor of traffic on State St. 100
yards away, nor of waves on Lake Michigan a mile away. It is in the
basement, in a room designed and built to house a nuclear reactor
(removed in the 1970s or 80s); it has an exceptionally thick concrete
floor with concrete walls.

Tom Roberts

On 3/6/23 10:08 PM, Rich Ulrich wrote:
> On Sun, 5 Mar 2023 12:48:31 -0600, Tom Roberts
> <tjoberts137@sbcglobal.net> wrote:
>> For most of the runs (53 out of 67, closed circles in Fig. 11), the
>> systematic model reproduces the data exactly. The other 14 runs
>> exhibit gross instability (see section IV of the paper).
>
> In my data universe, dropping 14 of 67 runs is a large fraction of
> the data.

I did not "drop" them, each one appears in Fig. 11.

Remember that my criterion for being an unstable run was that it have 5
or fewer stable turns (out of 20 total turns). My model of the
systematic drift cannot be expected to be valid for such unstable runs.

> As a data analyst, what satisfied me is what you showed in the
> figure as the results of runs. I take the results for 67 (or 53) runs
> as replications of the main parameter. There are 53 values of zero
> (if I understand correctly); plus 14 values that are non-zero from
> the 'unstable' runs.

Actually, five of the unstable runs have a zero result.

Tom Roberts

On 3/8/23 6:33 AM, Anton Shepelev wrote:
> Tom Roberts wrote:
>> I am the author of the arxiv paper 0608238v2.pdf, from 1986.

Oops. 2006.

> I find your statistical procedure in section IV described somewhat
> hurriedly so that I, as well as some other readers, had trouble
> understanding it. Below I describe in detail and with equations, yet
> with maximum concision, my best understanding of your transformations
> of the raw Miller data. Please, let me know whether I interpolate
> them correctly. I hope it will enable statisticians to see your
> procedure with better clarity.
>
> The raw data is a series of 20 runs, or interferometer

20 TURNS, not "runs". There are 67 runs, each consisting of of 20 turns.
Turn = rotation. These are Miller's terms, and I followed him.

Please don't change the meaning of technical words.
run != turn.

> revolusions (r), with fringe shift observations (S) taken at sixteen
> equidistant azimuths (a): S[r,a], where 1<=r<=20 and 1<=a<=16. You
> propose a model expressing the observations as a combination of
> aether drift D and systematic error E:
>
> S[r,a] = D[a] + E[t] ,
>
> where the drift is a function of orientation and the error a
> function of time. Time, in turn, may be considered equal to the
> observation number within the entire run, expressed in the number of
> revolutions:
>
> t[r,a] = r + (a-1)/16 ,
>
> so that a function of (r,a) is also a function of time, and:
>
> E[r,a] = E(t) = E[r + (a-1)/16] .
>
> You then observe that the signal D[a] may be cancelled out by
> subtracting the first run form the rest for each azimuth. Taking
> advantage, however, of the half-periodic symmetry in the predicted
> effect, you combine the observations half a cycle apart, defining
> eight interleaved sequences Ed[a] of systematic-error differences:
>
> Ed[r,a] = E[r,a] - E[1,a] Ed[a](r + (a-1)/16) = S[r,a] -
> S[1,a] ,
>
> each of which evaluates twice per revolution. From now on, the
> azimuth of the folded data is in [1,8]. These eight Ed[a]'s are
> plotted in your figure 10.
>
> Whereas Ed[a] are interlevaed in time, it is reasonable to assume
> they should combine into a single smooth function of
> systematic-error difference Edc(t) with 8*2*20 = 320 equidistant
> samples:
>
> Edc(t) = Ed[a](t) + B[a], 1 <= a <= 8 .
>
> Edc(t) is specified with eight degrees of freedom, corresponding to
> the baselines B[a] of the error-differences for individual combined
> orientations. Since the whole model is invariant to a constant
> additive, you fixed the baseline of the first sequence at zero:
>
> B[1] = 0
>
> ending up with seven degrees of freedom, wich you fitted on a
> computer to obtain as smooth a Edc(t) as possible. Knowing B[a], the
> systematic error can be restored:
>
> E[r,a ] = S[r,a ] - S[1,a ] + B[a] E[r,a+8] = S[r,a+8] - S[1,a+8]
> + B[a] .
>
> And the ether-drift is calculated by subtracting the error from the
> raw data:
>
> D[a] = S[r,a] - E[r,a] .

That looks correct. I don't see what use it might be.

> What I regret is that you selected the 67 runs from disparate
> experiments, instead of from the ones Miller considered his best
> (and might prove his worst!) -- performed on Mt. Wilson.

We have different criteria. I wanted to span his entire record.

> Are you certain you did not pick some of the sheets recording
> laboratory tests of the interferometer, including those to determine
> the effect of temperature irregularities, rather than actual ether-
> drift measurements?

Yes.

> To avoid the wrong imporession, he /never/ readjusted the
> interferometer mid-turn, but always during a special calibaration
> turn, when no observations were being made.

Yes.

> In other words, those adjustments took place /between/ complete
> full-turn series of observations and no doubt contribute large and
> sudden discontinuitites into your error-difference functions, for I
> think you did not sew-together the observation turns separated by
> such calibration turns, prior to fitting the model of systematic
> drift.

I _DID_ "sew them together". Miller recorded the value at orientation 1
just before the adjustment turn, and again just after it. For all data
thereafter I added (before-after) to every value, thus canceling the
effect of his adjustment, as best as can be done. This was done just
after reading the data file, before any analysis or plotting.

While I was at CWRU in 2006, after giving a colloquium on this analysis,
Prof. Fickinger and I visited the archives and spent an hour or two
scanning Miller's data sheets for runs without adjustments, indicating
the instrument was more stable than usual. We found several dozen, but I
never got around to analyzing them. I did look at them, and many of them
are just a monotonic drift from start to finish -- no signal at all.

[It certainly helped to be accompanied by a member of
the CWRU faculty who was well known to the archives
staff.]

> These calibration-caused irregularities may have a negative effect
> upon the fitting of combined systematic drift.

