statistics in Roberts. Was: RAW vs. raw image format

[Rich Ulrich]

Cross-posted to sci.stat.math
to see if anyone has comments.

On Sat, 25 Feb 2023 00:13:53 +0300, Anton Shepelev
<anto...@gmail.moc> wrote:

>Rich Ulrich:

<snip, about computers>
>
>Glad to find you here! I vaguely remember you were present
>in a statiscits newsgroup, but I can't find it now. Would
>you be interested in discussing Tom Roberts's statistical
>analysis of the Dayton Miller aether-drift experiments? It
>requires some light preparatory reading, but the analysis
>itself occupies about two pages in Section IV of this
>article:
>
> https://arxiv.org/vc/physics/papers/0608/0608238v2.pdf
>
>Since Roberts did not publish his data and code, his
>conclusions have zero reproducibility, but I need help in
>understanding the procedure and validity of this analysis as
>described. If you are interested, could we continue in an
>more appropriate newsgroup.

I've cross-posted to a .stat group that has a few readers left.

I read the citation, and I'm not very interested. - I know too little
about the device, etc., or about the ongoing arguments that
apparently exist.

I can say a few things about the paper and the analyses.

Modern statistical analyses and design sophistication for statistics
were barely being born in 1933, when the Miller experiment was
published. In regards to complications and pitfalls, Time series is
worse than analysis of independent points; and what I think of
as 'circular series' (0-360 degrees) is worse than time series. I once
had a passing acquaintance with time series (no data experience)
but I've never touched circular data.

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).

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. I
would want to know how the DEVICE made all those errors possible,
as a clue to how to exclude their influence on an analysis. If
Miller's data has something, Miller didn't show it right. Roberts
offers an alternative analysis, one that I'm too ignorant to fault.

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.

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.

--
Rich Ulrich

[David Duffy]

In sci.stat.math Rich Ulrich <rich....@comcast.net> wrote:
> Cross-posted to sci.stat.math
> to see if anyone has comments.
>
> On Sat, 25 Feb 2023 00:13:53 +0300, Anton Shepelev
> <anto...@gmail.moc> wrote:
>
>>Rich Ulrich:
>
> <snip, about computers>
>>

>>you be interested in discussing Tom Roberts's statistical
>>analysis of the Dayton Miller aether-drift experiments? It

>> https://arxiv.org/vc/physics/papers/0608/0608238v2.pdf
>>
>>Since Roberts did not publish his data and code, his
>>conclusions have zero reproducibility, but I need help in
>>understanding the procedure and validity of this analysis as
>>described. If you are interested, could we continue in an
>>more appropriate newsgroup.

This is a quick and dirty analysis in the R stats package. The script
below should be fed into R, so you can look at the plots, which
give a feel for what I did. The generalized additive mixed model I
fitted suggests there is a significant sine wave looking trend
as the interferometer is rotated, with
Approximate significance of smooth terms:
edf Ref.df F p-value
s(dirs) 4.206 4.206 9.572 1.92e-07

Here dirs is the 16 directions, the edf is the fitted degree of
spline, which when you plot it peaks at 0 and 180 degrees, and
the random effect is a separate intercept for each of the 20
rotations. I don't see how one can exclude other peculiarities
of the setup. The more recent meta-analyses of all such experiments
usually accept this result at face value, but demonstrate it is an outlier
when compared to more recent experiments that have greater precision.

require(locfit)
require(gamm4)

nrotations <- 20
nrunlen <- 17
miller <- c(10,11,10,10,9,7,7,8,9,9,7,7,6,6,5,6,7,
7,7,6,5,4,4,4,3,2,3,3,4,1,1,1,0,1,
1,1,0,-1,-2,-3,-2,-2,-2,-1,-1,-2,-3,-3,-5,-4,-4,
-4,-5,-5,-6,-6,-6,-7,-6,-6,-7,-9,-9,-10,-10,-10,-11,-13,
-13,-15,-15,-16,-17,-19,-19,-18,-17,-17,-18,-19,-19,-18,-17,-16,-15,
0,0,0,0,0,0,0,1,4,6,7,8,9,9,10,10,8,
8,7,5,5,3,3,3,4,5,5,5,4,1,0,-1,-1,-2,
-2,-2,-3,-3,-2,-2,-1,-1,-2,-3,-5,-7,-9,-9,-11,-12,-11,
-11,-11,-11,-12,-14,-14,-11, -10, -10,-9,-9,-8,-10,-10,-10,-10,-10,
8,8,8,7,7,6,6,5,4,4,3,1,0,0,-2,-3,-1,
-1,-1,-1,-2,-3,-3,-2,-2,-2,-1,0,-1,-2,-1,0,0,0,
0,1,1,1,1,3,4,6,7,7,7,9,9,9,9,8,9,
9,10,10,10,10,9,9,9,10,10,9,9,9,8,7,7,7,
7,8,9,8,9,9,9,10,11,12,12,12,11,11,11,11,10,
10,10,10,8,5,4,3,3,5,4,3,1,1,0,0,0,0,
0,0,-1,-1,-2,-3,-3,-5,-5,-5,-5,-5,-6,-6,-6,-5,-4,
-4,-5,-5,-4,-5,-6,-6,-5,-5,-6,-6,-6,-7,-7,-8,-9,-10,
-10,-10,-11,-11,-12,-12,-11,-10,-10,-10,-10,-11,-11,-11,-12,-12,-12,
-12,-13,-14,-15,-15,-16,-15,-16,-15,-15,-16,-17,-18,-19,-18,-20,-21,
1,1,2,1,1,2,4,5,7,7,8,7,6,5,4,4,4)
angles <- rep(seq(0,16),20)
repeats <- rep(seq(1,20),each=17)
#
# the four runs after a rezeroing
#
rezeroed <- c(86, 154, 324)
runs <- rep(1,length(miller))
runs[seq(86,153)] <- 2
runs[seq(154:323)] <- 3
runs[seq(324,340)] <- 4
runs <- factor(runs)

dups <- setdiff(17*seq(1,19)+1, rezeroed)
run1 <- setdiff(seq(1,85),dups)
run2 <- setdiff(seq(86,153),dups)
run3 <- setdiff(seq(154,323),dups)
run4 <- seq(324,340)
nr1 <- length(run1)
nr2 <- length(run2)
nr3 <- length(run3)
nr4 <- length(run4)
nuniq <- nr1+nr2+nr3+nr4
par(mfcol=c(2,1))
plot(miller[-dups])

fit_pieces <- function(sm=1) {
res <- list()
res$m1 <- locfit(miller[run1] ~ seq(1,nr1), alpha=sm)
res$m2 <- locfit(miller[run2] ~ seq(nr1+1,nr1+nr2), alpha=sm)
res$m3 <- locfit(miller[run3] ~ seq(nr1+nr2+1,nr1+nr2+nr3), alpha=sm)
res$m4 <- locfit(miller[run4] ~ seq(nr1+nr2+nr3+1,nuniq), alpha=sm)
res
}
mod <- fit_pieces(0.4)
lines(mod$m1, lwd=2, col="red")
lines(mod$m2, lwd=2, col="red")
lines(mod$m3, lwd=2, col="red")
lines(mod$m4, lwd=2, col="red")

raw <- miller[-dups]
runs <- runs[-dups]
res <- c(residuals(mod$m1), residuals(mod$m2), residuals(mod$m3), residuals(mod$m4))
dirs <- c(angles[run1], angles[run2], angles[run3], angles[run4])
rotations <- c(repeats[run1], repeats[run2], repeats[run3], repeats[run4])

plot(res, type="l")
abline(v=seq(8,324,8),col="grey80")
par(mfcol=c(1,1))
plot(res ~ dirs, t="p", axes=F, xlab="Markers", ylab="Detrended Residual")
box()
axis(2)
axis(1, at=c(0,4,8,12,16))
axis(3, at=c(0,4,8,12,16),
labels=c(0,expression(pi/2),expression(pi),
expression(3*pi/2),expression(2*pi)))
lines(locfit(res ~ dirs), lwd=5, col="red")
lines(dirs[1:17], cos(4*pi*dirs[1:17]/16), col="blue", lwd=3)

for(i in 1:nrotations) {
lines(dirs[rotations==i], res[rotations==i])
}
miller2 <- data.frame(raw,res,runs,dirs,rotations)
miller2$group <- factor(miller2$rotations)
g1 <- gamm4(raw ~ group + s(dirs), random=~(1|group), data=miller2)
summary(g1$mer)
anova(g1$gam)
plot(g1$gam)

Cheers, David Duffy.

[David Duffy]

In sci.stat.math David Duffy <davi...@tpg.com.au> wrote:
>
> This is a quick and dirty analysis in the R stats package.

> Approximate significance of smooth terms:
> edf Ref.df F p-value
> s(dirs) 4.206 4.206 9.572 1.92e-07
>
> Here dirs is the 16 directions, the edf is the fitted degree of
> spline, which when you plot it peaks at 0 and 180 degrees, and
> the random effect is a separate intercept for each of the 20
> rotations.

