Fine structure constant probably doesn't vary with direction in space

[Andy Resnick]

I don't know anything about the mechanics of gas dynamics. I do know something about quasar gas dynamics, and what they say doesn't make any since to me.

I don't understand- they are measuring the location of absorption peaks due to 'nearby' galaxies; what is the role of quasar gas dynamics as a source of error? It seems that the source does not have spectral features- at least, not in the spectral region they are using.

Yes, but there are quite a few systematic errors sources that don't get removed.

Such as...?

 

[Andy Resnick]

It's really quite simple. You have different groups do different experiments with different techniques, and if you have independent techniques that point to a change in the fine structure constant, then that's the most likely explanation for the results.

I don't understand how that relates to the results presented in the paper. Saying data contains systematic bias because there are no other measurements to compare to doesn't make sense (to me).

 

[Andy Resnick]

Going into 1008.3907v1 I see more and more problems the more I look.

I haven't quite worked all the way back up to this yet. Right now, I'm trying to understand why the VLT data they (re)analyzed in

http://onlinelibrary.wiley.com/doi/10.1111/j.1365-2966.2007.12695.x/abstract;jsessionid=1F069CF3CE9A708DFBB8843C9939DDB9.d03t01

has a negative change to the fine structure constant, when in the first paper (above), they claim the VLT data shows a positive change to the fine structure constant.

 

[VelocideX]

Hello all :)

This is Julian from the PRL paper. I'm not willing to debate many of the points here, because the paper is under peer review. Having said that, I'm glad to see that our work has brought much excitement to you over the last few weeks :). The discussion in this thread has been more lively than pretty much anywhere else on the internet.

A few points though to feed all your imagination:
1) There are several accompanying papers on arXiv which discuss the consistency of our work with atomic clock measurements, and also look for other cosmological dipoles. They will be submitted to journals soon.
Check out http://arxiv.org/abs/1008.3957 and http://arxiv.org/abs/1009.0591 if you're interested
2) The peer-reviewed version of http://arxiv.org/abs/astro-ph/0306483 is an extremely stringent analysis of the potential systematic errors in the Keck results. Certainly we've had claims that these results must be wrong because of a systematic error (as many posts here have noted), but I'm yet to see any specific analysis of these results which indicates where systematics have not been adequately accounted for. This isn't my paper though, so I can't speak too much about the results.
3) You might be interested in looking at http://arxiv.org/abs/1007.4347, which looks at various claims for cosmological dipoles. Many of the claims made fall in a similar area of the sky, which is interesting, but not convincing.
4) The dynamics of the quasar have no bearing on the analysis of the absorption. The quasar is just used as a bright continuum source. The absorbers have no dynamical association with the quasar.
5) We are very much aware of the fact that the dipole axis lies near the galactic plane. You guys may or may not be aware, but PRL has a 4 page limit on articles. We have plenty to say, and most of it will come out in the long paper (don't worry, it's coming :) ). Unfortunately we are severely space restricted in PRL, but there's nothing we can do about that.
6) All measurements have been corrected for heliocentric velocity
7) It can be quite difficult to get a full understanding of the analysis we do from a smattering of articles. One really needs to view the body of research as a whole. For those of you looking for a more detailed description of the Many Multiplet method, I'd strongly recommend taking a look at Michael's thesis ( at http://astronomy.swin.edu.au/~mmurphy/thesis.pdf ).
8) twofish-quant -- we'd love to do z ~ 0 observations, but this requires a high resolution (R ~ 50,000) UV spectrograph. Because the relevant transitions cannot be observed from the ground, this means a space telescope. With that spectral resolution, and a 4m space telescope, we'd need about the equivalent of ~200 nights as an extremely rough first guess. If you can get us the requisite time we'd be very grateful :)
9) bcrowell -- those points you refer to have a normalised chi squared of ~ unity about a weighted mean. There is therefore no reason to believe the error bars are under-estimated. See http://arxiv.org/abs/astro-ph/0306483 for detail on this.
10) Andy Resnick - check out Michael's thesis for a description of how we decide on the model. Essentially you add components until you have a statistically realistic model (normalised chisq ~ unity) and you cannot find another model which is statistically preferred
11) Andy Resnick - http://onlinelibrary.wiley.com/doi/1...939DDB9.d03t01 was a reanalysis of the Chand et al data using the same models that Chand et al used. It is described in that paper how the models used there are likely to be deficient.
12) bcrowell (I think) - uncertainties in determining the continuum are generally not considered to be a significant source of error when fitting metal lines when they lie above the quasar Lyman alpha peak.

By all means keep the criticism flowing, however :)

 

[twofish-quant]

I don't understand how that relates to the results presented in the paper. Saying data contains systematic bias because there are no other measurements to compare to doesn't make sense (to me).

In astronomical measurements, there are *always* systematic biases and there are *always* unknown systematic biases.

What you hope is that the systematic biases aren't enough to invalidate the results of your paper, and one way you figure that out is by doing radically different measurements that get at the same number.

 

[twofish-quant]

I don't understand- they are measuring the location of absorption peaks due to 'nearby' galaxies; what is the role of quasar gas dynamics as a source of error? It seems that the source does not have spectral features- at least, not in the spectral region they are using.