Hmmm. The instability of the instrument is at fault. The procedure I
used is the best that can be done, given Miller's methods.

> Not all the errors are systematic, as Miller himself noticed the
> action of sound in disturbing the air in the interferometer light
> path, let alone those due to the hypothetical aether wind, which, if
> partially entrained, will be affected by atmospheric turbulances, as
> well as show the typical instabilities occuring when a laminar flow
> meets with obstacles.

None of those are anywhere close to the magnitude of the drift.
Moreover, if they are in Miller's data then they are in my model of the
systematic.

>> Modern interferometers are ENORMOUSLY more stable. In the
>> precision optics lab I manage, we have a Michelson interferometer
>> that is ~ 10,000 times more stable than Miller's. We use it to
>> stabilize lasers, not search for an aether. That stability includes
>> a lack of 12-hour variations, with a sensitivity of ~ 0.00002
>> fringe (~ 10,000 times better than Miller's).
>
> How interesting. Is it installed in a basement and/or screened off
> from the hyphothetical aether by metal?

Our lab is located in the basement, in a room with an extra-thick
concrete floor and concrete walls; there surely is rebar inside them. We
instrument it by measuring frequency, and are not limited to an
eyeball's resolution of ~ 0.1 fringe.

[Also it has unequal arms, differing by 0.55 m (in
our application the length of the arms doesn't
matter, what matters is their difference); the
arms are about 10cm and 65cm long. The lasers have
a coherence length > 10 meters.]

> I should like to see it installed in a triple-glass casement on Mt.
> Wilson and left for an entire year. Hardly possible, of course...

That would be extremely arduous and expensive; it is not interesting to
us. For about $50,000 and a year of effort you could build a pair of
them and instrument the heterodyne between lasers locked to each. Point
one arm straight up so it behaves differently with orientation than the
other one (with two horizontal arms). Dedicate another year or two of
your life to taking data....

[Attempting to put them on a rotating table is
hopeless, as you can never get the vertical arm
to be vertical accurately enough; microradians
matter.]

>> By taking advantage of the 180-degree symmetry of the instrument,
>> only 8 orientations are used.
>
> No, I think you are taking advantage of the 180-degree symmetry of
> the hypothesised effect rather than of the instrument, which itself
> may be asymmetrical due to many factors, including an asymmetrical
> air flow and temperature in the aether house.

The INSTRUMENT is exactly 180-degree symmetrical, as light does not care
if it goes east then west, or west then east; deviations from exactly 90
degrees between the arms do not change this. Sources of error need not
be symmetric, but most of them have a symmetric effect on the symmetric
instrument.

> The subtraction of the first turn has but one effect -- that of
> offsetting each of the eight error-difference curves by a constant
> value, equal to the observation in the first turn at the
> corresponding azimuth. It has /no/ effect on the forms of those
> curves. Since your fitting consists in finding the seven relative
> vertical offsets between these curves, it may safely be applied to
> the raw drifts at each combined mark, in which case the seven fit
> parameters will represent the pure signal, if any!

No! The EIGHT fit parameters represent the signal PLUS THE VALUE OF THE
SYSTEMATIC AT THE START OF THE RUN (for each orientation), with the
entire run offset to start at zero.

I wrote:
> Tom Roberts:
> > BTW I still have these 67 runs on disk. If anyone
> > wants them, just ask.
>
> Yes, please, I shall be most grateful!

In case you prefer to send it by e-mail, my address in the
headers in munged. Please, use anton [full stop] txt (at)
gmail.com . May I use those data in my own analysys "courtesy
of Tomas Roberts"?

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I wrote:
> I wrote:
> > Tom Roberts:
> > > BTW I still have these 67 runs on disk. If anyone
> > > wants them, just ask.
> >
> > Yes, please, I shall be most grateful!
>
> In case you prefer to send it by e-mail, my address in the
> headers in munged. Please, use anton [full stop] txt (at)
> gmail.com . May I use those data in my own analysys "courtesy
> of Tomas Roberts"?

It will be "courtesy of Thomas J. Roberts" -- beg you
pardon.

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<snip all background to avoid a long message>

I'll give a little explanation for my past discussion and give some
thoughts on some things not raised in parallel threads, which I haven't
followed in detail.

It will be obvious that I am not particularly interested in the detail
of all this. But...

On the statistics newsgroup we were asked for opinions of the 2006
paper, which we started giving. My own contributions were based
entirely on the contents of that paper ... it's description of the
original "experiment", data collection, data analysis, etc., and of the
"new" work contributed by the paper.

We were later given a link to the 1933 paper, which I haven't followed
as my internet-safety stuff blocked the link. I couldn't be bothered to
avoid the block.

I did later do an internet search for citations of the paper, and found
a few. One of these is in

https://wiki.alquds.edu/?query=Dayton_Miller

which, being in Wikipedia, arguably places consideration of the paper
firmly in the public domain.

To be clear, when I wrote about "data-manipulation" I was referring to
the whole reduction of 5.2 million data points (as stated in the above
link) to a few hundred.

Any data analysis has to be mindful of the potential effects of
data-manipulation, and such a large-scale reduction from
"data-cleaning" and the other manipulations makes one wonder as to the
point of doing any analysis at all. I am particularly doubtful of the
apparent struggle to construct a single time-series for analysis, which
should not be necessary.

Other threads have brought out certain details of what is unclear in
this paper. Let me concentrate on something not yet covered.
Specifically the model-fitting.

Previous replies have said that the fitting was done using a
sum-of-squared-errors type of objective function and that, for some
reason, this gave something that was a discontinuous function of the
model parameters. There is an implication that this discontinuity was
derive from whatever allowance is made for the effect of quantisation,
but there are no details given.

This seems very strange. There are obvious ways of accounting for
quantisation effects within the model fitting that would not yield a
least-squares objective function but would give one that is a
continuous function.