I was too quick quick in writing this - I needed to unpack those
degrees of freedom into a linear decline over the rotation, due
to the overall drift, which explains most of that signal,
and the actual bump at 180 degrees. If I instead fit a polynomial term,
then we can decompose the chi-square for direction into linear
(highly statistically significant), and higher terms (weakly significant,
in physicist parlance say 2-sigma ;)).

g0: raw ~ group + (1 | group)
g1: raw ~ group + poly(dirs, 1) + (1 | group)
g4: raw ~ group + poly(dirs, 4) + (1 | group)
npar AIC BIC logLik deviance Chisq Df Pr(>Chisq)
g0 22 1524.7 1607.9 -740.37 1480.7
g1 23 1498.3 1585.2 -726.13 1452.3 28.476 1 9.486e-08 ***
g4 26 1494.0 1592.3 -721.00 1442.0 10.248 3 0.01657 *

You can see this in the last plot, which includes confidence envelopes
around the GAM fitted curve.

[David Jones]

> 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.

The paper is extremely difficult to understand and I have tried very
hard.. There seems a possibility that you are over-interpreting what
the author means by "chi-squared". I have heard some non-statistical
experts in other fields just using "chi-squared" to mean a sum of
squared errors. So not a formal test-statistic for comparing two models?

The various data-manipulations, both in the original paper and this one
are difficult to follow. My guess is that some of the stuff in this
paper is throwing-out some information about variability in whatever
"errors" are here. 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. There
would seem to be a possibility of extending this to remove other
systematic effects. I think the key point here is to try to
separate-out any isolated frequencies that may be of interest, rather
than to average across a range of neighbouring frequencies, as may be
going on in this paper.

To go any further in understanding this one would need to have a
mathematical description of whatever model is being used for the full
data-set, together with a proper description of what the various
parameters and error-terms are supposed to mean.

One wonders if an attempt has been made to contact the author of the
Roberts paper, for better information. A straightforward search in a
few steps finds:

Tom Roberts at Illinois Institute of Technology
Research Professor of Physics
630.840.2424
tom.r...@iit.edu

This appears to be current. The date of the paper is not clear.

[J. J. Lodder]

David Jones <dajh...@nowherel.com> wrote:
[Follow-up To: sci.physics.reativity]

[snip comments on a paper by Tom Roberts about Dayton Miller]

> One wonders if an attempt has been made to contact the author of the
> Roberts paper, for better information. A straightforward search in a
> few steps finds:

[snip personal adress]

> This appears to be current. The date of the paper is not clear.

No need for that.
If desired you can discuss the matter with Tom Roberts in person
out in the open in either sci.physics.research (moderated)
or in sci.physics.relativity.
He is a regular and well known poster in both groups.

I strongly disapprove of the attemps here
to discuss these matters behind his back,
and I won't participate for that reason.

Jan

[David Jones]

Those looking for the context of this should see recent posts on the
sci.stat.math newsgroup

[J. J. Lodder]

It started in AUE, when 'Anton Shepelev' (a well-known relativity crank)
called Roberts' reanalysis of Dayton Miller's experiment 'fishy'.

Again, all this should not be discussed behind Roberts' back,

Jan

[David Jones]

(1) Will anyone know what you mean by "AUE"?

(2) those on the relativity group might like to know that the paper
being discussed is at
https://arxiv.org/vc/physics/papers/0608/0608238v2.pdf

(3) on the statistics newsgroup there is a statistically sound
discussion of the data (not by me).

[J. J. Lodder]

Yes, many. And anyone may consult the Newsgroups: header.

> (2) those on the relativity group might like to know that the paper
> being discussed is at
> https://arxiv.org/vc/physics/papers/0608/0608238v2.pdf

They know.

> (3) on the statistics newsgroup there is a statistically sound
> discussion of the data (not by me).

If so, and not crossposted to SPR,
it is lost on the rest of the world,

Jan

[Anton Shepelev]

Rich Ulrich:

> I've cross-posted to a .stat group that has a few readers
> left.

Sad to hear that. Usenet should be taught in school as one
of the last heteratchical, accessible, and independent
communication media.

> I read the citation, and I'm not very interested. - I know
> too little about the device, etc., or about the ongoing
> arguments that apparently exist.

This little knowledge has its advantages -- you could verify
the model for internal consistency and then comment whether
it can be a/the right model for /any/ imaginary experiment.
But since you are not interested -- good luck with whatever
occupations fill you with enthusiasm, and feel free to skip
my comments below:

> Modern statistical analyses and design sophistication for
> statistics were barely being born in 1933, when the Miller
> experiment was published. In regards to complications and
> pitfalls, Time series is worse than analysis of
> independent points; and what I think of as 'circular
> series' (0-360 degrees) is worse than time series. I once
> had a passing acquaintance with time series (no data
> experience) but I've never touched circular data.

Futhermore, there are no time readings in Miller's data.
Although he tried to rotate the device at a steady rate,
irregularities were unavodable. But mark you that Miller's
original analysis is largely of independent points, so that
whatever linear correction he might have applied could not
have affected the harmonical dependency of the fringe shift
upon device orientation.

> 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).

Yes. Futhermore, Roberts picked 67 of about 300 data sheets
from different experiments performed with at different
locations and dates, instead of the entire data from one or
two of the best ones from Mt. Wilson, with the most
prominent positive results. I forget how Roberts acquired
those sheets. If he had manually to type them into the
computer, this incompleteness may be excused. But knowing
the importance of this seminal experiment and of his new
analysis, he realy should have found the time, resources,
and help to digitise the entire data. Yet, he has not put
online even the partial data he has.

> 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.

Does he show or tell? Do you comment on the graphs of
Miller data /after/ processing by his statistical model? It
is the model that I should like to understand better.

> I would want to know how the DEVICE made all those errors
> possible, as a clue to how to exclude their influence on
> an analysis.

This is an entirely different task -- an analysis of your
own -- perhaps more interesting and productive, but
impossible without Miller's original data. The device was a
large, super sensitive rotatable interferometer with two
orghogonal arms. The hypothesis tested was that, if the
Earth moved though the aether, the speed of light was
orientation-dependent, so that a half-periodic (in
orientation, not in time!) signal should be detected.

> If Miller's data has something, Miller didn't show it
> right.

Why do you think so?

> 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.

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. No
so with Roberts's model, which is neither symblic nor has
noise as an explicit term!

> 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.

I have a conjecture, and will discuss it with whoever agrees
to help me. With a my friend, a data scientist, we count
three people who find his explanation unclear.

> 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.

They /are/ usable in that they still contain the supposed
signal and less random noise (because of "multisampling").
But you will be surprised if you look at what that does to
the systematic error!

> 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.

OK. My complaint, however, is about the model that he
fitted, and the way he did it -- by enumerating the
combinations of the seven free parameters by sheer brute
force. Roberts jumped smack dab into the jaws of the curse
of dimensionality where I think nothing called for it! He
even had to "fold" the raw data in two -- to halve the
degrees of freedom. I wonder what he would say to applying
that technique to an experiment with 360 measurements per
cycle!

Thanks for your comments, Rich.

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

[Anton Shepelev]

David Jones:

> The paper is extremely difficult to understand and I have
> tried very hard..

Thank you! That makes four people who have found it
unclear.

> There seems a possibility that you are over-interpreting
> what the author means by "chi-squared". I have heard some
> non-statistical experts in other fields just using "chi-
> squared" to mean a sum of squared errors. So not a formal
> test-statistic for comparing two models?

That is the least problematic part. Before fitting anythng
to anything, one must create a good model -- the
parametrised function to fit, and make sure that function
correctly describes physcial process.

> The various data-manipulations, both in the original paper
> and this one are difficult to follow.

Well, I can help you with those in the original:

Miller D.C.
The Ether-Drift Experiment and the Determination of
the Absolute Motion of the Earth
Reviews of modern physics, Vol.5, July 1933
http://ether-wind.narod.ru/Miller_1933/Miller1933_ocr.pdf

I am sure I understand at least them, and that they are
really simple. Ask away or just ask me to recap it for you.

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

I beg pardon -- do you mean the paper by Roberts or the one
by Miller (the original)? I fear that Roberts does it, yes.
Miller, considering the level of statistical science in
1933, did a top-notch job. Both his graphs and results of
mechanical harmonic analysis[1] show a dominance of the
second harmonic in the signal, albeit at a much lower
magnitude that initially expected.

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

Actually, the sequences of consequtive interferometer "runs"
may be considered as uninterrupted time series, with the
reservation that the data has no time readings, because the
experimenters did not intend it for such analysis. They
averaged the signal between runs for each of the sixteen
orientations. The problem of separating the systematic error
from the signal is quite hard and, in my opinion, requires
an accurately consturcted model, which Roberts seems to
lack.

> I think the key point here is to try to separate-out any
> isolated frequencies that may be of interest, rather than
> to average across a range of neighbouring frequencies, as
> may be going on in this paper.

The second harmonic is of special interest, and I will say
for Roberts that he does try to meausre it in secions II-
III. This question of mine, however, is specifically about
Roberts's statistical model in secion IV.

> To go any further in understanding this one would need to
> have a mathematical description of whatever model is being
> used

If you think Roberts does not provide even this, you confim
my low opinion of his analysis. I thought that maybe
Roberts was simply too clever for me to understand. If
statisticians fail to understand his article and/or find it
incomplete, then something may be really wrong with it.