Even if you don't have spectral features your continuum isn't even, then this will cause the shape of the absorption line to shift and this could cause changes in the location of the peaks. Also the continuum spectra could be highly polarized causing other peaks to move.

The other thing is that the lines could come from different parts of the galaxy. You could have one set of lines come from the galactic core. And another line coming from out in the disk. If these two different gas clouds are moving with respect to each other, you are going to get spurtious doppler shifts.

Such as...?

If there is something about the clouds that cause all of the numbers to be shifted systemically the same amount, then I don't see how any of the tests that present would rule that out. Something that bothers me about their data is that if you just draw a straight line through it, it doesn't end up at z=0,alpha=0

I'm also not seeing how their systematics rules out a local (i.e. solar system effect).

Also just because it is in the solar system doesn't mean that it isn't interesting. There are some models of alpha variation in which alpha will change based on the locations of the earth...

http://arxiv.org/PS_cache/arxiv/pdf/1002/1002.4528v1.pdf

One thing that they've done a good job doing is to try to establish that the effect isn't in the telescope. As long as it is outside the telescope, it's likely to be something interesting.

 

[twofish-quant]

That's the assertion. I'm not convinced. The absorbers may have no dynamic association with the quasar, but there is a chance of some sort of bias if the quasar is putting out polarized light or if its not a flat continuum.

Also even if the quasar is creating a continuum there could be a gas cloud behind the galaxy that causes the light that goes into the gas cloud that you can see to be non-continuous.

7) It can be quite difficult to get a full understanding of the analysis we do from a smattering of articles. One really needs to view the body of research as a whole. For those of you looking for a more detailed description of the Many Multiplet method, I'd strongly recommend taking a look at Michael's thesis ( at http://astronomy.swin.edu.au/~mmurphy/thesis.pdf ).

I'd like to look at all of the assumptions that go into the laboratory measurements and how much they diverge from possible astrophysical conditions. In particular, what happens to the lines if you put a magnetic field or strong electric field or increase the temperature.

8) twofish-quant -- we'd love to do z ~ 0 observations, but this requires a high resolution (R ~ 50,000) UV spectrograph. Because the relevant transitions cannot be observed from the ground, this means a space telescope. With that spectral resolution, and a 4m space telescope, we'd need about the equivalent of ~200 nights as an extremely rough first guess. If you can get us the requisite time we'd be very grateful :)

Can you do it from Antarctica because of the ozone hole? (Quite serious here). I think you can see the copper doublet from there.

12) bcrowell (I think) - uncertainties in determining the continuum are generally not considered to be a significant source of error when fitting metal lines when they lie above the quasar Lyman alpha peak.

The problem that I have with this statement is that usually people are just trying to determine redshifts, and the tolerances there are much more relaxed, and no one cares about the exactly wavelength since those errors are less than the peculiar motion of the cloud.

You are doing extremely high precision spectroscopy, and it would be more comforting if you say that the estimated error is X and it's much less than Y. One way you can quantify this (and apologizes if you've done this) is to compare the required error with the width of the line. If the line is much, much narrower than the required error, that removes one class of systematics.

 

[VelocideX]

You are doing extremely high precision spectroscopy, and it would be more comforting if you say that the estimated error is X and it's much less than Y. One way you can quantify this (and apologizes if you've done this) is to compare the required error with the width of the line. If the line is much, much narrower than the required error, that removes one class of systematics.

In regions where the continuum fit does not appear good, we allow for a variable continuum. The error from this propagates into the error on each da/a measurement. You can show that in the case where the continuum fit is good, and you do this, that the impact on da/a is negligible (typically any shift in da/a is much less than 0.1 sigma). Errors on da/a increase negligibly, except in cases where there are significant trade-offs between the fitted components and the continuum estimation (in which case errors naturally increase to account for this, if it's relevant).

That's the assertion. I'm not convinced. The absorbers may have no dynamic association with the quasar, but there is a chance of some sort of bias if the quasar is putting out polarized light or if its not a flat continuum.

The continuum is absolutely not flat! How you model the continuum varies from person to person, but typically you fit medium order (say degree 6) Chebyshev or Legendre polynomials to sections of the data with absorption due to intervening gas. In the regions of absorption, the quasar continuum is assumed to be the interpolation of the polynomial across the absorption region. This actually works very well. We divide the actual quasar spectrum by the continuum model to work with normalised flux, which should be in the range ~ [0,1].

I realize that there is a lot that is unsaid in our papers, but this is because there are things which are controversial and things which are not. It's difficult to explicitly spell out every assumption made every time you write a paper, because otherwise they become impossibly long. The technical papers are written in large part to convince people who work in quasar spectroscopy that the results are valid (although obviously designed to be accessible to a more broader community also). This sort of approach is true in almost all areas of science.

Can you do it from Antarctica because of the ozone hole? (Quite serious here). I think you can see the copper doublet from there.

I'm unsure. There are people looking at putting large (>4m) telescopes in Antarctica because it's great for IR and optical viewing. The problem is that for what we're doing we really need 8m and 10m class telescopes to get enough photons in a reasonable amount of time.

To give you a feel for the numbers, I think there's about ~100 nights of observing time in the VLT sample.