It may well be that some of the data-manipulations have been applied to
the already-quantised observations, which makes things difficult and,
depending on the details of those manipulations, maybe impractical. But
let's suppose that there is a simple model, with the quantisation
applied to directly yield the data to be analysed. For example the
model-structure may have a sinusoid of known period and a random
observation error to represent what would have been observed without
the quantisation. Then, assuming statistical independence of the random
errors. the likelihood function for the quantised data can be found.
This gives an objective function (to be maximised) that is a sum of
logarithms of probabilities, where each probability refers to the
probability of the quantised observation falling in the bin that it was
observed in. These probabilities would be expressed as the difference
of the values of a cumulative distribution function at two points that
derive from the quantisation limits for the bin and the model
parameters. No discontinuities involved in treating the quantisation.

Of course, statistical independence here is very doubtful, but the
assumption leads to an objective function for fitting that is entirely
reasonable. One just has to avoid the trap of following standard
maximum-likelihood theory in constructing tests of significance and
confidence intervals. There are variants of the theory that allow for
statistical dependence while still using the simple objective function,
but it may not be worthwhile following any of these given their
difficulty. Instead, the obvious suggestion is to apply either
block-jackknifing or block-bootstrapping to get an assessment of
uncertainty.

The paper does give some discussion of "error-bars" but gives no
details of how these are calculated. It may be that the effects of
quantisation are treated as if they were random errors, which they are
not.

There is an obvious scientifically-valid alternative to all this, that
is feasible in this post-modern-computing world. Depending of course on
what you are trying to prove or disprove. You have a result from a
model-fitting procedure, and that procedure can be as awful as you
like, where that result supposedly measures the size of some effect
that may or may not be present. The obvious thing to do is to simulate
a large collection of sets of data, in this case each having 5.2
million data-points, where the putative effect is absent but which
include a good representation of all the supposed effects that your
data-manipulations are supposed to remove, and then to apply those data
manipulation steps before applying whatever your model-fitting
procedure is. It would of course help if the model-fitting procedure is
not written in an interpreted language like Java.

But is it worth doing any further analysis at all, given that the 1933
conclusions have been disproved by later experi

David Jones:

> We were later given a link to the 1933 paper, which I
> haven't followed as my internet-safety stuff blocked the
> link. I couldn't be bothered to avoid the block.

OK, I have avoided it for you:

https://freeshell.de/~antonius/file_host/Miller-EtherDrift-1933.pdf

> Previous replies have said that the fitting was done using
> a sum-of-squared-errors type of objective function

Tom Roberts explained that his objective function was a sum
a squred differences weighted with inverse errorbars.

> and that, for some reason, this gave something that was a
> discontinuous function of the model parameters.

It is discontinuous in that the raw data are discontinuous
(tabulated). 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.

> There is an implication that this discontinuity was derive
> from whatever allowance is made for the effect of
> quantisation, but there are no details given.

Can you please quote the relevant parts of the article?

> It may well be that some of the data-manipulations have
> been applied to the already-quantised observations, which
> makes things difficult and, depending on the details of
> those manipulations, maybe impractical.

Yes, the original raw observations are quantized to sixteen
fixed azimuths -- see the 1933 paper.

> For example the model-structure may have a sinusoid of
> known period and a random observation error to represent
> what would have been observed without the quantisation.

I expected some such model, too, but the device also shows a
strong systematic drift, which too must be modelled.

> The paper does give some discussion of "error-bars" but
> gives no details of how these are calculated.

Please, see the paragraph starting with: "While Fig. 3 shows
the inadequacy of assuming a linear drift, it is still
useful to obtain quantitative errorbars for these data
analyzed in this manner," and let us know whether you agree
with the author.

> There is an obvious scientifically-valid alternative to
> all this, that is feasible in this post-modern-computing
> world. Depending of course on what you are trying to prove
> or disprove. You have a result from a model-fitting
> procedure, and that procedure can be as awful as you like,
> where that result supposedly measures the size of some
> effect that may or may not be present. The obvious thing
> to do is to simulate a large collection of sets of data,
> in this case each having 5.2 million data-points, where
> the putative effect is absent but which include a good
> representation of all the supposed effects that your data-
> manipulations are supposed to remove, and then to apply
> those data manipulation steps before applying whatever
> your model-fitting procedure is. It would of course help
> if the model-fitting procedure is not written in an
> interpreted language like Java.

Yes, I agree, which is why I asked Thomas to please share
his raw data, which he says is still saved on his "disk". I
do not think Java is an interpreted language...

> But is it worth doing any further analysis at all, given
> that the 1933 conclusions have been disproved by later
> experi

I am rather interested in this. No later "null" experiment
that I know of tried to reproduce the Miller experiments but
always incorporated some important changes in the setup, but
this is not something I have come here to discuss. My
immediate focus in the Miller experiment and the Roberts
reanalysis of it.

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Tom Roberts:
> Anton Shepelev:
>
> > The raw data is a series of 20 runs, or interferometer
>
> 20 TURNS, not "runs". There are 67 runs, each consisting
> of of 20 turns. Turn = rotation. These are Miller's
> terms, and I followed him.

This is a mental slip recurring throughout my entire post.
I beg your pardon.

> > [Roberts reanalysis exressed in equations]
>
> That looks correct. I don't see what use it might be.

a) Equations do not have the ambiguity of natural language,
b) their writing requires complete understaning c) they may
be useful to other participants having trouble understanding
your statistical model.

> I _DID_ "sew them together". Miller recorded the value at
> orientation 1 just before the adjustment turn, and again
> just after it. For all data thereafter I added (before-
> after) to every value, thus canceling the effect of his
> adjustment, as best as can be done. This was done just
> after reading the data file, before any analysis or
> plotting.

Thanks, that's right.

> While I was at CWRU in 2006, after giving a colloquium on
> this analysis, Prof. Fickinger and I visited the archives
> and spent an hour or two scanning Miller's data sheets for
> runs without adjustments, indicating the instrument was
> more stable than usual. We found several dozen, but I
> never got around to analyzing them. I did look at them,
> and many of them are just a monotonic drift from start to
> finish -- no signal at all.

To your visual estimation? Well, OK...

Please, notice that I answered to your generous offer of the
digitized data of the 67 runs that you have on your HDD.
Let me know how you should like to share it, or how you want
me to take it.