> for the full data-set

I think we have to separate the model and the data to which
it is fitted and applied. Since Roberts's data is
incomplete -- he selected 67 datasheets from different
experiments accoding to undisclosed criteria! -- and as yet
unpublished, I propose to focus on the model per se, that is
the mathematics and method behind it, if any. I will peruse
futher feedback form statisticians and then share my
criticisms in more detail.

> together with a proper description of what the various
> parameters and error-terms are supposed to mean.

Indeed. I too found them rather muddy, if not internally
contradictory. Robert's model is:

singnal(orientation) + system_error(time)

but he seems to be confused about what he means by time. At
one point he says it is the number of the interferometer
revolution, at another he seems to imply that the sequence
of sixteen readings /during/ a revolution is also time. But
then, this kind of time includes orientation, because,
naturally, the device rotates in time. I therefore fail to
comprehend how this model gurrantees that the singal is not
misinterpreted as part of systematic error. Also -- where
is random error in the model? All in all, I am utterly
confused by Roberts's model from the start.

> One wonders if an attempt has been made to contact the
> author of the Roberts paper, for better information. A
> straightforward search in a few steps finds:

Yes. I had a long, yet emotional and unproductive,
discussion with him several years ago on in relativity
newsgroup, where he is still available. Now, I should like
to discuss his paper in a calmer manner, and with
statisciticians. Roberts being a physicist, I fear his
statistics are a bit rusty, which is only too bad because
the entire article, being a re-analysis of pre-existing
data, is built primarily upon statisics.

Futhermore, any decent scientific article should be
understandable without additional help form the author, and
contrary to J.J. Lodder -- who absurdly forbids me to
discuss this paper "behind the author's back" -- everyone is
entitiled and encourated to discuss published scientific
articles without the biasing presence of their authors. I
intended to contact Roberts again, after I had acuqired a
better understanding of his model, to be better armed. If we
invite Roberts now, I fear there is going to be much flame
and little argument. I am going to be labeled a "relativity
crank" &c. My honest intent now is to forget about
relativity and discuss statistics.

Thank you for the feedback, David. I begin to wonder if I
am going to meet a statistician that understands Roberts's
re-analysis, let alone validates his model as self-
consistent and sound. One cannot criticise what one does not
understand.
____________________
1. E.g. Michelson's harmonic analyser:
https://archive.org/details/pdfy-z5_uTnE-Kga9HKk6

[J. J. Lodder]

Anton Shepelev <anto...@gmail.moc> wrote:

> Futhermore, any decent scientific article should be
> understandable without additional help form the author,

Nonsense. Scientific articles are written for peers,
that is, those who do not need the author's help.
They are not intended for amateurs.
In actual practice the number of peers may be small indeed.

> and contrary to J.J. Lodder -- who absurdly forbids me to discuss this
> paper "behind the author's back" -- everyone is entitiled and encourated
> to discuss published scientific articles without the biasing presence of
> their authors.

I don't 'forbid' you, I tell you that you are misbehaving.
Talking about somebody else behind his back,
telling others that his work is no good, (fishy)
when he may actually be within earshot is very bad manners indeed.
(by standard nettiquette, and everyday manners)
And FYI, 'fishy' in English means: dodgy, shady, suspicious,
or even stinking, and it is a denigrating term.
It shouldn't be used lightly.

> I intended to contact Roberts again, after I had acuqired a better
> understanding of his model, to be better armed. If we invite Roberts now,
> I fear there is going to be much flame and little argument. I am going to
> be labeled a "relativity crank" &c. My honest intent now is to forget
> about relativity and discuss statistics.

I did not 'label' you a ralativity crank,
I noted that you are one, on basis of your postings.
I don't know whether or not Roberts would agree on that.

And while we are at it:
you should take this to the statistics or the relativity group.
The material is not appropriate for AUE,

Jan

[Tom Roberts]

[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).

> I think the key point here is to try to separate-out any isolated
> frequencies that may be of interest, rather than to average across a
> range of neighbouring frequencies, as may be going on in this
> paper.

The only frequency of interest is that corresponding to 1/2 turn, where
any real signal would be. The norm of that amplitude is what the paper
presents in Fig. 11.

> To go any further in understanding this one would need to have a

> mathematical description of whatever model is being used for the full
> data-set, together with a proper description of what the various

> parameters and error-terms are supposed to mean.

Read the paper, and my description above.

IMHO further analysis is not worth the effort -- Miller's data are so
bad that further analysis is useless.

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

> The date of the paper is not clear.

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.

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.

> knowing the importance of this seminal experiment [...]

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 -- Note that
Miller never presented plots of his data (as I did in Fig. 2). Had he
displayed such plots, nobody would have believed he could extract a
signal with a peak-to-peak amplitude < 0.1 fringe. Ditto for the
nonlinearity shown in Fig. 3.

> [I] realy should have found the time, resources, and help to
> digitise the entire data.

Where do you suppose that would come from? Remember that Rev. Mod. Phys.
would not even publish the paper, stating that the subject is too old
and no longer of interest. No sensible funding agency would support
further research on this. IMHO further analysis is not worthwhile, as
his instrument is so very unstable.

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.

> [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
task, and as I have said before, IMHO it is simply not worthwhile.

> 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.

> No so with Roberts's model, which is neither symblic nor has noise as
> an explicit term!

Hmmm. I don't know what "symblic" means. 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.

> They /are/ usable in that they still contain the supposed signal and
> less random noise (because of "multisampling"). But you will be
> surprised if you look at what that does to the systematic error!

Hmmm. The key idea was to subtract the first 1/2 turn from every half
turn, to remove the signal(orientation), leaving just systematic(time),
with each orientation individually zeroed in the first point (of 40).

> My complaint, however, is about the model that he fitted, and the
> way he did it -- by enumerating the combinations of the seven free
> parameters by sheer brute force.

Hmmm. With quantized data and quantized parameters, no conventional
fitting program will work, as they all need derivatives; enumerating the
parameter values was the only way I knew how to find the best set of
parameters. As the paper says, it typically took about 3 minutes per
run (on a now 40-year-old laptop), so this brute force approach was
plenty good enough.

Note the quantization was imposed by Miller's method of taking data, not
anything I did.

> Roberts jumped smack dab into the jaws of the curse of
> dimensionality where I think nothing called for it!

I have no idea of what you mean.

> He even had to "fold" the raw data in two -- to halve the degrees of
> freedom. I wonder what he would say to applying that technique to an
> experiment with 360 measurements per cycle!

a) "Folding" the data is due to the symmetry of the instrument and
is solidly justified on physics grounds.
b) I did apply the analysis to an experiment with 320 measurements
per run.
c) With this algorithm, the main driver for computer time is the
number of parameters, not the number of measurements [#].
The 7 parameters are due to the instrument and Miller's
method of data taking, not anything I did.
d) if you meant 360 orientations, that would indeed be infeasible
to analyze with this algorithm, even with supercomputer support.
But to get data like that would require a completely new
instrument, and it would be silly to not make it as stable
as modern technology permits, so a better algorithm could
surely be devised.

[#] IIRC in the enumeration I used the ten most
likely values for each parameter, so the computer
time for N parameters and K measurements is
roughly proportional to (10^N)*K.

> Miller, considering the level of statistical science in 1933, did a
> top-notch job. Both his graphs and results of mechanical harmonic
> analysis[1] show a dominance of the second harmonic in the signal,
> albeit at a much lower magnitude that initially expected.

See section III of my paper for why the second harmonic dominates -- his
analysis algorithm concentrates his systematic drift into the lowest DFT
bin, which "just happens" to be the second harmonic bin where any real
signal would be. Had Miller displayed plots of his raw data, like my
Fig. 2, nobody would have believed he could extract such a small
"signal" from such messy data. Ditto for the nonlinearities shown in
Fig. 3. Both plots are well within his capabilities.

Go look at my Fig. 2 -- do you seriously think you can extract a
sinewave signal with amplitude ~ 0.1 fringe from that data? Miller
fooled himself into thinking he could, but today you are not constrained
by the lack of knowledge and understanding that he had back in 1933.

> Actually, the sequences of consequtive interferometer "runs" may be
> considered as uninterrupted time series, with the reservation that
> the data has no time readings, because the experimenters did not
> intend it for such analysis.

Not true, as Miller re-aligned the instrument between runs. Indeed he
often realigned the instrument within runs. The need for such frequent
re-alighments indicates how very unstable his instrument is. (The
Michelson interferometer in our lab is realigned every few months, not
every few minutes as Miller's required.)

> The problem of separating the systematic error from the signal is
> quite hard and, in my opinion, requires an accurately consturcted
> model, which Roberts seems to lack.

Go back and read my paper. I developed an excellent model of the
systematic drift for each run I analyzed.

> Robert's model is:
>
> singnal(orientation) + system_error(time)
>
> but he seems to be confused about what he means by time. At one
> point he says it is the number of the interferometer revolution, at
> another he seems to imply that the sequence of sixteen readings
> /during/ a revolution is also time.

_I_ am not confused, but perhaps my description is not as clear as it
could be. As I said in the paper and above, "time" is represented by
successive data points. I used units of turns, with each successive
marker incrementing by 0.0625 turn; each run has "time" from 0 to 20.0
turns. (Miller's and my "turn" = your "revolution".)

