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[1004.5602] Large angle anomalies in the CMB
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Authors:Craig J. Copi (CWRU), Dragan Huterer (Michigan), Dominik J. Schwarz (Bielefeld), Glenn D. Starkman (CWRU)
Abstract:We review the recently found large-scale anomalies in the maps of temperature anisotropies in the cosmic microwave background. These include alignments of the largest modes of CMB anisotropy with each other and with geometry and direction of motion of the Solar System, and the unusually low power at these largest scales. We discuss these findings in relation to expectation from standard inflationary cosmology, their statistical significance, the tools to study them, and the various attempts to explain them.
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Boud Roukema



Joined: 24 Feb 2005
Posts: 82
Affiliation: Torun Centre for Astronomy, University of Nicolaus Copernicus

PostPosted: May 13 2010  Reply with quote

Andrew Pontzen wrote:
Boud Roukema wrote:

It seems to me that 1004.2706 makes the assumption that the alm's
are drawn from (statistically) independent Gaussian distributions. Is
this correct?


No, that's incorrect. The 'designer' theory in 1004.2706 allows
complete freedom in the covariance matrix, meaning the alm's can be
correlated in any way whatsoever. The restrictions are just that the
theory is Gaussian and has zero mean.


You're correct that if some of the <a_{lm} a_{l'm'}^*> can be
non-zero, then the alm's are not statistically independent
distributions :). So, let me try again to understand
your work.

Are you assuming that all the statistical information is contained in
the Cl's together with the covariances <a_{lm} a_{l'm'}^*>, under
the assumption that each of these is Gaussian distributed, and that
there are no further correlations e.g. the n-covariances for n > 2 ?
I do not see where the higher n>3-point spherical harmonic
correlations are included in your work.

Complete freedom in the covariance matrix does not mean that you
consider spatially-Gaussian perturbation theories in FLRW
models. For example, maybe I didn't go into enough detail above when I
wrote "If you're looking at the same point in comoving space when
you're observing widely separated sky positions,...". For example,
for one of the popular candidates for a best fit to the WMAP data,
i.e. the S3 / I * FLRW model (the Poincare dodecahedral space -
astro-ph/0310253), a single physical spatial point is in some cases
seen 12 times on the sky (considering naive SW only). So even when the
amplitudes of the comoving spatial amplitudes are distributed
according to Gaussian distributions that are statistically independent
from one another, you would need a lot of n>3-covariance matrices to
represent all this information using alm's. That doesn't
necessarily make a Cθ approach into a complete tool. Cθ
would probably also need n\gg 1-point angular correlations if the
aim were to represent the full information of a spatially-Gaussian
model. [Copi et al do not claim that Cθ represents all the
statistical information for spatially-Gaussian models; they state the contrary
(IV.C 1st paragraph, last sentence).]

So your statement that the "restrictions are just that the theory is
Gaussian and has zero mean" seems to me to be incomplete and ambiguous. You do seem
to be restricting yourself to simply-connected FLRW models, plus
a few particular multiply-connected FLRW models in which ignoring the
n>2-point alm cross-correlations is accurate.

Moreover, in II, just below Eq (4), you state that you use a finite
sum with l\le30, i.e. in effect you set a_{lm}=0 \;\; \forall \, l > 30,
in all numerical calculations, and in IV.B. 2nd paragraph, you assume
an infinite flat model for covariances for l > 10.

Hiranya Peiris wrote:
Andrew Pontzen wrote:
No, that's
incorrect. The 'designer' theory in 1004.2706 allows complete freedom
in the covariance matrix, meaning the alm's can be correlated in any
way whatsoever. The restrictions are just that the theory is Gaussian
and has zero mean.


And the obvious requirement that the covariance matrix of the theory
is positive definite.