> > These calibration-caused irregularities may have a
> > negative effect upon the fitting of combined systematic
> > drift.
>
> Hmmm. The instability of the instrument is at fault. The
> procedure I used is the best that can be done, given
> Miller's methods.

Since you sewed the observation turns across the calibration
turns, my suspicion does not hold. But thinking your
procedure the best possible one is somewhat immodest of you
:-) Have it been formally proven to be the best?

> > Not all the errors are systematic, as Miller himself
> > noticed the action of sound in disturbing the air in the
> > interferometer light path, let alone those due to the
> > hypothetical aether wind, which, if partially entrained,
> > will be affected by atmospheric turbulances, as well as
> > show the typical instabilities occuring when a laminar
> > flow meets with obstacles.
>
> None of those are anywhere close to the magnitude of the
> drift.

No, but they are larger than the magnitude of the alleged
signal.

> Moreover, if they are in Miller's data then they are in my
> model of the systematic.

Only as long as well-behaved noise, being symmetrical, does
not affect the optimal combination of the drift curves,
because the upward and downward spikes cancel out. Squared
differences, though, do not cancel out as well as if they
were L1:

s2 = s1 + s2 => s2^2 != s1^2 + s2^2

L2 needs more samples for the same stability.

> For about $50,000 and a year of effort you could build a
> pair of them and instrument the heterodyne between lasers
> locked to each. Point one arm straight up so it behaves
> differently with orientation than the other one (with two
> horizontal arms). Dedicate another year or two of your
> life to taking data....
>
> Attempting to put them on a rotating table is hopeless, as
> you can never get the vertical arm to be vertical
> accurately enough; microradians matter.

Indeed. It is much more practicable to let the Earth do the
rotation!

Tom Roberts:
> Anton Shepelev:
> > Tom Roberts:
> >
> > > By taking advantage of the 180-degree symmetry of the
> > > instrument, only 8 orientations are used.
> >
> > No, I think you are taking advantage of the 180-degree
> > symmetry of the hypothesised effect rather than of the
> > instrument, which itself may be asymmetrical due to many
> > factors, including an asymmetrical air flow and
> > temperature in the aether house.
>
> The INSTRUMENT is exactly 180-degree symmetrical, as light
> does not care if it goes east then west, or west then
> east;

You are talking about light, not about the instrument.
Reading on:

> deviations from exactly 90 degrees between the arms do not
> change this.

No, they do not change the behavior of light, not the half-
cycle symmetry of the device.

> Sources of error need not be symmetric, but most of them
> have a symmetric effect on the symmetric instrument.

One can easily imagine many faults that will disrupt the
half-period symmetry of the MMI interferometer, for
example -- a kink in the rotation mechanism causing an bump
at certain orientation, or a different thermal inertia of
one of the arms.

> > The subtraction of the first turn has but one
> > effect -- that of offsetting each of the eight error-
> > difference curves by a constant value, equal to the
> > observation in the first turn at the corresponding
> > azimuth. It has /no/ effect on the forms of those
> > curves. Since your fitting consists in finding the seven
> > relative vertical offsets between these curves, it may
> > safely be applied to the raw drifts at each combined
> > mark, in which case the seven fit parameters will
> > represent the pure signal, if any!
>
> No! The EIGHT fit parameters represent the signal PLUS THE
> VALUE OF THE SYSTEMATIC AT THE START OF THE RUN (for each
> orientation), with the entire run offset to start at zero.

Please, wait a minute. In your paper, where you operate with
the partial error-differences, the eight fit parameters
represent the initial drift (at the first rotation) at each
of the eight combined orientations. Consider a simple
situation of a sine signal and no drift. All the partial
error-differences are constantly zero and coincide. All the
fit parameters are zero -- because the drift is zero. It is
as I said -- in your paper the eight parameters represent
the pure value of the systematic drift!

If, however, you do the same thing sans subtracting the
first rotation from the rest, the eight fit parameters will
show the pure negative signal, because the fitting model
will in effect try to cancel the signal by aligning the
values at adjecent orientations. The two methods are
equivalent because, as you write in a footnote, "The chi^2
is made up of differences, so any constant can be added to
all 8 parameters without changing chi^2."

My point was the subtracting the first turn from the rest
was a redundant operation.

> > So you used a weighted form the of least-squares. But
> > then a complete enumeration is unnecessary, becuase
> > least-squares is designed to be an analitical method
> > with linear complexity: you simply write the smoothness
> > function as a sum of weighted squared differences over
> > the tabulated data and optimise it the usual way via
> > partial derivatives.
>
> It makes no sense to fit continuous parameters to
> quantized data,

At least, it would have save you from the brute-force
enumeration and have let you use the least-squares method as
it was intended. Also, 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.

> so the parameters are quantized like the data. Partial
> derivatives of the parameters are not possible, and
> enumeration is the only method I found.

The other method is not to quantize the seven parameters
before fitting. If you must, quantize them after fitting,
or better not a tall, taking advantage of the higher
precision of the exact values.

> > Notice, however, that large discontinuitites between
> > runs due to interferomenter calibration are likely to
> > dominate the fitting.
>
> I never combined runs, so as stated this is a non issue.
> If by "run" you mean turn, it is also a non issue because
> I corrected the data for the offset in each recalibration
> turn.

Yes, I meant a turn, or rotation. Understood.

> 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.

> > What is your opinion regarding the claimed galactic
> > orientation of the measured drift, as plotted in fig. 22
> > of the 1933 paper? Can an instumental error have a
> > concistent half-periodic dependency on 1) time of day
> > and 2) the season of the year so as to point into a
> > fixed direction in the galaxy?
>
> Computing an average always yields a value, so it's no
> surprise that he came up with an answer.