> But then, this kind of time includes orientation, because,
> naturally, the device rotates in time. I therefore fail to comprehend
> how this model gurrantees that the singal is not misinterpreted as
> part of systematic error.

The key point is that signal(orientation) is the same for every 1/2
nturn. So by subtracting the data from the first 1/2 turn from each 1/2
turn, signal(orientation) is canceled throughout and the result contains
just systematic(time), with each orientation individually zeroed for the
first point (of 40). See Fig. 10, noting that each orientation has its
own 0 along the vertical axis.

> Also -- where is random error in the model?

It is contained in Miller's data. I made no attempt to distinguish a
systematic drift from random noise or error; in this algorithm there's
no need to do so.

> All in all, I am utterly confused by Roberts's model from the start.

Perhaps a discussion can resolve your confusion.


BTW I still have these 67 runs on disk. If anyone wants them, just ask.
I am surprised that the analysis program source is not also there, but
it isn't, and I doubt it is still accessible. IIRC it was about 10 pages
of Java.

Tom Roberts

[J. J. Lodder]

Tom Roberts <tjobe...@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.

[Rich Ulrich]

On Sun, 5 Mar 2023 12:48:31 -0600, Tom Roberts
<tjobe...@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

[Anton Shepelev]

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] .

[Anton Shepelev]

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.

And your argument for a neglibible noise is -- that the
systematic drift as you estimated it explains alone most of
the raw observed data?

> Note the quantization was imposed by Miller's method of
> taking data, not anything I did.

Sure.

Tom Roberts:

> Anton Shepelev:

>
> > Roberts jumped smack dab into the jaws of the curse of
> > dimensionality where I think nothing called for it!
>
> I have no idea of what you mean.

I mean the following:
https://en.wikipedia.org/wiki/Curse_of_dimensionality

Tom Roberts:
> Anton Shepelev:

>
> > Miller, considering the level of statistical science in
> > 1933, did a top-notch job. Both his graphs and results
> > of mechanical harmonic analysis[1] show a dominance of
> > the second harmonic in the signal, albeit at a much
> > lower magnitude that initially expected.
>
> See section III of my paper for why the second harmonic
> dominates -- his analysis algorithm concentrates his
> systematic drift into the lowest DFT bin, which "just
> happens" to be the second harmonic bin where any real
> signal would be.

In section III, analysing Miller data-reduction's in
frequency domain, you write:

...And finally the two halves of the 16 point 1-turn
signal are averaged to an 8-point 1/2-turn signal.
That is another comb filter that retains only the
even-numbered frequency bins, giving the final
spectrum shown in Fig. 9; the 1/2-turn signal bin is
now number 1
[...]
A conspicuous feature of these spectra is that they
all have decreasing amplitude with increasing
frequency. And in the final plot the frequency bin in
which the real signal would appear is bin 1, the
lowest nonzero frequency bin. [...] This is a simple
consequence of the fact that the 1/2-turn Fourier
component is the lowest frequency retained by the
algorithm, and it will dominate because of the falling
spectrum. When a single frequency bin dominates the
Fourier spectrum, the signal itself looks
approximately like a sinusoid with that period. Using
this data reduction algorithm, any noise with a
falling spectrum will end up looking like an
approximately sinusoidal "signal" with a period of 1/2
turn -- precisely what Miller was looking for.

While correct in themselves, your inferences are based on
the assumption that Miller folded the turn's (orientation)
data in two /prior to/ harmonic analyis, which he did not,
except "the purpose of a preliminary study of the
observations" (Miller, 1933).

These charted "curves" of the actual observations
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. The present ether-drift investigation
is based entirely upon the second order effect, which
is periodic in each half revolution of the
interferometer. This second-order effect is completely
represented by the second term of the Fourier harmonic
analysis of the given curve. 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.

Figure 21 in the 1933 article clearly shows the second
harmonic to dominate over both the first and the higher-
order ones.

> Go look at my Fig. 2 -- do you seriously think you can
> extract a sinewave signal with amplitude ~ 0.1 fringe from
> that data?

I will need the entire Mt. Wilson runs to decide that
myself.

> BTW I still have these 67 runs on disk. If anyone wants
> them, just ask.

Yes, please, I shall be most grateful!

> I am surprised that the analysis program source is not
> also there, but it isn't, and I doubt it is still
> accessible. IIRC it was about 10 pages of Java.

I do not uderstand -- if you wrote the article 1986, how can
it be in Java?

[Tom Roberts]

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

[Tom Roberts]

On 3/5/23 2:47 PM, J. J. Lodder wrote:

> Tom Roberts <tjobe...@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

[Tom Roberts]

On 3/6/23 10:08 PM, Rich Ulrich wrote:
> On Sun, 5 Mar 2023 12:48:31 -0600, Tom Roberts
> <tjobe...@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

[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.

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.

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

> 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.

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

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

I did "sew them together", as described above. This is not an issue. Or
rather, if it is an issue then Miller's data are mostly useless.

>> 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.

My mistake. It was written in 2006.

>> 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?

Yes. Everywhere.

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.

> What is your opinion regarding the claimed galactic orientation of
> the measured drift, as plotted in fig. 22 of the 1933 paper?

Computing an average always yields a value, so it's no surprise that he
came up with an answer. Had he computed errorbars on it, they would have
been larger than 360 degrees, probably much larger.

Look at my Fig. 5. The phase of a fitted sinewave clearly does not
determine any direction whatsoever.

> 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?

I repeat: computing an average always yields a value, so it's no
surprise that he came up with an answer. Had he computed errorbars on
it, they would have been larger than 360 degrees, probably much larger.

Tom Roberts

[Anton Shepelev]

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"?

[Anton Shepelev]

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.

[David Jones]

<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 experiments?

[David Jones]

[Anton Shepelev]

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.

[Anton Shepelev]

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.

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. The
galactic motion of the Earth is dervied from observations at
four different epochs. This is a relatively simple
astronomical calculation using linear algebra. Regardless of
the enormous errorbars, Miller's curves seem to agree with
the hypothesis that the Solar system is moving toward the
constellation of the Dragon. Both the phrases and ampitudes
of their curves seem to correspond closely with those
calculated astronomically. I have not (yet) analysed them
myself.

[David Jones]

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.

[J. J. Lodder]

David Jones <dajh...@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)

[Tom Roberts]

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

[Anton Shepelev]

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 <anto...@gmail.moc>
Subject : Re: statistics in Roberts' paper on Miller
Date : Wed, 8 Mar 2023 15:33:02 +0300
Message-ID: <20230308153302.2e74...@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?

But it was! He measured the ether wind during several full-
days sessions at four different seasons, which let him
estimate the direction of the aether wind. 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. That is, every
day they show a clearly sinusoidal dependency on the time of
day with exactly the phase that would result from an
galactic aether wind rather than an earthly factor. Miller
reports his findings in the 1933 article. Do read
it -- clear and well-written.

> 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.

Yes, as well as I could understand that rather philosophical
passage :-)

[Tom Roberts]

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

[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

[Anton Shepelev]

[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 <anto...@gmail.moc>
Message-ID:<20230308191128.c5d1...@gmail.moc>

[Anton Shepelev]

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

[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
(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

[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

[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

[Anton Shepelev]

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. <20230310010415.84c4...@gmail.moc>
2. <20230308153302.2e74...@gmail.moc>

[Anton Shepelev]

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!

[Anton Shepelev]

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.

[Anton Shepelev]

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.

[David Duffy]

In sci.stat.math David Duffy <davi...@tpg.com.au> wrote:
> In sci.stat.math David Duffy <davi...@tpg.com.au> wrote:
>>
>> This is a quick and dirty analysis in the R stats package.
>
> I was too quick quick in writing this - I needed to unpack those
> degrees of freedom into a linear decline over the rotation, due
> to the overall drift, which explains most of that signal,
> and the actual bump at 180 degrees. If I instead fit a polynomial term,

I have put the resulting plots up at

http://users.tpg.com.au/davidd02/

I smoothed the trends in the data using localized regression separately
for each time the inferometer was readjusted, and have plotted the
resulting residuals. They appear roughly the same as Miller's plot. For
one formal test, I have fitted a random intercept model for the (20)
rotations, along with a fixed effects linear decline within the rotation,
and then added higher degree polynomials to show a weakly significant
non-linear term.

Cheers, David Duffy.

[Anton Shepelev]

David Duffy:

> I have put the resulting plots up at
> http://users.tpg.com.au/davidd02/

Thank you very much, David. Your great, clean, and pure-
HTML blog is an eye-cake.

> I smoothed the trends in the data using localized
> regression separately for each time the inferometer was
> readjusted,

Mr. Roberts "sewed" the entire run (20 turns) into a single
sequence of observations by joining the ends of adjustment
turns. Would it not be a better thing to do, yielding a
single analysable sequence?

> For one formal test, I have fitted a random intercept
> model for the (20) rotations, along with a fixed effects
> linear decline within the rotation, and then added higher
> degree polynomials to show a weakly significant non-linear
> term.

How did you determine the phase and amplitude of the signal
that you write "Miller was hoping for"? Altough it requries
additional work, the time and amplitude of the expected
signal may be estimated knowing the time and latitude.

