An Analysis of the Resolution of the Michelson-Morley Experiment
Tom Roberts
Experiment
Author: Tom Roberts, tjro...@lucent.com
Date: January 23, 2005
Introduction
------------
There have been several recent attempts to re-analyze the original
Michelson Morley experiment [1][2]. Cahill[3] has interpreted these
re-analyses as supporting his theory.
Unfortunately, none of these authors understand error analysis, and thus
do not know how silly their analyses actually are. Their basic problem
is that they, like the original authors, attempt to interpret this
experiment as "measuring the velocity of the earth relative to the
lumeniferous ether". While that was a reasonable approach in 1887, today
it is completely ludicrous -- not because of the mention of "ether", but
because today we use experiments like this to _test_theories_, not to
try to make "measurements" on concepts contained in some particular theory.
In this case, this change in outlook of the scientific method is clearly
required because of a simple observation:
In a hypothetical world in which:
a) a perfect MMX experiment would yield a truly null result
and
b) real measurements are subject to measurement errors
it is statistically highly unlikely that a real MMX measurement will
yield a null result. In such a hypothetical world, of course, the
non-null result is induced purely by the measurement errors. But
with an error analysis of the measurement, it can be determined
whether or not the measurement is consistent with a theory that
predicts a null result.
So when Munera[1] repeatedly proclaims "this is a non-null result" for
various experiments, he is repeating a fundamental error -- sure the
measurements can be interpreted as a non-null result, but the important
question is: are they _consistent_ with the predictions of a given
theory? As we will see below, the actual MMX data are consistent with
the predictions of SR, and with a wide range of theories in which the
earth moves relative to the ether.
Michelson and Morley's data are given, in a reduced form, in their 1887
paper[4]. The above attempts at analysis are based on the data in the
table on page 340 of [4]. Unfortunately these data are not the original
readings, but each row is an average over 6 turns of the interferometer
made over approximately 36 minutes. Note I am discussing only the six
rows for their six runs, not any of the rows containing means.
In performing an analysis on an experiment performed long ago, with only
limited access to the data and no access to the apparatus, we are
limited in our ability to determine the experiment's actual resolution.
I have identified three approaches:
1. Look into a modern Michelson interferometer and estimate the
measurement resolution.
2. Use the original authors' statements to infer their resolution.
3. Use the original authors' data in a statistical analysis of the
resolution displayed by the actual data.
There are in increasing order of confidence and accuracy.
Note that it is important to refer to the actual measurements, and not
to averages. Unfortunately, the available data are averages over 6 turns
of the interferometer, not the original readings. So I will assume that
the errors in the individual measurements are uncorrelated, and normally
distributed. While such an assumption is undesirable, the available data
essentially force it -- a competent modern repetition of this experiment
would take pains to accurately measure the actual resolutions.
Fortunately, the presence of a rather large systematic error in the data
implies that this statistical independence is reasonably likely[#]. In
keeping with the assumption of normal errors and with modern practice,
when I discuss "resolution", I mean the sigma of the associated normal
distribution for the original measurement (in this experiment the
location of a fringe).
[#] During each rotation the reading changed by 15-30
divisions. This forces the observer to reposition the
micrometer for each reading. While statistical independence
is not assured, it is clearly more likely for a system in
which the micrometer is repositioned for each reading than
for a system without the systematic error where the readings
vary by so little that it would be easy for the observer to
simply leave the micrometer untouched (thus inducing an
enormous correlation among readings).
When you plot the data given in the table of [4] for each day, it is
quite apparent that there is a large systematic error that dominates the
measurements -- the measurements at mark 16 before and after the turn
are not equal. In fact, for each of the six runs the difference in the
two marker-16 values is larger than the variations among the other
readings. The authors [4][1][2] all subtract off an assumed linear
dependence of this systematic error, and the original authors [4]
mention a "temperature effect". Given the limited availability of
original data, this is the best one can do, and I will do likewise.
Note, however, that this analysis technique _forces_ the data to be
cyclical. That is, the above subtraction ensures that at the beginning
and end of each turn the value will be exactly zero; any non-zero
measurement in between will naturally appear to be "cyclical". Given
non-zero resolution and independent measurements, there will be non-zero
measurements in between. So claims that somehow the "cyclical nature" of
the results implies or supports the "motion of the earth relative to the
ether" are bogus -- _any_ such data will be "cyclical".
Lets' look at the above three estimates of Michelson and Morley's actual
measurement resolution:
1. Look into a modern Michelson interferometer
----------------------------------------------
I believe that anyone who has ever done so will agree that
a) it is fairly easy to note the location of a fringe to within
about 1/5 of a fringe width
b) it is unlikely to be able to locate fringes to better than
1/10 of a fringe width
Basically the fringes do not have sharp edges, and one must inherently
guess where the center of a fringe is.
So this approach yields an estimate of resolution between 0.1 and 0.2
fringe widths.
2. Use the original author's statements to infer their resolution
-----------------------------------------------------------------
Michelson and Morley[4] state "The width of the fringes varied between
40 to 60 divisions, the mean value being near 50[...]". In keeping with
the assumption that the measurement errors are normally distributed,
I'll assume that this means that 95% of measurements of fringe widths
were contained in the interval from 40 to 60 divisions of their
micrometer. That means their resolution for measuring fringe width is 5
divisions, or 0.1 fringe. As the measurement of a fringe width requires
two measurements of the location of a fringe, their base resolution is
sqrt(2) time this.
So this approach yields an estimate of resolution of 0.14 fringe widths.
3. A statistical analysis of the resolution displayed in the data
-----------------------------------------------------------------
The key to doing this is to find instances in the data where they
measured the same value multiple times; then a histogram of the multiple
measurements will give a distribution of the errors, and the resolution
can be obtained from the distribution.
In an idealized Michelson interferometer, the interfering light rays
travel both directions along each path, so there is exact 180 degree
symmetry. In the actual apparatus, the ray paths are indeed
out-and-back, so this symmetry should apply to the measurements. The
original authors applied this symmetry in their analysis. Here we will
use it to estimate their resolution.
[In fact for perpendicular arms there is an additional
90-degree symmetry, unexploited by all authors including
me.]
The idea is to first subtract the linear systematic from each of the six
rows of data, thus forcing the two measurements at mark 16 to be equal
for each run. Then histogram the eight differences for measurements 180
degrees apart, for all six rows, and determine the resolution of the
measurement from the histogram. This was done in an Excel spreadsheet,
but it is not feasible to display the details in this ASCII medium. The
histogram does not look very Gaussian, but is rather flat between -5 and
+7 divisions. The likely source of this non-Gaussian behavior is the
systematic error that was _assumed_ to be linear, and nonlinearities due
to either non-uniform behavior or non-uniform spacing of the
measurements could cause this. The sigma of the histogram is 3.0
divisions, corresponding to 0.060 fringe widths; as each point is an
average of 6 turns, the resolution of the original measurements is
sqrt(6) times this value.
So this approach yields an estimate of resolution of 0.15 fringe widths.
Discussion
----------
None of the above estimates are particularly compelling, mainly because
the histogram of method 3 is not really Gaussian; this does not destroy
that approach, but makes it less compelling that it would be with
Gausssian errors. But their agreement indicates they are not crazy.
Certainly there is no support for any resolution estimate much lower
than 0.14-0.15 fringe width.
To compare to the original authors' data table, each row is an average
of 6 turns, and so should have a resolution of 0.14/sqrt(6) = 0.057
fringe width. After subtracting the assumed-linear systematic from the 6
rows, the largest deviation from zero is 0.132 fringe widths, or 2.3
sigma; of the 96 data points, only 1 point exceeds 2 sigma, and 11
exceed 1 sigma. Clearly the readings are not Gaussian distributed. But
equally clearly they are consistent with a null result, and provide only
equivocal support for the notion that there is a non-null result.
Interestingly, when one histograms the data with the assumed-linear
systematic subtracted, the deviations from zero are roughly Gaussian
distributed with a mean of -0.01 fringe and a sigma for individual
measurements of 0.1 fringe. While this is _not_ an error plot, when
compared to the above resolution estimates it solidly demonstrates that
the measurements are consistent with the hypothesis of a truly null result.
When Consoli and Costanzo [2] display a graph of the July 9 PM data,
they drew error bars approximately 0.005 fringe -- more than a factor of
ten too small. They give no indication whatsoever how they arrived at
this value; certainly the original authors gave no error bars. The above
estimate of 0.057 fringe is larger than their entire plot, and indicates
their fit is meaningless. Their fit has 10 parameters for 16 data
points, so it is not surprising that they can draw a line through most
of the points, even with tiny error bars. They do not mention any
chi-squared tests for goodness of fit, and without that and realistic
error bars their estimates on the errors in their parameters are
completely bogus. It is clear that with the above error estimate a
zero-parameter flat line fits the data as well as their 10-parameter
Fourier decomposition.
Munera[1] correctly points out that for a velocity relative to the ether
the MMX only displays the projection of the velocity vector onto the
plane of the interferometer, and this implies that it is unlikely that
such a signal will be a pure cosine. He goes on to claim that even the
intra-session average of 6 turns is invalid as during 36 minutes there
is a change in this projection. While true, that is not important,
as his values show it changes by at most ten percent -- this is wildly
exceeded by the resolution of the measurement.
Cahill[3] has interpreted this as a positive observation of motion
relative to his ether, with a value consistent with the CMBR dipole=0
frame. As mentioned above, he is performing an invalid comparison, and
is basically imposing his hopes and dreams onto the data. A proper
analysis would take his formulas with an unknown speed and direction of
motion relative to the ether, and _predict_ the results of the
measurement. Presumably this could then determine the speed and
direction of that motion. Had he done so, it is clear that with the
above resolution estimate his formula would fit the data for any speed
between zero and several thousand km/s and any direction whatsoever.
Conclusion
----------
The recent attempts to "re-analyze" the Michelson Morley
experiment[1][2] are woefully incomplete, and do not include an accurate
consideration of the experiment's actual resolution. If considered as a
measurement of the motion of the earth relative to some ether, the value
depends upon the details of the theory used to model such motion. For
the ether theory used by the original authors, an upper limit of 5 km/s
is appropriate, but might be reduced by a careful modern analysis. For
Cahill's theory an upper limit of several thousand km/s is appropriate.
In any case, the experiment is indeed solidly consistent with the
prediction of SR -- a null result.
[1] H.Munera, APEIRON _5_ (1998), p37.
[2] Consoli and Costanzo, http://arxiv.org/abs/astro-ph/0311576
[3] Cahill, http://arxiv.org/abs/physics/0501051
Cahill and Kitto, http://arxiv.org/abs/physics/0205070
[4] Michelson and Morley, Am. J. Sci., _XXXIV_ (1887), p333.
http://www.aip.org/history/gap/PDF/michelson.pdf
harry
Finally a clear scientific response of quality! - for [1], I have the
PDF.
I agree with your conclusion, although I must admit that my opinion may
be biased as here you support my intuitive estimation that although to
me it looks like some kind of signal, no hard conclusions are possible
based on so little data with so much noise.
One thing though: Your remark that the plots are "forced to be
cyclical" is a little beside the point, as the claim is that the plots
are cyclical in a way that is consistent with motion through an ether.
For example 3 cycles in one turn would be a bad match.
As counter argument one may point out that an inhomogeneous temperature
distribution may cause a similar 2-cycle periodicity as one would
expect from ether theory.
Thanks again.
Harald
Bill Hobba
"Tom Roberts" <tjro...@lucent.com> wrote in message
news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
> Title: An Analysis of the Resolution of the Michelson-Morley
> Experiment
> Author: Tom Roberts, tjro...@lucent.com
> Date: January 23, 2005
Just a note of thanks for posting your very interesting and informative
analysis. It is one I will be keeping.
Thanks Again
Bill
Koobee Wublee
"Tom Roberts" <tjro...@lucent.com> wrote in message
news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
Tom, it is a good work.
However, I don't see you addressing the fundamental hypothesis that makes
Cahill think the absolute motion can be detected (just the interpretation of
data). I would very much love to see your comments applied to the Gravity
Probe project where they are trying to detect frame grabbing from a set of
very noisy data.
Tom Roberts
Tom Roberts wrote:
> [...]
> 2. Use the original author's statements to infer their resolution
> -----------------------------------------------------------------
> Michelson and Morley[4] state "The width of the fringes varied between
> 40 to 60 divisions, the mean value being near 50[...]". In keeping with
> the assumption that the measurement errors are normally distributed,
> I'll assume that this means that 95% of measurements of fringe widths
> were contained in the interval from 40 to 60 divisions of their
> micrometer. That means their resolution for measuring fringe width is 5
> divisions, or 0.1 fringe. As the measurement of a fringe width requires
> two measurements of the location of a fringe, their base resolution is
> sqrt(2) time this.
>
> So this approach yields an estimate of resolution of 0.14 fringe widths.
This value is a difference of two measurements, not an average, so to
get their base resolution one must divide by sqrt(2), not multiply.
So this approach yields an estimate of resolution of 0.07 fringe widths.
Note, however, that such measurements were surely carried out over a
period much shorter than 36 minutes, or even 6 minutes, so the
contribution of their systematic error is significantly less than for
their real measurements.
If I were forced to pick a single value for their resolution, I would
pick 0.11 fringe widths, the average of estimates 2 and 3 (the two
quantitative methods). But I would not quarrel with values between 0.10
and 0.15.
Carrying this lower value into the rest of the article will change the
numerical details, but not the basic conclusions:
a. their resolution is still far larger than the variations in their
data
b. their data are insufficient to determine any value for "velocity
relative to the ether" other than an upper bound (which depends
on the theory, as discussed in the article)
c. a zero-parameter flat line will still fit their data as well as
that 10-parameter Fourier decomposition
Tom Roberts tjro...@lucent.com
harry
"> Michelson and Morley[4] state "The width of the fringes varied
between
> 40 to 60 divisions, the mean value being near 50[...]". In keeping
with
> the assumption that the measurement errors are normally distributed,
> I'll assume that this means that 95% of measurements of fringe widths
> were contained in the interval from 40 to 60 divisions of their
> micrometer. That means their resolution for measuring fringe width is
5
> divisions, or 0.1 fringe. As the measurement of a fringe width
requires
> two measurements of the location of a fringe, their base resolution
is
> sqrt(2) time this.
> So this approach yields an estimate of resolution of 0.14 fringe
widths.
This value is a difference of two measurements, not an average, so to
get their base resolution one must divide by sqrt(2), not multiply.
So this approach yields an estimate of resolution of 0.07 fringe
widths."
Tom are you sure?! In general a difference between two measurements
increases the error.
I may have misunderstood the text, in fact I doubt that the total width
was relevant in the first place but this is what I think, asuming that
your 0.1 fringe estimate of one reading is correct and that two
readings are needed:
Max. error 0.1 fringe line left + 0.1 fringe line right = 0.2 fringe
width.
Taking into acount the standard error of 2 measurements,
0.2 * sqrt 2 = 0.14 fringe resolution, as you had in the first place.
Harald
JM Albuquerque
"Tom Roberts" <tjro...@lucent.com> escreveu na mensagem
news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
> Title: An Analysis of the Resolution of the Michelson-Morley
> Experiment
> Author: Tom Roberts, tjro...@lucent.com
> Date: January 23, 2005
(snip)
> In any case, the experiment is indeed solidly consistent with the
> prediction of SR -- a null result.
I would like to discuss some basic principles.
Light is a lot of sine waves.
Those sine wave have a given frequency.
Light is bouncing back and forward in two orthogonal arms.
If the frequency of light doesn't change, the sum of sine waves of equal
frequency gives a sine wave of the same frequency.
In order to have interference, and an MMX positive result, one needs that
light's frequency in one arm changes frequency, namely blue or red shift.
Only if the frequency of the sine waves is not the same we got interference.
Hence, only if we have a blue or red shift in one arm an MMX positive is
possible, otherwise the sum of sine waves of equal frequency gives a sine
wave of the same frequency.
To have blue or red shift one needs relative speed between the source and
the observer.
Since in the MMX apparatus there is no such relative speed, source and
observer both moves at the same speed, I guess that it is obvious that the
only possible result for the MMX is a null result. So the MMX apparatus is
not qualified to measure the speed of light.
greywolf42
news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
> Experiment
> Author: Tom Roberts, tjro...@lucent.com
> Date: January 23, 2005
>
>
> Introduction
> ------------
>
> There have been several recent attempts to re-analyze the original
> Michelson Morley experiment [1][2]. Cahill[3] has interpreted these
> re-analyses as supporting his theory.
>
> Unfortunately, none of these authors understand error analysis, and thus
> do not know how silly their analyses actually are. Their basic problem
> is that they, like the original authors, attempt to interpret this
> experiment as "measuring the velocity of the earth relative to the
> lumeniferous ether". While that was a reasonable approach in 1887, today
> it is completely ludicrous -- not because of the mention of "ether", but
> because today we use experiments like this to _test_theories_, not to
> try to make "measurements" on concepts contained in some particular
> theory.
LOL! Well, Tom just trashed all statistical analysis courses. Measurement
theory is designed to measure *values* of observables. Not to test other
theories.
> In this case, this change in outlook of the scientific method is clearly
> required because of a simple observation:
LOL! Tom is requiring abandonment of the scientific method!
> In a hypothetical world in which:
> a) a perfect MMX experiment would yield a truly null result
Tom retreats immediately into a gedanken. Or is it simply allegory?
> and
> b) real measurements are subject to measurement errors
> it is statistically highly unlikely that a real MMX measurement will
> yield a null result.
This is simply setting up a straw man. Null result has a definite meaning.
Tom is trying to redefine it.
> In such a hypothetical world, of course, the
> non-null result is induced purely by the measurement errors.
That is simply because Tom first assumed that there was nothing to measure.
And because Tom has now attempted to mislead the audience, by claiming that
statistical fluctuations below the resolution of the instrument are claimed
to be "non-null." This is simply begging the question.
> But
> with an error analysis of the measurement, it can be determined
> whether or not the measurement is consistent with a theory that
> predicts a null result.
And error analysis can also determine whether or not the measurement is
consistent with a theory that predicts a *non-null* result.
But in the experiment, we don't really care what various theories claim.
The observations (data) stand on their own.
> So when Munera[1] repeatedly proclaims "this is a non-null result" for
> various experiments, he is repeating a fundamental error -- sure the
> measurements can be interpreted as a non-null result, but the important
> question is: are they _consistent_ with the predictions of a given
> theory?
That is important only to fixated priests, like Tom. If there is a 'signal'
that shows above pure noise or the physical resolution of the instrument, it
exists. Even if we don't (yet) have a theory that predicts that
experimental result.
> As we will see below, the actual MMX data are consistent with
> the predictions of SR, and with a wide range of theories in which the
> earth moves relative to the ether.
So, get to it, already, Tom! Enough of the preaching and hypotheticals!
> Michelson and Morley's data are given, in a reduced form, in their 1887
> paper[4]. The above attempts at analysis are based on the data in the
> table on page 340 of [4]. Unfortunately these data are not the original
> readings, but each row is an average over 6 turns of the interferometer
> made over approximately 36 minutes. Note I am discussing only the six
> rows for their six runs, not any of the rows containing means.
Yet this is still far more 'data' than modern papers typically include (i.e.
Krisher).
> In performing an analysis on an experiment performed long ago, with only
> limited access to the data and no access to the apparatus, we are
> limited in our ability to determine the experiment's actual resolution.
Tom, why don't you simply once again admit that you've merely
"guessed" about the physical resolution all these years in the FAQ?
> I have identified three approaches:
> 1. Look into a modern Michelson interferometer and estimate the
> measurement resolution.
What about duplicating the MMX interferometer. Why make this a *different*
interferometer?