I'd like to look at all of the assumptions that go into the laboratory measurements and how much they diverge from possible astrophysical conditions. In particular, what happens to the lines if you put a magnetic field or strong electric field or increase the temperature.

The low column density quasar absorbers are generally thought to be associated with galaxy halos (i.e. they're in the intergalactic medium). High density absorbers that are associated with damped Lyman alpha systems may include galactic components.

I presume you're talking about the Zeeman shift etc. The key idea behind the Many Multiplet method is that different transitions shift in different ways if da/a is different. See the attached image for a very much exaggerated viewpoint of how different transitions used shift. Any systematic which produces da/a <> 0 has to mimic this pattern. A key point of consideration is the Fe II ~ 2500A lines, which shift in one direction, and the Fe II 1608 line, which shifts in the opposite direction. Similarly the Cr/Zn lines shift in opposite directions. It is difficult to think of a systematic which can mimic this effect.

If there is something about the clouds that cause all of the numbers to be shifted systemically the same amount, then I don't see how any of the tests that present would rule that out. Something that bothers me about their data is that if you just draw a straight line through it, it doesn't end up at z=0,alpha=0

The problem is that we don't have a model for the evolution of alpha, if it exists. There are so-called chameleon models which suggest that the coupling constants depend on the local gravitational potential or matter density. It is natural to assume that the z=0 trend should agree with laboratory measurements, but this is not guaranteed -- it depends on what the universe is actually doing.

The other thing is that the lines could come from different parts of the galaxy. You could have one set of lines come from the galactic core. And another line coming from out in the disk. If these two different gas clouds are moving with respect to each other, you are going to get spurtious doppler shifts.

Absolutely. This is the origin of the many different components fitted in the models shown in the 2003 MNRAS paper. If you look at the typical velocity dispersion for the complicated fits, it's of the order of a few hundred km/s, which is ~ the rotational velocity of galaxies.

Think about how the doppler shift works. Suppose you have a galaxy at redshift z, and there is some cloud at the galactic core (unlikely I know) which is therefore at redshift z, and some other cloud at a higher redshift, z+dz. This will be observed as two gas clouds. If da/a = 0, all transitions in both gas clouds should be described by lambda_i = lambda_0 *(1+z) and lambda_i = lambda_0 * (1 + z + dz) respectively.

The question is: are there velocity shifts between transitions which arise from the same gas cloud?

One thing that they've done a good job doing is to try to establish that the effect isn't in the telescope. As long as it is outside the telescope, it's likely to be something interesting.

Actually all groups in this field generally consider astrophysical systematics to be less important than telescope systematics. People generally consider wavelength calibration to be the largest concern.

The point about certain astrophysical systematics is that there are plenty you can conceive of, but almost all of them should randomise out when averaged over large numbers of systems. Consider spatial segregation for instance: we make an assumption that all the transitions arise from the same point in space. This is almost certainly not true -- there are likely to be chemical inhomogeneities in the cloud. But only if such inhomogeneities occur systematically along lines of sight (e.g. Mg is always closer to Earth than Fe) can this generate a systematic over large numbers of absorbers. Such a situation would put Earth in a *very* privileged position, and no-one considers this seriously :)

However, this process (and others) may produce extra scatter in the data about models. The extra systematic error term that is estimated is an attempt to account for the overdispersion in the data (i.e. chisq_nu != 1). Having said that, we don't expect chisq_nu = 1 anyway, because our models are almost certainly wrong. A dipole model is just an interesting approximation. The goal is to determine whether alpha is varying or not, and parametric models are the easiest way to do that (with the obvious fact that statistical errors are conditional on the model being correct).

 

[twofish-quant]

It's difficult to explicitly spell out every assumption made every time you write a paper, because otherwise they become impossibly long.

I think it's really impossible to go through every assumption, because often you don't consciously think about the assumptions that are being made.

The technical papers are written in large part to convince people who work in quasar spectroscopy that the results are valid (although obviously designed to be accessible to a more broader community also). This sort of approach is true in almost all areas of science.

The problem in astronomy is that there are usually hundreds of steps that you need to run through in order to get a result, and at each point there is a chance for an "oops", even an unintentional one. The most that you can really do in a paper is to present a result as being solid enough to not be ignored, and then have people try to reproduce.

The low column density quasar absorbers are generally thought to be associated with galaxy halos (i.e. they're in the intergalactic medium). High density absorbers that are associated with damped Lyman alpha systems may include galactic components.

But this is guesswork since we don't know that much about galactic evolution.

Similarly the Cr/Zn lines shift in opposite directions. It is difficult to think of a systematic which can mimic this effect.

I'm a theorist, that sounds like a challenge. What you are basically measuring the strength of an electron charge, and it's not that hard for me to imagine some plasma effect in which effectively changes the charge of the electron. Suppose you have an complex atom in which you are looking at the behavior of the outer electron. Now you apply an electric field so that the lower electrons are polarized which allows more of the charge of the nucleus to go through. At that point what can happen is that the effective charge of the electron in the higher orbitals increase.

This is a hypothetical, and it probably work. But my point is that just because the lines seem to move in random ways, doesn't mean that there is some underlying systematic effect that causes all of the lines to move as if there is a different alpha in response to some external stimulus.

