From: Serena Nobili (serena@physto.se)
Date: Mon Jan 05 2004 - 04:48:09 PST
Dear Greg
thank you for your comments. I am really glad to see that you find this
work interesting. As I understand it, your main worry is about the
treatment of SN 1999Q. I hope I can help clarify this all in what follows:
On Mon, 5 Jan 2004, Greg Aldering wrote:
>
>Hi Serena,
>
>I found your draft paper on the I-band Hubble diagram quite
>interesting. It was generally quite easy to read and understand. I do
>have some more extensive commments which I will send along as soon as I
>can, but let me mention the main points regarding the analysis which
>are of interest to me based on my understanding of the paper so far.
>
>It is probably fair to say that in this paper we have a difficult time
>drawing conclusions with the high-redshift data because larger
>uncertainties have been assigned in this analysis compared to the Riess
>analysis. It is interesting to see how this arises. It seems that the
>main components are that a large statistical error is assigned to 99Q,
>and no stretch correction is applied in the high-z analysis so a large
>intrinsic dispersion applies.
>
I think it is important to separate the issue of the Hubble diagram at
z=0.5 (Section 5) from the issue of the test on gray dust using
multi-color measurements (Section 6). The analysis presented in Riess et
al. 2000 only concerns the latter issue. In that respect, you should note
that I did not use larger uncertainties on the data for the gray dust test
presented in section 6. The main reason for which we get a different
result is in the way we treat the data, i.e. we consider them correlated,
whereas Riess consider them independent measurements (as pointed out in
Section 6). This makes his analysis artificial, since it uses a statistic
that it actually does not have (5 points from 1 SN).
The results achieved in building the Hubble diagram are diverse. First we
show that one can build a Hubble diagram in restframe I-band up to
redshift 0.5. Second, we test a couple of different cosmological models
(among which, one model of gray dust) using the 3 high-z SNe. Note that we
do not fit the cosmology on the high-z SNe, we simply compute the chisq of
the data to the models (reported in table 9), with and without systematic
uncertainties.
>Now, the large uncertainty for 99Q arises from the fact that you have
>added a "systematic" error because you believe that the statistical
>error is underestimated due to the limited number of data points.
>However, by taking the systematic error as the range from fits with
>delta_chi^2 < 3 you are more than double-counting the statistical error
>itself. delta_chi^2 includes fits that are at 1.7 sigma, so you have
>included this statistical part and called it a systematic. In
>particular, this blows-up the uncertainty on 99Q quite a bit. While
>you may be correct in worrying about the reported statistical errors
>for 2000fr and 1999ff, which have fewer points, I don't think that we
>want to claim that 99Q's uncertainty has to be as large as the one that
>you have quoted because we don't believe the fitted errors.
>
>Instead, it seems that you need to Monte-Carlo the data points and see
>whether the observed scatter is larger than the expected statistical
>scatter. Even if it is, you still have to remove the statistical part
>of the scatter before assigning a systematic error. I bet you will find
>that 99Q is good to about 0.1 mag. If my guess is right, this may allow
>for stronger constraints in this paper.
>
I don't quite understand your point here. It is true I have added a
systematic uncertainty to the fitted I-band maximum. And it is true that
the one for 99Q is larger than for the other two SNe. (Note that this only
affect the Hubble diagram). The way I estimate this uncertainty is to look
at the lightcurve fits obtained using different templates. This has
nothing to do with the statistical errors, which are given by the
procedure performing the fit and were confirmed by the Monte-Carlo
simulation. The systematic uncertainty gives an estimate of the error I am
doing by fitting the lightcurve with a discrete set of templates, instead
of applying the same procedure as on the low-z data. However since I
compute the chisq to the different models both with and without the
systematic uncertainty, I don't think this is really diminishing the
quality of the work.
I think you would be interested in looking at the plot in the paper web
page about this:
http://www.physto.se/~snova/internal/papers/iband/figs/read_fitlog.ps
and discussion:
http://www.physto.se/~snova/internal/papers/iband/#hizfit
>Next, you decided to not stretch-correct, so the intrinsic scatter is
>larger. This is because you don't seem to have a stretch for 99Q.
