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Feb 27, 2023, 4:00:31 PM2/27/23

to

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

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

Feb 28, 2023, 2:47:07 AM2/28/23

to

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>

>>

> 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

>>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
>>

>>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.

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.

Feb 28, 2023, 4:12:18 AM2/28/23

to

In sci.stat.math David Duffy <davi...@tpg.com.au> wrote:

>

> This is a quick and dirty analysis in the R stats package.

>

> 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
> 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.

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.

Feb 28, 2023, 7:42:32 AM2/28/23

to

> 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
> 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.

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.

Feb 28, 2023, 8:23:02 AM2/28/23

to

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]

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

[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:

> 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

Feb 28, 2023, 9:01:35 AM2/28/23

to

sci.stat.math newsgroup

Feb 28, 2023, 9:12:35 AM2/28/23

to

called Roberts' reanalysis of Dayton Miller's experiment 'fishy'.

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

Jan

Feb 28, 2023, 9:57:43 AM2/28/23

to

(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).

Feb 28, 2023, 3:36:54 PM2/28/23

to

> (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).

it is lost on the rest of the world,

Jan

Mar 3, 2023, 3:33:30 PM3/3/23

to

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

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

> left.

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.

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.

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).

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.

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.

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.

> 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.

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.

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.

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.

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

Mar 3, 2023, 4:46:54 PM3/3/23

to

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

> The paper is extremely difficult to understand and I have

> tried very hard..

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?

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.

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.

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.

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.

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

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.

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:

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

Mar 3, 2023, 5:40:20 PM3/3/23

to

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,
> Futhermore, any decent scientific article should be

> understandable without additional help form the author,

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.

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 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

Mar 5, 2023, 1:48:45 PM3/5/23

to

[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

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

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

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

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

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).

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.

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,

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.

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.

appropriate.

David Jones wrote:

> I have heard some non-statistical experts in other fields just using

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.

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.

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.

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.

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

> 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.

and month are enshrined in the first four digits of the filename.

Anton Shepelev wrote:

> there are no time readings in Miller's data.

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.

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

> an explicit term!

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!

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.

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!

> 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!

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.

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.

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.

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.

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.

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?

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.

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

Mar 5, 2023, 3:48:02 PM3/5/23

to

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:
> [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.]

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.
> understand basic experimental technique. The interferometer is so very

> unstable that his measurements are not worth anything --

> 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.
> 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.

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.

Mar 6, 2023, 11:08:59 PM3/6/23

to

On Sun, 5 Mar 2023 12:48:31 -0600, Tom Roberts

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

Thanks for the responses here. Interesting.

me >

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

<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.
>> 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.

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).

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

Mar 8, 2023, 7:33:06 AM3/8/23

to

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] .

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

> 1986.

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] .

Mar 8, 2023, 11:11:31 AM3/8/23

to

Tom Roberts:

> David Jones:

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:

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:

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:

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:

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

Tom Roberts:

> Anton Shepelev:

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?

> 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
> > 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.

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.

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).

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.

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).

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.

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.

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
> > 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.

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.

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
> > 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.

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.

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.

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.

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).

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.

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

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
> > 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.

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.

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.

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:
> > 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.

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
> > 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.

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?

myself.

> 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.

it be in Java?

Mar 8, 2023, 10:09:22 PM3/8/23

to

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

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

My mistake, it was 2006.

Tom Roberts

Mar 8, 2023, 10:26:40 PM3/8/23

to J. J. Lodder

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

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 <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
>> 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.

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

Mar 8, 2023, 10:40:58 PM3/8/23

to

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.
> 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.

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.

Tom Roberts

Mar 9, 2023, 12:11:26 AM3/9/23

to

On 3/8/23 6:33 AM, Anton Shepelev wrote:

> 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).

>

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.

>

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.

>

>> Note that Miller never presented plots of his data (as I did in

>> Fig. 2).

>

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

> Tom Roberts wrote:

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

Oops. 2006.
>> 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

Turn = rotation. These are Miller's terms, and I followed him.

Please don't change the meaning of technical words.

run != turn.

> 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?

> 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.

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.

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.

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
> from the hyphothetical aether by metal?

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...

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
> 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.

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!

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.

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.

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.

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.
> The earlier dates explains a lot.

>> 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.
> for the statiscical reanalysis in section IV as well. Did you do it?

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?

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?

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

Mar 9, 2023, 3:48:37 AM3/9/23

to

I wrote:

> Tom Roberts:

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"?

> 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
> > wants them, just ask.

>

> Yes, please, I shall be most grateful!

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"?

Mar 9, 2023, 3:57:05 AM3/9/23

to

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
> 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"?

pardon.

Mar 9, 2023, 12:07:48 PM3/9/23

to

<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?

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?

Mar 9, 2023, 12:13:55 PM3/9/23

to

Mar 9, 2023, 3:26:58 PM3/9/23

to

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.

> 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.

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

a squred differences weighted with inverse errorbars.

> and that, for some reason, this gave something that was a

> discontinuous function of the model parameters.

(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.

> 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.

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.

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.

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.

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

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.

Mar 9, 2023, 5:04:18 PM3/9/23

to

Tom Roberts:

> Anton Shepelev:

I beg your pardon.

> > [Roberts reanalysis exressed in equations]

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:

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

> 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.

> 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.
> > 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.

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

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.

> 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.

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.

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.

signal.

> Moreover, if they are in Miller's data then they are in my

> model of the systematic.

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.

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.
> > > 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;

Reading on:

> deviations from exactly 90 degrees between the arms do not

> change this.

cycle symmetry of the device.

> Sources of error need not be symmetric, but most of them

> have a symmetric effect on the symmetric instrument.

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.

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,

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.

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.

> 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.

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

> > 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?

>

> > 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.
> 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.

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.

Mar 9, 2023, 8:37:29 PM3/9/23

to

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" ..
> 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.

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?

"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.

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.

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...

>

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.

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.

Mar 10, 2023, 5:25:32 AM3/10/23

to

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)

[-]

Some physics background.

> 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.

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

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?

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.

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)

Mar 10, 2023, 4:10:28 PM3/10/23

to

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
> The paper does give some discussion of "error-bars" but gives no

> details of how these are calculated.

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,

[@] 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

Mar 10, 2023, 4:13:40 PM3/10/23

to

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:

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

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 :-)

> "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.

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.

> It is unfortunate that the 2006 paper provides no actual

> details about what is being done by way of defining the

> objective function.

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
> > > 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

> 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
> 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"

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.

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,

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.

> 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.

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

> 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
> remove certain effects that are of no interest but which

> need to be included in a full model of the observations

> actually made.

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.

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.

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.

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"

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.

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.

> Why wasn't the experiment constructed so as to determine a

> direction for rthe drift if it existed?

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.

passage :-)

Mar 10, 2023, 4:25:33 PM3/10/23

to

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
> 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.

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.

"quantized".

> No later "null" experiment that I know of tried to reproduce the

> Miller experiments but always incorporated some important changes in

> the setup,

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

Mar 10, 2023, 4:42:28 PM3/10/23

to

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
> 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.

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

Mar 10, 2023, 5:14:47 PM3/10/23

to

[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>

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.

>

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

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

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

Mar 10, 2023, 5:32:42 PM3/10/23