beta Cru paper change log, response to referee's report 6February2008 cg@ras.org.uk wrote: > > Editor's Comments: > > Because of the paper's length, I will be looking to see that all the referee's > suggestions regarding the figures that may be cut, are implemented. I agree that the paper is quite lengthy, and that some of the suggested figures can be cut without negative consequences. I will argue below, however, for the inclusion of one of the figures the referee has recommended cutting. > > Reviewer's Comments: > > Reviewer: Ian Howarth Thanks for the review; it's quite helpful. I respond to all the referee's comments below, and add a couple of comments only tangentially related to them (including at least one small change not related directly to this referee's report). My comments are listed below mostly in the order in which the relevant issues arise in the (revised) manuscript. Note that this puts some of them (e.g. eliminated figures) not exactly adjacent to the referee's comments about them. --- First comment, unrelated to referee's report: There was a poster at IAU250 by Maiz Apellaniz on a reanalysis of Hipparcos data. This study isn't yet published, but it finds a smaller distance (by almost 20%) for the star. We've added a footnote in the first paragraph of sec. 2 (p. 2) discussing this briefly. But we haven't changed any of the numbers in Table 1 or the rest of the text. Next, on p. 3 in sec. 2, we've added a parenthetical note that Vink, de Koter, and Lamers (2000) mass-loss rate formula gives a result that agrees with the value we adopted from Abbott (1982). > > (i) Section 3. I'm afraid that the first couple of paragraphs suffer > greatly from "observer familiarity", leaving the general reader > bewildered about, e.g., what exactly the "ACIS-S/HETG configuration" > is, what "HEG" and "MEG" are, and, especially, what the purpose of > "observation-specific rmfs and garfs" might be. Can we have some > references to instrument/software writeups, not only for the benefit > of today's reader from outside the field, but also for the reader > twenty years hence - today's jargon will become tomorrow's > indecipherable code. [Note that the MN production staff will require > expansion of all acronyms on first usage, as a matter of house style.] Absolutely. Thanks for pointing this out. We are indeed hopeful that some people outside of the X-ray community will read this paper. We have spelled out all the acronyms, and added some specific description, as well as referencing a recent paper (Canizares et al. 2005) that reviews the characteristics and performance of the Chandra grating spectrometer. We also reference the "Proposers' Observatory Guide" which is the handbook of current observatory capabilities (and which seems to often be referenced for this purpose in other papers, despite its status as a web-only, non-refereed document). > > For what it's worth, it seems to me that the key information of basic > interest is the same for all spectroscopy: resolution, signal/noise, > and wavelength/energy coverage - none of which are given in this > introduction to the data. Indeed, I didn't notice a resolution quoted > anywhere, which concerned me given that much of the discussion > revolves around line profiles that "are only barely resolved" (see > item (v) below). Excellent suggestion. We now state the spectral coverage, average effective area, spectral resolution, and spatial resolution. We don't discuss the energy dependence of these last three properties in any real detail, but figures and text showing/discussing the wavelength dependence of the effective areas of the MEG and HEG, as well as their spectral resolution, are in the Canizares paper (and the proposers' observatory guide). In section 3, we eliminated Fig. 2 (image of chips with Park and Finley sources), and slightly modified text at the end of sec. 3 (to describe what the now-deleted figure had shown). It was suggested that we eliminate Fig. 3 (the two panels showing the unbinned MEG spectrum of beta Cru) because it is somewhat redundant with Fig. 5 (now Fig. 4), which shows the adaptively smoothed spectrum along with the best-fit two-temperature thermal model. I would like to request that we be allowed to keep both figures. Fig. 3 (now Fig. 2 - on p. 5) shows the data unprocessed with the natural sampling rate (and resolution), and (therefore) counts per pixel are preserved and the reader can visually estimate the error per pixel (from Poisson statistics). By the way, from here on out, we'll just refer to the original figure numbers, but beware that the ones in the revised manuscript will be different (lower by one, two, or three). > > (ii) While I have considerable sympathy with the authors' discussion > of the inappropriateness of formal errors (Section 4.1.1), their > insight and experience might allow them to give a rough quantitative > indication of likely realistic uncertainties, perhaps in the caption > to Table 3, for the benefit of the less informed reader. OK, well - we've gone in the other direction now, and we'd be interested to hear the referee's opinion: We now do list the formal errors on each parameter in Table 3 (90% confidence limits). However, as we explain now in the text (middle and end of sec. 4.1.1) - even ignoring systematic errors - these formal confidence limits are likely underestimates of the true *random* errors. This is because when finding confidence limits on one parameter of a multi-parameter model fit, one should let the *other* parameters vary while testing different values of the parameter in question (we use delta-chisquare formalism as described in Lampton, Margon, and