> 2. Use the original authors' statements to infer their resolution.
> 3. Use the original authors' data in a statistical analysis of the
> resolution displayed by the actual data.
#3 has nothing to do with the physical resolution of the instrument -- which
doesn't change regardless of how many readings we take. Resolution is not
precision (sigma).
> There are in increasing order of confidence and accuracy.
You've got it backwards, Tom. The best way is to recreate the MMX apparatus
and directly measure the physical resolution. The worst way is to play with
statistics.
> Note that it is important to refer to the actual measurements, and not
> to averages. Unfortunately, the available data are averages over 6 turns
> of the interferometer, not the original readings.
At the moment, we are discussing how to determine the physical resolution of
the apparatus. But Tom is here simply presupposing that he's going to use
#3. (The first two were provided only as a diversion.) Tom never even
considered looking at the actual apparatus, or at the statements made by
Michelson and Morely.
> So I will assume that
> the errors in the individual measurements are uncorrelated, and normally
> distributed. While such an assumption is undesirable, the available data
> essentially force it -- a competent modern repetition of this experiment
> would take pains to accurately measure the actual resolutions.
Tom is calling Michelson incompetent! And more modern efforts *did* take
great pains to measure the actual physical resolution. (Miller. But Tom
doesn't like that one, either.)
> Fortunately, the presence of a rather large systematic error in the data
> implies that this statistical independence is reasonably likely[#].
I am presuming that Tom is referring to the apparent drift in the readings
(2 to 5 divisions per minute) as a "large systematic error".
> In
> keeping with the assumption of normal errors and with modern practice,
> when I discuss "resolution", I mean the sigma of the associated normal
> distribution for the original measurement (in this experiment the
> location of a fringe).
Ah, but sigma is not "resolution!" That is the statistical "precision".
The
resolution of the instrument is the minimum values detectable by the device.
It is completely independent of the number of measurements made *with* the
device.
For example, a series of measurements made with a meter stick may reveal an
average with a "sigma" of 5 cm. But the resolution of the meter stick will
still be about 1-2 mm. Tom has simply attempted to define his way out of the
problem.
> [#] During each rotation the reading changed by 15-30 divisions.
At a rotational speed of one turn each 6 minutes (page 339), that is a
change of 2 to 5 divisions per minute. Since "one division means 0.02
wave-length", that is a change of 0.04 to 0.10 wavelength per minute. Or a
total of 0.3 to 0.6 wavelength per rotation.
> This forces the observer to reposition the
> micrometer for each reading.
That *is* the method for taking the reading ... the change in the screw
position for the micrometer.
> While statistical independence
> is not assured, it is clearly more likely for a system in
> which the micrometer is repositioned for each reading than
> for a system without the systematic error where the readings
> vary by so little that it would be easy for the observer to
> simply leave the micrometer untouched (thus inducing an
> enormous correlation among readings).
A completely unsupported, and fallacious statement. Correlations are no
more likely if the micrometer is left untouched (because the system is more
stable).
> When you plot the data given in the table of [4] for each day, it is
> quite apparent that there is a large systematic error that dominates the
> measurements -- the measurements at mark 16 before and after the turn
> are not equal. In fact, for each of the six runs the difference in the
> two marker-16 values is larger than the variations among the other
> readings. The authors [4][1][2] all subtract off an assumed linear
> dependence of this systematic error, and the original authors [4]
> mention a "temperature effect". Given the limited availability of
> original data, this is the best one can do, and I will do likewise.
Michelson and Morely mention a temperature effect as follows:
"It was found that by keeping the apparatus in slow uniform motion, the
results were much more uniform and consistent than when the stone was
brought to rest, and during this time effects of change of temperature came
into action."
But Tom is correct that M&M aren't very clear what they mean.
> Note, however, that this analysis technique _forces_ the data to be
> cyclical. That is, the above subtraction ensures that at the beginning
> and end of each turn the value will be exactly zero; any non-zero
> measurement in between will naturally appear to be "cyclical".
A linear assumption in no way forces a cyclical variation onto data. What
Tom is alluding to here, is that point 16 is both the start and end location
of each turn of the apparatus -- and is zeroed. However, *true* noise would
have no correlation with position of the apparatus. There would be no
reason for the "noise" to correlate to specific orientations of the table.
And the correct way of addressing the issue is to do a chi squared fit on a
sinusoidal pattern.
> Given
> non-zero resolution and independent measurements, there will be non-zero
> measurements in between. So claims that somehow the "cyclical nature" of
> the results implies or supports the "motion of the earth relative to the
> ether" are bogus -- _any_ such data will be "cyclical".
A complete falsehood by Tom.
> Lets' look at the above three estimates of Michelson and Morley's actual
> measurement resolution:
>
> 1. Look into a modern Michelson interferometer
> ----------------------------------------------
> I believe that anyone who has ever done so will agree that
> a) it is fairly easy to note the location of a fringe to within
> about 1/5 of a fringe width
> b) it is unlikely to be able to locate fringes to better than
> 1/10 of a fringe width
> Basically the fringes do not have sharp edges, and one must inherently
> guess where the center of a fringe is.
>
> So this approach yields an estimate of resolution between 0.1 and 0.2
> fringe widths.
Tom in earlier posts claimed 0.1 fringe. But that was before it was pointed
out to him that Miller's results were 0.2 fringe. (So Tom has changed his
standards to try to exclude Miller.) Tom has also championed 0.01 fringe
for Cahill -- simply because Tom "likes" Cahill's conclusion.
But let's stick with Tom's estimate for physical resolution of the
apparatus -- for the purposes of this post. The physical resolution of the
MMX -- according to Tom -- is 0.1 to 0.2 fringes. This is equivalent to 5
to 10 divisions.
Other people might assume a better physical resolution -- or actually
measure it (i.e. like Miller). The results of Tom's analysis are completely
dependent upon his starting assumption (which is different than Tom's
earlier assumptions).
> 2. Use the original author's statements to infer their resolution
> -----------------------------------------------------------------
> Michelson and Morley[4] state "The width of the fringes varied between
> 40 to 60 divisions, the mean value being near 50[...]". In keeping with
> the assumption that the measurement errors are normally distributed,
> I'll assume that this means that 95% of measurements of fringe widths
> were contained in the interval from 40 to 60 divisions of their
> micrometer. That means their resolution for measuring fringe width is 5
> divisions, or 0.1 fringe. As the measurement of a fringe width requires
> two measurements of the location of a fringe, their base resolution is
> sqrt(2) time this.
>
> So this approach yields an estimate of resolution of 0.14 fringe widths.
That is between 0.1 and 0.2 fringe, so I won't belabor this one.
> 3. A statistical analysis of the resolution displayed in the data
> -----------------------------------------------------------------
> The key to doing this is to find instances in the data where they
> measured the same value multiple times; then a histogram of the multiple
> measurements will give a distribution of the errors, and the resolution
> can be obtained from the distribution.
The physical resolution has already been obtained, above. 0.14 fringe
(according to Tom). Variations in actual measurements are merely
statistical error. Better known as 'precision' or 'sigma.'
> In an idealized Michelson interferometer, the interfering light rays
> travel both directions along each path, so there is exact 180 degree
> symmetry. In the actual apparatus, the ray paths are indeed
> out-and-back, so this symmetry should apply to the measurements. The
> original authors applied this symmetry in their analysis. Here we will
> use it to estimate their resolution.
Sic, precision (sigma).
> [In fact for perpendicular arms there is an additional
> 90-degree symmetry, unexploited by all authors including
> me.]
Symmetry is irrelevant in determining statistical variations (precision).
> The idea is to first subtract the linear systematic from each of the six
> rows of data, thus forcing the two measurements at mark 16 to be equal
> for each run. Then histogram the eight differences for measurements 180
> degrees apart, for all six rows, and determine the resolution of the
> measurement from the histogram. This was done in an Excel spreadsheet,
> but it is not feasible to display the details in this ASCII medium.
I'll take your word for it for the 3.0 division value, below for the moment.
> The
> histogram does not look very Gaussian, but is rather flat between -5 and
> +7 divisions. The likely source of this non-Gaussian behavior is the
> systematic error that was _assumed_ to be linear, and nonlinearities due
> to either non-uniform behavior or non-uniform spacing of the
> measurements could cause this.
Or, the data may simply be sinusoidal on top of random error. :)
> The sigma of the histogram is 3.0
> divisions, corresponding to 0.060 fringe widths; as each point is an
> average of 6 turns, the resolution
Sic, precision or experimental error.
> of the original measurements is
> sqrt(6) times this value.
Nice try, but no. You cannot determine the variation in the orginal data
from the average value. {You cancel this error, later.}
> So this approach yields an estimate of resolution of 0.15 fringe widths.
This is within the physical resolution range already mentioned. Thus
obviating any of the above manipulations.
> Discussion
> ----------
> None of the above estimates are particularly compelling, mainly because
> the histogram of method 3 is not really Gaussian; this does not destroy
> that approach, but makes it less compelling that it would be with
> Gausssian errors. But their agreement indicates they are not crazy.
> Certainly there is no support for any resolution
sic, precision (sigma).
> estimate much lower
> than 0.14-0.15 fringe width.
0.06 fringe width, according to your own spreadsheet.
> To compare to the original authors' data table, each row is an average
> of 6 turns,
Clarification: Each value on the table is an average of indifidual readings
made during six separate turns.
> and so should have a resolution
sic, precision (or sigma)
> of 0.14/sqrt(6) = 0.057 fringe width.
You can't determine the precision of the average measurement from the
absolute value of the measurement! However, in this case, your prior error
cancels your former error. And you return yourself to the 0.06 fringe width
given by your spread sheet. (Hint: Tom, you are trying too hard.)
> After subtracting the assumed-linear systematic from the 6
> rows, the largest deviation from zero is 0.132 fringe widths,
> or 2.3 sigma; of the 96 data points, only 1 point exceeds 2 sigma,
> and 11 exceed 1 sigma. Clearly the readings are not Gaussian distributed.
As would be expected if there were an underlying sinusoidal pattern. ;)
> But equally clearly they are consistent with a null result, and provide
> only equivocal support for the notion that there is a non-null result.
How would you know, Tom? You haven't attempted an analysis for a sinusoidal
pattern. You've only done your analysis for an SR zero prediction.
As I noted in the other thread, Tom assumed a zero result, and calcuated the
"sigmas" from zero. But he did not determine a chi-squared fit to a
sinusoidal curve, and then compare the two -- to see which theory was the
'better' fit.
Tom is now claiming that the MMX is both "consistent" with SR (null result)
and "equivocal" with a non-null result. But it can't be both. If it is
"equivocal" for non-null, then it is "equivocal" for SR.
> Interestingly, when one histograms the data with the assumed-linear
> systematic subtracted, the deviations from zero are roughly Gaussian
> distributed with a mean of -0.01 fringe and a sigma for individual
> measurements of 0.1 fringe. While this is _not_ an error plot, when
> compared to the above resolution estimates it solidly demonstrates that
> the measurements are consistent with the hypothesis of a truly null
> result.
The same would be true of a pure sine wave, Tom.
> When Consoli and Costanzo [2] display a graph of the July 9 PM data,
> they drew error bars approximately 0.005 fringe -- more than a factor of
> ten too small.
No, they simply started with a value that was a factor of 10 smaller than
you started with, Tom.
> They give no indication whatsoever how they arrived at
> this value;
In this, they are no different than you were, Tom. You simply started with
a bald assertion that the physcial resolution *was* between 0.1 and 0.2
fringe.
> certainly the original authors gave no error bars.
In this, they are no different than you were, Tom, in the claims you have
made in the FAQ and many posts on this newsgroup -- where you have admitted
that you simply "guessed" what the resolutions were.
> The above
> estimate of 0.057 fringe is larger than their entire plot, and indicates
> their fit is meaningless.
No, it simply means that Tom's intial estimate of error is different than
C&C's intial estimate of error.
> Their fit has 10 parameters for 16 data
> points, so it is not surprising that they can draw a line through most
> of the points, even with tiny error bars. They do not mention any
> chi-squared tests for goodness of fit,
But then, neither does Tom, here. Or anywhere else. :)
Tom is afraid to do the chi squared fit for a sinusoid versus a straight
line. Because he can see the wave just as well as anyone else. (Tom, if
you'll send me a copy of your spreadsheet, I'll be happy to do the chi
squared fits for you.)
> and without that and realistic error bars
> their estimates on the errors in their parameters are
> completely bogus.
And so, without a chi-squared test, Tom's estimate on the errors is
completely bogus. :)
> It is clear that with the above error estimate a
> zero-parameter flat line fits the data as well as their 10-parameter
> Fourier decomposition.
But then, there is no reason for them to use Tom's estimate of error. For
Tom used his own (quite arbitrary) values at the beginning of his effort.
We'll need to see C&C's criteria to see what support they have. (Tom has in
the past supported a 0.01 fringe physical resolution for Cahill.)
> Munera[1] correctly points out that for a velocity relative to the ether
> the MMX only displays the projection of the velocity vector onto the
> plane of the interferometer, and this implies that it is unlikely that
> such a signal will be a pure cosine.
Projection will change only the zero point and the magnitude of the signal.
Not the fundmental shape.
> He goes on to claim that even the
> intra-session average of 6 turns is invalid as during 36 minutes there
> is a change in this projection. While true, that is not important,
> as his values show it changes by at most ten percent -- this is wildly
> exceeded by the resolution of the measurement.
Only by Tom's estimate, of course. Tom doesn't mention what Munera claims
for a physical resolution.
> Cahill[3] has interpreted this as a positive observation of motion
> relative to his ether, with a value consistent with the CMBR dipole=0
> frame. As mentioned above, he is performing an invalid comparison, and
> is basically imposing his hopes and dreams onto the data.
Well, Tom mentioned this in his prosyletising intro, but he's never
supported the claim. He's not even looked at Cahill's data -- at least in
this post.
> A proper
> analysis would take his formulas with an unknown speed and direction of
> motion relative to the ether, and _predict_ the results of the
> measurement.
Tom, if you don't *know* the speed and direction of the motion relative to
the aether, then you can't predict anything! Except a sinusoidal shape with
table orientation.
> Presumably this could then determine the speed and
> direction of that motion. Had he done so, it is clear that with the
> above resolution estimate his formula would fit the data for any speed
> between zero and several thousand km/s and any direction whatsoever.
Only because Tom assumes a null result. But runs away from doing a chi
squared fit on a sinusoid.
> Conclusion
> ----------
> The recent attempts to "re-analyze" the Michelson Morley
> experiment[1][2] are woefully incomplete, and do not include an accurate
> consideration of the experiment's actual resolution.
Translation: They disagree with Tom.
> If considered as a
> measurement of the motion of the earth relative to some ether, the value
> depends upon the details of the theory used to model such motion.
Yes. Lorentz would have a different answer.
> For the ether theory used by the original authors,
Michelson and Morely didn't use an aether theory. They used an absolute
space.
> an upper limit of 5 km/s
> is appropriate, but might be reduced by a careful modern analysis. For
> Cahill's theory an upper limit of several thousand km/s is appropriate.
>
> In any case, the experiment is indeed solidly consistent with the
> prediction of SR -- a null result.
Only if you first fudge the numbers, then avoid doing any chi squared
fits -- or actually reading (or addressing) Cahill's paper.
> [1] H.Munera, APEIRON _5_ (1998), p37.
> [2] Consoli and Costanzo, http://arxiv.org/abs/astro-ph/0311576
> [3] Cahill, http://arxiv.org/abs/physics/0501051
> Cahill and Kitto, http://arxiv.org/abs/physics/0205070
> [4] Michelson and Morley, Am. J. Sci., _XXXIV_ (1887), p333.
> http://www.aip.org/history/gap/PDF/michelson.pdf
--
greywolf42
ubi dubium ibi libertas
{remove planet for return e-mail}
Tom Roberts
> [Tom Roberts wrote:]
> This value is a difference of two measurements, not an average, so to
> get their base resolution one must divide by sqrt(2), not multiply.
> So this approach yields an estimate of resolution of 0.07 fringe
> widths."
>
> Tom are you sure?! In general a difference between two measurements
> increases the error.
Yes. The difference has a resolution of 0.1 fringe widths, so the
individual measurements must have a resolution smaller by a factor of
1/sqrt(2), or 0.07 fringe widths. I am computing the resolution of the
individual measurements from the known resolution of the difference, not
the other way 'round.
Tom Roberts tjro...@lucent.com
Henri Wilson
But why would anyone bother?
The MMX null result was obviously 10% correct and was caused by the fact that
light moves at c wrt its source and is reflected from a mirror at the incident
speed wrt that mirror.
Null results don't really reveal much.
>
>Thanks Again
>Bill
>
>
>
HW.
www.users.bigpond.com/hewn/index.htm
"If it's repeated often enough they'll eventually believe it" __Albert Bush
Henri Wilson
>On Sun, 23 Jan 2005 23:53:04 GMT, "Bill Hobba" <bho...@rubbish.net.au> wrote:
>
>>
>>"Tom Roberts" <tjro...@lucent.com> wrote in message
>>news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
>>> Title: An Analysis of the Resolution of the Michelson-Morley
>>> Experiment
>>> Author: Tom Roberts, tjro...@lucent.com
>>> Date: January 23, 2005
>>
>>Just a note of thanks for posting your very interesting and informative
>>analysis. It is one I will be keeping.
>
>But why would anyone bother?
>
>The MMX null result was obviously 10% correct and was caused by the fact that
>light moves at c wrt its source and is reflected from a mirror at the incident
>speed wrt that mirror.
Typo alert!!! Make that 100%
greywolf42
> Error...
>
> Tom Roberts wrote:
> > [...]
> > 2. Use the original author's statements to infer their resolution
> > -----------------------------------------------------------------
> > Michelson and Morley[4] state "The width of the fringes varied between
> > 40 to 60 divisions, the mean value being near 50[...]". In keeping with
> > the assumption that the measurement errors are normally distributed,
> > I'll assume that this means that 95% of measurements of fringe widths
> > were contained in the interval from 40 to 60 divisions of their
> > micrometer. That means their resolution for measuring fringe width is 5
> > divisions, or 0.1 fringe. As the measurement of a fringe width requires
> > two measurements of the location of a fringe, their base resolution is
> > sqrt(2) time this.
> >
> > So this approach yields an estimate of resolution of 0.14 fringe widths.
>
> This value is a difference of two measurements, not an average, so to
> get their base resolution one must divide by sqrt(2), not multiply.
You are welcome. ;)
> So this approach yields an estimate of resolution of 0.07 fringe widths.
sic, precision (sigma).
> Note, however, that such measurements were surely carried out over a
> period much shorter than 36 minutes, or even 6 minutes,
Michelson explicitly stated that each turn of the apparatus took 6 minutes.
> so the
> contribution of their systematic error is significantly less than for
> their real measurements.
LOL! The "real" measurements took place over six minutes.
> If I were forced to pick a single value for their resolution, I would
> pick 0.11 fringe widths, the average of estimates 2 and 3 (the two
> quantitative methods). But I would not quarrel with values between 0.10
> and 0.15.
So now Tom completely abandons his method.... but attempts to retain the
answer -- just without any support.
> Carrying this lower value into the rest of the article will change the
> numerical details, but not the basic conclusions:
LOL! The conclusions were based explicitly on the precision (sigma) being
0.15 fringe. Now that sigma is claimed to be 2/3 of the original value
(though it's actually 1/4 of the original), Tom attempts to claim that there
is "no change".
> a. their resolution is still far larger than the variations in their
> data
Ooopsy. It seems that the variations in the data no longer mimic a gaussian
distribution. Tom's prior claim was that the variations in the data were
precisely equal to a gaussian distribution.