One fact that you should be aware of is that it is known that alpha does vary. If you increase energy scales, the the value of alpha will change, and there is enough commonality between high energy physics and the physics of plasmas to make me worry that you can end up with an "effective alpha" that is different in astrophysical situations than in the lab.

The problem is that we don't have a model for the evolution of alpha, if it exists.

My worry is that if I look at these results, they look to me like \alpha being shifted by some constant amount, and that is worrisome.

This will be observed as two gas clouds. If da/a = 0, all transitions in both gas clouds should be described by lambda_i = lambda_0 *(1+z) and lambda_i = lambda_0 * (1 + z + dz) respectively.

If the two gas clouds are in line of sight, you can end up mixing and match measurements.

The point about certain astrophysical systematics is that there are plenty you can conceive of, but almost all of them should randomise out when averaged over large numbers of systems.

I'm less sure of this than you are. :-) :-)

Consider spatial segregation for instance: we make an assumption that all the transitions arise from the same point in space. This is almost certainly not true -- there are likely to be chemical inhomogeneities in the cloud. But only if such inhomogeneities occur systematically along lines of sight (e.g. Mg is always closer to Earth than Fe) can this generate a systematic over large numbers of absorbers. Such a situation would put Earth in a *very* privileged position, and no-one considers this seriously :)

But I can *easily* think of a plausible way that this can happen.

Suppose you have a galaxy in which you have a more massive star formation in center of the galaxy than in the halo. The stars in the core are more likely to go type II that in the halo which is more likely to go type I supernova. OK, you now have a galaxy that is richer in iron in the center than in the halo which has a higher concentration of Mg.

Now because of gas and dust you aren't going to see the Mg on the other side of the galaxy, but what you will see is that Mg is always closer to the Earth than Fe.

It may be that for whatever reason this doesn't work, but I've seen enough actual situations in which something similar to that happen that I'm not going to underestimate the perversity of the universe.

What happens with most astronomical sources is that random variations *don't* statistically cancel out, which is why it's a tough game.

However, this process (and others) may produce extra scatter in the data about models.

The problem is that without knowing more about the dynamics of the emitters and the absorbers you can't rule out the scenario that I mentioned above.

A dipole model is just an interesting approximation.

What really bothered me about the data is actually how *well* the data fit a dipole. If alpha was varying over space, a dipole would be the last thing I'd expect, because you run into the problem of causality. How do two quasars on the opposite side of the Earth know that they are supposed to adjust alpha in opposite directions.

It also bothers me a lot that the equator of the dipole seems to be 180 degrees out of phase with the ecliptic.

 

[VelocideX]

Suppose you have a galaxy in which you have a more massive star formation in center of the galaxy than in the halo. The stars in the core are more likely to go type II that in the halo which is more likely to go type I supernova. OK, you now have a galaxy that is richer in iron in the center than in the halo which has a higher concentration of Mg.

Now because of gas and dust you aren't going to see the Mg on the other side of the galaxy, but what you will see is that Mg is always closer to the Earth than Fe.

Whilst this might be true if the absorbers were in the galactic cores, many of the absorbers have optical depths much less than unity and appear to be located in the galaxy halo.

You might like to note that estimates of the quasar absorbers sizes range from ~ 10 to ~100 parsecs
http://adsabs.harvard.edu/abs/2001AJ...122..679C

It's good that you're thinking about the issues :)

 

[Andy Resnick]

Hello all :)

This is Julian from the PRL paper. I'm not willing to debate many of the points here, because the paper is under peer review. Having said that, I'm glad to see that our work has brought much excitement to you over the last few weeks :). The discussion in this thread has been more lively than pretty much anywhere else on the internet.

Julian, thanks for joining in this discussion.

I'm the one with the least amount of expertise here- my research is decidedly terrestrial- so let me first me sure I understand what you guys have been doing:

1) the data- you are performing spectroscopic measurements, using quasars as the source and intervening galaxies/dust/etc which provide narrow absorption lines (you guys mostly use Mg and Fe).

2) the analysis- the location(s) of the spectral peaks are shifted due to a variety of factors, which are combined into a parameter 'q'. This parameter 'q' is also a measure of how the fine structure constant at the absorber may differ from the value at earth. Mg and Fe were chosen because one has a very low 'q' while the other has a (relatively) high 'q'.

Am I on the right track so far?

 

[VelocideX]

1) the data- you are performing spectroscopic measurements, using quasars as the source and intervening galaxies/dust/etc which provide narrow absorption lines (you guys mostly use Mg and Fe).

2) the analysis- the location(s) of the spectral peaks are shifted due to a variety of factors, which are combined into a parameter 'q'. This parameter 'q' is also a measure of how the fine structure constant at the absorber may differ from the value at earth. Mg and Fe were chosen because one has a very low 'q' while the other has a (relatively) high 'q'.

Am I on the right track so far?