Anton Shepelev wrote:

> David Jones:
>
> > We were later given a link to the 1933 paper, which I
> > haven't followed as my internet-safety stuff blocked the
> > link. I couldn't be bothered to avoid the block.
>
> OK, I have avoided it for you:
>
> https://freeshell.de/~antonius/file_host/Miller-EtherDrift-1933.pdf
>
> > Previous replies have said that the fitting was done using
> > a sum-of-squared-errors type of objective function
>
> Tom Roberts explained that his objective function was a sum
> a squred differences weighted with inverse errorbars.
>
> > and that, for some reason, this gave something that was a
> > discontinuous function of the model parameters.
>
> It is discontinuous in that the raw data are discontinuous
> (tabulated). 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.

" It is discontinuous in that the raw data are discontinuous" ..
That explains nothing. An "error" that is squared is derived from an an
observed and a modelled value. Given the quantisation, the "observed"
part of this for a single observation is either just a single value
(usually the centre of the interval), or two values denoting the end
points of the interval. In either case these values are fixed and don't
depend on the mode parameters and hence cannot contribute a
discontinuity to the objective function. The basic form of the modelled
value is a continuous function of the model parameters. The usual error
comparing the modelled value with the centre of the interval gives the
error as a continuous function of the parameters. The obvious variant
of this taking explicit account of the quantisation might set the error
as zero of the modelled value is within the quantisation interval and
the distance to the closet edge otherwise. Again this gives can error
that is a continuous function of the model parameters, but the
derivative is not continuous.Now it may be that the "error" is being
constructed as a comparison of the quantised observation with a
quantised version of the continuous modelled values. This seems to be
very inadvisable, but it would produce a discontinuous objective
function. It is unfortunate that the 2006 paper provides no actual
details about what is being done by way of defining the objective
function.

>
> > There is an implication that this discontinuity was derive
> > from whatever allowance is made for the effect of
> > quantisation, but there are no details given.
>
> Can you please quote the relevant parts of the article?

Well on page 6 there is this ..

"As the data are quantized at 0.1 fringe, so are
the parameters, and instead of the usual minimization programs an
enumeration of all reasonable sets of parameters
was used with an algorithm that finds the minimum
?2. The result of the fit is a complete quantitative model of
systematic(time) for the run. This fit has 313 degrees of freedom, and
the histogram of X2 for all runs has a mean of
300, indicating that the estimate of the individual measurement
resolution (0.1 fringe) is reasonable. Fitting each run
took about 3 minutes of computer time to enumerate several million
combinations of the 7 parameters to find both
the best fit and the errorbar"

I might well have misinterpreted this use of a search over "several
million combinations" and the use of a "quantised" set of possible
parameter values as being a response to discontinuity. How the
parameters can be "quantised at 0.1 fringe" and what this means is a
mystery, but it seems to be what is being said. But perhaps this part
of the overall data analysis is not what I thought it was. But, if the
objective function is actually continuous and well-behaved, I don't see
why you would choose to do a multi-dimensional grid search.

>
> > It may well be that some of the data-manipulations have
> > been applied to the already-quantised observations, which
> > makes things difficult and, depending on the details of
> > those manipulations, maybe impractical.
>
> Yes, the original raw observations are quantized to sixteen
> fixed azimuths -- see the 1933 paper.
>
> > For example the model-structure may have a sinusoid of
> > known period and a random observation error to represent
> > what would have been observed without the quantisation.
>
> I expected some such model, too, but the device also shows a
> strong systematic drift, which too must be modelled.

Well yes, one would need to include in a model all of the effects that
need to be modelled. But the point was that the quantisation should be
treated properly as it seems to have been judged to be of such
importance. This means having a model describing what would have been
observed if there were no quantisation being done and then to treat the
consequences of the quantisation.

The above may sound a simple approach but, without thinking too deeply
about this, I am worried that the "data manipulation" that is going on
may make it infeasible. If the data-manipulation were simply that the
data actually being analysed were simply the differences of two
quantised observations, I think the approach could be carried
through.But the steps being taken seem more complicated than that ...
possibly in an attempt to remove certain effects that are of no
interest but which need to be included in a full model of the
observations actually made.

>
> > The paper does give some discussion of "error-bars" but
> > gives no details of how these are calculated.
>
> Please, see the paragraph starting with: "While Fig. 3 shows
> the inadequacy of assuming a linear drift, it is still
> useful to obtain quantitative errorbars for these data
> analyzed in this manner," and let us know whether you agree
> with the author.

Well yes error bars would be useful, but one would need to know what
they are error bars for, and one would need to know that they have been
derived in a way that is statistically valid.

>
> > There is an obvious scientifically-valid alternative to
> > all this, that is feasible in this post-modern-computing
> > world. Depending of course on what you are trying to prove
> > or disprove. You have a result from a model-fitting
> > procedure, and that procedure can be as awful as you like,
> > where that result supposedly measures the size of some
> > effect that may or may not be present. The obvious thing
> > to do is to simulate a large collection of sets of data,
> > in this case each having 5.2 million data-points, where
> > the putative effect is absent but which include a good
> > representation of all the supposed effects that your data-
> > manipulations are supposed to remove, and then to apply
> > those data manipulation steps before applying whatever
> > your model-fitting procedure is. It would of course help
> > if the model-fitting procedure is not written in an
> > interpreted language like Java.
>
> Yes, I agree, which is why I asked Thomas to please share
> his raw data, which he says is still saved on his "disk". I
> do not think Java is an interpreted language...
>

Well I did look up a description of Java. This confuses the issue, but
a summary is that the Java package itself is compiled, but that the
treatment by the package of a supplied script is that it interprets
and executes it line by line. Now there may be some version that
compiles a script into executable code, but that is not really the
point ... which is that Java is not usually counted as producing
quickly-executing code as would be the case for Fortran or C(plus?). It
may even be that there is some version of Java that is capable of
calling subroutines written in Fortran or C, as is the case with the R
package.

> > But is it worth doing any further analysis at all, given
> > that the 1933 conclusions have been disproved by later
> > experi
>
> I am rather interested in this. No later "null" experiment
> that I know of tried to reproduce the Miller experiments but
> always incorporated some important changes in the setup, but
> this is not something I have come here to discuss. My
> immediate focus in the Miller experiment and the Roberts
> reanalysis of it.