> b. their data are insufficient to determine any value for "velocity
> relative to the ether" other than an upper bound (which depends
> on the theory, as discussed in the article)
And is irrelevant to this discussion, of course. The experimental results
don't *need* a theory -- in order to show a non-zero result.
> c. a zero-parameter flat line will still fit their data as well as
> that 10-parameter Fourier decomposition
But Tom has no support for this claim.
Another Roberts missive torpedoed as it left harbor.
Tom Roberts
> "Tom Roberts" <tjro...@lucent.com> escreveu na mensagem
> news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
> Those sine wave have a given frequency.
> Light is bouncing back and forward in two orthogonal arms.
> If the frequency of light doesn't change, the sum of sine waves of equal
> frequency gives a sine wave of the same frequency.
> In order to have interference, and an MMX positive result, one needs that
> light's frequency in one arm changes frequency, namely blue or red shift.
You are confused. Consider the inertial frame in which the
interferometer is at rest: If one placed a frequency meter anywhere
along the light beams it would measure the same value as the source is
emitting. Just think about it -- if it registered a higher frequency,
then if one waited long enough it would register more cycles than the
source had emitted; if it registered a lower frequency, then if one
waited long enough an arbitrarily-large number of cycles would have to
"pile up" between source and detector. Clearly neither of those happen.
In a Michelson interferometer there is always interference and the
pattern of dark and bright bands is always visible. This occurs because
the slightly-off-axis paths have a slightly different length than the
on-axis path, and the path length for the two arms is affected
differently for such off-axis paths (i.e. to reach a point slightly
off-axis to one side of the image, one arm's ray must follow a path
slightly longer than the on-axis path, and the other must follow a
slightly shorter path than the on-axis path).
> In order to have interference, and an MMX positive result, one needs that
> light's frequency in one arm changes frequency, namely blue or red shift.
No. The frequency remains constant. But since the speed of a wave is the
product of its wavelength and frequency, if its speed changed then its
wavelength would change, and _that_ is what generates a fringe shift in
a Michelson interferometer. This is so because the image of light and
dark bands depends on the wavelength of the light, and a straightforward
geometrical analysis shows that if the wavelength in one arm changes
then the image will shift sideways. That is what Michelson measured.
Tom Roberts tjro...@lucent.com
Tom Roberts
represented, and says nothing about how close the value is to the actual
value being measured. That is _not_ what I am discussing. The usual
words we use are: "errors", "errorbars", and "resolution"; "accuracy" is
not used because we do not know the true value. I did not use "error"
because around here that is certain to be misconstrued. I deliberately
chose to use the word "resolution, AND I TOLD THE READER WHAT I MEAN BY
THAT WORD. Regardless of what greywolf42 says, this _IS_ how these words
are used today by working physicists.
I choose to ignore (and snip) all of greywolf42's insults and vacuous
statements.
greywolf42 wrote:
> Tom Roberts <tjro...@lucent.com> wrote in message
> news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
>> with an error analysis of the measurement, it can be determined
>> whether or not the measurement is consistent with a theory that
>> predicts a null result.
>
> And error analysis can also determine whether or not the measurement is
> consistent with a theory that predicts a *non-null* result.
Sure. But please look at my title -- I am discussing their RESOLUTION,
not their results.
> But in the experiment, we don't really care what various theories claim.
> The observations (data) stand on their own.
No, they don't. One must know how accurate they are. One cannot know
that without knowing the resolution of the underlying measurements.
Hence my article.
And you are quite wrong on a different level: the theory Michelson
implicitly used gives a wildly different value for "speed relative to
the ether" than does Cahill's. As is well known, a theory is required to
interpret experimental data -- otherwise one has just a set of numbers
without meaning.
> If there is a 'signal'
> that shows above pure noise or the physical resolution of the instrument, it
> exists. Even if we don't (yet) have a theory that predicts that
> experimental result.
Hmmmm. You cannot know that without knowing the noise level and/or
resolution of the instrument. THAT is what I am discussing here. And the
conclusion is clear: the variations seen in their plot on page 340 are
much smaller than the errorbars that should be drawn on the data points.
>>I have identified three approaches:
>> 1. Look into a modern Michelson interferometer and estimate the
>> measurement resolution.
>
> What about duplicating the MMX interferometer. Why make this a *different*
> interferometer?
A. OHSA would never permit the construction or use of such an instrument
today (gallons of mercury in the open -- you've got to be kidding!).
B. No competent physicst today would use such an instrument to make
this sort of measurement -- VASTLY better techniques are avilable
today. We live in 2005, not 1887. <shrug>
C. The details of the interferometer are not very important -- what is
at issue is the actual appearance of interference fringes, and the
ability of the human eyeball to resolve and locate them. That has
not changed significantly since 1887, AFAIK.
D. I have neither the resources not interest to construct such an
apparatus. But in college I did have the opportunity to use a
version of a Michelson interferometer, as have many generations of
physicists.
>> 3. Use the original authors' data in a statistical analysis of the
>> resolution displayed by the actual data.
>
> #3 has nothing to do with the physical resolution of the instrument -- which
> doesn't change regardless of how many readings we take.
You have to READ my article and UNDERSTAND the analysis I am
performing. The analysis I perform does indeed relate directly to the
physical resolution of the instrument. <shrug>
>>So I will assume that
>>the errors in the individual measurements are uncorrelated, and normally
>>distributed. While such an assumption is undesirable, the available data
>>essentially force it -- a competent modern repetition of this experiment
>>would take pains to accurately measure the actual resolutions.
>
> Tom is calling Michelson incompetent!
Yes, in 2005 a paper like this would be rightly rejected due to its
author's incompetence. But in 1887 it was state-of-the-art. Perhaps you
should look around you and notice that science has progressed since
1887. <shrug>
>>Fortunately, the presence of a rather large systematic error in the data
>>implies that this statistical independence is reasonably likely[#].
>
> I am presuming that Tom is referring to the apparent drift in the readings
> (2 to 5 divisions per minute) as a "large systematic error".
Yes. Over the course of measuring one row in their table this totaled as
much as 30 divisions (0.6 fringe width), or almost 30 times the largest
excursion from zero in the figure on page 340 of their paper. I think
that qualifies as "large". That it is a systematic error is clear -- the
value at mark 16 is not the same before and after a turn.
>>Note, however, that this analysis technique _forces_ the data to be
>>cyclical. That is, the above subtraction ensures that at the beginning
>>and end of each turn the value will be exactly zero; any non-zero
>>measurement in between will naturally appear to be "cyclical".
>
> A linear assumption in no way forces a cyclical variation onto data.
This linear SUBTRACTION most definitely does. It forces the signal to
be zero at the beginning and end of a turn.
> And the correct way of addressing the issue is to do a chi squared fit on a
> sinusoidal pattern.
I am discussing their RESOLUTION, not their results.
> Tom has also championed 0.01 fringe
> for Cahill -- simply because Tom "likes" Cahill's conclusion.
You sure cannot read at all. I disagree completely with Cahill's
approach, and have said so several times. And I have _NEVER_ "championed
0.01 fringe" for any manual optical measurement like this. Quite the
contrary, I have repeatedly pointed out that such a claim is far too small.
>>3. A statistical analysis of the resolution displayed in the data
>>-----------------------------------------------------------------
>>The key to doing this is to find instances in the data where they
>>measured the same value multiple times; then a histogram of the multiple
>>measurements will give a distribution of the errors, and the resolution
>>can be obtained from the distribution.
>
> The physical resolution has already been obtained, above.
Yes, two estimates of it. I am determining multiple estimates so they
can be compared. And estimate #3 is the one most relevant to be used
in fits to their data, becuase it COMES FROM their data.
> Variations in actual measurements are merely
> statistical error.
You simply do not understand the analysis here.
If one makes multiple measurements of a single quantity, and then
histograms the results, the sigma of that histogram gives an estimate of
the resolution of the underlying measurement. That is what I am doing
here.
>>[In fact for perpendicular arms there is an additional
>>90-degree symmetry, unexploited by all authors including
>>me.]
>
> Symmetry is irrelevant in determining statistical variations (precision).
The symmetries are used to determine which values are multiple
measurements of the same quantity, so the differences between such
measurements can be histogrammed to determine the resolution of the
underlying measurement.
I chose not to use the 90-degree symmery, because it is more complicated
than the 180-degree one, and because the arms are not exactly perpendicular.
>>of the original measurements is
>>sqrt(6) times this value.
>
> Nice try, but no. You cannot determine the variation in the orginal data
> from the average value.
I am not looking at "the average value", I am looking at the difference
between two average values that measure the same real signal. With the
assumption of independent errors one can determine the resolution of the
original meausurement from this (as described above).
The main reason I relate this back to the resolution of the original
position measurement is to compare to the other estimates of that. As
you point out, this does not affect the application of the error
estimate to the data below.
>>To compare to the original authors' data table, each row is an average
>>of 6 turns,
>>and so should have a resolution of 0.14/sqrt(6) = 0.057 fringe width.
>
> You can't determine the precision of the average measurement from the
> absolute value of the measurement!
I did not do that. I took the estimate of their resolution and used it
to determine the resolution of the average. Given my assumptions this is
valid. As you pointed out, this cancels the early multiplication by sqrt(6).
> As I noted in the other thread, Tom assumed a zero result, and calcuated the
> "sigmas" from zero.
That is BLATANTLY false. I determined the sigma of their measurement
from the histogram of the DIFFERENCES between measurements 180 dgrees
apart. As any real signal must be the same for orientations 180 degrees
apart, this is a valid way to measure their actual resolution because
_any_ real signal is removed. You really should READ the article you are
attempting to criticise.
I repeat: I am discussing their RESOLUTION, not their result.
> But he did not determine a chi-squared fit to a
> sinusoidal curve, and then compare the two -- to see which theory was the
> 'better' fit.
Right. I am discussing their RESOLUTIONS, not their result. In order to
perform such a fit, one must know their actual resolution.
> Tom is now claiming that the MMX is both "consistent" with SR (null result)
> and "equivocal" with a non-null result.
Let me jump ahead 1 paragraph:
>>Interestingly, when one histograms the data with the assumed-linear
>>systematic subtracted, the deviations from zero are roughly Gaussian
>>distributed with a mean of -0.01 fringe and a sigma for individual
>>measurements of 0.1 fringe. While this is _not_ an error plot [...]
Yes, here and nowhere else I am briefly discussing ther result, and not
their resolution. And I said so ("While this is _not_ an error plot [...]").
This histogram of their data has a sigma of 0.1 fringe. And the
estimates for their resolution are 0.11 or 0.15 fringe. That directly
implies that if one computes the chi-square for the fit to a 0-parameter
straight line one will obtain a good fit and a high-confidence
chi-square. That's what I meant when I said
>> it solidly demonstrates that
>>the measurements are consistent with the hypothesis of a truly null
>>result.
>
> The same would be true of a pure sine wave, Tom.
No. You must include a constant term as well (except for an orientation
along marker 16 which was forced to have a zero signal by the
subtraction of the assumed-linear systematic). But yes, such a fit could
be equally good as long as the amplitude is small enough to fit inside
the error bars. <shrug>
>>When Consoli and Costanzo [2] display a graph of the July 9 PM data,
>>they drew error bars approximately 0.005 fringe -- more than a factor of
>>ten too small.
>
> No, they simply started with a value that was a factor of 10 smaller than
> you started with, Tom.
Again you do not understand my analysis. I have shown, that the value
they used is a factor of ~10 too small. I did not "start with" any
value, my estimates #2 and #3 come directly from the data; while that
phrase could apply to my estimate #1, it does not affect the value used.
And estimate #1 is not invalid or arbitrary, it only seems so to someone
who has never actually looked into a Michelson interferometer. <shrug>
>>They give no indication whatsoever how they arrived at
>>this value;
>
> In this, they are no different than you were, Tom.
Then you indeed cannot read. I have described in detail how I obtained
estimates of their resolution of 0.1-0.2, 0.07, and 0.15 fringe widths.
They give no indication whatsoever how they arrived at the value they
used. Anybody who can actually read can easily verify this.
> You simply started with
> a bald assertion that the physcial resolution *was* between 0.1 and 0.2
> fringe.
Go back and actually READ my original article. I described in detail
how I obtained 3 different estimates of their resolution.
> Tom is afraid to do the chi squared fit for a sinusoid versus a straight
> line.
I am not "afraid" at all. It's just that my subject here does not
include it -- I am discussing their RESOLUTIONS and not their results.
Yes, a fit to their data for small-amplitude sinusoids will have good
chi-squares. So what? I am discussing their RESOLUTION. <shrug>
> Because he can see the wave just as well as anyone else.
The "wave" is much smaller in amplitude than the errorbars on the
points. I cannot help it if Michelson and Morley did not actually draw
those errorbars -- in their day the necessity of doing so was not known.
But YOU are not living in 1887, and YOU have no such excuse.
Neither do Consoli and Costanzo; I cannot help it if they pulled
errorbars out of the air that are a factor of ~10 too small. I have
provided an analysis of the experiemnt that gives three estimates of
what the errorbars actually are.
>>It is clear that with the above error estimate a
>>zero-parameter flat line fits the data as well as their 10-parameter
>>Fourier decomposition.
>
> But then, there is no reason for them to use Tom's estimate of error.
Why is that? You think they are not using Michelson and Morley's data?
Internal relationships among those data imply they have an underlying
resolution of 0.15 fringe (estimate #3), and the author's statements
imply a resolution of 0.07 fringe (estimate #2). And the difference
between these estimates can be qualitatively explained by their large
systematic error, present in the former (#3) but almost absent in the
latter (#2). Applied to C&C's plot, these estimates yield errorbars ~10
time larger than they used, and which are larger than their entire plot.
> For
> Tom used his own (quite arbitrary) values at the beginning of his effort.
Please go back and READ the article. I used data from the Michelson and
Morley paper to obtain estimates #2 and #3 of their resolution. These
are not "quite arbitrary" at all.
> (Tom has in
> the past supported a 0.01 fringe physical resolution for Cahill.)
Blatantly false. You _REALLY_ need to learn how to read.
>>Conclusion
>>----------
>>The recent attempts to "re-analyze" the Michelson Morley
>>experiment[1][2] are woefully incomplete, and do not include an accurate
>>consideration of the experiment's actual resolution.
>
> Translation: They disagree with Tom.
You REALLY need to learn how to read. Neither of those papers "include
an accurate consideration of the experiment's actual resolution", which
anybody who can actually read can confirm quite easily.
>>In any case, the experiment is indeed solidly consistent with the
>>prediction of SR -- a null result.
>
> Only if you first fudge the numbers, then avoid doing any chi squared
> fits
I fudged no numbers. And I did do enough analysis of their result to
know that a chi-squared fit to the 0-parameter flat line will have an
excellent chi-squared (see above). But this article is focusing on their
RESOLUTION, not their result.
In another article greywolf42 wrote in reply to this (discussing
estimate #2):
>> Note, however, that such measurements were surely carried out over a
>> period much shorter than 36 minutes, or even 6 minutes,
>
> Michelson explicitly stated that each turn of the apparatus took 6 minutes.
Yes. But the "such measurements" here are their measurements of a fringe
width, presumably made while the interferometer is not rotating. Surely
this took much less than 6 minutes per measurement, as I said. Perhaps
you should READ the article you are attempting to criticise.
In summary, greywolf42 again proves he does not bother to actually read
the article he is trying to criticise. As that will likely happen for
this article, too, don't expect me to respond to him.
Tom Roberts tjro...@lucent.com
JM Albuquerque
> JM Albuquerque wrote:
> > "Tom Roberts" <tjro...@lucent.com> escreveu na mensagem
> > news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
> > Light is a lot of sine waves.
> > Those sine wave have a given frequency.
> > Light is bouncing back and forward in two orthogonal arms.
> > If the frequency of light doesn't change, the sum of sine waves of equal
> > frequency gives a sine wave of the same frequency.
> > In order to have interference, and an MMX positive result, one needs
> > that light's frequency in one arm changes frequency, namely blue
> > or red shift.
>
> You are confused.
I don't think so.
I'm trying to learn, has usual.
(I do respect you and your work.)
> Consider the inertial frame in which the
> interferometer is at rest: If one placed a frequency meter anywhere
> along the light beams it would measure the same value as the source is
> emitting.
Agree.
> Just think about it -- if it registered a higher frequency,
> then if one waited long enough it would register more cycles than the
> source had emitted; if it registered a lower frequency, then if one
> waited long enough an arbitrarily-large number of cycles would have to
> "pile up" between source and detector. Clearly neither of those happen.
Fully agree.
> In a Michelson interferometer there is always interference and the
> pattern of dark and bright bands is always visible. This occurs because
> the slightly-off-axis paths have a slightly different length than the
> on-axis path, and the path length for the two arms is affected
> differently for such off-axis paths (i.e. to reach a point slightly
> off-axis to one side of the image, one arm's ray must follow a path
> slightly longer than the on-axis path, and the other must follow a
> slightly shorter path than the on-axis path).
It's strange your statement that: "In a Michelson interferometer there
is always interference and the pattern of dark and bright bands is
always visible."
You say this occurs because the slightly-off-axis paths have a slightly
different length than the on-axis path, and the path length for the two
arms is affected differently for such off-axis paths
I'm confused here.
I guess it is a constructive problem?
Could you explain please?
Please explain also what is "on-axis" and "off-axis" because I have a bad
English.
> > In order to have interference, and an MMX positive result, one needs
> > that light's frequency in one arm changes frequency, namely blue or
> > red shift.
>
> No. The frequency remains constant. But since the speed of a wave is the
> product of its wavelength and frequency, if its speed changed then its
> wavelength would change, and _that_ is what generates a fringe shift in
> a Michelson interferometer. This is so because the image of light and
> dark bands depends on the wavelength of the light, and a straightforward
> geometrical analysis shows that if the wavelength in one arm changes
> then the image will shift sideways. That is what Michelson measured.
But, if the frequency remains constant when you sum the two light
frequencies you always get the same frequency (mathematics is 100% exact and
it cannot fail).
Moreover, I can't see any difference between frequency and wave length
(Physically they are one and the same thing, unless you assume the outcome -
the speed of light constant - has a condition, which cannot be if the goal
is to verify if the speed of light is constant or not).
>
>
> Tom Roberts tjro...@lucent.com
>
Harry
"JM Albuquerque" <jm.aR...@sapo.pt> wrote in message
news:35nlpaF...@individual.net...
>
> "Tom Roberts" <tjro...@lucent.com> escreveu na mensagem
> news:LEkJd.21632$by5....@newssvr19.news.prodigy.com...
> > JM Albuquerque wrote:
> > > "Tom Roberts" <tjro...@lucent.com> escreveu na mensagem
> > > news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
> > > Light is a lot of sine waves.
> > > Those sine wave have a given frequency.
> > > Light is bouncing back and forward in two orthogonal arms.
> > > If the frequency of light doesn't change, the sum of sine waves of
equal
> > > frequency gives a sine wave of the same frequency.
> > > In order to have interference, and an MMX positive result, one needs
> > > that light's frequency in one arm changes frequency, namely blue
> > > or red shift.
> >
> > You are confused.
>
> I don't think so.
Tom Roberts is right and there can be no Doppler shift if only the medium
changes speed and everything else is static.
SNIP
> > > In order to have interference, and an MMX positive result, one needs
> > > that light's frequency in one arm changes frequency, namely blue or
> > > red shift.
> >
> > No. The frequency remains constant. But since the speed of a wave is the
> > product of its wavelength and frequency, if its speed changed then its
> > wavelength would change, and _that_ is what generates a fringe shift in
> > a Michelson interferometer. This is so because the image of light and
> > dark bands depends on the wavelength of the light, and a straightforward
> > geometrical analysis shows that if the wavelength in one arm changes
> > then the image will shift sideways. That is what Michelson measured.
