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

Oops. 2006.

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

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

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

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

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

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

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

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

Yes.

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

Yes.

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

> So you used a weighted form the of least-squares. But then a
> complete enumeration is unnecessary, becuase least-squares is
> designed to be an analitical method with linear complexity: you
> simply write the smoothness function as a sum of weighted squared
> differences over the tabulated data and optimise it the usual way
> via partial derivatives.

It makes no sense to fit continuous parameters to quantized data, so the
parameters are quantized like the data. Partial derivatives of the
parameters are not possible, and enumeration is the only method I found.

> Notice, however, that large discontinuitites between runs due to
> interferomenter calibration are likely to dominate the fitting.

I never combined runs, so as stated this is a non issue. If by "run" you
mean turn, it is also a non issue because I corrected the data for the
offset in each recalibration turn.

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

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

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

>> Arxiv says it was last revised 15 Oct 2006; the initial submission
>> year and month are enshrined in the first four digits of the
>> filename.
>
> Which is why I thought it was published in 2006 rather than in 1986.
> The earlier dates explains a lot.

My mistake. It was written in 2006.

>> Note that Miller never presented plots of his data (as I did in
>> Fig. 2).
>
> I see that has the adjustments included, as I am sure you had to do
> for the statiscical reanalysis in section IV as well. Did you do it?

Yes. Everywhere.

So look at my Fig. 2 and say with a straight face that you think a
signal with amplitude ~ 0.1 fringe can be extracted from the data.

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

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

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

> Can an instumental error have a concistent half-periodic dependency
> on 1) time of day and 2) the season of the year so as to point into
> a fixed direction in the galaxy?

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

Tom Roberts