Observe also that Mr. Roberts has uploaded the enire dataset
he used for his article:

https://www.dropbox.com/sh/8z5svuenaabegoq/AAAPrjK9AOqP-yyPRr5wNBwra?dl=0

[Anton Shepelev]

David Duffy:

> [http://users.tpg.com.au/davidd02/]

> For one formal test, I have fitted a random intercept
> model for the (20) rotations, along with a fixed effects
> linear decline within the rotation, and then added higher
> degree polynomials to show a weakly significant non-linear
> term.

I have a question about your plot of detrended data: why do
some rotations start at marker 1 and some at marker 0? This
may have to do with adjustment rotations, and marker 0 is
the same orientation as marker 16, but still I think the
sine should be fitted to a sequences of sixteen observations
at sixteen markers, not seventeen. The extra marker should
be used to take adjustments into account.

[David Duffy]

Anton Shepelev <anton.txt@g{oogle}mail.com> wrote:
> David Duffy:
>
>> [http://users.tpg.com.au/davidd02/]
>> For one formal test, I have fitted a random intercept
>> model for the (20) rotations, along with a fixed effects
>> linear decline within the rotation, and then added higher
>> degree polynomials to show a weakly significant non-linear
>> term.
>
> I have a question about your plot of detrended data: why do
> some rotations start at marker 1 and some at marker 0? This
> may have to do with adjustment rotations, and marker 0 is

Yes, I dropped duplicate datapoints, though this nicety probably makes
little difference. I didn't stitch the post-adjustment runs together out
of caution, because eyeballing those you see an initial uptick before
they return to that overall downward slope - I think the adjustment was
actually bending the arm, wasn't it? This choice may discard some
information, in the same way the random effects model might lose some
information on the overall measurement drift (not the ether drift!),
since it is being modelled as 20 rotation starts (so a piecewise way of
dealing with nonlinearities) plus a simple linear decline over the 16
markers. One could test a random slope for this as well, so it varies
from rotation to rotation.

Anyway, I think this agrees pretty well with Roberts's overall
conclusions, though I do not explicitly estimate physical model
parameters and confidence limits.

THe other approach to this type of data, it seems to me, is as
a time series analysis with "seasonality" - this strikes me as
a very similar setup mathematically, and the software is already
available.

Anyway, enough from me.

[David Jones]

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.

[J. J. Lodder]

David Jones <dajh...@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

[David Jones]

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.

[J. J. Lodder]

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

Jan

[Tom Roberts]

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

[Anton Shepelev]

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

[Anton Shepelev]

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.

The Miller data /are/ a time series in a way, with the
readings as uniform as the rotation of the device. Would it
be possible to analyse it using the SigSpec algorithm:

https://en.wikipedia.org/wiki/SigSpec

using the eponymous program:

https://arxiv.org/pdf/1006.5081.pdf

[David Jones]

Anton Shepelev wrote:

> 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.
>

> The Miller data are a time series in a way,

They are only a time-series because they have been manipulated in the
form of a time-series. You should not remove real structure in the form
of groups of data unless you can sure that doing so
(a) does not remove or mask effects you are looking
(b) does not introduce effects of the kind you are looking for.

> with the
> readings as uniform as the rotation of the device. Would it
> be possible to analyse it using the SigSpec algorithm:
>
> https://en.wikipedia.org/wiki/SigSpec
>
> using the eponymous program:
>
> https://arxiv.org/pdf/1006.5081.pdf

There may be better/more-capable packages available from time-series
analysis specialists. But you should be aware that any statistical
tests would depend on the validity of the usual assumptions which would
need to be given serious consideration, If you were planning on doing
something depending in a simple way on FFTs you would need to consider
that there is an inherent assumption that the series being analysed is
a good representative of a stationary process (in terms of the length
of the series being analysed). Loosely speaking, can you imagine in a
general way how the observed time-series would have behaved before and
after the period supposedly observed. The "time-series" in the 2006
paper seems to show a distinct change in behaviour part way through.

One might consider a logical way forward that doesn't place heavy
reliance on assumptions would be to show that the apparent peak in the
FFT, such as shown in the 2006 paper, is or is not removed when any
explanatory effects are removed, perhaps leaving this to be judged on
an informal basis. Even if this can be done, you could still be left
with the problem that you are looking for an effect whose cause is
indistinguishable from the effects of other causes, as previously
identified in other literature.

[Tom Roberts]

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

[Tom Roberts]

On 3/18/23 4:41 PM, Anton Shepelev wrote:
> The Miller data /are/ a time series in a way, with the readings as

> uniform as the rotation of the device. [...]

Each run can be considered to be a (regular) time series ONLY if it has
no omitted adjustment turns. From the dozen or so of those that I have
seen [#], I can say that you are HIGHLY unlikely to find any significant
1/2-turn or 1-turn "signal" in them. The ones I remember were simply a
monotonic drift totaling less than 1 fringe during 20 turns -- this is a
self-fulfilling prophecy, because if it drifted much more than that, he
would have made an adjustment. (My memory 17 years later is hazy.)

[#] When I was at CWRU to give a physics colloquium on
this, Prof. Fickinger and I spent a few hours in the
archives scanning Miller's data sheets for runs with no
adjustments. Our only selection criteria were 20 turns
with no adjustments (some runs have fewer turns, a very
few have more). I don't remember if we looked at every
sheet or had to quit before that; I believe we looked
at more than half. IIRC we found several dozen -- that
was 17 years ago and my memory is hazy. I have copies
somewhere, but have no interest in typing them in.

Interestingly, Dayton Miller was the first head of the physics
department at what is now CWRU. He designed their physics building, and
it has several pillars intended to support interferometers, which go all
the way down to bedrock and never connect to the rest of the building
(for vibration isolation). Also: the archives' exhibit on Dayton Miller
was primarily about his extensive collection of flutes; they had to dig
to find his interferometer data sheets, which were kept loose in about a
dozen folders.

Tom Roberts

[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

[Anton Shepelev]

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

[Anton Shepelev]

David Jones:

> > The Miller data are a time series in a way,
>
> They are only a time-series because they have been
> manipulated in the form of a time-series.

Not at all: each run, consisting of 20 consequtive turns
with perhaps a few "adjustment" turns, spans about 20
minutes and represents and single measurement of the aether-
drift. The manipulation comprises reinstating the
adjustments and unrolling the 20 turns of 16 observasions
into a sequence 320 observations.

> You should not remove real structure in the form of groups
> of data

No such structure was removed. The periodicity of individual
turns is preserved in the observatsion indices and time
markings. The data of a "run" is physically a time-series.

> unless you can sure that doing so
> (a) does not remove or mask effects you are looking
> (b) does not introduce effects of the kind you are
> looking for.

I am sure the serialisation in question does neither.

> > with the
> > readings as uniform as the rotation of the device. Would it
> > be possible to analyse it using the SigSpec algorithm:
> > https://en.wikipedia.org/wiki/SigSpec
> > using the eponymous program:
> > https://arxiv.org/pdf/1006.5081.pdf
>
> There may be better/more-capable packages available from
> time-series analysis specialists.

There may be, but SigSpec seems one of the very best, and
specifically designed to detect significant spectral
components in time series. It will no doubt find significant
high-magnitude and low-frequency components in the Miller
signal, but we are interested in whether full- and half-
period components are prominent above the others, and by how
much. "Multisine" analysis (like SigSpec) seems more
unbiased in this case than the standard Fourier, with its
fixed set of harmonics.

> But you should be aware that any statistical tests would
> depend on the validity of the usual assumptions which
> would need to be given serious consideration, If you were
> planning on doing something depending in a simple way on
> FFTs you would need to consider that there is an inherent
> assumption that the series being analysed is a good
> representative of a stationary process (in terms of the
> length of the series being analysed).

The signal sought is stationary within each run, the noise
is also stationary, whereas the instrumental drift is
probably not.

> Loosely speaking, can you imagine in a general way how the
> observed time-series would have behaved before and after

> the period supposedly observed. But if we assume the
> instrumental drift to be free of any periodicity in turn,
> we may discrard spectral components whose frequencies are
> not multiples of 1/turn.

I can imagine that about the hypothetical signal and noise,
but not about the instrumental drift. The assumption,
however, that it is of lower frequency than the signal, may
help to separate one from the other.

> The "time-series" in the 2006 paper seems to show a
> distinct change in behaviour part way through.

It does.

> One might consider a logical way forward that doesn't
> place heavy reliance on assumptions would be to show that
> the apparent peak in the FFT, such as shown in the 2006
> paper, is or is not removed when any explanatory effects
> are removed, perhaps leaving this to be judged on an
> informal basis.

I thought that the spectral-significance (SigSpec) measure
was made to answer such questions.

> Even if this can be done, you could still be left with the
> problem that you are looking for an effect whose cause is
> indistinguishable from the effects of other causes, as
> previously identified in other literature.

Yes, the instrumental error itself could be periodic, but
then it would be present with similar parameters in all
"runs", which is not the case. Mr. Roberts made the same
assumtion -- that the instrumental error is not periodic in
a turn.