>
> But, if the frequency remains constant when you sum the two light
> frequencies you always get the same frequency (mathematics is 100% exact
and
> it cannot fail).
But you already know that the frequency must be the same. Here above Tom
Roberts means average speed.
Compare driving 100 km/h for 100 km with driving 50 km/h for 50 km and then
150 km/h for the next 50 km.
The average speed is not the same...
> Moreover, I can't see any difference between frequency and wave length
> (Physically they are one and the same thing, unless you assume the
outcome -
> the speed of light constant - has a condition, which cannot be if the goal
> is to verify if the speed of light is constant or not).
Throw pieces of paper in a flowing river, one per second. What is the
distance between the pieces?
Would the distance be the same when the river flows twice as fast?
Cheers,
Harald
Dirk Van de moortel
"Tom Roberts" <tjro...@lucent.com> wrote in message news:ct657n$f...@netnews.proxy.lucent.com...
[snip for brevity]
> In summary, greywolf42 again proves he does not bother to actually read
> the article he is trying to criticise. As that will likely happen for
> this article, too, don't expect me to respond to him.
Sure he reads, but 1) he doesn't understand, and 2) he has
the agenda of a religious fanatic. He wouldn't even *want*
to understand.
No one should ever respond (in technical terms) to someone
like that. It does not work.
Dirk Vdm
mountain man
> Title: An Analysis of the Resolution of the Michelson-Morley
> Experiment
> Author: Tom Roberts, tjro...@lucent.com
> Date: January 23, 2005
>
>
> Introduction
> ------------
>
> There have been several recent attempts to re-analyze the original
> Michelson Morley experiment [1][2]. Cahill[3] has interpreted these
> re-analyses as supporting his theory.
Data from 7 experiments have been re-analysed, not just the MMX.
> Unfortunately, none of these authors understand error analysis, and thus
> do not know how silly their analyses actually are. Their basic problem
> is that they, like the original authors, attempt to interpret this
> experiment as "measuring the velocity of the earth relative to the
> lumeniferous ether". While that was a reasonable approach in 1887, today
> it is completely ludicrous -- not because of the mention of "ether", but
> because today we use experiments like this to _test_theories_, not to
> try to make "measurements" on concepts contained in some particular
> theory.
What was measured was the velocity of the apparatus. It does not follow
and has not been claimed by Cahill, that this was with respect to an aether.
The data from seven experiments is consistent with a speed of some
420 +/-30km/s in a direction RA=5.2hr, Dec=-67deg
> In this case, this change in outlook of the scientific method is clearly
> required because of a simple observation:
> In a hypothetical world in which:
> a) a perfect MMX experiment would yield a truly null result
> and
All gas-mode MMX experiments show rotation-induced fringe shifts.
To talk of a hypothetical world where Roberts knows that these experiments
would be null is not science.
> b) real measurements are subject to measurement errors
> it is statistically highly unlikely that a real MMX measurement will
> yield a null result.
Miller did an MMX experiment with 20,000 rotations with a much larger
apparatus, and in 4 months of the year. That data, in the form of 20
rotations
per A4 page, is now available in 1000 A4 pages. Various people have that
data,
and some have put it into electronic files. The results from that agree
with those from the 1991 coaxial cable experiment by DeWitte. He used
1.5 km of buried coax, and 6 cesium atomic clocks to measure the change in
travel
time of RF signal as the earth rotated. The MMX experiment is being repeated
with high precision resonant cavity techniques,but with a gas in the
cavities.
Vacuum cavity experiments are incapable of detecting absolute motion.
>In such a hypothetical world, of course, the
> non-null result is induced purely by the measurement errors.
How does one know that. Why would two different techniques, namely
M interf and coax cables give the same result?
> But
> with an error analysis of the measurement, it can be determined
> whether or not the measurement is consistent with a theory that
> predicts a null result.
>
> So when Munera[1] repeatedly proclaims "this is a non-null result" for
> various experiments, he is repeating a fundamental error -- sure the
> measurements can be interpreted as a non-null result, but the important
> question is: are they _consistent_ with the predictions of a given
> theory?
Nonsense. Observational data can exist and be reliable.
Of course to interpret that data one needs a theory.
>As we will see below, the actual MMX data are consistent with
> the predictions of SR, and with a wide range of theories in which the
> earth moves relative to the ether.
The postulates of SR, as distinct from the relativistic effects, are in
disagreement with the data. It is now clear that it is the Lorentzian
interpretation that is in agreement with the data.
Look at the Miller data. There is data from 20,000 rotations.
Work out the speed and direction. Then make a prediction,
based on the Miller data, as to what MM should have seen.
You will find a good agreement, but of course not perfect.
Some of the rotations look very noisy. Others are in remarkable
agreement. So we can see that MM were seeing a real effect.
MM rejected their own data not because it did not produce the
expected form, but because it did not agree with the Newtonian
theory for the interferometer. Based on that theory and the
minimal speed of 30 km/s, from the orbital speed of the earth,
they expected fringe shifts of a certain size.
The actual fringe shifts were much smaller, but were seen.
This is what happens when you judge an experiment by what
you expect to see, and not what is actually seen. The
interpretation that experimentalists put on their data may be
of anecdotal interest, but is certainly not a part of science.
> Lets' look at the above three estimates of Michelson and Morley's actual
> measurement resolution:
>
> 1. Look into a modern Michelson interferometer
> ----------------------------------------------
> I believe that anyone who has ever done so will agree that
> a) it is fairly easy to note the location of a fringe to within
> about 1/5 of a fringe width
> b) it is unlikely to be able to locate fringes to better than
> 1/10 of a fringe width
> Basically the fringes do not have sharp edges, and one must inherently
> guess where the center of a fringe is.
This is nonsense. Read Miller's paper about accuracy.
You are referring to the Cahill and Kitto paper.
There the speed was noted to be comparable to
the CMB speed, but the direction was not indicated.
Subsequently, in numerous papers by Cahill, it
became clear that the direction was almost
perpendicular to the CMB direction.
Also, get it right please Roberts, Cahill has never
referred to prefered frame as the aether.
> is basically imposing his hopes and dreams onto the data. A proper
> analysis would take his formulas with an unknown speed and direction of
> motion relative to the ether, and _predict_ the results of the
> measurement.
This has been done in great detail in Cahill, Apeiron 11,
No. 1, 2004, pp.53-111, for the Miller data. One can
then determine a best speed and direction from a least
squares fit.
The speed then comes out to be 420+/-30 km/s.
> Presumably this could then determine the speed and
> direction of that motion. Had he done so, it is clear that with the
> above resolution estimate his formula would fit the data for any speed
> between zero and several thousand km/s and any direction whatsoever.
>
>
> Conclusion
> ----------
> The recent attempts to "re-analyze" the Michelson Morley
> experiment[1][2] are woefully incomplete, and do not include an accurate
The main data on absolute motion is Miller.
Would Roberts please analyse that data
and report back.
> consideration of the experiment's actual resolution. If considered as a
> measurement of the motion of the earth relative to some ether, the value
> depends upon the details of the theory used to model such motion. For
> the ether theory used by the original authors, an upper limit of 5 km/s
> is appropriate, but might be reduced by a careful modern analysis. For
> Cahill's theory an upper limit of several thousand km/s is appropriate.
This is incorrect. See above results from analysis of Miller data.
The results of all seven experiments were never null.
The small value from MMX was because they used an invalid
theory. Why does Roberts use the Newtonian theory to get a
speed of 5km/s?, and then claims that this supports his case for
SR. In analysing an experiment one must use one theory
throughout the analysis., and not swap back and forwards to
suit the desired outcome.
The relativistic effects must be used in the theory for the
apparatus, in particular the Fitzgerald-Lorentz contraction effect.
As well the gas has an important role. Without that the other
effects cancel. The relativistic effects are real.
The spacetime ontology is invalidated by experiment. What needs
to be done is to reassess all the data in respect of the Lorentzian
interpretation of these relativistic effects.
It looks like Lorentz got it right long ago.
> In any case, the experiment is indeed solidly consistent with the
> prediction of SR -- a null result.
To summarise by repetition ... the postulates of SR, as distinct
from the relativistic effects, are in disagreement with the data.
It is now clear that it is the Lorentzian interpretation that is in
agreement with the data.
> [1] H.Munera, APEIRON _5_ (1998), p37.
> [2] Consoli and Costanzo, http://arxiv.org/abs/astro-ph/0311576
> [3] Cahill, http://arxiv.org/abs/physics/0501051
> Cahill and Kitto, http://arxiv.org/abs/physics/0205070
> [4] Michelson and Morley, Am. J. Sci., _XXXIV_ (1887), p333.
> http://www.aip.org/history/gap/PDF/michelson.pdf
Have a nice day,
--
Pete Brown
Falls Creek
OZ
www.mountainman.com.au/process_physics
Tom Roberts
> "Tom Roberts" <tjro...@lucent.com> wrote in message
> news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
>>Michelson Morley experiment [1][2]. Cahill[3] has interpreted these
>>re-analyses as supporting his theory.
>
> Data from 7 experiments have been re-analysed, not just the MMX.
OK. I'm just discussing the MMX here. But by implication, and from
knowledge I have of at least Miller's experiment, I strongly suspect the
others will yield similar results as my analysis here.
> The data from seven experiments is consistent with a speed of some
> 420 +/-30km/s in a direction RA=5.2hr, Dec=-67deg
OK. So Cahill claims using wildly invalid errorbars for at least the
MMX. But for that theory the MMX is also consistent with 0 km/sec, and
with 5,000 km/sec in any direction whatsoever. And I'm pretty sure
Miller's measurements will yield a similarly wide range of consistency.
To claim that the MMX "determines" a speed and direction is ludicrous. I
strongly suspect a similar error analysis of all those other experiments
will yield results that show that none of them "determine" speed and
direction with any reasonable errorbar, and that all are also consistent
with 0.
> All gas-mode MMX experiments show rotation-induced fringe shifts.
_ANY_ measurement with non-zero measurement errors made on a rotating
apparatus and from which an assumed-linear systematic is subtracted will
show variations that can be interpreted as "rotation-induced". But they
won't necessarily be significant, and those of the MMX itself aren't.
> To talk of a hypothetical world where Roberts knows that these experiments
> would be null is not science.
That was merely an aside showing why a proper fit is required.
> Miller did an MMX experiment with 20,000 rotations with a much larger
> apparatus, and in 4 months of the year. That data, in the form of 20
> rotations
> per A4 page, is now available in 1000 A4 pages. Various people have that
> data,
> and some have put it into electronic files.
How can I obtain this? I'm only interested in an elecronic version, as I
have no resources for data entry of this magnitude. Though I could
sample a printed version, I suppose.
> The results from that agree
> with those from the 1991 coaxial cable experiment by DeWitte.
I have his "data". It is utterly and completely useless. And if you
don't know that from looking at it and his writings you are deceiving
yourself.
> The MMX experiment is being repeated
> with high precision resonant cavity techniques,but with a gas in the
> cavities.
That should be quite relevant as a test of Cahill's theory. And SR. Make
sure the experimenters measure their systematic errors and perform an
error analysis....
> Vacuum cavity experiments are incapable of detecting absolute motion.
In Cahill's theory. Not in other theories. But, of course, most of those
other theories are refuted experimentally.
> Why would two different techniques, namely
> M interf and coax cables give the same result?
When one interprets errors as signal, one gets out what one puts in.
>>As we will see below, the actual MMX data are consistent with
>>the predictions of SR, and with a wide range of theories in which the
>>earth moves relative to the ether.
>
> The postulates of SR, as distinct from the relativistic effects, are in
> disagreement with the data.
I have no idea what you mean by that. SR predicts zero fringe shift for
all orientations, and the MMX data are consistent with that. This, of
course, implies that the postulates of SR are indeed consistent with the
MMX data.
> Look at the Miller data. There is data from 20,000 rotations.
> Work out the speed and direction.
I only have whatever data he presented in his RMP article, and have not
looked at it. But from an ancient analysis I did I suspect his data will
not determine a direction or speed very well at all. That was only
qualitative, and from my new insight used in this article a quantitative
error analysis ought to be possible if I can get his data.
> MM rejected their own data not because it did not produce the
> expected form, but because it did not agree with the Newtonian
> theory for the interferometer. Based on that theory and the
> minimal speed of 30 km/s, from the orbital speed of the earth,
> they expected fringe shifts of a certain size.
>
> The actual fringe shifts were much smaller, but were seen.
But what was "seen" is not significant. In their plot on page 340, when
one plots their actual errorbars, the errorbars are larger than the
entire picture, and they dwarf the variations in the points.
This does not constitute "seen" in any reasonable sense.
> This is what happens when you judge an experiment by what
> you expect to see, and not what is actually seen.
Yes. The authors conformed to the norms of their day, not ours. One
cannot expect otherwise, of course.
> The
> interpretation that experimentalists put on their data may be
> of anecdotal interest, but is certainly not a part of science.
Right. So claiming that Michelson and Morley's experiment "sees actual
fringe shifts corresponding to some cosmic motion of the earth" is also
not science. Saying it is consistent with SR, and saying it is
consistent with Cahill's theory for any speed between 0 and X (with X
something like 5,000-10,000 km/s) is science [I have verified the first
but not the second].
>>Lets' look at the above three estimates of Michelson and Morley's actual
>>measurement resolution:
>>
>>1. Look into a modern Michelson interferometer
>>----------------------------------------------
>>I believe that anyone who has ever done so will agree that
>> a) it is fairly easy to note the location of a fringe to within
>> about 1/5 of a fringe width
>> b) it is unlikely to be able to locate fringes to better than
>> 1/10 of a fringe width
>>Basically the fringes do not have sharp edges, and one must inherently
>>guess where the center of a fringe is.
>
> This is nonsense. Read Miller's paper about accuracy.
Have you ever looked into a Michelson interferometer??? This is not
nonsense.
> The main data on absolute motion is Miller.
> Would Roberts please analyse that data
> and report back.
If I can obtain the data, and can find the time, I intend to.
>>consideration of the experiment's actual resolution. If considered as a
>>measurement of the motion of the earth relative to some ether, the value
>>depends upon the details of the theory used to model such motion. For
>>the ether theory used by the original authors, an upper limit of 5 km/s
>>is appropriate, but might be reduced by a careful modern analysis. For
>>Cahill's theory an upper limit of several thousand km/s is appropriate.
>
> This is incorrect. See above results from analysis of Miller data.
I am discussing the MMX data _ONLY_, not Miller's.
> The results of all seven experiments were never null.
The MMX is consistent with a null result. Saying "the result is null" is
not warranted. Saying "the result is not null" is downright wrong.
> Why does Roberts use the Newtonian theory to get a
> speed of 5km/s?, and then claims that this supports his case for
> SR.
You misunderstand. I said "For the ether theory used by the original
authors, an upper limit of 5 km/s is appropriate". That is most
definitely not SR.
My claim that the MMX data are consistent with SR is based on the
observation that a flat line will fit their data WITH ERRORBARS with a
good chi-square. I have not computed that chi-square, but from the plots
I have made I know it will be less than 1 per degree of freedom, for 90
degrees of freedom. That implies a good if not excellent fit.
> The relativistic effects must be used in the theory for the
> apparatus, in particular the Fitzgerald-Lorentz contraction effect.
I have no interest in such a theory. I am interested in SR, and the SR
prediction is simple and clear: zero fringe shift for any orientation.
> As well the gas has an important role.
For SR the gas makes no difference.
> The spacetime ontology is invalidated by experiment. What needs
> to be done is to reassess all the data in respect of the Lorentzian
> interpretation of these relativistic effects.
You WAY overstep the data.
> It looks like Lorentz got it right long ago.
Lorentz's theory is experimentally indistinguishable from SR. At least
if one only applies it to uncharged systems, or if one fixes up his
mistake in defining \rho' and uses Poincare's definition.
>>In any case, the experiment is indeed solidly consistent with the
>>prediction of SR -- a null result.
>
> To summarise by repetition ... the postulates of SR, as distinct
> from the relativistic effects, are in disagreement with the data.
Your repetition is still wrong. The prediction of SR is consistent with
the data WITH ERRORBARS.
Tom Roberts tjro...@lucent.com
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
news:DxYJd.136156$K7.8...@news-server.bigpond.net.au...
> Miller did an MMX experiment with 20,000 rotations with a much
larger
> apparatus, and in 4 months of the year. That data, in the form of 20
> rotations
> per A4 page, is now available in 1000 A4 pages.
All of which is rubbish, since his experiment was done in a room with
substabtial temperature variations which Miller did not take into
account. And remember that the work stretched over more than a
complete weather season.
You have been told this before and yet you keep trotting that stuff
out as if you are telling us something new.
Have you ever heard about a concept called intellectual integrity?
[snip]
> The results from that agree
> with those from the 1991 coaxial cable experiment by DeWitte. He
used
> 1.5 km of buried coax, and 6 cesium atomic clocks to measure the
change in
> travel
You have been told previously that that buried coax. lay below the
streets of Brussels in an environment in which the temperature was not
controlled. The lengths of the cables therefore were not constant.
I ask again, why do you trot this out over and over again? Have you
no intellectual integrity?
[snip]
> The main data on absolute motion is Miller.
Thanks for the reminder.
You and I know perfectly well that Miller's data has been discredited
because the worked in an environment in which there were uncontrolled
temperature fluctuations and the data was gathered over a period of 4
months
[snip]
Franz
Harry
"Tom Roberts" <tjro...@lucent.com> wrote in message
news:oa_Jd.13396$Vj3....@newssvr17.news.prodigy.com...
> mountain man wrote:
> > "Tom Roberts" <tjro...@lucent.com> wrote in message
> > news:x1TId.8807$ZV4....@newssvr31.news.prodigy.com...
> >>There have been several recent attempts to re-analyze the original
> >>Michelson Morley experiment [1][2]. Cahill[3] has interpreted these
> >>re-analyses as supporting his theory.
> >
> > Data from 7 experiments have been re-analysed, not just the MMX.
>
> OK. I'm just discussing the MMX here. But by implication, and from
> knowledge I have of at least Miller's experiment, I strongly suspect the
> others will yield similar results as my analysis here.
Don't forget to account for each experiment as one meta data point. With the
"hic" that it may turn out that the data has been "selected", so that it
possibly is not a representative sample.
> > The data from seven experiments is consistent with a speed of some
> > 420 +/-30km/s in a direction RA=5.2hr, Dec=-67deg
>
> OK. So Cahill claims using wildly invalid errorbars for at least the
> MMX. But for that theory the MMX is also consistent with 0 km/sec, and
> with 5,000 km/sec in any direction whatsoever. And I'm pretty sure
> Miller's measurements will yield a similarly wide range of consistency.
> To claim that the MMX "determines" a speed and direction is ludicrous. I
> strongly suspect a similar error analysis of all those other experiments
> will yield results that show that none of them "determine" speed and
> direction with any reasonable errorbar, and that all are also consistent
> with 0.
As I pointed out the other time, you still neglected analysis of the data
themselves. Surely you won't claim that a combination of white noise with a
visible 50 Hz noise interference is consistent with no 50 Hz noise at all
because it is drowned in white noise!
SNIP
> That should be quite relevant as a test of Cahill's theory. And SR. Make
> sure the experimenters measure their systematic errors and perform an
> error analysis....
I know of one ongoing MMX experiment; the experimenter also has such a
signal, but he thinks that his results can be fully explained by temperature
effects only. (I'll let you know when I know more).
SNIP
> When one interprets errors as signal, one gets out what one puts in.