Bowyer 1976 and in Numerical Recipes Ch. 14 - http://astro.swarthmore.edu/~cohen/projects/porosity/zpup_taustar_porosity_www/figs/numrec_delta_chi.png). However, for the variation of the temperatures to be meaningful, one should examine the entire spectrum, whereas for individual elemental abundances, one has to look at a narrow range of the spectrum containing only the lines in question. Thus, the temperature cannot be allowed to vary in a meaningful way while the abundance constraints are being determined. We think we have explained this situation concisely relatively clearly where we first discuss the uncertainties shown in Tab. 3 (4th paragraph of 4.1.1) and also where we discuss the abundance results (penultimate paragraph of 4.1.1). > > [As a specific example: I was unsure how to reconcile "abundances... > overall are slightly subsolar is...robust" with "only O and Mg > show...subsolar abundances, while others are consistent with solar". > Is the suggestion that there is a uniform, global subsolar metallicity > (ca. 0.7 solar?), or that only O and Mg are depleted? I couldn't > think of an astrophysical reason why Mg might be depleted in this > star; is the suggestion that the depletion is physical, or could be > the result of shortcomings in the analysis?] Well, we've rethought the situation a little, especially in light of the formal 90% confidence limits we now list in Tab. 3. If we expand these limits somewhat, due both to unaccounted for systematic errors and the impossibility of varying the temperature while determining the abundance confidence limits, then all the elements with the exception of oxygen are consistent with solar abundance values. However, the bulk of the confidence ranges are somewhat below solar. And the one element - Si - with a best-fit value that actually exceeds solar, has the largest uncertainties. As we now state in the text, there appears to be an overall trend of modestly sub-solar abundances, but an overall value of half solar is about as low as one can go and still account for the data for all the elements. Oxygen is a bit of an exception. It seems (both from the formal confidence limits, even expanded due to systematics and the difficulty related to the temperature variation, and from trying models where we forced solar oxygen abundances) that the oxygen abundance cannot be solar. We still mention the low oxygen abundance (in the penultimate paragraph of 4.1.1) but don't claim any special status for the Mg, and emphasize the overall modest subsolar abundances. A uniform metallicity of 0.7 solar would be consistent with the data, in our opinion, though it's outside of the formal 90% confidence limits for oxygen. To answer your physical question - while dust depletion isn't at work here, there is a trend seen in X-ray spectra of active cool stars (and seen in solar active regions) whereby individual elemental abundances vary such that there is a correlation between an element's abundance and its first ionization potential (the FIP effect). This is thought to be due to magnetic diffusion. There's no physical reason to think this particular effect is present in hot stars - especially if their x-rays are due to wind shocks - but it is somewhat traditional to look for variations in individual elemental abundances when fitting thermal spectral models to stellar x-ray data. > > For the authors' info, prompted by this paper I measured the > interstellar column of neutral atomic hydrogen to beta Cru, from the > merged IUE spectrum. Because the number is very low, the answer > depends slightly on the adopted photospheric profile; I think it must > be somewhat larger than the adopted 3.5E19/cm2, but my best estimate > is only around 6(+/-1.5)E+19. I infer from the authors' comments that > this will make no significant changes to their numbers. Yes; specifically, exp(-tau_ISM) ~ 0.97 at the longest relevant wavelength in the data (and closer to unity at shorter wavelengths). Doubling the column density will only, obviously, change this to 0.94. > > (iii) The clarity of several of the diagrams could be improved, if my > (reasonably good-quality) printout is anything to go by. Fig 6, the Well, I think my printout may be significantly better, but we certainly shouldn't assume every reader (of the electronic version) will have a high-fidelity hardcopy. > "grey" and "black" symbols are barely distinguishable (perhaps use OK; we - the coauthors - had some disagreement about how "fair" it is to distinguish the results from the higher S/N lines as compared to those from lower S/N lines, and so we decided to make the symbols not all that different from each other (as the first author, I'd made the black symbols also significantly larger than the gray ones, but changed them back to being the same size before submission). So, in this particular case, we think we'd like the referee's and editor's permission to keep the figure (now Fig. 5) as-is. We're quite sure the somewhat subtle color difference will show up adequately in the published journal. Unrelated: We've removed the sentence at the end of the second paragraph of 4.1.3 that claimed that DR satellite emission of Ne IX was visible near the forbidden line. We're not sure this is DR satellite emission rather than just iron L-shell emission. So... we no longer comment on it. > open and filled?), as are the "circles" and "squares" in Fig 13 (ditto > open/filled). The dotted diagonal line in Fig. 16 is essentially > imperceptible. Yes, we're eliminating Fig. 16. And have changed the symbols a bit in Fig. 13. > > (iv) As a related point: the MN editorial office raised the overall > length of