[David Jones]

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

[David Jones]

Anton Shepelev wrote:

> David Jones:
>
> > > The Miller data are a time series in a way,
> >
> > They are only a time-series because they have been
> > manipulated in the form of a time-series.
>
> Not at all: each run, consisting of 20 consequtive turns
> with perhaps a few "adjustment" turns, spans about 20
> minutes and represents and single measurement of the aether-
> drift. The manipulation comprises reinstating the
> adjustments and unrolling the 20 turns of 16 observasions
> into a sequence 320 observations.
>
> > You should not remove real structure in the form of groups
> > of data
>
> No such structure was removed. The periodicity of individual
> turns is preserved in the observatsion indices and time
> markings. The data of a "run" is physically a time-series.
>
> > unless you can sure that doing so
> > (a) does not remove or mask effects you are looking
> > (b) does not introduce effects of the kind you are
> > looking for.
>
> I am sure the serialisation in question does neither.

The question will be: will anyone else be sure?

I think I see a common approach between you and Prof. Roberts:
"I think I see a problem, this is what I think will solve the problem,
this is what I have done, therefore I have solved the problem"

You will need to get someone competent to check all the assumptions
involved.

>
> > Even if this can be done, you could still be left with the
> > problem that you are looking for an effect whose cause is
> > indistinguishable from the effects of other causes, as
> > previously identified in other literature.
>
> Yes, the instrumental error itself could be periodic, but
> then it would be present with similar parameters in all
> "runs", which is not the case. Mr. Roberts made the same
> assumtion -- that the instrumental error is not periodic in
> a turn.

But it is not just "instrumental errors" that need to be thought, it is
all the possible explanations put forward by people like Shankland.

[David Jones]

David Jones wrote:

> Anton Shepelev wrote:
>
> > > One might consider a logical way forward that doesn't
> > > place heavy reliance on assumptions would be to show that
> > > the apparent peak in the FFT, such as shown in the 2006
> > > paper, is or is not removed when any explanatory effects
> > > are removed, perhaps leaving this to be judged on an
> > > informal basis.
> >
> > I thought that the spectral-significance (SigSpec) measure
> > was made to answer such questions.
>
> You will need to get someone competent to check all the assumptions
> involved.
>

Let me expand on that. It seems that the "statistical tests" are based
on asymptotic properties/results that are only valid if there is a
stationary process to be analysed. You agreed that the observed series
looks non-stationary. So the basic results cannot be used. However the
package might contain something to allow some version to be applied.

You may be hoping that a spectral analysis package will provide all
your answers, but recall that results of the FFT are just a
sophisticated version of regression analysis, and you may be better off
looking to that for a way to proceed.... provided that you don't apply
the parts of the theory of regression that are not valid here.

[Anton Shepelev]

David Jones to Anton Shepelev:
> > David Jones to Anton Shepelev:

> >
> > > > The data of a "run" is physically a time-series.
> > >
> > > unless you can sure that doing so
> > > (a) does not remove or mask effects you are looking
> > > (b) does not introduce effects of the kind you are
> > > looking for.
> >
> > I am sure the serialisation in question does neither.
>
> The question will be: will anyone else be sure?

Indeed, but it is hard to prove the absense of either loss
you mention.

If you, or anybody else, think that the serialisation of the
turns of a run may introduce some distorition or make the
signal otherwise less noticeable, then please share you
specific concerns, that we may discuss whether they are
justified.

For my part, I can only repeat the each "run" represents
twenty or more consequent turns of the interferometer within
a space of 15-20 minutes. It contains 20*16+1=321
observations made over twenty "observation turns",
occasionally interrupted by "adjustment turns", during which
no observations were recorded. The data, therefore, is a
physical time series with gaps. You can view them in this
form in the seq_t directory in this archive:

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

Since the signal we seek is half-periodic in a turn,
adjustment turns do not disrupt it (in any way that I can
think of).

> I think I see a common approach between you and Prof.
> Roberts: "I think I see a problem, this is what I think
> will solve the problem, this is what I have done,
> therefore I have solved the problem"

Please note, that I initiated discussion of the statistical
analysis of the Miller experiemnts in this group,
specifically because I needed your help and advice as expert
statisticians. Mr. Roberts, on the other hand, professes no
such desire...

> > I thought that the spectral-significance (SigSpec)
> > measure was made to answer such questions.
>
> You will need to get someone competent to check all the
> assumptions involved.

Can you help me first to identify those assumtptions? That
the signal saught is stationary and periodic in a half-turn
is a fact. Noise is not periodic. The instrumental dirft may
be assumed to be aperiodic from looking at the measurements,
but a specific phycial or statistical justification is
welcome. The key point is to determine whether it may pose
as signal or not.

> Let me expand on that. It seems that the "statistical
> tests" are based on asymptotic properties/results that are
> only valid if there is a stationary process to be
> analysed. You agreed that the observed series looks non-
> stationary. So the basic results cannot be used. However
> the package might contain something to allow some version
> to be applied.

How does one determine whether the instrumental drift is a
stationary process? What do you think can make that process
non-stationary? The dominance of the basic linear drift
during the entire run seems to indicate that it is
statuionary within the period of the run. After consulting
the definitiona of a stationary process, I retract my
previous statement to the contrary.

The SigSpec program performs a multisine analysys of a time
series, finding its most significant spectral components (in
no way limited to multiples of a fundamental frequency),
their respective significance, and the residual data. This
should work as well if the singal is stationary and the
error is not.

> You may be hoping that a spectral analysis package will
> provide all your answers, but recall that results of the
> FFT are just a sophisticated version of regression
> analysis, and you may be better off looking to that for a
> way to proceed.... provided that you don't apply the parts
> of the theory of regression that are not valid here.

With FFT, we know our basis beforehand. With multisine, we
do not, which makes it less "prejudiced" to what is sought.
If a significant half-period component appear in multisine,
it will indicate much more than such a component in the FFT,
where it is mathematicaly bound to appear, as Mr. Roberts
correctly observes. Thank you for the advice about
regression. I will think how I can apply it to the data in a
way different from that of Mr. Roberts. Basically,j

> But it is not just "instrumental errors" that need to be
> thought, it is all the possible explanations put forward
> by people like Shankland.

Yes, and that is another direction of research. Can such a
termperature gradient in the room be imagined as to produce
a half-period effect? Can this situation occur in reality?
Is it compaible with the thermometer indications during the
experiment? Is the themal inerita of the insulated
interferometer arms sufficient to suppress that effect to a
magnitude much lower than that of the observed signal?
Unfortunately, I have not been able to read Shankland's
original, and am only acquainted with it through the
criticism of James DeMeo:

http://www.orgonelab.org/miller.htm

See there "see: Shankland Team's 1955 Critique of Miller,"
which is quite interesting, e.g.:

If the periodic effects observed by Miller were the
product of temperature variations, as was claimed by
Shankland and Joos, then why would that variation
systematically point to the same set of azimuth
coordinates along the celestial sidereal clock, but not
to any single terrestrial coordinate linked to civil
time? Miller repeatedly asked this question of his
critics, who had no answer for it. The Shankland team
likewise evaded the question.

[Anton Shepelev]

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).

[Anton Shepelev]

Tom Roberts:

> > The Miller data /are/ a time series in a way, with the
> > readings as uniform as the rotation of the device. [...]
>
> Each run can be considered to be a (regular) time series
> ONLY if it has no omitted adjustment turns.

If regular means gapless. In my pre-processing, I
incorporated the adjustments as you did but instead of
cutting the adjustment turns out I counted them, producing
time series with gaps in readings. Thankfully, there are
methods and even software to analyse such series.

> From the dozen or so of those that I have seen [#], I can
> say that you are HIGHLY unlikely to find any significant
> 1/2-turn or 1-turn "signal" in them.

You published set contains several runs marked "steady",
"very steady", and "perfectly steady" in your
transcriptions. They are not, however, literally monotonic,
but often predominantly so.

> The ones I remember were simply a monotonic drift totaling

> less than 1 fringe during 20 turns this is a self-

> fulfilling prophecy, because if it drifted much more than
> that, he would have made an adjustment. (My memory 17
> years later is hazy.)

Of course, yet there are "perfect" Mt. Wilson runs with no
adjustments and a considerable (in comparison to others)
half-periodic signal, present before any comb-filtering.

> When I was at CWRU to give a physics colloquium on this,
> Prof. Fickinger and I spent a few hours in the archives
> scanning Miller's data sheets for runs with no
> adjustments. Our only selection criteria were 20 turns
> with no adjustments (some runs have fewer turns, a very
> few have more). I don't remember if we looked at every
> sheet or had to quit before that; I believe we looked at
> more than half. IIRC we found several dozen -- that was 17
> years ago and my memory is hazy. I have copies somewhere,
> but have no interest in typing them in.

Will you share all your scans so that I can type them in?

> Interestingly, Dayton Miller was the first head of the
> physics department at what is now CWRU. He designed their
> physics building, and it has several pillars intended to
> support interferometers,

Why more than one? One might think he was erecting a temple
ofthe Ether Wind :-)

> which go all the way down to bedrock and never connect to
> the rest of the building (for vibration isolation).

Similar to some of my loudspeaker designs isolating the
driver from the front baffle of the enclosure.

> Also: the archives' exhibit on Dayton Miller was primarily
> about his extensive collection of flutes;

Does it include his works on acoustics, and particularly the
Phonodeik?