As you showed all too clearly, when one interprets a signal as pure noise,
one gets out what one puts in.
SNIP
> But what was "seen" is not significant. In their plot on page 340, when
> one plots their actual errorbars, the errorbars are larger than the
> entire picture, and they dwarf the variations in the points.
In our lab we have such signals all the time. We simply average the noise
away - problem is that here the number of data points is IMO too meager to
be really sure. A statistics professional should be able to give us an
estimation of how likely it is that there is a 2-cycle sinus present in one
turn.
SNIP
> The MMX is consistent with a null result.
Agree
> Saying "the result is null" is not warranted.
Agree.
Saying "the result is not null" is downright wrong.
Disagree. IMO it may be "right" (that is, more likely true) and a possible
cause is temperature inhomogeneity.
Best regards,
Harald
mountain man
news:ctaamq$t7v$1...@hercules.btinternet.com...
> "mountain man" <hobbit@southern_seaweed.com.op> wrote in message
> news:DxYJd.136156$K7.8...@news-server.bigpond.net.au...
>
>> Miller did an MMX experiment with 20,000 rotations with a much
> larger
>> apparatus, and in 4 months of the year. That data, in the form of 20
>> rotations
>> per A4 page, is now available in 1000 A4 pages.
>
> All of which is rubbish, since his experiment was done in a room with
> substabtial temperature variations which Miller did not take into
> account. And remember that the work stretched over more than a
> complete weather season.
Miller did many experiments to check on any effects due to
temperature. His data tracks sidereal time and not solar time.
One effect that temperature has on the Miller experiment is
that during any rotation (each 6 minutes in duration) the temperature
of the arms will change ever so slightly. That changes the length of
the arms. But that effect is easily seen in the data..it causes a fringe
drift linear in rotation angle (i.e. time).
That means that the data looks like
fringe shift = a*theta +ACos(2(theta - psi)),
where the a*theta is the temperature effect.
One fits this form to the data, to get at the value of A and psi from
the average of 20 rotations, eaching taking about 6 minutes.
Miller was very aware of that, as was Michelson and Morley who
did the same correction. Another effect is that any major temperature
change will affect the refractive index of the air. This affects the
calibration of the instrument over hours, but not the fringe shift
pattern from each 6 minute rotation.
>
> You have been told this before and yet you keep trotting that stuff
> out as if you are telling us something new.
> Have you ever heard about a concept called intellectual integrity?
>
> [snip]
Why dont you elucidate further
Crackpot Patroman Heymann?
>> The results from that agree
>> with those from the 1991 coaxial cable experiment by DeWitte. He
> used
>> 1.5 km of buried coax, and 6 cesium atomic clocks to measure the
> change in
>> travel
>
> You have been told previously that that buried coax. lay below the
> streets of Brussels in an environment in which the temperature was not
> controlled. The lengths of the cables therefore were not constant.
The DeWitte cables were deeply buried beneath the streets
of Brussells, so temperature effects were not a problem - no
solar time correlations effects were seen, ie the curves tracked
sidereal time and not solar time
Have a nice day Crackpot Patrolman.
Bjoern Feuerbacher
[snip]
> The postulates of SR [...] are in disagreement with the data.
Care to explain what you mean here?
[snip]
Bye,
Bjoern
mountain man
news:ctahdc$97p$3...@news.urz.uni-heidelberg.de...
> mountain man wrote:
> [snip]
>
>
>> The postulates of SR [...] are in disagreement with the data.
>
> Care to explain what you mean here?
See Cahill's last 2 papers:
http://www.mountainman.com.au/process_physics/index_of_papers.htm
dlzc1 D:cox T:net@nospam.com N:dlzc D:aol T:com (dlzc)
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
news:HL2Kd.136718$K7.3...@news-server.bigpond.net.au...
> "Franz Heymann" <notfranz...@btopenworld.com> wrote in message
> news:ctaamq$t7v$1...@hercules.btinternet.com...
...
>> All of which is rubbish, since his experiment was done in a room with
>> [substantial] temperature variations which Miller did not take into
>> account. And remember that the work stretched over more than a
>> complete weather season.
>
>
> Miller did many experiments to check on any effects due to
> temperature. His data tracks sidereal time and not solar time.
>
> One effect that temperature has on the Miller experiment is
> that during any rotation (each 6 minutes in duration) the temperature
> of the arms will change ever so slightly. That changes the length of
> the arms. But that effect is easily seen in the data..it causes a fringe
> drift linear in rotation angle (i.e. time).
>
> That means that the data looks like
> fringe shift = a*theta +ACos(2(theta - psi)),
> where the a*theta is the temperature effect.
>
> One fits this form to the data, to get at the value of A and psi from
> the average of 20 rotations, eaching taking about 6 minutes.
>
> Miller was very aware of that, as was Michelson and Morley who
> did the same correction. Another effect is that any major temperature
> change will affect the refractive index of the air. This affects the
> calibration of the instrument over hours, but not the fringe shift
> pattern from each 6 minute rotation.
This is fine to say, but not very believable, based on the structure that
he assembled to make his measurements. It had a very large surface area,
and very little thermal mass. Temperature effects would most certainly be
larger than for MMX's apparatus.
At least he didn't make it out of wood.
And it is interesting that you made the statement:
> The main data on absolute motion is Miller.
When this MMX style measurement has been repeated, Miller's "correlation"
has not been found. So it looks like it is Lorentz aether, or no aether.
David A. Smith
Tom Roberts
> "mountain man" <hobbit@southern_seaweed.com.op> wrote in message
> news:DxYJd.136156$K7.8...@news-server.bigpond.net.au...
>>Miller did an MMX experiment with 20,000 rotations with a much
>> larger
>>apparatus, and in 4 months of the year. That data, in the form of 20
>>rotations
>>per A4 page, is now available in 1000 A4 pages.
>
> All of which is rubbish, since his experiment was done in a room with
> substabtial temperature variations which Miller did not take into
> account.
It is well known that Miller's measurements have problems. The insight I had in
looking at the MMX data should apply to his as well, and it should be possible
to make an accurate quantitative estimate of his actual errorbars. That should
settle the question of his measurements' reliability, and whether or not they
are consistent with SR, and whether or not they are consistent with other
theories (such consistency testing requires accurate knowledge of the errorbars).
>>The results from that agree
>>with those from the 1991 coaxial cable experiment by DeWitte.
>
> You have been told previously that that buried coax. lay below the
> streets of Brussels in an environment in which the temperature was not
> controlled. The lengths of the cables therefore were not constant.
That's only one aspect of the problems with DeWitte's data. They are hopeless
and useless.
Tom Roberts tjro...@lucent.com
Tom Roberts
> As I pointed out the other time, you still neglected analysis of the data
> themselves. Surely you won't claim that a combination of white noise with a
> visible 50 Hz noise interference is consistent with no 50 Hz noise at all
> because it is drowned in white noise!
If the "signal" due to the 50 Hz is ten times smaller than your measurement
errorbars, you have no hope of determining either the magnitude or phase of the
50 Hz signal. Unless you can obtain more data, do a phase-locked analysis, or
similar.
My example is roughly comparable to the MMX data, but no more data are available
and no phase-locked analysis is possible.
>>But what was "seen" is not significant. In their plot on page 340, when
>>one plots their actual errorbars, the errorbars are larger than the
>>entire picture, and they dwarf the variations in the points.
>
> In our lab we have such signals all the time. We simply average the noise
> away
Unless you can show that your underlying systematic errors are smaller than the
errorbars attributed to the averages, you are fooling yourselves.
- problem is that here the number of data points is IMO too meager to
> be really sure. A statistics professional should be able to give us an
> estimation of how likely it is that there is a 2-cycle sinus present in one
> turn.
The likelihood for such a signal with amplitude < 5 km/s is high -- this of
course does NOT mean that one is actually present, merely that one cannot be
ruled out. The likelihood for such a signal with amplitude >10 km/s is quite
low. Here I use Michelson and Morley's correspondence between signal and
velocity, and knowledge that the errorbars are the roughly same size as a
"signal" of 5 km/s. More quantitative answers could easily be obtained by
fitting....
Tom Roberts tjro...@lucent.com
Harry
> Harry wrote:
> > "Tom Roberts" <tjro...@lucent.com> wrote in message
> > news:oa_Jd.13396$Vj3....@newssvr17.news.prodigy.com...
> > As I pointed out the other time, you still neglected analysis of the
data
> > themselves. Surely you won't claim that a combination of white noise
with a
> > visible 50 Hz noise interference is consistent with no 50 Hz noise at
all
> > because it is drowned in white noise!
>
> If the "signal" due to the 50 Hz is ten times smaller than your
measurement
> errorbars, you have no hope of determining either the magnitude or phase
of the
> 50 Hz signal. Unless you can obtain more data, do a phase-locked analysis,
or
> similar.
>
> My example is roughly comparable to the MMX data, but no more data are
available
> and no phase-locked analysis is possible.
I agree with the lack-of-data argument in this case. Just consider it worth
mentioning.
> >>But what was "seen" is not significant. In their plot on page 340, when
> >>one plots their actual errorbars, the errorbars are larger than the
> >>entire picture, and they dwarf the variations in the points.
> >
> > In our lab we have such signals all the time. We simply average the
noise
> > away
>
> Unless you can show that your underlying systematic errors are smaller
than the
> errorbars attributed to the averages, you are fooling yourselves.
Of course.
> - problem is that here the number of data points is IMO too meager to
> > be really sure. A statistics professional should be able to give us an
> > estimation of how likely it is that there is a 2-cycle sinus present in
one
> > turn.
>
> The likelihood for such a signal with amplitude < 5 km/s is high -- this
of
> course does NOT mean that one is actually present, merely that one cannot
be
> ruled out. The likelihood for such a signal with amplitude >10 km/s is
quite
> low. Here I use Michelson and Morley's correspondence between signal and
> velocity, and knowledge that the errorbars are the roughly same size as a
> "signal" of 5 km/s. More quantitative answers could easily be obtained by
> fitting....
Fine, thanks for the clarifications.
Harald
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
> "Franz Heymann" <notfranz...@btopenworld.com> wrote in message
> news:ctaamq$t7v$1...@hercules.btinternet.com...
> > "mountain man" <hobbit@southern_seaweed.com.op> wrote in message
> > news:DxYJd.136156$K7.8...@news-server.bigpond.net.au...
> >
> >> Miller did an MMX experiment with 20,000 rotations with a much
> > larger
> >> apparatus, and in 4 months of the year. That data, in the form of
20
> >> rotations
> >> per A4 page, is now available in 1000 A4 pages.
> >
> > All of which is rubbish, since his experiment was done in a room
with
> > substabtial temperature variations which Miller did not take into
> > account. And remember that the work stretched over more than a
> > complete weather season.
>
>
> Miller did many experiments to check on any effects due to
> temperature. His data tracks sidereal time and not solar time.
I don't care what time his data tracks.
What I do know is that a prominent physicist visited him at the time
and commented specifically on the lack of temperature control.
My memory is not perfect on this issue, but I seem to remember that
that visitor even didi a little demonstration to prove his point.
Can you remember the details?
>
> One effect that temperature has on the Miller experiment is
> that during any rotation (each 6 minutes in duration) the
temperature
> of the arms will change ever so slightly. That changes the length of
> the arms. But that effect is easily seen in the data..it causes a
fringe
> drift linear in rotation angle (i.e. time).
>
> That means that the data looks like
> fringe shift = a*theta +ACos(2(theta - psi)),
> where the a*theta is the temperature effect.
>
> One fits this form to the data, to get at the value of A and psi
from
> the average of 20 rotations, eaching taking about 6 minutes.
Oh dear.
> Miller was very aware of that, as was Michelson and Morley who
> did the same correction. Another effect is that any major
temperature
> change will affect the refractive index of the air. This affects the
> calibration of the instrument over hours, but not the fringe shift
> pattern from each 6 minute rotation.
>
>
> >
> > You have been told this before and yet you keep trotting that
stuff
> > out as if you are telling us something new.
> > Have you ever heard about a concept called intellectual integrity?
> >
> > [snip]
>
>
>
> Why dont you elucidate further
> Crackpot Patroman Heymann?
I will:
Miller's precision was a lot worse than he thought.
> >> The results from that agree
> >> with those from the 1991 coaxial cable experiment by DeWitte. He
> > used
> >> 1.5 km of buried coax, and 6 cesium atomic clocks to measure the
> > change in
> >> travel
> >
> > You have been told previously that that buried coax. lay below the
> > streets of Brussels in an environment in which the temperature was
not
> > controlled. The lengths of the cables therefore were not
constant.
>
>
> The DeWitte cables were deeply buried beneath the streets
> of Brussells, so temperature effects were not a problem - no
> solar time correlations effects were seen, ie the curves tracked
> sidereal time and not solar time
Oh dear.
> Have a nice day Crackpot Patrolman.
Franz
mountain man
Yes. One of the dwarves, Sneezy, visited Miller's mountain
retreat. It was a nice story, but one must bear in mind the
social, professional and political European-centric environment
of the time.
Miller, president of the American Physical Society ,
got shafted by the European professionals, and then
worked over after his death by Shankland, et al.
His data however, persists.
...[snip]...
Have a nice day,
mountain man
> mountain man wrote:
...[trimmed]...
>> Miller did an MMX experiment with 20,000 rotations with a much larger
>> apparatus, and in 4 months of the year. That data, in the form of 20
>> rotations
>> per A4 page, is now available in 1000 A4 pages. Various people have that
>> data,
>> and some have put it into electronic files.
>
> How can I obtain this? I'm only interested in an elecronic version, as I
> have no resources for data entry of this magnitude. Though I could sample
> a printed version, I suppose.
e-form of the Miller data might be obtained
by requesting copy from
Thomas Goodey: tho...@flyingkettle.com
or Glen Deen: glen...@gte.net
James DeMeo de...@mid.net has in the past been
prepared to sell photocopies of the original handwritten
Miller data.
Note: These people have their own interpretations of the
data. All that matters here is the data itself.
Some of the Miller results are shown in Cahill:
http://www.arxiv.org/abs/physics/0501051
and all is analysed in considerable detail in various
other earlier Cahill papers. In this paper the plot of
absolute velocity azimuth varying with siderial time
is very clean. To claim that these results are dragged
out from nothing but errors is an insult to the
undisputed integrity of Miller. He was the President
of the American Physical Society at the time.
>> The results from that agree
>> with those from the 1991 coaxial cable experiment by DeWitte.
>
> I have his "data". It is utterly and completely useless. And if you don't
> know that from looking at it and his writings you are deceiving yourself.
The DeWitte experiment was truly outstanding. The only data
that exists, apparently, are the time variations over three
sidereal days. This is shown in Cahill:
http://www.arxiv.org/abs/physics/0501051
and is analysed in considerable detail in various other earlier
Cahill papers.
How anyone could describe that data as "as utterly and
completely useless. " is beyond comprehension. The only
other piece of DeWitte data is his plot of the cross-over
time for 178 days. This shows the effect tracking siderial
time and not solar time. This was an important check on
that experiment.
Cahill is preparing to repeat the DeWitte experiment.
Note that the DeWitte data should not be rejected
because of his nonsensical theorising, the theory and
the data are two separate things.
...[trim]...
>> The spacetime ontology is invalidated by experiment. What needs
>> to be done is to reassess all the data in respect of the Lorentzian
>> interpretation of these relativistic effects.
>
> You WAY overstep the data.
Time alone will tell.
>> It looks like Lorentz got it right long ago.
>
> Lorentz's theory is experimentally indistinguishable from SR. At least if
> one only applies it to uncharged systems, or if one fixes up his mistake
> in defining \rho' and uses Poincare's definition.
In analysing absolute motion experiments we must forget about
the Newtonian theory for the apparatus. That theory has been
rendered invalid for over 100 years!
The Einstein spacetime ontology (which is not the same as the
various established relativistic effects) has no absolute motion
by definition. So what the seven experiments, so far (more new
ones in progress), are implying is that the spacetime ontology is
wrong, not that there are no relativistic effects.
To analyse the various interferometer experiments one needs
a relativistic theory for the device. The data shows that the gas
present matters: with no gas (vacuum) the device fails to detect
any absolute motion. With gas present, the effect size is
determined by the refractive index of the gas.
This is not surprising: the presence of a gas changes the speed
of light, and so the operation of the device. Analysing
interferometer data without a relativistic theory for the device is
simply generating noise.
Jesse Mazer
mountain man wrote:
>"Tom Roberts" <tjro...@lucent.com> wrote in message
>news:oa_Jd.13396$Vj3....@newssvr17.news.prodigy.com...
>
>
>>Lorentz's theory is experimentally indistinguishable from SR. At least if
>>one only applies it to uncharged systems, or if one fixes up his mistake
>>in defining \rho' and uses Poincare's definition.
>>
>>
>
>In analysing absolute motion experiments we must forget about
>the Newtonian theory for the apparatus. That theory has been
>rendered invalid for over 100 years!
>
>The Einstein spacetime ontology (which is not the same as the
>various established relativistic effects) has no absolute motion
>by definition. So what the seven experiments, so far (more new
>ones in progress), are implying is that the spacetime ontology is
>wrong, not that there are no relativistic effects.
>
What do you mean by "Einstein spacetime ontology"? Even if there was an
ether, as long as light moves at at velocity c in all directions in the
ether frame, and as long as rulers moving at velocity v wrt the ether
shrink by a factor of sqrt(1 - v^2/c^2) while ticks of a clock moving at
velocity v wrt the ether stretch out by a factor of 1/sqrt(1 - v^2/c^2),
then if different observers synchronize their clocks by *assuming* light
moves at the same speed in all directions in their frame (even if this
assumption is wrong), then all observers will measure the speed of light
to be exactly c, and the Lorentz transformations will correctly
transform between different observer's coordinate systems. What's more,
if Maxwell's laws are correct in the ether frame, they must look correct
in every frame, as long as rulers shrink and clocks slow down in this
way, and as long as there is no independent way to synchronize spatially
separated clocks by using some non-Lorentz-invariant law of nature.
Jesse
Franz Heymann
A;ll of which wouldbe purely of historic interest, since a number of
much better experiments of that type have been done since, and none
have given any "non-null" result.
>
>
> >>The results from that agree
> >>with those from the 1991 coaxial cable experiment by DeWitte.
> >
> > You have been told previously that that buried coax. lay below the
> > streets of Brussels in an environment in which the temperature was
not
> > controlled. The lengths of the cables therefore were not
constant.
>
> That's only one aspect of the problems with DeWitte's data. They are
hopeless
> and useless.
Franz
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
I could tell you about one or two past presidents of the Royal Society
too, who were bad experimentalists, but I won't
> got shafted by the European professionals, and then
> worked over after his death by Shankland, et al.
Quite. I could not have put it better myself, except by reinforcing
that they demolished him.
Which makes me wonder why you are trying so hard, albeit
unsuccessfully, to resuscitate him.
> His data however, persists.
Yes.
Franz
Mark Fergerson
<snip>
> Vacuum cavity experiments are incapable of detecting absolute motion.
Would you care to explain precisely why not?
While you're winding up to do that, please define "vacuum" explicitly.
Mark L. Fergerson
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
Of course. He was a lousy experimentalist and quite independently
also a lousy theorist.
[snip]
Franz
Tom Roberts
>>In a Michelson interferometer there is always interference and the
>>pattern of dark and bright bands is always visible. This occurs because
>>the slightly-off-axis paths have a slightly different length than the
>>on-axis path, and the path length for the two arms is affected
>>differently for such off-axis paths (i.e. to reach a point slightly
>>off-axis to one side of the image, one arm's ray must follow a path
>>slightly longer than the on-axis path, and the other must follow a
>>slightly shorter path than the on-axis path).