We perform high resolution (R ~ 50,000) spectroscopy on quasar absorbers. The precise origin of the absorption is unknown, but thought to be gas clouds of size ~10 to ~100 pc that are found in both the disk of the galaxy and the halo. The transitions we analyse arise from: Mg I, Mg II, Fe II, Al II, Si II, Al III, Ni II, Zn II, Cr II, Ti II, Mn II

If the fine structure constant doesn't change (da/a=0), then all transitions should occur at their redshifted rest wavelength. On the other hand, if the fine structure constant does change, then we would see velocity shifts with respect to that redshift governed by a particular pattern.

Ignoring redshift for the moment, the position of each line shifts by a certain amount as omega = omega_0 + q*([da/a]^2) where da/a = (alpha_z - alpha_0)/alpha_0, and this formula is only valid for small (da/a). The coefficient q determines the sensitivity to the effect. You can find a table of the q coefficients and wavelengths at http://arxiv.org/abs/physics/0408017

Effectively, it is the relative spacing of the lines which gives sensitivity to da/a. The values of q are determined through quantum many-body methods. q is small for Mg I, Mg II, Si II, Al II (these are often referred to as "anchor lines"). q is large and positive for all Fe II lines (positive shifters) except Fe II 1608 (negative shifter). q is large and positive for the Zn lines, large and negative for the Cr lines, and negative of varying magnitude for Ni.

At low z (z less than about 1.5 to 1.8 ish), the Mg II/Fe II combination dominates (most other transitions are at too low observed wavelength). From there upwards, Al II and Si II become useful. At sufficiently high redshifts, The Fe II 1608/Al II/ Si II combination becomes dominant.

The point is that the q coefficients are arranged in a rather unique manner. It is difficult to come up with systematics which mimic da/a. For instance, if you just compress a synthetic spectrum with da/a = 0, you find that da/a goes one way at low redshifts (I think negative from memory but can't remember) and goes the other way at high redshifts. The 2003 paper demonstrates quite convincingly, I think, that the observed results there can't be from a simple compression or expansion of the spectrum.

It's certainly true that you can come up with systematics which might cause da/a at lower redshifts. In particular, the result is sensitive to the isotopic abundance of Mg. A non-zero da/a from Fe/Mg systems *might* be attributed to evolution in the isotopic abundance of Mg. However the higher redshift systems are essentially unaffected by this (this was demonstrated in the 2004 paper).

Unfortunately the analysis of the whole thing is rather tricky. The current VLT sample has taken about 3 years of work to get to this point. It's pretty time intensive.

 

[twofish-quant]

Whilst this might be true if the absorbers were in the galactic cores, many of the absorbers have optical depths much less than unity and appear to be located in the galaxy halo.

I was just using that as an illustration of how one has to be careful about assuming that unknown effects will add to the scatter rather than cause systematic bias.

You might like to note that estimates of the quasar absorbers sizes range from ~ 10 to ~100 parsecs

In that case if you have clouds that are areas of active star formation, then you could have cores that have higher iron because of increased star formation than the outer layers. If they are small then you could get different elements have different doppler shifts because of movement of gas in the cloud.

Also if the size of the clouds are small then you could have dust systematically block out parts of the clouds, and this wouldn't getting noticed.

Question: How do we know that the clouds aren't high velocity ejecta from the quasar?

 

[VelocideX]

Question: How do we know that the clouds aren't high velocity ejecta from the quasar?

The absorbers are at cosmological redshifts from the quasar. The exact distribution of absorbers isn't uniform, due to galaxy evolution, GR angular size effects (which relates to the chance of getting line of sight intersections), but to a very very rough first approximation absorbers are uniformly distributed in redshift between here and the quasar emission redshift.

e.g. for a z=3 emission quasar you might find absorbers at z=0.7, 1.2, 2.1 and 2.4. In a typical spectrum you might find two or three Fe/Mg absorbers of moderate column density. Some spectra have many (>10), others have none.

Careful studies of some absorbers manage to identify the host galaxies definitively, which are at the expected redshift.

There are selection effects on what sort of absorbers you actually use, because of the Lyman alpha forest, selection of observation targets, contamination by atmospheric transitions etc, but this isn't a problem.

There are a few absorbers which *are* associated with the quasar host galaxy (e.g. the famous z=2.811 absorber toward Q0528-250, where the absorption redshift is higher than the emission redshift of the quasar. The velocity difference is due to the fact that the absorber is moving toward the quasar source), but these are few and far between.

 

[Andy Resnick]

Ignoring redshift for the moment, the position of each line shifts by a certain amount as omega = omega_0 + q*([da/a]^2) where da/a = (alpha_z - alpha_0)/alpha_0, and this formula is only valid for small (da/a).

Thanks for the reply, it greatly clarifies your work for me.

The blurb above reminds me of power-series expansions for (say) the relativistic Hamiltonian. For example, Cohen-Tannoudji's Chapter 12,page 1213-4. Is this correct- 'q' is determined only by local interactions between parts of the atom, so measurements of 'q' can be performed in the lab?

Thinking about sources of (systemic) bias, how does uncertainty in knowledge of 'z' affect the results? That is, your analysis seems to assign definite values of 'z' to the absorbers- how were those determined, and how does that error propagate?

 

[VelocideX]

Is this correct- 'q' is determined only by local interactions between parts of the atom, so measurements of 'q' can be performed in the lab?