this paper as a possible "issue". The writing style is > engaging rather than excessively formal; though one might edit down a > line or two here or there (notably in the rather discursive Section 2 > [what are the other two nations?]), I think that any savings would be Papua New Guinea and Western Samoa, of course! > minor, and would detract from the readability. Thanks; we agree. > > However, it seems to me that several of the figures are redundant or > unnecessary (at least, their necessity wasn't clear to me). Fig 16, > and its accompanying discussion, seemed to me pretty pointless; why > infer the significance and form of the light-curve from a CDF when > it's directly evident (as in "bleeding obvious") in Fig 17 (where I > think the caption might identify the "companion" rather than the > "secondary", for consistency)? We basically agree with you, and have removed Fig. 16 and shortened the accompanying discussion. Our reason for including the EDF figure (which we certainly considered cutting prior to submission) was to show the variability properties of the two objects on the same plot and on somewhat equal footing. But a visual comparison of the light-curves does well enough at meeting this goal. > > Similarly, I didn't really see much virtue in presenting both Figs 3 > and 5 (if the caption to Fig 5 were to give a rough indication of the We've addressed this above, and hope you'll agree that keeping Fig. 3 (now Fig. 2) is reasonable. > total number of detected counts in the stronger lines); both Figs 4 and Fig. 4 shows the ACIS - low-resolution, CCD - spectrum of beta Cru. We think it's worth showing (along with the model fit), where it's first discussed in the text (section 4). Later, in sec. 5, when we discuss the companion, showing its ACIS spectrum seems warranted. Plotting the ACIS spectrum of beta Cru (again) in the same figure facilitates comparison between the two. We could meet your logical objection by keeping Fig. 13 and just removing the beta Cru data and model from it; showing only the companion. But that wouldn't save a figure and would require the reader to flip back and forth between the pages where the two objects' ACIS spectra are displayed. Therefore, we'd like to keep Fig. 13 as is. > 13; and both Figs 14 and 15. Fig 2 seemed a bit indulgent, too; I'm We originally included both Figs. 14 and 15 for the same reason we'd like to keep Fig. 3 along with Fig. 5 (showing the spectrum in an unsmoothed/unbinned manner). We feel a little less strongly about this, though, and have cut Fig. 14, and added small amount of text to the caption of Fig. 15 indicating the overall S/N of the lines in the (adaptively smoothed) spectrum, as compared to that of beta Cru. > quite happy to take on trust a simple statement that none of the Park > & Finley stars were in the field. As discussed above, we've eliminated this figure. (We liked it (a) because it shows the whole ACIS detector with the dispersed spectra imaged, giving the reader not very familiar with Chandra a more visual sense of what the instrument is actually measuring, and (b) because it's quite a bit of bad luck, in a sense, that we didn't have the detector oriented to capture any of these sources. The reader might wonder how that could be.) In any case, we agree that this figure represented a luxury and have eliminated it. > > (v) I was unsure of the basis for (and surprised at) the claims > associated with Fig 8, that the delta-function model "cannot be > absolutely ruled out", while "the modestly wind-broadened profile is > preferred...at the 99% confidence level". From very rough > measurements of a blown-up version of Fig 8, and assuming the error > bars shown are 1-sigma, I estimate chi-squareds of about 6 for both > models, from the 13 points between 14.98A and 15.04A (okay, maybe 5.5 > for the wind model, 6.5 for the narrow line). What exactly is the > test that so strongly discriminates between them? As we mention (briefly) in sec. 4.1.1, we use the Cash C statistic as our fit statistic. This is the maximum likelihood statistic for data with Poisson distributed errors, just as chi-square is the maximum likelihood statistic for data with Gaussian distributed errors. Often people will bin x-ray spectral data to get >10 counts per bin (so Poisson ~ Gaussian) in order to justify using chi-sq. But this throws away spectral information and/or never really works perfectly, since the wings and continuum have very few counts per bin. The C statistic is not only the rigorously correct fit statistic to use when the data have some bins with few counts, but it is significantly more robust for such low S/N data (this is "accepted wisdom" but we've also done some fitting exercises with low S/N line complexes in Chandra spectra as part of another project, and found this to be empirically true). Now, the C statistic has no analytically defined distribution (unlike chi square) and so the actual value of the C statistic for any given fit cannot be analytically assessed for overall goodness of fit (i.e. there's no analog to having reduced chi square equal to one). However, to assess the goodness of fit, one can perform a Monte Carlo simulation - where you generate a large ensemble of fake data sets with the same noise characteristics as the data, then you fit the same type of model you fit to the data to each of these MC-generated data sets and thereby generate an empirical, numerical distribution of C statistic values. You can then compare the value of the C statistic that you derived for your best-fit model (and the real data) to this MC-generated C statistic distribution in order to answer the question, "What's