Obviously I know nothing about concepts of "Aether drift" and how this
might fit into modern versions of cosmology. But there seems to be an
assumption that, if it exists, it is in some way constant in size and
direction. Why wasn't the experiment constructed so as to determine a
direction for rthe drift if it existed? If the "drift" might vary, how
fact might it vary ... might it vary at a frequency similar to that of
visible light?
I guess the point is that there are certain mathematical theories in
which things related to reality either do or do not interact and one is
either; (a) looking for things already in the model that interact when
the theory says they do not; or (b) looking for evidence that there are
things not already in the theory that do have an effect on things that
are.

David Jones <dajhawkxx@nowherel.com> wrote:
[-]
Some physics background.

> Obviously I know nothing about concepts of "Aether drift" and how this
> might fit into modern versions of cosmology.

Not. A forteriori, not at all.

> But there seems to be an assumption that, if it exists, it is in some way
> constant in size and direction.

Yes. That's called Lorentz aether theory.
In Lorentz aether theory the aether is fixed,
and it has a rest frame, so speed wrt the aether exists.
(aka aether drift)
But in Lorentz aether theory this speed is in principle not observable.
It's like relativity in all its predictions.

> Why wasn't the experiment constructed so as to determine a
> direction for the drift if it existed?

Yes. There was, it is called the Michelson-Morley experiment.
It found a null result. (like other experiments to measure the same)
Einstein's theory of relativity retrodicted that.
(for M&M and all other possible experiments)
Lorentz agreed.

Then the fudging started. Michelson theorised
that his laboratory dragged the aether along.
(think like an aeroplane taking the air inside with it,
so inside you cannot measure the air velocity outside)
He thought this dragging might be less on a mountain top.
(think like in a plane with an open cockpit
where you can measure some speed behind your windshield)
So Michelson wanted to redo his experment on a mountain top.
He never found the resources, but Dayton Miller did.

> If the "drift" might vary, how
> fact might it vary ... might it vary at a frequency similar to that of
> visible light?

There just isn't any viable theory
that can accomodate variable aether drift.
It also conflicts with other well established physics.
(and no, frequency doesn't come into it)

> I guess the point is that there are certain mathematical theories in
> which things related to reality either do or do not interact and one is
> either; (a) looking for things already in the model that interact when
> the theory says they do not; or (b) looking for evidence that there are
> things not already in the theory that do have an effect on things that
> are.

No. There isn't any viable model for partial aether drag.
Dayton Miller' experiment just contradicts special relativity.
It does not support something else, because there is nothing else.
You cannot have an aether that is AND fixed, AND deformable in some way.

But you seem to be purely a data analist.
You should be familiar with "Trash in, Trash out".
If the original data are flawed, you can analyse all you want,
but whatever result you obtain will be flawed too.

You should also be familiar with the fact
that some reputable scientist insisting very much
that the data are not flawed doesn't make it so. [1]

Jan

[1] In this context, what Shankland and Roberts have shown
is that even if you take Dayton Miller and his experiment at face value
there is still no nugget of gold hidden in the dungheap.
But of course you can always dig again...

--
"But I was thinking of a plan
To dye one's whiskers green,
And always use so large a fan
That it could not be seen." (The White Knight)

On 3/9/23 11:13 AM, David Jones wrote:
> The paper does give some discussion of "error-bars" but gives no
> details of how these are calculated.

Miller's analysis algorithm averaged 40 values to get each of his final
8 points [@]. To calculate the errorbar for each of his 8 points,
compute the sigma for the 40 values that contributed to it [$], and then:
A) divide by 1 if you think this is a systematic error [#]
or:
B) divide by sqrt(40) if you think this is a purely statistical
error and each contributing data point is independent of
all the others [#].
or:
C) divide by some value between 1 and sqrt(40) if you think
this is a mixture of statistical and systematic errors.

Regardless of which you choose, the resulting errorbars are larger than
the variation in Miller's plot. IMHO the only sensible choice is (A)
[#], and that's what I did in Fig. 4.

> It may be that the effects of quantisation are treated as if they
> were random errors,

Nope.

[@] He also subtracted an assumed linear drift -- for
each orientation that is a constant and so does not
affect the errorbar.

[$] Miller subtracted the linear drift after
averaging the data points; that is equivalent to
subtracting the linear drift of each turn (the lines
of Fig. 3), and to compute the sigma you must do the
latter.

[#] In the histogram for one column, observe how the
points from successive turns march systematically from
right to left, jump to the right at each adjustment,
and resume their march from right to left. This
is NOT the behavior of random (statistical) errors
from uncorrelated data. I had a plot of this, but
don't know what happened to it.

Tom Roberts

David Jones:

> "It is discontinuous in that the raw data are
> discontinuous" .. That explains nothing. An "error" that
> is squared is derived from an an observed and a modelled
> value. Given the quantisation, the "observed" part of this
> for a single observation is either just a single value
> (usually the centre of the interval), or two values
> denoting the end points of the interval. In either case
> these values are fixed and don't depend on the mode
> parameters and hence cannot contribute a discontinuity to
> the objective function.

I misunderstood you. I thought you were talking about the
systematic drift model, which consists of a set of points
and is of course discontinous in time. The least-squares
objective function, however, need not be discotinous in the
parameters being fitted, yet Mr. Roberts chose to make it
so. Had he kept it natually continous, he would have been
able to find the optimum by solving it in partial
derivatives.

> Now it may be that the "error" is being constructed as a
> comparison of the quantised observation with a quantised
> version of the continuous modelled values. This seems to
> be very inadvisable, but it would produce a discontinuous
> objective function.

I think Mr. Roberts did the inadvisable thing.

> It is unfortunate that the 2006 paper provides no actual
> details about what is being done by way of defining the
> objective function.

Oh, no, it does explain that in part IV, albeit not very
clearly. I have tried to re-express his procedure with the
clarity and unambiguity of mathematical language, see my
post here:

From : Anton Shepelev <anton.txt@gmail.moc>
Subject : Re: statistics in Roberts' paper on Miller
Date : Wed, 8 Mar 2023 15:33:02 +0300
Message-ID: <20230308153302.2e74b7a62f096863323df7dd@gmail.moc>

Perhaps if you ask specific questions I can help you better.