Thinking about sources of (systemic) bias, how does uncertainty in knowledge of 'z' affect the results? That is, your analysis seems to assign definite values of 'z' to the absorbers- how were those determined, and how does that error propagate?

q depends on the value of the fine structure constant in the atom. From the formula above, you can see that it is given by d omega / d x, where x = [(alpha_z - alpha_0)/alpha_0]^2.

To the best of my knowledge, the q values can only be calculated, not measured. In principle, if you could go to high enough energies (where alpha is higher) then you could do it. But most of our measurements are in singly ionised species. At those energies, electrons aren't exactly well bound to atoms :) This is one source of criticism of the experiment, although the q values have been reproduced by independent groups and so they are regarded as reliable.

For a single transition, da/a is degenerate with z. If you have two or more transitions where some have different qs, then da/a is not degenerate with z. z is fitted as a free parameter for each modeled gas cloud, and determined simultaneously with da/a from standard non-linear weighted least squares methods (obviously the quantities will be correlated, but as you add more and more transitions the correlation decreases).

The errors are given by the diagonal terms of the covariance matrix at the best-fitting solution. The curvature of chi squared with respect to all free parameters means that the uncertainty on determining z is taken into account. Each transition is described by three components: the column density (the number of atoms per square cm integrated along the line of sight), the velocity dispersion (due to thermal + turbulent broadening) and the redshift. We impose physicality relationships between the velocity dispersion relationships for different transitions, but all free parameters are determined simultaneously with da/a, and so the uncertainty propagates correctly. We have conducted extensive simulations to show that da/a is effectively Gaussian in all reasonable cases considered, and so can be correctly described by just a best estimate and standard error.

For the Fe II / Mg II combo typically seen at low redshift, the Fe II lines have q ~ 1500 and the Mg II lines have q ~ 200. Therefore there is a relative degeneracy between z and da/a (although the higher the SNR of the data the smaller this gets obviously). However at higher redshifts, one can include the Fe II 1608 line, which has q ~ -1300 from memory. This strongly helps to break the relative degeneracy between z and da/a, and in systems where Fe II 1608 can be included, you typically see a reduction in the error on da/a of about a factor of 2 for this reason.

 

[Old Smuggler]

(Sorry about the delay in responding to your post.)

No finite distance is small enough. (And no physical experiment is smaller than finite volume.) I think bcrowell's citing of controversy shows, at the very least, that plenty of relativists are less attached to EEP than you are portraying.

But that is what local means here - in the tangent space-time where gravitational effects are of
higher order in small quantities and can be ignored to arbitrary accuracy by making the volume small
enough..

How obtuse. If the argument is too complex to reproduce, you could at least have given a page reference. But let me quote from that book for you: "In the previous two sections we showed that some metric theories of gravity may predict violations of GWEP and of LLI and LPI for gravitating bodies and gravitational experiments." My understanding is that the concept of the EEP is simply what inspired us to use metric theories of gravity. That quote seems to show your own source contradicting your notion that LPI is prerequisite for metric theories of gravity.

There seems to be a misunderstanding here. In most metric theories the LPI does not hold for
local gravitational experiments (e.g., Cavendish experiments); that is what your quotation says.
However, the LPI is required to hold for all local non-gravitational experiments. The EEP is all
about local non-gravitational experiments in curved space-time.

Could you clarify? Surely the Lorentz force law is a coupling other than via the metric (unless you're trying to advocate Kaluza-Klein gravity)? (And what about if X is one of the matter fields?)

Here I wrote something that does not make sense, sorry about that. What I should have written is,
that if X couples to gravity in other ways than via the metric, it would violate the EEP.

The argument that a variable alpha field would violate the EEP is not complex. First, if one could
construct a theory of time-varying alpha consistent with SR, there would be no problem since the
corresponding theory in curved space-time would reduce to the SR-compatible theory for small
enough regions. Then the EEP would be saved. However, to construct a theory of time-variable alpha
compatible with SR seems impossible, since this means that there would be a way to distinguish
between inertial frames by doing local non-gravitational experiments, even in vacuum.
(In particular, there might be a "preferred" inertial frame where alpha varies only in time, not in space.
Maybe there is a loophole here by adopting LET rather than SR as the flat space-time theory.)

Second, if it is not possible to construct a theory of time-variable alpha compatible with SR, the
time-variability of alpha must depend on something connected to gravity, e.g., space-time curvature
("curvature coupling"). Then the local non-gravitational physics would couple to gravity in other ways
than via the metric, and the EEP would be violated.

I can see no obvious way to circumvent said argument, but maybe you do.

 

[Old Smuggler]

GR is solely a theory of gravity which a prescription of how to convert non-gravitational theory to include gravity. If you have any weird dynamics then you can fold that into the non-gravitational parts of the theory without affecting GR.

Sure, what I wrote does not make sense, sorry about that. But the crucial question is how to construct
a theory of time-varying alpha compatible with SR. See my previous reply to cesiumfrog.

 

[twofish-quant]

To the best of my knowledge, the q values can only be calculated, not measured. In principle, if you could go to high enough energies (where alpha is higher) then you could do it. But most of our measurements are in singly ionised species. At those energies, electrons aren't exactly well bound to atoms :) This is one source of criticism of the experiment, although the q values have been reproduced by independent groups and so they are regarded as reliable.