>
> It's strange your statement that: "In a Michelson interferometer there
> is always interference and the pattern of dark and bright bands is
> always visible."
This is not "strange", it is quite simply true -- just look into one.
At base, the interference fringes are caused by geometrical differences
in path length, not differences in frequency as you seem to think.
> You say this occurs because the slightly-off-axis paths have a slightly
> different length than the on-axis path, and the path length for the two
> arms is affected differently for such off-axis paths
Yes.
> I'm confused here.
> I guess it is a constructive problem?
> Could you explain please?
> Please explain also what is "on-axis" and "off-axis" because I have a bad
> English.
Draw the usual diagram for a Michelson interferometer:
M1 M1 = mirror for path 1
___ M2 = mirror for path 2
| BS = beam splitter
| S = light source
| D = detector
| BS | and - are the on-axis light rays
|/ !
S---/------------! M2
/| !
|
D
Assume that the length BS to M1 is the same as BS to M2 and is an
integral number of wavelengths of the light. The straight rays I drew
("-" and "|") are the on-axis rays, and there will be constructive
interference there -- a maximum intensity. Now look a small distance to
the right of D -- for a ray to reflect from M1 and get there it must
travel a slightly different distance than for a ray to reflect from M2
and get there. If that difference is a half wavelength then there will
be destructive interference and a minimum intensity. Similarly for other
differences adding an integral number of wavelengths. This is why the
observer sees multiple fringes.
> But, if the frequency remains constant when you sum the two light
> frequencies you always get the same frequency (mathematics is 100% exact and
> it cannot fail).
Sure. But this interferometer isn't looking at that. The locations for
positions slightly off-axis at D have different path lengths in the two
arms, and this geometrical difference generates the interference fringes
-- they do not change with time (in an idealized apparatus).
> Moreover, I can't see any difference between frequency and wave length
> (Physically they are one and the same thing, [...]
No, they are not. Wavelength is the distance between successive crests
when the wave is viewed at a single time. Frequency is the time interval
between successive crests when the wave is observed at a single
position. Their product is the speed with which the wave propagates.
As the earlier demonstration shows, the frequency of the light does not
change with orientation. But if its propagation speed varies with
orientation, so does its wavelength. This last will cause the fringe
pattern at D to vary with orientation.
Tom Roberts tjro...@lucent.com
Tom Roberts
> [references to people who might have Miller's data]
Thanks. I'm following up.
> with no gas (vacuum) the device fails to detect
> any absolute motion. With gas present, the effect size is
> determined by the refractive index of the gas.
So why does the presence of a solid not do the same?
How about liquids?
Or glasses?
Or plasma (e.g. inside a He-Ne laser)?
Why does type of material matter so much more than its refractive index?
> This is not surprising: the presence of a gas changes the speed
> of light, and so the operation of the device. Analysing
> interferometer data without a relativistic theory for the device is
> simply generating noise.
SR + Maxwell's equations is such a theory, and predicts no measurable
fringe shift for any Michelson-type interferometer as it is rotated,
independent of material type or refractive index. This is not "noise"
(in the silly sense you use that word).
No knowledgeable people are likely to belive Cahill's theory based on
old, experiments with large and essentially unknown systematic errors.
To get anyone to believe in it requires several competent modern
experiments with proper error analyses and a range of refractive
indexes. Why haven't any such experiments been reported?
I estimate I could put together an apparatus to test
this for a few thousand dollars and a few months of work.
Why haven't any advocates of this theory done that?
Tom Roberts tjro...@lucent.com
Harry
"Jesse Mazer" <vze2...@mail.verizon.net> wrote in message
news:41F9F435...@mail.verizon.net...
Jesse, great summary!
What you wrote does not guarantee in itself that the PoR can't be broken. In
this case, the question is to prove theoretically and experimentally that
the refractive index of moving gas perfectly obeys the PoR. Not easy. Start
with deriving the wave equation for moving sources and then work out light
scattering (I think this has never been done). And how many Fizeau
experiments have been done with gas? Those usually suffer from a low
accuracy.
Harald
mountain man
news:fOrKd.1184$Jt.297@fed1read02...
Here are a summary of Cahill's claims:
There are three key aspects to the interferometer:
It operates by revealing, by means of fringe shifts,
a change in relative travel time of the light in the two
arms when the device is rotated caused by
(1) the geometry of the device. This is the effect
that Michelson used in his original analysis. This
effect is caused by absolute motion.
BUT (2) we know that there is contraction of the
arm in the direction of motion, also caused by
absolute motion. In vacuum these two effects
exactly cancel. So to get a non-null result, we
have to upset that cancellation.
This can be done by (3) having gas in the light
paths. This slows the light, and effect (1) and
(2) no longer exactly cancel.
The above is a relativistic analysis of the device.
It was first worked out in 2002. The Newtonian
analysis, which amazingly many people still use,
eg Tom Roberts, uses only effect (1), and so
predicts fringe shifts that are far too large.
There have been a number of interferometers
with gas, some using air, and some using He,
and one using He-Ne, so the gas effect has
been confirmed by analysis of all that data.
Modern interferometers run with vacuum, is
the light passes through space without any gas.
Then the perfect cancelation of effects (1) and
(2) occurs, and no fringe shifts occur on rotation
of this device: so this mode of operation gives a
dud experiment.
Nevertheless Physical Review Letters loves
publishing the `null' results from these experiments;
they think that it proves that absolute motion is
not observable.
mountain man
> mountain man wrote:
...[trim]...
>> with no gas (vacuum) the device fails to detect
>> any absolute motion. With gas present, the effect size is
>> determined by the refractive index of the gas.
>
> So why does the presence of a solid not do the same?
> How about liquids?
> Or glasses?
> Or plasma (e.g. inside a He-Ne laser)?
> Why does type of material matter so much more than its refractive index?
See the summary/explanation below.
>> This is not surprising: the presence of a gas changes the speed
>> of light, and so the operation of the device. Analysing
>> interferometer data without a relativistic theory for the device is
>> simply generating noise.
>
> SR + Maxwell's equations is such a theory, and predicts no measurable
> fringe shift for any Michelson-type interferometer as it is rotated,
> independent of material type or refractive index. This is not "noise" (in
> the silly sense you use that word).
Here are a summary of Cahill's claims.
> No knowledgeable people are likely to belive Cahill's theory based on old,
> experiments with large and essentially unknown systematic errors. To get
> anyone to believe in it requires several competent modern experiments with
> proper error analyses and a range of refractive indexes. Why haven't any
> such experiments been reported?
No idea Tom. Gas mode devices went out of favour
for some aetherial reason. The physics of their operation
has been incorrect until Cahill (if the above claims are
found to be correct) paper of 2002.
> I estimate I could put together an apparatus to test
> this for a few thousand dollars and a few months of work.
> Why haven't any advocates of this theory done that?
AFAIK Cahill has a number of experiments under way.
Have anice day,
mountain man
Time alone, and not anyone here, will determine
the substance of those assertions.
Tom Roberts
> "Tom Roberts" <tjro...@lucent.com> wrote:
>>So why does the presence of a solid not do the same?
>>How about liquids?
>>Or glasses?
>>Or plasma (e.g. inside a He-Ne laser)?
>>Why does type of material matter so much more than its refractive index?
>
> See the summary/explanation below.
You didn't address this. To me, this is a critical issue of believability of
Cahill's theory -- why are solids excluded? (etc.) I know of no other theory in
which type of material matters for optical properties, index of refraction tells
it all. And at least one of his articles simply dismisses experiments using
solid media without giving a reason.
So why does the presence of a solid not do the same? And how about liquids,
glasses, and plasma?
Tom ROberts tjro...@lucent.com
Bilge
>publishing the `null' results from these experiments;
>they think that it proves that absolute motion is
>not observable.
>
A null result means that |data - theory| = 0 to within the experimental
error, with the theoretical fitting function is obtained from a theory.
For example, a set of data points, (x_i, y_i) is meaningless without
some theoretical basis for relating x_i to y_i. Given _any_ theoretical
relationship, you have a result which is potentially null, meaning that
the theory agrees with the data. So what a null result proves is that the
data agree with a particular theory. The fact that the theory in this case
is that absolute motion is unobservable, means that the data are
consistent with absolute motion being unobservable. That is not arguable.
The fact that you can find a different theory which is conistent with the
data is irrelavent without an experiment that can distinguish between the
two theories. I can find a theory that fits the data _exactly_ merely by
using an n-1 order polynomial to fit n data points and then inventing a
name for each non-zero coefficient. That doesn't make it a better theory
than a straight line.
mountain man
[Cahill]:
"The insight here is that transparent solids don't behave like gases.
The explanation appears to be that the Lorentz contraction in the
direction of motion affects, via the elasticity of the solid, the
refractive index in the orthogonal direction.
In other words solids are much more complex than gases,
which display no such effect."
Have a nice day,
Uncle Al
Non-linear optical effects in media have nothing whatsoever to do with
Lorentz invariance. Breaking the speed of light in media is child's
play - Cerenkov radiation. Doesn't mean squat vs. breaking lightspeed
in vacuum.
Brown, you are an ignorant ineducable idiot.
--
Uncle Al
http://www.mazepath.com/uncleal/
(Toxic URL! Unsafe for children and most mammals)
http://www.mazepath.com/uncleal/qz.pdf
Tom Roberts
> "Tom Roberts" <tjro...@lucent.com> wrote in message
> news:ctmeln$6...@netnews.proxy.lucent.com...
>>So why does the presence of a solid not do the same? And how about
>>liquids, glasses, and plasma?
>
> [Cahill]:
>
> "The insight here is that transparent solids don't behave like gases.
> The explanation appears to be that the Lorentz contraction in the
> direction of motion affects, via the elasticity of the solid, the
> refractive index in the orthogonal direction.
>
> In other words solids are much more complex than gases,
> which display no such effect."
I see. A special plead with no substance or reason. That isn't a theory,
it is a pipe dream.
Tom Roberts tjro...@lucent.com
mountain man
news:41FEEAC6...@hate.spam.net...
It is an attempted explanation for what appears
to be observed in experiment. ie: null results in
vacuum and solid state devices, but positive results
in gas-mode interferometer devices.
> Brown, you are an ignorant ineducable idiot.
One day you will learn you know nothing.
Have a nice day Crackpot Patrolman Schwartz.
mountain man
It is an attempted explanation for what appears
to be observed. ie: null results in vacuum and
solid state devices, but positive results in gas-mode
interferometer devices.
Have a nice day,
Ken S. Tucker
The Speed of Light and the Einstein Legacy: 1905-2005
http://www.arxiv.org/abs/physics/0501051
It reports a >300km/sec variation in c. That is >1/1000 th of c.
(c~300,000 km/sec).
1/1000 == 1mm/ meter, I can cut plywood that accurate.
Unless I've misunderstood things, that sounds like a very
big number. Did I?
Ken
Bilge
the data and negating, a priori, simple tests which would resolve the
issue, precisely because the tests would resolve the issue. Your
(and cahill's) arguments are very reminiscent of those used by
fundamentalists to try and represent creationism as a scientific
theory - lots of platitudes, little substance.
Tom Roberts
>>I see. A special plead with no substance or reason. That isn't a theory,
>>it is a pipe dream.
>
> It is an attempted explanation for what appears
> to be observed. ie: null results in vacuum and
> solid state devices, but positive results in gas-mode
> interferometer devices.
Hmmm. Except it "just so happens" that those "positive results" are all
equivocal at best, when one applies a realistic estimate of errors to them.
IOW: an explanation that is at least as good is that SR and GR are correct in
their predictions for these experiments.
As I said before: nobody is going to believe this theory until and until and
unless multiple modern experiments support it (and therefore disprove SR and GR).
Tom Roberts tjro...@lucent.com
Mark Fergerson
> "Mark Fergerson" <nu...@biz.ness> wrote in message
> news:fOrKd.1184$Jt.297@fed1read02...
>
>>mountain man wrote:
>>
>><snip>
>>
>>>Vacuum cavity experiments are incapable of detecting absolute motion.
>>
>> Would you care to explain precisely why not?
> Here are a summary of Cahill's claims:
Same fringe shifts regardless of gas fill composition or pressure?
Bet not.
> Modern interferometers run with vacuum, is
> the light passes through space without any gas.
> Then the perfect cancelation of effects (1) and
> (2) occurs, and no fringe shifts occur on rotation
> of this device: so this mode of operation gives a
> dud experiment.
>
> Nevertheless Physical Review Letters loves
> publishing the `null' results from these experiments;
> they think that it proves that absolute motion is
> not observable.
That's all very nice, but you failed to respond to my second question:
>> While you're winding up to do that, please define "vacuum" explicitly.
I want that definition because the MMX, either in vacuum or gas, only
tells you what's happening within the interferometer. But Absolute
Motion must be defined for motions through space, and I want to know if
Cahill is willing to consider the intergalactic case frinst where there
ain't no gas.
Mark L. Fergerson
Tom Roberts
I think so. As best I can tell, this "theory" claims the effect is visible only
in a gas, and the effect is multiplied by a factor (n-1)/n (here n is the index
of refraction for the gas). In terms of the usual way of stating this, that
brings the measurable value down to less than 1 km/s, well within the errorbars
of the measurements he uses[%]. And he carefully avoids mentioning experiments
that disagree with his predictions, like the GPS (and surely others)[#]. And he
makes a special plead to exclude measurements using solid media that would
clearly refute his "theory".
You cannot cut 1m of plywood that accurately, as it is below the size of the
individual wood cells.
But I, too, could have misunderstood....
[%] Of course if he didn't achieve such a reduction he would have
nothing.
[#] This is a claimed variation in the measurement of the round-trip
speed of light in a gas (and ONLY in a gas).
My point in this thread is that the data of Michelson and Morley do not say what
Cahill (and his references) claim. Their data has errorbars an order of
magnitude larger than claimed, and the actual errorbars include the flat line
prediction of SR, and in Cahill's "theory" they include speeds in excess of
10,000 km/s.
Tom Roberts tjro...@lucent.com
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
Elasticity, my foot.
That story shows that whoever wrote that knew sweet fanny adams about
relativity.
Lorentz contraction has nothing in common with anyelastic
derformation of anything.
I suggest you and Cahill learn the difference between measuring the
space-like projection of an object which has been rotated in space
time, and an elastic deformation.
>
> In other words solids are much more complex than gases,
> which display no such effect."
Balls.
By the way, Mountain Man, do you have any knowledge or understanding
or views of your own, or are you forever bound to parrot the tripe
produced by Cahill?
Franz
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
Boy, oh boy, you and that twit Cahill aren't half scraping the bottom
of the barrel.
Franz
Ken S. Tucker
> Ken S. Tucker wrote:
> > 1/1000 == 1mm/ meter, I can cut plywood that accurate.
> You cannot cut 1m of plywood that accurately, as it is below the size
of the
> individual wood cells.
Sure I can it's easy, (I had a 24'x28' woodshop, sold it
last year). My standard accuracy was 1/16" but for custom
desk tops 1/64" min was required for the *hidden* openings
in the top to disappear. I got it so a piece of paper
wouldn't slide into the gap!
Tucker on Plywood...
Begin with good quality plywood, it can have twist of
course but no curvature, i.e. it must be visually
euclidian. Using a sharp pencil measure from a straight
side the points to cut. Clamp and/or screw a straight
guide to the plywood, after offsetting for blade
thicknesses etc. Use a good quality circular saw with
a fine toothed cutter, set depth. Begin sawing by just
touching the wood and then inspect for guide offset
accuracy, tweak if needed. For really accurate cuts you
usually will need the tweak, that tweak will get you
better that 1/64" probably closer to 1/100".
Recheck, have a couple of drinks, think because plywood
and labor isn't cheap.
When you're psyched cut it patiently, check that the
cord won't get caught. If the guide is true, accurate
and secure, protecting the piece, not the waste, you
can't go wrong.
I enjoy doing things like that because it pushes the
practical math-physics envelope. After the cut my son
would check it, call out "better than 1/64th", or
frowl and bitch that it's closer to a 32nd, ~1mm.
Ken S. Tucker
> Tom Roberts tjro...@lucent.com
mountain man
Crackpot Patrolman Heymann, learn to think outside
the square, and enjoy life a little.
mountain man
news:1107246076.1...@f14g2000cwb.googlegroups.com...
No, this is correct. Cahill's thesis is that absolute
motion has been detected. The (absolute) speed
then comes out to be 420+/-30 km/s - directions
are supplied.
mountain man
news:slrncvut0p....@radioactivex.lebesque-al.net...
That might have been the case were it not for the subject
matter of his other papers (dark matter and gravitation,
quantum foam inflow and the GPS, etc), the predictions
that are contained therein (eg: Gravity Probe B) and the
experiments that are currently being conducted and planned
at Flinders Uni, Oz.
Have a nice day,
--
Pete Brown
Falls Creek
OZ
mountain man
And this is fair enough - par for the course.
These experiments are being conducted and planned
at Flinders Uni. Additionally, Cahill has predicted
specific results for the Gravity Probe B experiment,
and these are at variation with GR/SR.
mountain man
And what about the Lorentz ether theory?
> I suggest you and Cahill learn the difference between measuring the
> space-like projection of an object which has been rotated in space
> time, and an elastic deformation.
>>
>> In other words solids are much more complex than gases,
>> which display no such effect."
>
> Balls.
>
> By the way, Mountain Man, do you have any knowledge or understanding
> or views of your own,
I could ask you the same question
Crackpot Patrolman Heymann.
> or are you forever bound to parrot the tripe
> produced by Cahill?
Or are you forever bound to parrot the
tripe produced by the current paradigms
and promulgated by academics for the
last 100 years.
mountain man
According to Cahill, the "vacuum" is filled with "quantum foam"
which is in motion towards the center of galactic hubs, stars,
planets and all ponderable matter. It is the motion WRT to
the flow of this "quantum foam" that he claims is being measured
as absolute motion in the interferometers.
His list of papers contain reference to galactic structure, and
the resolution of the 'dark matter' conundrum.
The pdf versions are available from:
http://www.mountainman.com.au/process_physics/index_of_papers.htm
Here is a chronological index of papers:
PP25 - The Speed of Light and the Einstein Legacy: 1905-2005 [Jan 2005]
PP24 - The Einstein Postulates: 1905-2005; A Critical Review of the Evidence
[Dec 2004]
PP23 - Novel Gravity Probe B Gravitational Wave Detection [Aug 2004]
PP22 - The Dynamical Velocity Superposition Effect in the Quantum-Foam
In-Flow Theory of Gravity [July 2004]
PP21 - Novel Gravity Probe B Frame-Dragging Effect [June 2004]
PP20 - Space and Gravitation [Jan 2004]
PP19 - 'Dark Matter' as a Quantum Foam In-Flow Effect [June 2004]
PP18 - Gravity, 'Dark Matter' and the Fine Structure Constant [Jan 2004]
PP17 - Quantum-Foam In-Flow Theory of Gravity and the GPS [2003] (Revised
2004)
PP16 - Quantum-Foam, Gravity and Gravitational Waves [2003]
PP15 - Gravity as Quantum Foam In-Flow [2003]
PP14 - Absolute Motion and Gravitational Effects [2003]
PP13 - Process Physics: Process Studies Supplement (Issue 5, [2003])
PP12 - Dynamical Hierarchies in Fundamental Physics [2003]
PP11 - Absolute Motion and Quantum Gravity ... superceded in PDF13 (above)
[2002]
PP10 - Analysis of Data from a Quantum Gravity Experiment [2002]
PP09 - Michelson-Morley Experiments Revisted and the CBR Preferred Frame -
corrects arXiv:physics/0205065 [2002]
PP08 - Process Physics: From Quantum Foam to General Relativity [2002]
PP07 - Smart Nanostructures and Synthetic Quantum Systems [2001]
PP06 - Process Physics: Inertia, Gravity and the Quantum [2001]
PP05 - Process Physics: Modelling Reality as Self-Organising Information
[2000]
PP04 - Self-Referential Noise as a Fundamental Aspect of Reality [1999]
PP03 - Self-Referential Noise and the Synthesis of Three-Dimensional Space
[1998]
PP02 - Bootstrap Universe from Self-Referential Noise [1997]
PP01 - Pregeometric Modelling of the Spacetime Phenomenology [1996]
Hope this helps to answer your question.
mountain man
> Ken S. Tucker wrote:
>> The Speed of Light and the Einstein Legacy: 1905-2005
>> http://www.arxiv.org/abs/physics/0501051
>>
>> It reports a >300km/sec variation in c. That is >1/1000 th of c.