the probability of getting a C statistic value as good as or better than the one I got from fitting the real data?" You can then treat that probability as a rejection probability. Values above 90% raise a flag (that result implies that there's only a 10% chance that the C statistic from your best-fit model could be as bad as it is due simply to the presence of random noise, and assuming that the model is correct). XSPEC has this Monte Carlo assessment-of-goodness-of-fit capability built in. For all the lines we fit, we get good fits by this criterion. So - what about the parameter confidence limits? Well, there's a long-established method of determining this that relies on the delta-chi-square formalism (see Ch. 14 of Numerical Recipes). We mentioned this earlier in our response. The 68% confidence limit for a model with one free parameter of interest is defined by the extreme values of that parameter that provide model fits that give a value of chi-square that is <1 greater than the global minimum chi-square. For 90% confidence limits, this critical value of delta-chi-square is 2.71, for example. All other free parameters must be allowed to vary while you test the variation of chi-square as you let the parameter of interest vary. (As discussed already, this is not completely doable when testing abundance values, in terms of letting the temperature of the spectral model vary.) As an aside, you can test the joint probabilities of multiple model parameters simultaneously, but then the specific values of delta-chi-square that correspond to specific confidence limits are different (see Lampton et al. 1976 or Numerical recipes 14.5). In any case, it turns out (see Cash 1979) that when your errors are Poisson distributed and you use the C statistic as your goodness of fit statistic, the delta-chi-square formalism for parameter confidence limits is still valid (you just use delta-C instead of delta-chi-square). OK, that's background. Here's what we mean by "the completely narrow profile model cannot be ruled out but the modestly broadened model is preferred at >99%" - The completely narrow model gives a C statistic that is acceptable based on the Monte Carlo method, but the modestly broadened model gives a C statistic that is even better. And when we take that second value of the C statistic and treat is as the global minimum that it is, and then apply the delta-C criterion for assessing model parameter confidence limits, we find that the narrow profile model lies outside the 99% confidence interval in the line-width dimension of parameter space. This situation is completely analogous to a situation where one is using chi-square as the fit statistic and you have, say, 10 degrees of freedom and get chi-square=11 for one particular model but get chi-square=9, say, for a different flavor of the model. A reduced chi-square of 11/10 = 1.1 is an acceptable fit for 10 degrees of freedom. But 9/10=0.9 is better - and the difference is statistically significant (delta-chi-square = 2). (Actually, this very situation occurs and is described in the caption of the final figure in the paper, where we examine the time-dependence of the X-ray hardness ratio of the companion.) Sorry to be so long-winded, but we wanted this explanation to be as complete and clear as possible. We have added a clause at the very end of sec. 4.1.2 that states that the difference in the C statistic values for the two profile models is the basis for claiming that the modestly broadened model is preferred at the 99% level. We've also referenced Ch. 14 in Numerical Recipes. The interested reader should be able to figure out exactly what we did by following the reference trail. Oh, and we made some cosmetic changes to Fig. 8 that, we hope, makes it easier to read (data as filled circles instead of a histogram). > > Noting that the lines are *barely* resolved (as is very clear from the > delta-function model in Fig 8), I wonder what "cannot be absolutely > ruled out" really means; could it be "is entirely consistent with the > observations"? Of course, it would open up a whole new can of worms > if it were suggested that the emission didn't come from an extended > wind at all...(modelling of f/i ratios notwithstanding). > > [I guess the answer may be that other lines, not plotted, provide > stronger discrimination, individually or collectively? But how well > is the instrumental PSF understood? Could it be, say, 10% broader > than assumed? That is, is it known, and spatially and temporally > invariant, at a level that assures confidence in elimination of the > delta-function model? Could the companion's spectrum provide a reliable > PSF in this particular case?] The basic relevant fact is that the Chandra spectra of cool stars - coronal sources - never show resolved lines in their HETGS spectra (i.e. the PSF is very well known - from observations of narrow-lined sources). Typical HWHM values are between 0 and ~50 km/s for these objects (consistent with thermal broadening), with uncertainties also of order 50 km/s, if the S/N is good enough. This is true of the lines in the companion's spectrum, though the signal-to-noise is generally lower (than for beta Cru) there, which makes some sort of formal, fitting comparison between these two spectra a bit problematic. We also can tell you, for example, that some of us are currently working on the analysis of a Chandra spectrum of a cool, pre-main-sequence star. We measure widths of emission lines that are sometimes non-zero, but about 9/10 of the lines in the spectrum have 90% lower confidence limits on their widths that are consistent with zero. David Cohen, et al.