Could you please give or cite a proof that the covariance matrix
in FLRW models is always positive definite, i.e. without the assumption
of comoving spatial simple-connectedness? Given that the definition of
positive definiteness is for multiplying a matrix by an arbitrary
vector, it's not obvious to me that this is correct. If it is incorrect,
then this is another restriction resulting from assuming simple
connectedness. If it is correct, then it would be useful to have
that proof available.

Hiranya Peiris wrote:

Boud Roukema wrote:
I agree that 1004.5602 is a very clear review of
the issue, and gives clear responses to several recent papers.


I didn't see that it had responded to any of the points made in
1004.2706. We would obviously welcome a discussion of these points
here, if the authors are watching.



Please see Copi et al. 1004.5602's 4th and 5th paragraphs and the
above comments. In addition to the references given by the authors,
you might try a few early review papers (gr-qc/9605010,
astro-ph/9901364) or if you are impatient, a short pedagogical review
(astro-ph/0010185). Copi et al do not want to restrict themselves
necessarily to FLRW models, but FLRW models are an obvious start.
Comoving space must be a 3-manifold to a good approximation.

Please also see IV intro (2 paragraphs), IV.C 1st paragraph, 2nd and 3rd
sentences.

Maybe consider it this way. It is correct that all the information in
a function f(θ,φ) on S2 is contained in the infinite set
of alm's, given some restriction on the class of possible
functions f, and using theorems about vector spaces regarding
orthonormal basis sets, linear independence, etc. However, this does
not guarantee that the physically valid information in f is
represented in the alm's in a simple way. It may seem
that ignoring n>3-point correlations between alm's and ignoring
e.g. l > 20 is simple. However, S2 is not 3D comoving space. What
is simple in comoving space (Gaussian amplitudes of projections of a
function on comoving space M onto a set of orthonormal
eigenfunctions) may be complicated on S2.

Where is simplicity more important: in the physical model or in the observational model?

Andrew Pontzen wrote:
(Of course, a theory which is non-Gaussian on
large scales but highly Gaussian on small scales might come along and
evade our limits. I'll eat my hat...)


It would help if you could be clearer about the difference between
Gaussianity and independence of distributions of the amplitudes of
spatial eigenmodes, versus the same properties of Ylm's. These
are not equivalent conditions. FLRW models which are spatially
Gaussian at small length scales and can be modelled as spatially
Gaussian at large scales are well-known. If sky map analysis is
done by forcing onto alm's, then in some ways these
are non-Gaussian and have (n\ge2)-correlations of alm. Since you appear
to be unware of these, please see Copi et al. 1004.5602's 4th and 5th paragraphs,
papers they cite elsewhere in their text, "early" review
papers (gr-qc/9605010, astro-ph/9901364) or if you are impatient, a
short pedagogical review (astro-ph/0010185). Detailed calculations
require a lot of work. Please see Fig. 4 of astro-ph/0412569 for an
example.

You might also like to see some a priori (i.e. published before ˜ 1990) references:
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Hiranya Peiris



Joined: 28 Sep 2004
Posts: 54
Affiliation: University College London

PostPosted: May 13 2010  Reply with quote

glenn starkman wrote:
Andrew Pontzen writes:

Quote:
As far as I can tell, in the absence of theory, it's impossible to quantify unambiguously the significance of any anomaly.


Okay, we can go back and forth about frequentist vs. Bayesian approaches to statistics until we're blue in the face,


Yes, we agree that such a course is pointless. What we have done instead in 1004.2706 is to go back to physics to decide whether the "anomaly" points to anything interesting beyond the standard model. Dragan states above that
Quote:
All of the talk about theory expectation muddles this simple fact
but I would hope that he agrees that in the end we want to do physics, not numerology. To do physics I am afraid one has to tangle with the "muddles" of theory expectation.