>> (c~300,000 km/sec).
>>
>> 1/1000 == 1mm/ meter, I can cut plywood that accurate.
>>
>> Unless I've misunderstood things, that sounds like a very
>> big number. Did I?
>
> I think so. As best I can tell, this "theory" claims the effect is visible
> only in a gas, and the effect is multiplied by a factor (n-1)/n (here n
> is the index of refraction for the gas). In terms of the usual way of
> stating this, that brings the measurable value down to less than 1 km/s,
> well within the errorbars of the measurements he uses[%]. And he carefully
> avoids mentioning experiments that disagree with his predictions, like the
> GPS (and surely others)[#].
This is patently false.
Cahill has a paper specifically on the GPS ..... PP17
Quantum-Foam In-Flow Theory of Gravity and the GPS
[Written 2003] (Revised 2004), and he makes predictions
in regard to the Gravity Probe B experiments which are
different from GR - in other papers.
PP23 - Novel Gravity Probe B Gravitational Wave Detection [Aug 2004]
PP21 - Novel Gravity Probe B Frame-Dragging Effect [June 2004]
>And he makes a special plead to exclude measurements using solid media that
>would clearly refute his "theory".
Effects are not being seen in solid media.
Effects are not being seen in vacuo.
Effects have only been seen in gas mode devices.
> You cannot cut 1m of plywood that accurately, as it is below the size of
> the individual wood cells.
>
> But I, too, could have misunderstood....
>
> [%] Of course if he didn't achieve such a reduction he would have
> nothing.
>
> [#] This is a claimed variation in the measurement of the round-trip
> speed of light in a gas (and ONLY in a gas).
>
>
> My point in this thread is that the data of Michelson and Morley do not
> say what Cahill (and his references) claim. Their data has errorbars an
> order of magnitude larger than claimed, and the actual errorbars include
> the flat line prediction of SR, and in Cahill's "theory" they include
> speeds in excess of 10,000 km/s.
Further experimentation is the only mechanism
to distinguish or extinguish Cahill.
Bilge
>> I want that definition because the MMX, either in vacuum or gas, only
>> tells you what's happening within the interferometer. But Absolute Motion
>> must be defined for motions through space, and I want to know if Cahill is
>> willing to consider the intergalactic case frinst where there ain't no
>> gas.
>According to Cahill, the "vacuum" is filled with "quantum foam"
Which is a perfect example of cahill's use of buzzwords and jargon.
He could have used the word ``stuff'' without losing any content.
JM Albuquerque
"Tom Roberts" <tjro...@lucent.com> escreveu na mensagem
news:0ZQKd.4063$wA5....@newssvr33.news.prodigy.com...
(snip)
> As the earlier demonstration shows, the frequency of the light does not
> change with orientation. But if its propagation speed varies with
> orientation, so does its wavelength. This last will cause the fringe
> pattern at D to vary with orientation.
Thank you for the reply.
I'm still confused about the above point.
You've said above:
"the frequency of the light does not change with orientation. But if its
propagation speed varies with orientation, so does its wavelength."
Since we have:
c = frequency * wavelength
And:
Frequency = circular motion / time
Wavelength = meters
Time (or frequency) doesn't change. OK.
So, in order to have a change on the speed of light "c" the wavelength must
change, which means that the length unit must change. But if the length unit
changes so does time, since frequency remains constant (circular motion does
have an enclosed circular length in it).
In other words:
Speed of light = c = length / time
If length and time contracts equal due to speed, the obvious result is that
the speed of light is constant. Relativity looks like a circular reasoning
to me, but I could be wrong.
The MMX is a 3-dimensional problem for each arm of the apparatus that you
and all others want to analyse like if it is a one-dimension problem for
each arm of the apparatus.
Notice that light is the classical limit of the quantized radiation fields
for the eletromagnetic force = Maxwell's equations.
And since nobody has a picture of what light looks like under Maxwell's
equations all the Physics is based on a non-picture of what light is.
Light could be more electric or more magnetic and also it could be more or
less quantized. Light looks like a rubber-band (solutions of Maxwell's
equations).
Light is composed of a non-conservative field (electric) plus a conservative
field (magnetic) at right angle and both together could be quantized.
Light energy could be ideally continuously dispersed by a huge volume
and by miracle it could also be quantized and appear all at once on a
single point (if a detector is used).
Before taking conclusions on MMX I guess that one should try to
understand what light really is.
Best Regards
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
It has been superceded by a theory which does not require the
existence of the ether.
> > I suggest you and Cahill learn the difference between measuring
the
> > space-like projection of an object which has been rotated in space
> > time, and an elastic deformation.
> >>
> >> In other words solids are much more complex than gases,
> >> which display no such effect."
> >
> > Balls.
> >
> > By the way, Mountain Man, do you have any knowledge or
understanding
> > or views of your own,
>
>
> I could ask you the same question
> Crackpot Patrolman Heymann.
I know some physics. You only parrot one man without understanding
what you are saying.
> > or are you forever bound to parrot the tripe
> > produced by Cahill?
>
>
> Or are you forever bound to parrot the
> tripe produced by the current paradigms
> and promulgated by academics for the
> last 100 years.
Said paradigms turn out predictions whch, wherever possible, have been
tested and have always, in the hands of competent physicists, given
confirmatory results.
Franz
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
[snip]
> According to Cahill, the "vacuum" is filled with "quantum foam"
In what way does that duffer from "gunk"?
[snip]
Franz
mountain man
> mountain man:
> >"Mark Fergerson" <nu...@biz.ness> wrote in message
>
> >> I want that definition because the MMX, either in vacuum or gas, only
> >> tells you what's happening within the interferometer. But Absolute
> >> Motion
> >> must be defined for motions through space, and I want to know if Cahill
> >> is
> >> willing to consider the intergalactic case frinst where there ain't no
> >> gas.
>
> >According to Cahill, the "vacuum" is filled with "quantum foam"
>
> Which is a perfect example of cahill's use of buzzwords and jargon.
On the contrary, it is *an* approach to the non resolved
problem confronting physics for the last 4-5 generations
of physicists, namely the unification of the quantum and
the gravity theories.
Let me ask you a very simple question: what jargon
might you expect to represent some form of unification
of the two major (ie" dual foundation) theories now
promugated by the academics?
> He could have used the word ``stuff'' without losing any content.
Why dont you write to him and complain?
Better yet, use the peer reviewed system.
If it will accept papers trying to fathom the mythology
of the beginnings of the cosmos, indeed the 10^-n th
second thereof, it will accept anything.
mountain man
But does require the existence of a cosmic pervading substance
termed "dark matter" and "dark energy".
Yeah, that is really superceeding stuff.
>> > I suggest you and Cahill learn the difference between measuring
> the
>> > space-like projection of an object which has been rotated in space
>> > time, and an elastic deformation.
>> >>
>> >> In other words solids are much more complex than gases,
>> >> which display no such effect."
>> >
>> > Balls.
>> >
>> > By the way, Mountain Man, do you have any knowledge or
> understanding
>> > or views of your own,
>>
>>
>> I could ask you the same question
>> Crackpot Patrolman Heymann.
>
> I know some physics.
That's lovely. But that does not appear to be
a view of your own, rather the views of a collective.
> You only parrot one man without understanding
> what you are saying.
Whereas you parrot the collective and know
exactly what you are saying: book, chapter
and verse.
>> > or are you forever bound to parrot the tripe
>> > produced by Cahill?
>>
>>
>> Or are you forever bound to parrot the
>> tripe produced by the current paradigms
>> and promulgated by academics for the
>> last 100 years.
>
> Said paradigms turn out predictions whch, wherever possible, have been
> tested and have always, in the hands of competent physicists, given
> confirmatory results.
1) Why dont you reinforce the confidence to be placed
in this (Crackpot Patrolmans') holy creed by adding
the phrase "with no exceptions"?
2) Said paradigms are not unified by a single theory
and therefore cannot logically be completely consistent.
End of story (for the moment).
mountain man
It duffers in the spelling.
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
You need to read a litle about the expected nature of darl matter ans
dark energy instead of making a fool of yourself by introducing those
ideas here.
[snip]
> >> > By the way, Mountain Man, do you have any knowledge or
> > understanding
> >> > or views of your own,
> >>
> >>
> >> I could ask you the same question
> >> Crackpot Patrolman Heymann.
> >
> > I know some physics.
>
> That's lovely. But that does not appear to be
> a view of your own, rather the views of a collective.
Which I have studied for many years and much of which I actually do
understand and can use to produce new work.
> > You only parrot one man without understanding
> > what you are saying.
>
> Whereas you parrot the collective and know
> exactly what you are saying: book, chapter
> and verse.
> >> > or are you forever bound to parrot the tripe
> >> > produced by Cahill?
> >>
> >>
> >> Or are you forever bound to parrot the
> >> tripe produced by the current paradigms
> >> and promulgated by academics for the
> >> last 100 years.
> >
> > Said paradigms turn out predictions whch, wherever possible, have
been
> > tested and have always, in the hands of competent physicists,
given
> > confirmatory results.
>
> 1) Why dont you reinforce the confidence to be placed
> in this (Crackpot Patrolmans') holy creed by adding
> the phrase "with no exceptions"?
I have used the word "always". Your suggestion is therefore
redundant.
>
> 2) Said paradigms are not unified by a single theory
> and therefore cannot logically be completely consistent.
> End of story (for the moment).
Two theories, to be precise.
Relativity and quantum mechanics.
All else follows from one or the other of those.
Franz
Tom Roberts
> Tom Roberts wrote:
>>Ken S. Tucker wrote:
>>>1/1000 == 1mm/ meter, I can cut plywood that accurate.
>
>>You cannot cut 1m of plywood that accurately, as it is below the size
>> of the individual wood cells.
>
Again you lost the context. Perhaps you should actually READ the articles to
which you are replying.
My remark was for (n-1)/n for air times your 1mm/meter, or about 0.2 microns per
meter. Indeed, you cannot plywood that accurately, as it is below the size of
the individual wood cells.
Tom Roberts tjro...@lucent.com
Mark Fergerson
I'd really like a direct answer to this. Do his papers reference it?
>>>Modern interferometers run with vacuum, is
>>>the light passes through space without any gas.
>>>Then the perfect cancelation of effects (1) and
>>>(2) occurs, and no fringe shifts occur on rotation
>>>of this device: so this mode of operation gives a
>>>dud experiment.
>>>
>>>Nevertheless Physical Review Letters loves
>>>publishing the `null' results from these experiments;
>>>they think that it proves that absolute motion is
>>>not observable.
>>
>> That's all very nice, but you failed to respond to my second question:
>>>> While you're winding up to do that, please define "vacuum" explicitly.
>>
>> I want that definition because the MMX, either in vacuum or gas, only
>>tells you what's happening within the interferometer. But Absolute Motion
>>must be defined for motions through space, and I want to know if Cahill is
>>willing to consider the intergalactic case frinst where there ain't no
>>gas.
> According to Cahill, the "vacuum" is filled with "quantum foam"
> which is in motion towards the center of galactic hubs, stars,
> planets and all ponderable matter. It is the motion WRT to
> the flow of this "quantum foam" that he claims is being measured
> as absolute motion in the interferometers.
Now I'm confused. If he acknowledges that vacuum-filled
interferometers give null results, what's being measured, especially
since the quantum foam ought to also be in motion through the arms of
the interferometer? If the idea is that the foam is in vertical motion,
while the interferometers are set up to measure lateral-motion-cause
shifts, why is no vertical "drag" seen? Why is the foam's motion through
gas any different from its motion through vacuum?
Besides, why should the quantum foam be in motion?
> His list of papers contain reference to galactic structure, and
> the resolution of the 'dark matter' conundrum.
>
> The pdf versions are available from:
> http://www.mountainman.com.au/process_physics/index_of_papers.htm
<snip>
> Hope this helps to answer your question.
Not really, and thanks for the list of papers (saved for the moment)
but until I can make more sense of his premises I'm not gonna plow
through them.
> Have a nice day,
Will fake it at best speed.
Mark L. Fergerson
Bilge
>news:ctqfd1$832$1...@sparta.btinternet.com...
>>
>> "mountain man" <hobbit@southern_seaweed.com.op> wrote in message
>> news:scTLd.144297$K7.2...@news-server.bigpond.net.au...
>>
>> [snip]
>>
>>> According to Cahill, the "vacuum" is filled with "quantum foam"
>>
>> In what way does that duffer from "gunk"?
>>
>> [snip]
>
>
>It duffers in the spelling.
Precisely.
Bilge
>news:slrnd00chq....@radioactivex.lebesque-al.net...
>> mountain man:
>> >"Mark Fergerson" <nu...@biz.ness> wrote in message
>>
>> >> I want that definition because the MMX, either in vacuum or gas, only
>> >> tells you what's happening within the interferometer. But Absolute
>> >> Motion
>> >> must be defined for motions through space, and I want to know if Cahill
>> >> is
>> >> willing to consider the intergalactic case frinst where there ain't no
>> >> gas.
>>
>> >According to Cahill, the "vacuum" is filled with "quantum foam"
>>
>> Which is a perfect example of cahill's use of buzzwords and jargon.
>
>
>On the contrary, it is *an* approach to the non resolved
>problem confronting physics for the last 4-5 generations
>of physicists, namely the unification of the quantum and
>the gravity theories.
>
>Let me ask you a very simple question: what jargon
>might you expect to represent some form of unification
>of the two major (ie" dual foundation) theories now
>promugated by the academics?
that makes it meaningul.
>> He could have used the word ``stuff'' without losing any content.
>
>
>Why dont you write to him and complain?
>Better yet, use the peer reviewed system.
>
>If it will accept papers trying to fathom the mythology
>of the beginnings of the cosmos, indeed the 10^-n th
>second thereof, it will accept anything.
All of that ``mythology'' really failed, since technology hasn't
advanced since 1900, huh?
tj Frazir
Gravityphysics defined gravity as a push to less mass .
Atoms pussh them selves down energy slopes.
The gain in mass is F pushing te wieght of the atom.
Newton had is right, F = dp/dt is right on!
"
F is the gain in mass and up is a gain in mass SAM . M is the
wieght
of the atom befor the gain in mass .
Gravity is the energy slope across the atom. all the mass of the
atom falls twards its center. Atoms change mass at C. So the tom
has more mass falling twards its center from one side than the other and
the atom pushes its self down the energy slope . V will be the
same for evry atom as the mass gain pushes the wieght and the gain is
allways proportinal to the mass. SAM wrote
F
= ma
Here F is the applied force, m is the mass of the
particle, and a = dv/dt is the particle's acceleration, with v being
the particle's velocity. This equation, together with the principle
that bodies act symmetrically on one another--so that the force
particle A feels from particle B is equal to the force B feels from
A--is the basis for understanding particle dynamics".
"Newton's law completely describes all the phenomena
of classical mechanics...."
V is allways the same for evry atom.
evry gain in mass is proportional to the atoms wieght.
The atom gains mass on on side and the gain in mass is falling
twards the center of the atom and is more mass than the oposit mass on
the other side of the atom.
This has got to hurtsome heads.
The math proves it SR or GR.
mountain man
> mountain man:
> >"Bilge" <dub...@radioactivex.lebesque-al.net> wrote in message
> >news:slrnd00chq....@radioactivex.lebesque-al.net...
> >> mountain man:
> >> >"Mark Fergerson" <nu...@biz.ness> wrote in message
> >>
> >> >> I want that definition because the MMX, either in vacuum or gas,
> >> >> only
> >> >> tells you what's happening within the interferometer. But Absolute
> >> >> Motion
> >> >> must be defined for motions through space, and I want to know if
> >> >> Cahill
> >> >> is
> >> >> willing to consider the intergalactic case frinst where there ain't
> >> >> no
> >> >> gas.
> >>
> >> >According to Cahill, the "vacuum" is filled with "quantum foam"
> >>
> >> Which is a perfect example of cahill's use of buzzwords and jargon.
> >
> >
> >On the contrary, it is *an* approach to the non resolved
> >problem confronting physics for the last 4-5 generations
> >of physicists, namely the unification of the quantum and
> >the gravity theories.
>
> Except that he doesn't say anything.
You are entitled to an opinion.
> >Let me ask you a very simple question: what jargon
> >might you expect to represent some form of unification
> >of the two major (ie" dual foundation) theories now
> >promugated by the academics?
>
> I don't expect jargon. I expect a term to be defined in some way
> that makes it meaningul.
He defines the terms he uses in his papers.
You probably didn't read that part.
> >> He could have used the word ``stuff'' without losing any content.
> >
> >
> >Why dont you write to him and complain?
> >Better yet, use the peer reviewed system.
> >
> >If it will accept papers trying to fathom the mythology
> >of the beginnings of the cosmos, indeed the 10^-n th
> >second thereof, it will accept anything.
>
> All of that ``mythology'' really failed, since technology hasn't
> advanced since 1900, huh?
Technological physics has advanced, however
natural physics has remained stagnant since 1900.
Are you able to appreciate the difference?
mountain man
Here, Carackpot Patrolman Heymannn, is not a very
prestigous place. WTF does it matter?
What is there to understand except the fact that additional
unknown variables are being introduced at the foundation
of attempts to determine a consistent theory of gravity?
>> >> > By the way, Mountain Man, do you have any knowledge or
>> > understanding
>> >> > or views of your own,
>> >>
>> >>
>> >> I could ask you the same question
>> >> Crackpot Patrolman Heymann.
>> >
>> > I know some physics.
>>
>> That's lovely. But that does not appear to be
>> a view of your own, rather the views of a collective.
>
> Which I have studied for many years and much of which I actually do
> understand and can use to produce new work.
That's all fine and good, but if you are asking me whether
I have any original ideas, then you should also expect to
be asked the same question.
>> > You only parrot one man without understanding
>> > what you are saying.
>>
>> Whereas you parrot the collective and know
>> exactly what you are saying: book, chapter
>> and verse.
>
>> >> > or are you forever bound to parrot the tripe
>> >> > produced by Cahill?
>> >>
>> >>
>> >> Or are you forever bound to parrot the
>> >> tripe produced by the current paradigms
>> >> and promulgated by academics for the
>> >> last 100 years.
>> >
>> > Said paradigms turn out predictions whch, wherever possible, have
> been
>> > tested and have always, in the hands of competent physicists,
> given
>> > confirmatory results.
>>
>> 1) Why dont you reinforce the confidence to be placed
>> in this (Crackpot Patrolmans') holy creed by adding
>> the phrase "with no exceptions"?
>
> I have used the word "always". Your suggestion is therefore
> redundant.
There are always exceptions,
Crackpot Patrolman Heymann.
It is just a matter of consensus concerning
the level of confidence to be placed in such
exceptions.
For example, the failure of modern theories of gravity
to explain observed phenomena. (galactic rotation).
>> 2) Said paradigms are not unified by a single theory
>> and therefore cannot logically be completely consistent.