One problem that I see is that it's not clear to me that there is some environmental factor that can simulate a change in alpha. In plasma and condensed matter physics, there are physical situations in which you can describe the electron as having an effective charge that is different than actual charge, and I can think of situations in which this can arise in this context. For example, it may (or may not be) that a magnetic field or charged environment would be described in terms of a higher or lower effective electron charge.

Also, I didn't get a good sense of how these results relate to other results (and it may be that you are writing for PRL and it's a stylistic thing). I think that what you are arguing is that your results have lower error bars than the other techniques, but I didn't see an explicit statement that this is why you've gotten the results you have. If your results are 100x more sensitive than anyone else, its a different experimental situation than if your results are 2x more sensitive. If other groups are claiming experimental errors on the same order as you and they aren't seeing anything, then things get very, very interesting.

I don't want to sound too negative since it is an impressive piece of work. There is one and only one thing that I see which might make the paper unpublishable. The fact that the equator of the dipole is 180 degrees out of phase with the ecliptic is very disturbing, and you need to be extremely, extremely careful that there isn't a calculation error. I'd quadruple check that part of the data reduction and think really hard about things that might cause a calibration error including silly things like GR or SR effects and coding bugs.

Something that I'd look at is to see how much of a doppler shift would be needed to cause the results that you see, and if it's anywhere close to the movement of the earth, then alarm bells should go off. Also something that would be useful would be to take a spectrum of laboratory values, doppler shift it by the movement of the Earth's orbit and then see what the program spits out. I get your point that a general doppler shift shouldn't affect your results, but I'd be interested to see if it does.

The reason that I'd focus on this error is that if it turns out not to be due to a miscalculation, then it's an interesting result even if it turns out that you are seeing something else.

 

[Old Smuggler]

The way you've stated LPI seems to say that the e.p. is trivially violated by the existence of any nongravitational fundamental fields. For example, I can do a local nongravitational experiment in which I look at a sample of air and see if sparks form in it. This experiment will give different results depending on where it is performed, because the outcome depends on the electric field.

I said any given non-gravitational experiment. In your example, two different choices of electric field would give two different experiments.

 

[twofish-quant]

However, to construct a theory of time-variable alpha
compatible with SR seems impossible, since this means that there would be a way to distinguish between inertial frames by doing local non-gravitational experiments, even in vacuum.

But you can already. Look at the doppler shift with respect to CMB. If the difference in alpha is due to some big-bang field that is weakening over time, then I don't see any problems that are worse than the fact that the CMB creates a preferred reference frame.

(In particular, there might be a "preferred" inertial frame where alpha varies only in time, not in space.)

Sure. The preferred reference frame of the CMB.

I'm still not seeing out a time shifting alpha is worse than dark energy. You could in principle measure the space time curvature that is caused by dark energy, and that is going to change over time.

I can see no obvious way to circumvent said argument, but maybe you do.

I still don't see how a time varying alpha field is worse than dark energy or anything else that is already in the standard model, and none of those is considered to break GR. One thing that should be pointed out is that in the 1960's these sorts of arguments were taken pretty seriously as reasons why the BB could not be correct. The BB creates a preferred reference frame.

For example, you can come up with a theory in which dark energy creates some sort of shielding effect on electric charge and as the universe expands, changes in dark energy causes observable effects in alpha.

 

[twofish-quant]

I said any given non-gravitational experiment. In your example, two different choices of electric field would give two different experiments.

And if you attribute the change in time of alpha over time is due to the X-field, which you can set differently for different parts or space by increasing or decreasing the strength of the X-field.

Yes this means that we could create a device that could change electron masses and charges which could destroy the earth, but we've already created Earth destroying devices before, and the fact that this is a possibility is why the generals keep funding this research.

If you view alpha as some fundamental property of the universe then I can see the issue, but most high energy physicists don't. In most HEP theories, the charge of the electron is due to GUT fields which can change from place to place just like the mass is due to the strength of the Higgs field which can change from place to place. The fact that we seem to observe electrons having constant mass and charge is explained by cosmic inflation. Under current theories, none of these properties are fundamental, which is why anthropic arguments have suddenly gotten popular.

Yes this sounds a lot like the return of ether, but so what? Among the theoretical cosmological community there isn't this idolatry of mathematical principles that you seem to think exists.

 

[twofish-quant]

One reason I find this sort of experiment exciting is that if you find nothing, you have a lot to explain. If GUT theories are correct, then a constant alpha is weirder than one that varies over space-time.

 

[twofish-quant]

Sure, what I wrote does not make sense, sorry about that. But the crucial question is how to construct a theory of time-varying alpha compatible with SR.

It depends on what you mean by "compatible with SR". Most physicists will require that your field equations are Lorenz covariant, but that's not hard to satisfy, and the reason that is required is that we know of no violations of Lorenz covariance, and if you break that then a 100 other things break.

The condition of "no preferred inertial frames" is not a condition that a strongly constrains what people will accept because we have examples of preferred inertial frames (namely the CMB background).