To summarize Andrew's points:

- you propose S1/2(cut) as a statistic which returns a highly anomalous p-value for LCDM for the observed realization.
- neither you (nor others) proposed a competing physical model which provides a much better likelihood for S1/2(cut) for the observed realization.
- we therefore decided to maximize the likelihood of this statistic over an entire class of models (all anisotropic Gaussian theories with a zero mean).
- The available likelihood gain is demonstrated to be small. Thus we conclude that this anomaly based on the value of the S1/2(cut) statistic is likely to have no physical relevance.

As Andrew says, one can make up infinitely many a posteriori statistics by multiplying together a bunch of properties of the observed realization that are unlikely at the 1−2 sigma level. This is a pointless exercise unless some physical motivation for the statistic can be found. If you are coming up with some other statistic now, our method could be a useful recipe for you to follow. You can maximize the likelihood for your new statistic over a wide class of models and see if a model can be found which vastly improves the statistical gain over LCDM. The procedure is described in our Appendix.
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Andrew Pontzen



Joined: 07 Mar 2007
Posts: 8
Affiliation: IoA, Cambridge

PostPosted: May 13 2010  Reply with quote

A quick response to Boud, and then I'm afraid I'm likely to stop posting replies, unless I feel there are scientific points I can respond to constructively.

Boud Roukema wrote:


Are you assuming that all the statistical information is contained in
the Cl's together with the covariances <a_{lm} a_{l'm'}^*>, under
the assumption that each of these is Gaussian distributed, and that
there are no further correlations e.g. the n-covariances for n > 2 ?
I do not see where the higher n>3-point spherical harmonic
correlations are included in your work


As I said, we assume Gaussianity. A Gaussian theory is completely characterized by its two-point function; see Isserlis theorem (or equivalently Wick's theorem).

Boud Roukema wrote:

Complete freedom in the covariance matrix does not mean that you
consider spatially-Gaussian perturbation theories in FLRW
models. For example, maybe I didn't go into enough detail above when I
wrote "If you're looking at the same point in comoving space when
you're observing widely separated sky positions,...".


In fact, the CMB is described at first order by a linear transfer function acting on the linear spatial perturbation variables. Given the magnitude of the perturbations, we know this has to be an excellent approximation – whatever your cosmology, and whatever precise form the transfer function takes. Therefore if the spatial perturbations are Gaussian distributed with zero mean, so too are the alm's.

You seem particularly worried by identified points on the sky, but these can be perfectly represented in a Gaussian theory by exactly correlating the pixels in question.


Quote:

So your statement that the "restrictions are just that the theory is
Gaussian and has zero mean" seems to me to be incomplete and ambiguous.


Following the above considerations, it seems to me our statement is totally transparent.


Quote:

Could you please give or cite a proof that the covariance matrix
in FLRW models is always positive definite, i.e. without the assumption
of comoving spatial simple-connectedness?


I refer you to any book on statistics. All covariance matrices have to be positive semidefinite. The distinction between positive definite and semidefinite is unimportant for our work.

With these points covered, I don't see any need to respond to the subsidiary criticisms in your post.
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Dragan Huterer



Joined: 18 Jul 2005
Posts: 24
Affiliation: University of Michigan

PostPosted: May 14 2010  Reply with quote

Andrew Pontzen wrote:

As far as I can tell, in the absence of theory, it's impossible to quantify unambiguously the significance of any anomaly.


Hiranya Peiris wrote:
Dragan states above that
Quote:
All of the talk about theory expectation muddles this simple fact
but I would hope that he agrees that in the end we want to do physics, not numerology. To do physics I am afraid one has to tangle with the "muddles" of theory expectation.


Hmm, I guess I agree with Andrew that we fundamentally disagree from the beginning. I just find it unreasonable to trust only those anomalies for which a suitable theoretical model can be found. Plus, who is to guarantee that we know how to comb through all theoretical models for any anomaly.