>However, Riess published the B-I colors for 99Q, from which you might
>be able to constrain the stretch well enough so that the error in using
>it still leads to a net gain for the overall sample. Note also that at
>least the HST R and I data for 99Q are public and Riess says this SN
>has no host. So, we can certainly measure a lightcurve from that.
>
Re-doing the data reduction of those data would certainly be interesting
and, I am sure, will provide us with a lot of new surprises, however, I
personally don't have the time to do it before the end of my thesis
(whilst I do need this paper out before the end of it).
A problem occurring when using the B-I data published for 99Q is in the
fact that they are already K-corrected. I have tried to estimate the
stretch in B by computing B= (B-I)+I, where I and (B-I) are from Riess'
paper. In this way I obtain the B-band values they have interpolated on
the fitted lightcurve at the time the observations were done in the
infrared. I have fitted these five data points with the B-band template,
fixing the time of maximum at the given epoch, and fitting the peak value
and the stretch. I got sB = 0.65 +- 0.1 which I consider too extreme to be
used. Something is weird with this data, or with the k-corrections they
applied. I would be happy if some one volunteers for checking this.
Anyway, for this reason I ended up by not using this estimate.
>On a related theme, in the past we have argued that it is always better
>to stretch correct even if the result is noisier because this
>eliminates a systematic trend in the data - you seem to make the
>opposite arguement here.
>
There are different opinions about this point, thus I
decided to show the residuals of the Hubble diagram for both cases (see
Figure 15 where the middle and bottom panel are respectively non
corrected and corrected for the stretch).
>Because Riess has made strong claims using just 99Q, I believe it is
>incumbent on us to try to squeeze all we can out of the available
>data. This is also true because we promised the TAC's that we could do
>so much with this NIR data. If people can see that we have tried to do
>this, it will make the paper much stronger. Conversely, it would be bad
>for it to appear that we are just inflating the uncertainties to
>undermine Riess (not that we are, but then sometimes people don't read
>as carefully as they should). This further reinforces the need to
>take another look at the uncertainties which have been assigned in
>your paper.
>
I agree with you. Riess has made a lot of noise on this data claiming
results he should not have claimed. I think it is time some one brings out
the weakness of his analysis. However, as I said above, I did not inflate
the uncertainty to his data points, I have simply considered a correlation
he neglected to include in the analysis (Section 6).
>Finally (for now), I believe it is possible that the CT data are offset
>from the CfA data. Examining figure 10, it appears by eye that the
>offset could be as much as 0.10 mag. If this is confirmed it would have
>a big effect on this paper (for the better). Since you have the data in
>hand, could you examine the mean, and error in the mean, for CT and CfA
>separately? It would also be interesting to test CT versus CfA/Jha and
>CfA/Riess, as well as CfA with the two different filters that you said
>were used. This could help explain why I-band has more scatter than
>other optical and NIR bands.
>
here is the statistics on the residuals of each data set from the
solid line in figure 10 (bottom panel).
set mean r.m.s. # SNe
-----------------------------------------------------------------
CT: 0.13 +- 0.05 0.16 +/- 0.05 9
CfA: 0.06 +- 0.11 0.27 +/- 0.04 6
CfA2: 0.00 +- 0.04 0.15 +/- 0.02 13
I hope this helps answering your point. I am not sure I understand what
you suggest to do with the different filters used.
>I would be happy to further discuss these and other points with you.
>Right now I'm just trying to meet the deadline imposed by the Exec,
>so have had to be rather brief. As I mentioned, I will also send
>some more specific comments on the text and figures, most of which
>should be rather straightforward.
>
The deadline imposed by the Exec was suggested by me (actually I had even
tried to suggest an earlier one!) due to the deadline I have for finishing
my thesis. For this reason I would really much appreciate if you could
send me the rest of your comments a soon as possible.
I hope I have given an answer to your doubts, in any case, let me know if
you want to discuss further these issues.
Happy new year to you too!
Serena
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