 

[VelocideX]

Something that I'd look at is to see how much of a doppler shift would be needed to cause the results that you see, and if it's anywhere close to the movement of the earth, then alarm bells should go off. Also something that would be useful would be to take a spectrum of laboratory values, doppler shift it by the movement of the Earth's orbit and then see what the program spits out. I get your point that a general doppler shift shouldn't affect your results, but I'd be interested to see if it does.

The program has been thoroughly tested with rounds of simulations on synthetic spectra over many years. In all cases, the input value of da/a is recovered with the expected statistical errors.

da/a of 10^(-5) corresponds to shifts of between ~100 and ~230 m/s for the Fe II lines of interest. The shifts are extremely small. The size of the pixels is of the order of 1 to 2 km/s. This is the reason the wavelength calibration has to be so good.

 

[Haelfix]

One reason I find this sort of experiment exciting is that if you find nothing, you have a lot to explain. If GUT theories are correct, then a constant alpha is weirder than one that varies over space-time.

I don't follow.

That alpha (or any coupling constant) runs under renormalization group flow is of course not in dispute. That is I think *not* what is meant by these experiments, which presumably accounts for these effects by taking appropriate ratios.

This seems to be a stronger claim, namely that alpha truly does vary with position in spacetime in a nontrivial way (eg decoupled from the thermal background).

You can write down a simple model for this, by simply promoting alpha to be the expectation value of a scalar field (a moduli). Of course this type of theory is troubled from the getgo and is very much unlike the standard GUT picture.

 

[VelocideX]

For example, it may (or may not be) that a magnetic field or charged environment would be described in terms of a higher or lower effective electron charge.

Large scale electric fields cannot build up in the plasma; the electric field gradient would rapidly cause mixing of charges.

Magnetic fields in galaxy clusters typically have strength of ~ microGauss, which is roughly 9 orders of magnitude below the strength required to cause significant effects.

 

[Jonathan Scott]

Given the extraordinary weirdness of this result, I'm tempted to consider controversial explanations.

Consider for example the suggestion that gravitational collapse doesn't actually occur (for which there is some recent evidence) for some unknown reason. In that case, quasars could for example be huge star-like objects with an extremely intense magnetic field, rapid spin and an intrinsically redshifted luminous surface, as in the "MECO" model. That would mean that much of the redshift range, and hence most of the absorbing clouds, would be close to the quasar, and hence potentially affected by its intense magnetic field in a way which would increase with proximity to the quasar and hence with redshift.

Can we rule that out, or at least find some observational constraints on that possibility?

 

[Andy Resnick]

q depends on the value of the fine structure constant in the atom. From the formula above, you can see that it is given by d omega / d x, where x = [(alpha_z - alpha_0)/alpha_0]^2.

To the best of my knowledge, the q values can only be calculated, not measured. In principle, if you could go to high enough energies (where alpha is higher) then you could do it. But most of our measurements are in singly ionised species. At those energies, electrons aren't exactly well bound to atoms :) This is one source of criticism of the experiment, although the q values have been reproduced by independent groups and so they are regarded as reliable.

Thank you so much for your explanation- best of luck with the review process!

 

[TrickyDicky]

Consider for example the suggestion that gravitational collapse doesn't actually occur (for which there is some recent evidence) .

Can you give some reference about this evidence?

 

[granpa]

Can you give some reference about this evidence?

I would be curious to read about this too.

 

[Jonathan Scott]

Can you give some reference about this evidence?

I'm referring to the recent news from ESO about a star in the Westerlund 1 cluster with a mass of at least 40 times that of the sun having apparently unexpectedly collapsed into a magnetar instead of a black hole. Here's a link:http://www.eso.org/public/news/eso1034/"

 

[TrickyDicky]

I'm referring to the recent news from ESO about a star in the Westerlund 1 cluster with a mass of at least 40 times that of the sun having apparently unexpectedly collapsed into a magnetar instead of a black hole. Here's a link:http://www.eso.org/public/news/eso1034/"

Fascinating stuff, thanks.

 

[twofish-quant]

Large scale electric fields cannot build up in the plasma; the electric field gradient would rapidly cause mixing of charges.

But you could have a situation where there are lots of small electric fields. Say caused by black holes.

Magnetic fields in galaxy clusters typically have strength of ~ microGauss, which is roughly 9 orders of magnitude below the strength required to cause significant effects.

That's the overall field. If the objects are 10 pc to 100 pc and an area of active star formation, it's very easy to imagine large numbers of black holes generating very strong magnetic fields.

 

[twofish-quant]

In that case, quasars could for example be huge star-like objects with an extremely intense magnetic field, rapid spin and an intrinsically redshifted luminous surface, as in the "MECO" model.

MECO is just a name for black holes by people that don't understand general relativity and don't understand that black holes can have strong magnetic fields. Quasars *are* huge star-like objects with an extremely intense magnetic field, rapid spin and an intrinsically redshifted luminous surface.

That would mean that much of the redshift range, and hence most of the absorbing clouds, would be close to the quasar, and hence potentially affected by its intense magnetic field in a way which would increase with proximity to the quasar and hence with redshift.

Can we rule that out, or at least find some observational constraints on that possibility?

The fact that the objects are uniformly distributed suggests otherwise. Also you can tell the temperature from the clouds and if they are rapidly moving with respect to a magnetic field, you should seem massive synchrontron radiation.