Consider the discovery of the accelerating universe. The "theory prior" for it is surely tiny - explaining dark energy involves things like extremely fine tuned particle physics models, or else fantastically unlikely values of the vacuum energy (in units of planck mass). So are we to say that this anomalous finding should be discarded, and that looking at the Hubble diagram represents an a posteriori choice? Of course not! While this is a bit of an extreme example, you see my point.
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Hiranya Peiris



Joined: 28 Sep 2004
Posts: 54
Affiliation: University College London

PostPosted: May 14 2010  Reply with quote

Dragan, actually I don't see the relevance. In the case of cosmic acceleration we have the LCDM model which not only improves the likelihood greatly in a number of completely different datasets (not just for the Hubble diagram) and makes testable new predictions for future data.

I don't think anyone ever said no possible anomaly is ever of physical interest. That's a silly statement. Our paper is specifically about the S1/2(cut) statistic, and unless we are discussing that I am unlikely to reply in this thread again.
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Andrew Pontzen



Joined: 07 Mar 2007
Posts: 8
Affiliation: IoA, Cambridge

PostPosted: May 14 2010  Reply with quote

Dragan Huterer wrote:


Hmm, I guess I agree with Andrew that we fundamentally disagree from the beginning. I just find it unreasonable to trust only those anomalies for which a suitable theoretical model can be found. Plus, who is to guarantee that we know how to comb through all theoretical models for any anomaly.


Well, I didn't qute say that, I said that the significance values are just uninterpretable until you have a physical model. My view is pretty well summarised by the introduction to 1004.2706; it hasn't changed since then. I don't belong to the hardline that think 'a posteriori frequentist statistics are necessarily meaningless'.

Quote:

Consider the discovery of the accelerating universe. The "theory prior" for it is surely tiny - explaining dark energy involves things like extremely fine tuned particle physics models, or else fantastically unlikely values of the vacuum energy (in units of planck mass). So are we to say that this anomalous finding should be discarded, and that looking at the Hubble diagram represents an a posteriori choice? Of course not! While this is a bit of an extreme example, you see my point.


Suppose no one had come up with a theory of dark energy or lambda. Then our observational data wouldn't be discrepant with our models at the 0.03% level. It would be discrepant at the 0.0000000000000000...3% level. And you are right: in that limit, the frequentist results become so overwhelming that you have to listen.

But I'd argue this is just telling you that the DE data is compelling enough to overcome your priors on a new theory once you finally formulate it. This is exactly what we set out to test in 1004.2706; and the result is that C(theta) anomalies fail to overcome even very moderately low priors, i.e. the anomaly is unlikely to be physically meaningful.

Would be interesting to discuss this with you in person sometime, Dragan, as I'm not convinced forever posting these replies in cosmocoffee is the best way to resolve this.
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Hiranya Peiris



Joined: 28 Sep 2004
Posts: 54
Affiliation: University College London

PostPosted: May 14 2010  Reply with quote

Dear Dragan,

Andrew says that my response to you sounded harsh, this was not my intention at all so let me clarify. I personally don't think it is productive to start talking about all possible anomalies in all possible contexts, and try to say generically whether they are physically relevant. The answer will be different in different cases.

In this particular case our paper only focuses on the possible physical relevance of S1/2(cut). In this case, no alternative physical theory had been proposed which substantially increases the likelihood of this statistic for our observed realization. You could stop there if you don't care about "theory expectations", the statistic would have a low p-value and you would not be able to say anything further.

But you do not have to stop there; in the absence of a proposed alternative theory, you could maximize the likelihood over a whole class of possible theories. In the case of our paper, we reinterpreted S1/2(cut) as a probe of breakdown of statistical isotropy, and considered the class of theories described above. In this case our "designer theory" which maximizes the likelihood of S1/2(cut) is a strawman model which stands in for the "best possible" theory in this class.

This is a method that can be applied to any other anomalous statistic. The conclusions may be different for other statistics (i.e. you may find they do have physical relevance). There are technical discussions we can have if you disagree with our methods or analysis, and I would prefer to have them off-line.

Best,
Hiranya
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