>> End of story (for the moment).
>
> Two theories, to be precise.
> Relativity and quantum mechanics.
>
> All else follows from one or the other of those.
Except for the exceptions, they have integrity.
Look very carefully.
Have a nice day,
Dirk Van de moortel
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message news:munMd.146106$K7.1...@news-server.bigpond.net.au...
I guess that "natural physics" stands for Mingst Seto Stowe Brown
physics?
Dirk Vdm
PD
Except for quantum mechanics and quantum field theory, general
relativity, the standard model, and the entire fields of nuclear
physics, condensed matter physics, and elementary particle physics.
Franz Heymann
"mountain man" <hobbit@southern_seaweed.com.op> wrote in message
OK. I am happy to accept that it does not matter. But then it leaves
us with an unanswered question, namely, why did you drag in the
concepts of dark matter and dark energy if , in your own words "WTF
does it matter?"
>
> What is there to understand except the fact that additional
> unknown variables are being introduced at the foundation
> of attempts to determine a consistent theory of gravity?
The present theory of gravity is pretty self-consistent in the
classical domain, and there is so much evidence in its favour that it
is highly unlikely that it will ever be thrown out of the window.
Whatever succeeds it must surely encompass GR as a limiting case.
> >> >> > By the way, Mountain Man, do you have any knowledge or
> >> > understanding
> >> >> > or views of your own,
> >> >>
> >> >>
> >> >> I could ask you the same question
> >> >> Crackpot Patrolman Heymann.
> >> >
> >> > I know some physics.
> >>
> >> That's lovely. But that does not appear to be
> >> a view of your own, rather the views of a collective.
> >
> > Which I have studied for many years and much of which I actually
do
> > understand and can use to produce new work.
>
>
> That's all fine and good, but if you are asking me whether
> I have any original ideas, then you should also expect to
> be asked the same question.
The answer is in the affirmative in my case.
> >> > You only parrot one man without understanding
> >> > what you are saying.
> >>
> >> Whereas you parrot the collective and know
> >> exactly what you are saying: book, chapter
> >> and verse.
> >
> >> >> > or are you forever bound to parrot the tripe
> >> >> > produced by Cahill?
> >> >>
> >> >>
> >> >> Or are you forever bound to parrot the
> >> >> tripe produced by the current paradigms
> >> >> and promulgated by academics for the
> >> >> last 100 years.
> >> >
> >> > Said paradigms turn out predictions whch, wherever possible,
have
> > been
> >> > tested and have always, in the hands of competent physicists,
> > given
> >> > confirmatory results.
> >>
> >> 1) Why dont you reinforce the confidence to be placed
> >> in this (Crackpot Patrolmans') holy creed by adding
> >> the phrase "with no exceptions"?
> >
> > I have used the word "always". Your suggestion is therefore
> > redundant.
>
>
> There are always exceptions,
> Crackpot Patrolman Heymann.
Said exception has not yet turned up.
> It is just a matter of consensus concerning
> the level of confidence to be placed in such
> exceptions.
>
> For example, the failure of modern theories of gravity
> to explain observed phenomena. (galactic rotation).
There is sufficient observational information on gravitational matters
to make it very much more likely that there are unseen distributed
sources of mass rather than that the theory should be dumped.
> >> 2) Said paradigms are not unified by a single theory
> >> and therefore cannot logically be completely consistent.
> >> End of story (for the moment).
> >
> > Two theories, to be precise.
> > Relativity and quantum mechanics.
> >
> > All else follows from one or the other of those.
>
>
> Except for the exceptions, they have integrity.
> Look very carefully.
No exceptions are known.
I have now passed the time of day with you for long enough.
Please have the last word if you feel it imperative.
Franz
Franz Heymann
"Dirk Van de moortel" <dirkvand...@ThankS-NO-SperM.hotmail.com>
wrote in message news:wXnMd.7142$PM5....@news.cpqcorp.net...
It is doubtful if the sayings of those four are mutually consistent.
So what's the plural of "physics", natural or otherwise?
Franz
PD
"Physicses"
What's the plural of "hell of a guy"? Hells of a guy?
>
> Franz
Dirk Van de moortel
"PD" <pdr...@yahoo.com> wrote in message news:1107446382.7...@c13g2000cwb.googlegroups.com...
> Franz Heymann wrote:
> > "Dirk Van de moortel" <dirkvand...@ThankS-NO-SperM.hotmail.com>
> > wrote in message news:wXnMd.7142$PM5....@news.cpqcorp.net...
> > >
> > > "mountain man" <hobbit@southern_seaweed.com.op> wrote in message
> > news:munMd.146106$K7.1...@news-server.bigpond.net.au...
> > > > "Bilge" <dub...@radioactivex.lebesque-al.net> wrote in message
> > > > news:slrnd02qlt....@radioactivex.lebesque-al.net...
[snip]
> > > > > All of that ``mythology'' really failed, since technology
> > > > > hasn't advanced since 1900, huh?
> > > >
> > > >
> > > > Technological physics has advanced, however
> > > > natural physics has remained stagnant since 1900.
> > > >
> > > > Are you able to appreciate the difference?
> > >
> > > I guess that "natural physics" stands for Mingst Seto Stowe Brown
> > > physics?
> >
> > It is doubtful if the sayings of those four are mutually consistent.
Fully consistent on mountainbrown's webpage.
> > So what's the plural of "physics", natural or otherwise?
>
> "Physicses"
>
> What's the plural of "hell of a guy"? Hells of a guy?
Hell of a newsgroup?
Dirk Vdm
JM Albuquerque
"Franz Heymann" <notfranz...@btopenworld.com> escreveu na mensagem
news:ctqfd0$832$1...@sparta.btinternet.com...
>
> "mountain man" <hobbit@southern_seaweed.com.op> wrote in message
> news:rcTLd.144296$K7.9...@news-server.bigpond.net.au...
(big snip)
> > Or are you forever bound to parrot the
> > tripe produced by the current paradigms
> > and promulgated by academics for the
> > last 100 years.
>
> Said paradigms turn out predictions whch, wherever possible,
> have been tested and have always, in the hands of competent
> physicists, given confirmatory results.
Not always and most of the times not possible.
There are at least two situations where relativity fails:
1 - Galaxy rotation curves (dark matter is bullshit because one needs a
special distribution of dark matter in order to the curves be flat - A flat
rotation curve means that galaxies revolve like a solid body and I never
seen any attempt to explain how dark matter distribution should be in order
to give a flat curve in all spiral galaxies - Dark matter distribution with
an inverse square law - more in the outside and less in the center is a very
stupid distribution which matter never shows, why dark matter does it?)
2 - Pioneer 10-11 anomalous acceleration which is exactly equal to Hubble
Constant is considered to be a coincidence by those that support relativity.
Pioneer 10-11 was caught by the Big-Bang? Or else Hubble is wrong.
I don't believe in coincidences, nor strange matter distributions.
Something is very wrong.
Franz Heymann
"JM Albuquerque" <jm.aR...@sapo.pt> wrote in message
news:36f6o6F...@individual.net...
You have the sign of the Pioneer anomalous acceleration wrong. It is
*towards* the sun, and it is *not* "exactly equal to Hubble Constant".
The last reference I saw said "within a factor 2 of the Hubble
acceleration.
>
> I don't believe in coincidences, nor strange matter distributions.
> Something is very wrong.
Not wrong, just not yet understood. Both the cases you cite are still
sub judice.
Franz
Franz Heymann
and chemical physics.
Franz
PD
> "Franz Heymann" <notfranz...@btopenworld.com> wrote in message
> news:ctqfd1$832$1...@sparta.btinternet.com...
> >
> > "mountain man" <hobbit@southern_seaweed.com.op> wrote in message
> > news:scTLd.144297$K7.2...@news-server.bigpond.net.au...
> >
> > [snip]
> >
> >> According to Cahill, the "vacuum" is filled with "quantum foam"
> >
> > In what way does that duffer from "gunk"?
> >
> > [snip]
>
>
> It duffers in the spelling.
> Have a nice day,
Whoops. In that case, how does "vaciim qiantim foam" differ from
"gink"?
PD
JM Albuquerque
> Hubble
> > Constant is considered to be a coincidence by those that support
> relativity.
> > Pioneer 10-11 was caught by the Big-Bang? Or else Hubble is wrong.
>
> You have the sign of the Pioneer anomalous acceleration wrong. It is
> *towards* the sun, and it is *not* "exactly equal to Hubble Constant".
> The last reference I saw said "within a factor 2 of the Hubble
> acceleration.
The real sign of the anomalous acceleration was very difficult to read
(within hundreds of papers published) and there was lots of discussion in
the past about the subject, without any good conclusion. I've read papers
where it was claimed to be equal to Hubble constant. I my self have done the
calculation in the past and it is exactly equal to Hubble Constant. About
the right direction of the acceleration, my latest reference is from the
authors of the discover (those from NASA that run the equipment) in a long
final paper from 2004, where they explicitly confirm that the acceleration
mimics Hubble Constant. It is only a few lines within more then 50 pages of
other possibilities, but that's enough to me to show that the anomalous
acceleration mimics Hubble expansion. If you need I will look for the said
paper and I will tell you where to read those few undercover lines.
Paul Stowe
<notfranz...@btopenworld.com> wrote:
>
> "Dirk Van de moortel" <dirkvand...@ThankS-NO-SperM.hotmail.com>
> wrote in message news:wXnMd.7142$PM5....@news.cpqcorp.net...
[Snip...]
>>> Are you able to appreciate the difference?
>>
>> I guess that "natural physics" stands for Mingst Seto Stowe Brown
>> physics?
At LEAST Pete is without prejudice when it comes to providing a
compendium of articles on the topic.
Unlike you Dinky...
> It is doubtful if the sayings of those four are mutually
> consistent.
Three out of four ain't bad...
And in our case (Mingst & I) we HAVE a totally internally consistent
system that,
1. Matches published & observed values
2. Simplifies the required dimensionful irreducible constants
to four, ß (kg-m/sec), L (m), c (m/sec), ¿ (m^2/kg) and two
dimensionless constants, a (7.297E-03, the fine structure constant)]
and Z the magnetic moment anomaly (~1.00116).
3. Provides rational dimensions (mass/length/time) units for ALL
physical terms
4. Leads to NEW physical relationships.
What have Franz done in physics lately???
> So what's the plural of "physics", natural or otherwise?
The Choir :)
Paul Stowe
Tom Roberts
> "mountain man" <hobbit@southern_seaweed.com.op> wrote in message news:munMd.146106$K7.1...@news-server.bigpond.net.au...
>>natural physics has remained stagnant since 1900.
>
> physics?
I interpreted mountain man's statement to mean that the physical world
has "remained stagnant" since 1900 (presumably the big picture, not the
details). What those four denizens of this newsgroup do cannot
reasonably be characterized as physics.
Tom Roberts tjro...@lucent.com
Bilge
My opinion appears to be shared by the physics journals that
haven't published his articles.
>> I don't expect jargon. I expect a term to be defined in some way
>> that makes it meaningul.
>
>
>He defines the terms he uses in his papers. You probably didn't
>read that part.
Then perhaps you can point out the article in which he defines,
``quantum foam,'' and where he explains what the words ``information-
theoretic modelling of reality, known as process physics,'' have
in common with each other, since he uses the words ``information
theory'' a lot without ever using any information theory to
do anything.
[...]
>> All of that ``mythology'' really failed, since technology hasn't
>> advanced since 1900, huh?
>
>
>Technological physics has advanced, however
>natural physics has remained stagnant since 1900.
Oh, then I guess it was that magic wand, not quantum mechanics,
that brought you semiconductors. I suppose the standard model
is a figment of my imagination, too.
>Are you able to appreciate the difference?
Yes, technology is predicated on science. Do you know anything
about this subject or are you just acting as a shill on cahill's
behalf?
Franz Heymann
>
> "Franz Heymann" <notfranz...@btopenworld.com> escreveu na
mensagem
> news:ctu35e$ba6$1...@titan.btinternet.com...
> >
> > "JM Albuquerque" <jm.aR...@sapo.pt> wrote in message
> > news:36f6o6F...@individual.net...
> > >
> > > 2 - Pioneer 10-11 anomalous acceleration which is exactly equal
to
> > Hubble
> > > Constant is considered to be a coincidence by those that support
> > relativity.
> > > Pioneer 10-11 was caught by the Big-Bang? Or else Hubble is
wrong.
> >
> > You have the sign of the Pioneer anomalous acceleration wrong. It
is
> > *towards* the sun, and it is *not* "exactly equal to Hubble
Constant".
> > The last reference I saw said "within a factor 2 of the Hubble
> > acceleration.
>
> The real sign of the anomalous acceleration was very difficult to
read
> (within hundreds of papers published) and there was lots of
discussion in
> the past about the subject, without any good conclusion.
If you refer to that nonsense of Aladar Stolmar, well, that was
nonsense.
Anderson himself has quite unequivocally state that the anomalous
acceleration is *towards* the sun.
> I've read papers
> where it was claimed to be equal to Hubble constant. I my self have
done the
> calculation in the past and it is exactly equal to Hubble Constant.
About
> the right direction of the acceleration, my latest reference is from
the
> authors of the discover (those from NASA that run the equipment) in
a long
> final paper from 2004, where they explicitly confirm that the
acceleration
> mimics Hubble Constant. It is only a few lines within more then 50
pages of
> other possibilities, but that's enough to me to show that the
anomalous
> acceleration mimics Hubble expansion. If you need I will look for
the said
> paper and I will tell you where to read those few undercover lines.
No. I don't need.
Anderson has stated that the acceleration is towards the sun.
Franz
JM Albuquerque
(snip)
> No. I don't need.
> Anderson has stated that the acceleration is towards the sun.
Yes, it is the same John D. Anderson that in the paper gr-qc/0104064 v4 11
Apr 2002 says that the anomalous acceleration is equal to Hubble constant
(see page 44 of the pdf file, close to equation 57), plus page 45 "C. New
suggestions stimulated by the Pioneer effect".
It says:
ao = ap if H = 82 km/s/Mpc and ap = 8x10^-8 cm^2/s
Being:
ap = cH
You won't see only if you don't want to see.
That's true evidence.
dlzc1 D:cox T:net@nospam.com N:dlzc D:aol T:com (dlzc)
"JM Albuquerque" <jm.aR...@sapo.pt> wrote in message
news:36h8c0F...@individual.net...
True evidence is that the acceleration is towards the Sun. The magnitudes
(three different ones for three different satellites) cluster around the
Hubble constant. The SIGN is wrong. Expansion is supposed to be away from
the Sun.
Note that Cassinni was constructed specifically not to have the *design
flaws* in those other three satellites, and it went through *no* anomalous
sunward acceleration, even though it passed the "radius" (three different
radii for three different satellites) where the acceleration was suddenly
supposed to occur.
Note that the Moon also has a recession magnitude (with the right SIGN)
that is a little higher than the Hubble parameter, most of which is due to
angular momentum transfer from the Earth. One estimate of "residual"
recession is that *really* local Hubble expansion is about half the
established value.
You do not need to seek wild theories. You do not need to seek a mound of
dirt to draw your sword upon. The Man of La Mancha, Don Quixote, is girded
in glory. But it is a mound of dirt still, and there are so many.
David A. Smith
Alex
in disagreement with the data. It is now clear that it is the
Lorentzian interpretation that is in agreement with the data."
No, the GAS based MMX measurements are in disagreement with a part of
SR when adjusted with Cahill's adjustments. The cool headed approach
to this would be to analyse the adjustments, adjustments which have
been introduced with the intention of inflating the apparent
discrepancy from SR. Perhaps there is another phenomenon occurring,
perhaps SR is wrong, but it is hugely premature to throw out SR without
considering the other options!
Just consider what would happen if things were the other way round,
suppose everyone accepted the adjusted gas based MMX and the vaccuum
and solid and liquid based measurements (Fizeau expts) all showed
something different. Would all those who are crying 'empirical evidence
should rule' still be saying the same thing?
Best Wishes
Alex Green
JM Albuquerque
"N:dlzc D:aol T:com (dlzc)" <N: dlzc1 D:cox T:n...@nospam.com> escreveu na
mensagem news:AGKMd.2058$Yu.1129@fed1read01...
> Dear JM Albuquerque:
>
> "JM Albuquerque" <jm.aR...@sapo.pt> wrote in message
> news:36h8c0F...@individual.net...
> >
> > "Franz Heymann" <notfranz...@btopenworld.com> escreveu na mensagem
> > news:ctvocj$9q0$2...@sparta.btinternet.com...
> >
> > (snip)
> >
> >> No. I don't need.
> >> Anderson has stated that the acceleration is towards the sun.
> >
> > Yes, it is the same John D. Anderson that in the paper gr-qc/0104064 v4
> > 11
> > Apr 2002 says that the anomalous acceleration is equal to Hubble
constant
> > (see page 44 of the pdf file, close to equation 57), plus page 45 "C.
New
> > suggestions stimulated by the Pioneer effect".
> >
> > It says:
> > ao = ap if H = 82 km/s/Mpc and ap = 8x10^-8 cm^2/s
> > Being:
> > ap = cH
> >
> > You won't see only if you don't want to see.
> > That's true evidence.
>
> True evidence is that the acceleration is towards the Sun.
Towards the Sun means (to me) in the direction of the Sun and the sense
of the acceleration vector is not defined.
The most qualified person about the subject - John D. Anderson - says it is
equal to Hubble constant. Moreover, it also refers to the Rosales and
Sanchez-Gomez paper to be a valid possible explanation - New Physics. And
the said Rosales and Sanchez-Gomez gives you no doubts about what he is
talking about.
> The magnitudes
> (three different ones for three different satellites) cluster around the
> Hubble constant. The SIGN is wrong. Expansion is supposed to be away
> from the Sun.
If it was the case it had been very simply for John D. Anderson to say - the
sign is wrong - about the Rosales and Sanchez-Gomez paper. Nevertheless it
comments that Rosales and Sanchez-Gomez is a valid proposition.
Therefore one must conclude the sign is right.
> Note that Cassinni was constructed specifically not to have the *design
> flaws* in those other three satellites, and it went through *no* anomalous
> sunward acceleration, even though it passed the "radius" (three different
> radii for three different satellites) where the acceleration was suddenly
> supposed to occur.
Suddenly ?
Is the Cassinni at 20 AU?
Only at a distance above 20 AU the effect is confirmed.
I guess the Cassinni didn't get out of the solar system and so you have
no argument.
> Note that the Moon also has a recession magnitude (with the right SIGN)
> that is a little higher than the Hubble parameter, most of which is due to
> angular momentum transfer from the Earth. One estimate of "residual"
> recession is that *really* local Hubble expansion is about half the
> established value.
The moon is out of question, only above 20 AU.
> You do not need to seek wild theories. You do not need to seek a mound of
> dirt to draw your sword upon. The Man of La Mancha, Don Quixote, is
> girded in glory. But it is a mound of dirt still, and there are so many.
Don Quixote is a Spanish romance I never read.
Comparative to the Big-Bang theory and relativity paradoxes nothing in this
world could be more wild then that. All the Universe in a single point? What
have you see more wild then that? It will be very difficult to kill that fat
dinosaur since it is a bad carnivore one.
> David A. Smith
>
>
Franz Heymann
He *is* Cahill.
Franz
Franz Heymann
Precisely.
And you should therefore not have pretended that there has been only
one published value of the magnitude of that acceleration. There have
been more then one spacecraft for which this quantity has been
measured. At least three values have been published. They are all in
the vicinity of the Hubble acceleration, but at least one of them
differs from Hubble by nealry a factor 2.
And please do remember that the acceleration is in the opposite
direction to the Hubble expansion.
Franz