> they had to dig to find his interferometer data sheets,
> which were kept loose in about a dozen folders.

I believe they came from Shankland, after a long period of
being unaccounted and missing. Have you an idea how I can
order scans of those sheets wihtout actually coming to CWRU?
If all hope for a positive result is to be abanandoned, I
will do it after a diligent study of the available data,
meaning some 300 or so sheets from the Mt. Wilson
experiments.

[J. J. Lodder]

Anton Shepelev <anton.txt@g{oogle}mail.com> wrote:

> Tom Roberts:
[-]

> > Interestingly, Dayton Miller was the first head of the
> > physics department at what is now CWRU. He designed their
> > physics building, and it has several pillars intended to
> > support interferometers,
>
> Why more than one? One might think he was erecting a temple
> ofthe Ether Wind :-)

Of course not. There are a great many other physics experiments
that require a stable and vibration-free foundation.
(clocks, mechanical galvanometers, spectroscopes, etc)

Any prudent designer would foresee the need for stable foundations,

Jan

[J. J. Lodder]

Tom Roberts <tjobe...@sbcglobal.net> wrote:

[-]

> Interestingly, Dayton Miller was the first head of the physics
> department at what is now CWRU. He designed their physics building, and
> it has several pillars intended to support interferometers, which go all
> the way down to bedrock and never connect to the rest of the building
> (for vibration isolation). Also: the archives' exhibit on Dayton Miller
> was primarily about his extensive collection of flutes; they had to dig
> to find his interferometer data sheets, which were kept loose in about a
> dozen folders.

That sounds like he no longer believed in it himself,

Jan

[Anton Shepelev]

J. J. Lodder to Anton Shepelev:
> > Tom Roberts:

> >
> > > Interestingly, Dayton Miller was the first head of the
> > > physics department at what is now CWRU. He designed
> > > their physics building, and it has several pillars
> > > intended to support interferometers,
> >
> > Why more than one? One might think he was erecting a
> > temple ofthe Ether Wind :-)
>
> Of course not. There are a great many other physics
> experiments that require a stable and vibration-free
> foundation. (clocks, mechanical galvanometers,
> spectroscopes, etc)

But they are not interferometers.

[Anton Shepelev]

J. J. Lodder to Tom Roberts:

> > Also: the archives' exhibit on Dayton Miller was
> > primarily about his extensive collection of flutes; they
> > had to dig to find his interferometer data sheets, which
> > were kept loose in about a dozen folders.
>
> That sounds like he no longer believed in it himself,

Loose sheets probably means they are not bound (cf. Pascal's
Pensees), not they are in disarray. Miller entrusted his
records to Shankland to "analyse them or burn them."
Prompted in 2002 by antirelativist speculations about
Shankland's destuction of them, CWRU staff made an
intensive search, finding the Miller archive in the Physics
Department.

I have no evidence whatsoever of Miller's disappointment in
the idea of either wind. The last publication, made in 1940
and a year before his death, is a short recap of his ether-
drift experiments and their positive results.

[David Jones]

<snip>


Obviously we can’t hope to deal with the whole of statistical theory
here. But we can look, in some simple cases, at the effects of dealing
or not dealing with pre-analysis data-manipulations within the data
analysis.

Even the most basic statistics work relates to dealing with
within-analysis manipulations. For example the usual formula for the
estimated variance contains the divisor (n-1) instead of the divisor n,
and this can be considered to be an adjustment to take account of the
fact that you subtract-off the sample mean within the analysis.
Similarly, in regression, the sum-of-squares is divided by (n-p) to
take account of fitting a total of p parameters. In both cases the
adjustment is made to get an unbiased estimate of the variance.

So, let’s consider some pre-analysis data manipulations. Let’s assume
you have two pairs of observations (X1,X2) and (Y1,Y2), with
statistical independence within and between pairs. Let the theoretical
mean of each observation in the first pair be M1, and let the
theoretical mean of each observation in the second pair be M2. Suppose
it is assumed the theoretical variance for each of the four
observations is the same, and consider two cases where this is either
known to be 1, or else it needs to be estimated. Then consider four
versions of analyses with different pre-analysis manipulations as
follows.

(a) Separate analysis. Here the data being analysed consists of the two
pairs (X1,X2) and (Y1,Y2). Then the sample-means with each pair,
provide unbiased estimates of the two values M1 and M2, and the
theoretical variance of each estimate is 1/2 if the variance of the
observations is assumed known at 1. If the variance of observations is
unknown, one could get and use two different estimates of that variance
from the sample variance applied within each pair. Each such estimate
would be unbiased.

(b) Separate analysis, but pooled. This is the same as for (a), above,
except that the variance of the observations is estimated by the
average the sampling variances from the two pairs. The theoretical
variances of the means remain the same as in (a), but one gets better
estimates of those variances. This is achieved by making use of an
assumed structure across the pairs (that the variances are the same).

(c) Subtraction of means. To yield a special case of what might be done
for longer series, suppose that a single dataset of 4 values
(Q1,Q2,Q3,Q4) is constructed from the two pairs by subtracting the two
sample means, giving
Q1=(X1-X2)/2, Q2=(X2-X1)/2, Q3=(Y1-Y2)/2, Q4=(Y2-Y1)/2
Obviously doing this prevents any estimation of the means M1 and M2.
Applying the usual formula to get a sample variance from (Q1,Q2,Q3,Q4)
gives an estimate that has a mean value of 2/3 when the true
observation variance is known to be 1. To get a good (unbiased)
estimate you have to know the structure of the pre-analysis data
manipulation that yielded the data-to-be-analysed (Q1,Q2,Q3,Q4). In
fact this turns out to be the pooled sample variance from the original
pairs as in (b). Thus, not all is necessarily lost in doing
pre-analysis data-manipulations, provided that the actual analysis
takes account of those manipulations.

(d) Joining of data. To emulate the data-joining of the paper and of
your proposed analysis, we can consider dealing with a revised dataset
(Z1,Z2,Z3), where
Z1=X1, Z2=X2, Z3=Y2+X2-Y1
Then the mean of each value is M1, and it clear that M1 can be
estimated but not M2. One might use the sample mean of (Z1,Z2,Z3) to
estimate M1: this estimate has a theoretical variance of 7/9. Thus this
estimate is worse than the sample mean of just (Z1,Z2), which is the
same as the sample mean of (X1,X2), whose variance is 1/2. The usual
sample variance obtained from (Z1,Z2,Z3) has an expected value of 5/3
when the theoretical observation variance is 1. If the usual sample
variance obtained from (Z1,Z2,Z3) is used to estimate the variance of
the sample mean of (Z1,Z2,Z3), this would have an expected value of 5/9
rather than the true variance of this sample mean which is 7/9. So
here, if one ignores the way in which (Z1,Z2,Z3) were obtained and just
uses the usual sample estimates, we get an estimate for M1 which is
worse (in terms of variance) than what might have been obtained by just
using one the one sample pair (X1,X2). Moreover the usual formula would
give estimated variances which are biased in either case of trying to
estimate the observation variance or the variance of the sample mean.
One might consider other estimates here, derived from (Z1,Z2,Z3), but
whether or not one looked for optimal estimates this would involve
taking into account the structure by which the dataset was created. To
summarise, poor performance will arise from any attempt to analyse the
constructed dataset without taking into account the details of how it
was constructed. In this example, the data-manipulation throws away any
ability to estimate an important property (M2) of one part the original
dataset whereas retaining all the original data and the structure
therein allows everything to be estimated.

So my conclusion is that you should not try to merge groups of data
into one supposedly-continuous time-series as you don’t have to do so.
It is possible to do a combined analysis of all groups within joining
them. Since there is just one pre-specified frequency there is no need
to do a spectral analysis. But, if you really wanted to do a spectral
analysis combining all groups without joining them together, this is
certainly possible ... you just have to understand the meaning of the
quantities produced in the analysis of a single series.

[Tom Roberts]

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]

On 3/20/23 6:07 AM, Anton Shepelev wrote:
> Have you an idea how I can order scans of those sheets wihtout
> actually coming to CWRU?

Send email to the archives, arch...@case.edu. Ask for an inventory of
Miller's data sheets. They used to be willing to copy them for a nominal
fee, if you told them precisely which sheets to copy (e.g. all sheets
from Mt. Wilson).

When Prof. Fickinger and I visited the archives in 2006, they extended
him (+me) the ability to handle the sheets and flag individual ones for
copying. We had to be careful and preserve the order in the folders.
They snail-mailed paper copies to me. Today you can probably
request that they scan them to PDF and send them to you via email.

Tom Roberts

[Anton Shepelev]

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 <anto...@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.

[Anton Shepelev]

Thank you for the answer, David Jones:

> Obviously we can't hope to deal with the whole of
> statistical theory here. But we can look, in some simple
> cases, at the effects of dealing or not dealing with pre-
> analysis data-manipulations within the data analysis.
>
> Even the most basic statistics work relates to dealing
> with within-analysis manipulations.

Understood.

> For example the usual formula for the estimated variance
> contains the divisor (n-1) instead of the divisor n, and
> this can be considered to be an adjustment to take account
> of the fact that you subtract-off the sample mean within
> the analysis.

In my understanding, this relates to the summands (and
degrees of freedom) being one fewer than the elements in the
sample.