> > David Jones:
> >
> > > There is an implication that this discontinuity was
> > > derive from whatever allowance is made for the effect
> > > of quantisation, but there are no details given.
> >
> > Can you please quote the relevant parts of the article?
>
> Well on page 6 there is this ..
>
> "As the data are quantized at 0.1 fringe, so are the
> parameters, and instead of the usual minimization programs
> an enumeration of all reasonable sets of parameters was
> used with an algorithm that finds the minimum X2. The
> result of the fit is a complete quantitative model of
> systematic(time) for the run. This fit has 313 degrees of
> freedom, and the histogram of X2 for all runs has a mean
> of 300, indicating that the estimate of the individual
> measurement resolution (0.1 fringe) is reasonable. Fitting
> each run took about 3 minutes of computer time to
> enumerate several million combinations of the 7 parameters
> to find both the best fit and the errorbar"

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. The least-squares method
works well with quantised data and a continuous objective
function.

> I might well have misinterpreted this use of a search over
> "several million combinations" and the use of a
> "quantised" set of possible parameter values as being a
> response to discontinuity.

Mr. Roberts first /created/ that discontinuity by deciding
to quantise the naturally continous model parameters, and
then responded to his own decision by brute-force
enumeration of the several million combinations. He also
had to "fold" earch interferometer turn in two, because
partly the brute-force enumeration could not handle the 16
azimuth orientations.

> How the parameters can be "quantised at 0.1 fringe" and
> what this means is a mystery,

`ringe' is the unit of measurement, and also the quantum.
Each of the paramters may assume a fixed set values: 0.0,
0.1. 0.2, &c up the the practical maximum obvious from the
data.

> but it seems to be what is being said. But perhaps this
> part of the overall data analysis is not what I thought it
> was. But, if the objective function is actually continuous
> and well-behaved, I don't see why you would choose to do a
> multi-dimensional grid search.

Nor do I.

> Well yes, one would need to include in a model all of the
> effects that need to be modelled.

His model of the systematic drift includes them.

> But the point was that the quantisation should be treated
> properly as it seems to have been judged to be of such
> importance. This means having a model describing what
> would have been observed if there were no quantisation
> being done and then to treat the consequences of the
> quantisation.

In that case, the consequences of the quantisation are the
quantised values of the model parameters and a potential
small loss of precision -- nothing catastophiic. But still
idea artificially to quanise the naturally continuous
parameters seems unjustified.

> The above may sound a simple approach but, without
> thinking too deeply about this, I am worried that the
> "data manipulation" that is going on may make it
> infeasible. If the data-manipulation were simply that the
> data actually being analysed were simply the differences
> of two quantised observations, I think the approach could
> be carried through. But the steps being taken seem more
> complicated than that ... possibly in an attempt to
> remove certain effects that are of no interest but which
> need to be included in a full model of the observations
> actually made.

Well, this sound rather vague to me, so I can only refer you
to the 2006 article and my explanatory post mentioned above.
I will be glad to answer whatever specific questions you may
have.

> > Please, see the paragraph starting with: "While Fig. 3
> > shows the inadequacy of assuming a linear drift, it is
> > still useful to obtain quantitative errorbars for these
> > data analyzed in this manner," and let us know whether
> > you agree with the author.
>
> Well yes error bars would be useful, but one would need to
> know what they are error bars for, and one would need to
> know that they have been derived in a way that is
> statistically valid.

The paragraph referred-to above contains the entire
explanation of how those error bars were obtained. If you
brew some tea and take the time to read and understand the
2006 article, with my help when/if you need it, I am sure
you will understand those error bars and will be able judge
their correcness.

> Well I did look up a description of Java. This confuses
> the issue, but a summary is that the Java package itself
> is compiled, but that the treatment by the package of a
> supplied script is that it interprets and executes it line
> by line.

Well, Java is not an interpreted language at the top level.
It is compiled into `bytecode', which may be either
interpreted or compiled into machine code.

> Now there may be some version that compiles a script into
> executable code, but that is not really the point ...
> which is that Java is not usually counted as producing
> quickly-executing code as would be the case for Fortran or
> C(plus?). It may even be that there is some version of
> Java that is capable of calling subroutines written in
> Fortran or C, as is the case with the R package.

There is nothing wrong with interpreted languages for data
analysis as long as they defer the number-crunching to
compiled submodules. Python, Julia, or Wolfram Mathematica
are all good great choices. I don't know about R, but it too
seems great for the purpose.

> Obviously I know nothing about concepts of "Aether drift"

The aether is a hypothetical substance that fills all space,
because "nature brooks no emptiess", and "empty space cannot
be the arena of whatsoever interactions." If the Solar
system, -- and the Earth with it, -- moves through the
aether, the effect should be similar to the wind one feels
on one's face when riding a bicyle fast, whence the term
`aether wind', e.g.:

The Earth moving though aether, bound votixes causing
the phenomena of "the roaring forties":
https://freeshell.de//~antonius/file_host/ether-wind.png

> and how this might fit into modern versions of cosmology.

I have come hither to discuss the statistical model in the
2006 article regardless of theoretical cosmology :-)

> But there seems to be an assumption that, if it exists, it
> is in some way constant in size and direction.

Yes, especially in direction.

> Why wasn't the experiment constructed so as to determine a
> direction for rthe drift if it existed?

On 3/9/23 2:26 PM, Anton Shepelev wrote:
> 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". The removal of signal(orientation) was performed by
subtracting the values of the first 1/2-turn. But that also removes the
values of systematic(time) for the first 1/2 turn, so parameters were
used to represent the values of that first 1/2 turn, and the fit was
used to make the overall systematic(time) be as smooth as possible.

> Yes, the original raw observations are quantized to sixteen fixed
> azimuths -- see the 1933 paper.

They are also quantized to 0.1 fringe. Indeed this is what I mean by
"quantized".

> No later "null" experiment that I know of tried to reproduce the
> Miller experiments but always incorporated some important changes in
> the setup,

Yes. 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.