> Similarly, in regression, the sum-of-squares is divided by
> (n-p) to take account of fitting a total of p parameters.
> In both cases the adjustment is made to get an unbiased
> estimate of the variance.

Understood.

> So, let's consider some pre-analysis data manipulations.
> Let's assume you have two pairs of observations (X1,X2)
> and (Y1,Y2), with statistical independence within and
> between pairs. Let the theoretical mean of each
> observation in the first pair be M1, and let the
> theoretical mean of each observation in the second pair be
> M2. Suppose it is assumed the theoretical variance for
> each of the four observations is the same, and consider
> two cases where this is either known to be 1, or else it
> needs to be estimated. Then consider four versions of
> analyses with different pre-analysis manipulations as
> follows.
>
> (a) Separate analysis. Here the data being analysed
> consists of the two pairs (X1,X2) and (Y1,Y2). Then the
> sample-means with each pair, provide unbiased estimates of
> the two values M1 and M2, and the theoretical variance of
> each estimate is 1/2 if the variance of the observations
> is assumed known at 1. If the variance of observations is
> unknown, one could get and use two different estimates of
> that variance from the sample variance applied within each
> pair. Each such estimate would be unbiased.

OK.

> (b) Separate analysis, but pooled. This is the same as for
> (a), above, except that the variance of the observations
> is estimated by the average the sampling variances from
> the two pairs. The theoretical variances of the means
> remain the same as in (a), but one gets better estimates
> of those variances. This is achieved by making use of an
> assumed structure across the pairs (that the variances are
> the same).

In this case, we calculate the means separately, but then
pool the samples together to calculate their common
variance.

> (c) Subtraction of means. To yield a special case of what
> might be done for longer series, suppose that a single
> dataset of 4 values (Q1,Q2,Q3,Q4) is constructed from the
> two pairs by subtracting the two sample means, giving
> Q1=(X1-X2)/2, Q2=(X2-X1)/2, Q3=(Y1-Y2)/2, Q4=(Y2-Y1)/2

I don't like the method of this subtaction, because it
produces a reduandant dataset: Q1=-Q2 and Q3=-Q4. Since the
size of the dataset is equal to the total size of the
original datasets, half the information has been lost.

> Obviously doing this prevents any estimation of the means
> M1 and M2. Applying the usual formula to get a sample
> variance from (Q1,Q2,Q3,Q4) gives an estimate that has a
> mean value of 2/3 when the true observation variance is
> known to be 1.

Indeed, but this estimate belongs to a very different
sample. The difference of random variables is distributed
quite unlike either variable.

> To get a good (unbiased) estimate you have to know the
> structure of the pre-analysis data manipulation that
> yielded the data-to-be-analysed (Q1,Q2,Q3,Q4).

Yes.

> In fact this turns out to be the pooled sample variance
> from the original pairs as in (b).

Hmmmm. I don't see why, but will take it for granted now.
Will check later.

> Thus, not all is necessarily lost in doing pre-analysis
> data-manipulations, provided that the actual analysis
> takes account of those manipulations.

Thou shalt know thy data.

> (d) Joining of data. To emulate the data-joining of the
> paper and of your proposed analysis, we can consider
> dealing with a revised dataset (Z1,Z2,Z3), where
> Z1=X1, Z2=X2, Z3=Y2+X2-Y1

If the (X1,X2) represent the first turn and (Y1,Y2) the
second turn, then the revised dataset according to the paper
is: (X1, X2, Y1, Y2). Later Tom Roberts constucts error-
differences:

Ed1[0 ] = 0; Ed1[1 ] = Y1-X1
Ed2[1/2] = 0; Ed2[3/2] = Y2-X2

and fits their initial levels b1 and b2 to make the error
function E

E = b1 * Ed1 + b2 * Ed2

as smooth as possible in terms of L2 between adjacent values
weighted by the inverse errorbar. His calculation of the
errorbars is another story.

I did not propose subract the subsequences.

> Then the mean of each value is M1, and it clear that M1
> can be estimated but not M2. One might use the sample mean
> of (Z1,Z2,Z3) to estimate M1: this estimate has a
> theoretical variance of 7/9. Thus this estimate is worse
> than the sample mean of just (Z1,Z2), which is the same as
> the sample mean of (X1,X2), whose variance is 1/2. The
> usual sample variance obtained from (Z1,Z2,Z3) has an
> expected value of 5/3 when the theoretical observation
> variance is 1. If the usual sample variance obtained from
> (Z1,Z2,Z3) is used to estimate the variance of the sample
> mean of (Z1,Z2,Z3), this would have an expected value of
> 5/9 rather than the true variance of this sample mean
> which is 7/9. So here, if one ignores the way in which
> (Z1,Z2,Z3) were obtained and just uses the usual sample
> estimates, we get an estimate for M1 which is worse (in
> terms of variance) than what might have been obtained by
> just using one the one sample pair (X1,X2). Moreover the
> usual formula would give estimated variances which are
> biased in either case of trying to estimate the
> observation variance or the variance of the sample mean.

Yes, because the new data is transformed from the original,
it has a different distribution and, generally, different
moments.

> One might consider other estimates here, derived from
> (Z1,Z2,Z3), but whether or not one looked for optimal
> estimates this would involve taking into account the
> structure by which the dataset was created. To summarise,
> poor performance will arise from any attempt to analyse
> the constructed dataset without taking into account the
> details of how it was constructed.

That is /as if/ that dataset were the original,
untransformed, sample, which it is not.

> In this example, the data-manipulation throws away any
> ability to estimate an important property (M2) of one part
> the original dataset whereas retaining all the original
> data and the structure therein allows everything to be
> estimated.

Yes.

> So my conclusion is that you should not try to merge
> groups of data into one supposedly-continuous time-series
> as you don't have to do so.

No, I should not. But in the experiment in question[1], the
data is truly a continuous times series, arranged in a two-
dimensional table for presentation. Therefore, when I (and
Mr. Roberts) merge it back into a single time series, I
commit no fallacy nor transform the data in a statistically
significant manner. Of course, I should not join the
sequences of individual turns if they did not come from the
same pool, and were not produced in the same uninterruted
sequence of observations.

> It is possible to do a combined analysis of all groups
> within joining them.

Without?

> Since there is just one pre-specified frequency there is
> no need to do a spectral analysis.

Perhaps not, but I think it one of valid approaches (if not
the best): a comparison of the various spectral components
may provide insights into whether the one component in
question is genuine signal or part of the noise and
systematic device drift.

> But, if you really wanted to do a spectral analysis
> combining all groups without joining them together, this
> is certainly possible ... you just have to understand the
> meaning of the quantities produced in the analysis of a
> single series.

So, you propose to amend my analysis by performing 20
separate spectral analyses?
____________________
1. https://freeshell.de//~antonius/file_host/Miller-EtherDrift-1933.pdf

[David Jones]

Anton Shepelev wrote:

> Thank you for the answer, David Jones:
>
>
>

> > But, if you really wanted to do a spectral analysis
> > combining all groups without joining them together, this
> > is certainly possible ... you just have to understand the
> > meaning of the quantities produced in the analysis of a
> > single series.
>
> So, you propose to amend my analysis by performing 20
> separate spectral analyses?
> ____________________

No, I suggest you do a single combined spoectral analysis, or that you
do a sine-curve regression, by not pretending you have a single
time-series. You have to understand that an ordinary spectral analysis
is just a special case of regression.

A usual time-series analysis would proceed on the basis that the
relevant "times" are equally spaced and that the position/index within
a single array can be used as a time, instead of having the time
specified explicitly. Then when the time is needed, for example to use
in a sine or cosine function, it is immediately available, rather than
deriving it from the position in the array, So, as a starting position
you would have a dataset that closely corresponds to the actual results
of the experiment. Thus, in instances where the "joining" approach
would replace two values with one, the two original values would be
kept separately, and there would be no related adjustments.
Additionally where there were actually gaps in the original
observations, this can be included. Similarly for incomplete sequences.

Of course this means that the usual time-series packages would not be
useable and, specifically, not the FFT. BUt the series for your problem
are not very long, so no strong need for the FFT.

If you take the view that one of your objectives is to leave a set of
data that are available for others to re-analyse, then it would be good
to include as much explicit information as possible, without
pre-judging what analysis might be done.

To analyse the data, you need to have a statstical model for the
original observations. Such a model explicitly represents what the
modeller thinks explains the variation in the observations. Possibly
this would be represented as an ordinary regression model, but a mixed
fixed- and random-effects model might be considered. THere are
reasonably standard procedures linked to regression that allow checks
to be made on the various assumptions and to look-out for unexplained
effects.

To turn this into a "spectral analysis", YOu would just need to do a
sequence of regression analyses, where each one would have a sine- and
cosine-pair of a single frequency, and where the corresponding value in
the "spectrogram" would be the sum of the square of the regression
coefficients of the sine and cosine terms. It may be possible to
justify reducing the compuations here, by first do a single regression
with no sinusoid at all, and then doing the spectral analysis on the
residuals.

I Suggest you find an experienced statistician to undertake much of
this. At the very least you need someone with the time and ability to
think, and someone who will not try to force the analysis to fit within
the compass of some existing computer package.