Tom Roberts

On 3/9/23 7:37 PM, David Jones wrote:
> Well yes error bars would be useful, but one would need to know what
> they are error bars for, and one would need to know that they have
> been derived in a way that is statistically valid.

Miller averaged 40 measurements to get each of his 8 points. The
errorbar on the mean is at least as large as the sigma of those 40
points divided by sqrt(40). But that's valid only if the points are
uncorrelated, and a simple glance at Fig. 2 shows that is not at all the
case here. For a systematic error like this, one uses the sigma of the
data points, which I did in Fig. 4. So these are errorbars on his
measurement values, not on any model fitting the data.

[This is how this is usually done in physics -- each
measurement has an errorbar, and one fits a model to
them. The model usually is exact, but if not then its
errorbars must be included in the fit. Note the fit
in my paper is NOT fitting model to data, it is used
to determine the systematic error to subtract from
the data to obtain the signal.]

Tom Roberts

[sci.stat.math dropped because by Google Groups, reinstating]

RichD to 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.
Since the hypothetical ether-wind effect is half-periodical
(second-order), this might seem valid, except that it is
not, because the fundamental full-period component is
cancelled out, and the half-period (second-order) component
becomes the lowest present in the "folded" data, making it
easily confusible with the lowest component of typical 1/f
noise, or even white noise.

> Was it intentional by Miller, or inadvertent?

To the best of my knowledge and understanding, Miller /did
not/ do it all: it the full-period, 16-point, curves that he
fed to the mechanical harmonic analyser, showing a clear
dominance of the second harmonic over both the fundamental
and the higher ones. Read about it in Miller, 1933:

http://freeshell.de/~antonius/file_host/Miller-EtherDrift-1933.pdf

or at least in my post, where I quote Miller:

Subject : Re: statistics in Roberts' paper on Miller
Date : Wed, 8 Mar 2023 19:11:28 +0300
From : Anton Shepelev <anton.txt@gmail.moc>
Message-ID:<20230308191128.c5d1c9143873eb3fef450b00@gmail.moc>

--
() ascii ribbon campaign -- against html e-mail
/\ www.asciiribbon.org -- against proprietary attachments

Tom Roberts:

> Miller averaged 40 measurements to get each of his 8
> points.

No, he averaged 20 measurements to get each of his 16
points, because that is what he fed to the harmonic analyser
according to the 1933 article[1]:

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 above shows it was full-period curves that Miller
analysed, and the 1/2-turn bin was not the lowest one. Your
insistance upon Miller's "halving" of the turns seems
groundless.

P.S.: You wrote earlier that you had on your HDD the
digitised Miller data used in your paper and were
ready to share it with whoever "just asks". This is a
reminder that I ask for it, for I should like to
analyse that data, too.

____________________
1. http://freeshell.de/~antonius/file_host/Miller-EtherDrift-1933.pdf

--
() ascii ribbon campaign -- against html e-mail
/\ www.asciiribbon.org -- against proprietary attachments

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
(delete a newline if one is inserted into the link by your reader. The
final component is 'AAAPrjK9AOqP-yyPRr5wNBwra?dl=0'.)

Start by looking at the file README.txt.

Tom Roberts

On 3/9/23 4:04 PM, Anton Shepelev wrote:
> My point was the subtracting the first turn from the rest was a
> redundant operation.

You are thinking of an alternate analysis. In the analysis I did, that
subtraction is not redundant, it is necessary because I am fitting to
find the drift without the signal.

>> Tom Roberts wrote: It makes no sense to fit continuous parameters
>> to quantized data,
>
> At least, it would have save you from the brute-force enumeration
> and have let you use the least-squares method as it was intended.

No matter. As I said before, it typically took just 3 minutes per run,
on a now-40-year-old laptop.

> Also, 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.

>> 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.

>>> What is your opinion regarding the claimed galactic orientation
>>> of the measured drift, as plotted in fig. 22 of the 1933 paper?
>>> Can an instumental error have a concistent half-periodic
>>> dependency on 1) time of day and 2) the season of the year so as
>>> to point into a fixed direction in the galaxy?
>>
>> Computing an average always yields a value, so it's no surprise
>> that he came up with an answer.
>
> Of course. Any noise or drift will have a Fourier spectrum.
>
>> Had he computed errorbars on it, they would have been larger than
>> 360 degrees, probably much larger.
>
> I cannot comment upon your estimation of the errorbars, yet.
>
>> Look at my Fig. 5. The phase of a fitted sinewave clearly does not
>> determine any direction whatsoever.
>
> 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. A modern
analysis can reduce those errorbars considerably, as mine did....

> 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.

> Mr. Roberts first /created/ that discontinuity by deciding to
> quantise the naturally continous model parameters,

NO! The parameters of the model OF THE DRIFT are inherently quantized,
as the drift itself is quantized.

> The aether is a hypothetical substance that fills all space, because
> "nature brooks no emptiess", and "empty space cannot be the arena of
> whatsoever interactions." If the Solar system, -- and the Earth with
> it, -- moves through the aether, the effect should be similar to the
> wind one feels on one's face when riding a bicyle fast, whence the
> term `aether wind', e.g.:
>
> The Earth moving though aether, bound votixes causing the phenomena
> of "the roaring forties":
> https://freeshell.de//~antonius/file_host/ether-wind.png

Sure. 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....

> 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.

> That is, every day they show a clearly sinusoidal dependency

Only when one does not display the errorbars.

Tom Roberts

On 3/10/23 4:14 PM, Anton Shepelev wrote:
> [sci.stat.math dropped because by Google Groups, reinstating] RichD
> to 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.

As his final result for a single run is the plot at the bottom of my
Fig. 1, with 8 points, my discussion is of the fact that he averaged 40
values to get each point of the plot. 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.

>> Was it intentional by Miller, or inadvertent?
>
> To the best of my knowledge and understanding, Miller /did not/ do
> it all:

Yes, he did, because he averaged each of the 16 orientations, and then
averaged the two halves of that result.

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

Tom Roberts