D. Cohen 4 october 2013 response to referee's report (received 2 August 2013) Suggestions about clarity in the referee's preamble: 1. kappa(r) in 3.3 should be restructured; 2. more comparison to measured mass-loss rates; 3. Fig. 4 (Mdot fits to taustar(lambda)) should be replot with Mdot on the y-axis (??) (Only submitting what's below this line) --------------- We thank the referee and respond to the comments one by one below, in the order the referee raises them. Major issues: 1. Possible radial dependence of the opacity: should be made explicit in section 3.1, which should be rearranged to alter the narrative flow of the section. We have implemented this change requested by the referee, rearranging the order of equations 2, 3, and 4, and noting explicitly the radial dependence of the opacity and noting that ignoring the radial dependence and taking it out of the integral is an assumption/approximation that will have to be justified later. We've also credited MacFarlane et al. 1991 for first identifying tau_star (their tau_o) as a key parameter, though we note that they treat it simply as an adjustable parameter and don't appear to provide an analytic expression (at least in terms of M-dot) for it. 2. Suggest that Fig. 4 would provide more information if the wavelength dependence were scaled out, and the referee suggests, "...it might be more instructive to plot wavelength vs \dot M, and the mean \dot M (essentially ratio residuals)." The referee notes that "Such a plot would also be more commensurate with Fig.5, which shows the other key parameter directly, R_0." This is an interesting suggestion, and certainly has merit, but ultimately we think the current figure, with tau_star on the y-axis, is more in the spirit of the individual R_o values for each line shown in Fig. 5 -- Fig. 4 shows individual tau_star values for each line. R_o is not necessarily the same for every line in a given star, and tau_star isn't either, but M_dot is. It is especially important to show the actual tau_star information, with its wavelength dependence, because only some of the stars show the wavelength dependence. In almost half the cases it wouldn't make sense to scale out the effect of an un-physically low mass-loss rate. And it is good for the reader to be able to see the actual wavelength trend of tau_star (or lack thereof) in each star. So, for these reasons, we respectfully request that Fig. 4 remain as it is. 3. A few key points about citations -- addressed individually: "MacFarlane et al (1991) should be cited in the introduction or early in Section 3, since they first described the profile from an expanding shell." Yes, this classic paper deserves citation, and it is now cited in the introduction and also in section 3.1, where the basic profile model is described. "The work of Waldron and Cassinelli (2007; ApJ668:456) should be cited, since they analyzed 12 of the 15 X-ray spectra included here. In particular, they derived a minimum radius of X-ray formation from the f/i ratios (under the assumption of local, not distributed, emission). There should be some discussion of how the current R_0 relates to their values." We are of course aware of this seminal paper, but as it doesn't deal with line profiles we didn't find a good place to cite it. We have now added some text about the R_fir results from Waldron & Cassinelli (2007). We've kept the discussion short, however, as the f/i constraints on hot plasma location are just not very constraining once a distributed source is assumed. "Section 3.2 cites Leutenegger et al (2006) for UV photoexcitation of f/i. This should instead refer to Blumenthal, Drake, and Tucker (1972; ApJ172:205), with the former as an application for some of these specific spectra." Thank you, you are correct. We have made the change. But maybe we should cite Gabriel and Jordan 1969 too? Its comprehensiveness and focus on massive stars, exclusively, are the reasons we chose to cite Leutenegger et al. 2006, but have made the requested change. "Section 3.3 states that "... this correlation between \tau_\star and \kappa was not noted in the initial analyses of Chandra grating spectra, it has recently been shown for the high signal-to-noise spectrum of \zeta Pup that if all lines in the spectrum are considered... then the wavelength trend in the ensemble of \tau \star values is consistent with the atomic opacity (Cohen et al. 2010a)." There were, in fact, very early correlations noted between the radius of \tau=1 and wavelength (Cassinelli et al 2001; ApJ554:L55), which is closely related to the wavelength vs \tau_\star shown here. Kramer, Cohen, and Owocki (2003; ApJ592:532) explicitly related the "commonly quoted radius of optical depth unity" (their wording) to \kappa in their eq.3." We respectfully disagree. The R_1 vs. wavelength correlation is a statement about the wind opacity (which can only be assumed/computed/modeled, not derived from X-ray spectra), not about the line profile shapes and quantities derived from them. We're saying that the early papers (e.g. Cassinelli et al. (2001), Kahn et al. (2001), Waldron & Cassinelli (2001), Kramer et al. (2003)) did not claim to see a correlation between taustar or Gaussian centroid position and wavelength. We're making a statement about claims pertaining to data themselves and specifically to line profile asymmetry and blue shift. 4. "While it is good to provide the uniformly determined theoretical mass loss rates for comparison, there are also values determined from data (UV or X-ray, typically) for many of these stars. Some attempt should be made to quote these prior results (without going into an extensive review). E.g., Table 3 could contain an additional column with \dot M from literature (e.g., as in Waldron & Cassinelli 2007)." We originally had more emphasis on observed as opposed to theoretical mass-loss rates. However, there are quite a few measurements for each star, yet no source with a uniform determination for all or even almost all of the stars in our paper. So, it's impossible to assemble a consistent list of uniformly measured mass-loss rates. And even beyond that, what type of determinations should we use and should they be corrected for clumping or not? We bring in traditional density-squared, primarily H-alpha, mass loss rates via our discussion of clumping factors derived from H-alpha. If there were a uniform, H-alpha analysis that assumed a smooth wind for each of our program stars, we would certainly include it in the main results table. And then use it in conjunction with the lower, clumping-insensitive X-ray mass-loss rates to determine an optically thin clumping factor. Unfortunately, a complete data set with a uniform analysis does not (yet!) exist. And after careful consideration of the referee's suggestion, we request that we be allowed to keep the current emphasis on the very widely used theoretical mass-loss rates and discuss specific mass-loss rate determinations from other bandpasses primarily in the context of determining clumping factors. Minor issues: "p.2, L, 13 The discussion about types of diagnostics is a bit vague, regarding line vs simultaneous broad-band fits. The point seems to be that there is emissivity structure (temperature distribution --- the emission measure, and radial density structure), affecting (primarily) continuum emission and relative line strengths, and there is wind structure affecting (primarily) line profiles (and the latter are of interest in this paper). Next paragraph: "this X-ray diagnostic": "this" should be made explicit: the line profile? the parameters derived from line profile modeling?" We have clarified both of these. "p.2, L, 49: use of "hide" (in quotes) should be explained, and quotes removed since there is nothing suggestive about it. If a clump optical depth is large, then not all ions can see photons, and you can't count ions using photons." The referee is correct. Upon reflection, we used the quotes only because "hide" seemed perhaps overly colloquial. We have removed them. "p2, R, 21: typo: is f_cl 3.5^2 or sqrt( 12 )?" Thank you for catching this typo. It should be squared, and has now been fixed. "p3, L, 41: "lower sensitivity" needs to be qualified. HEG is more sensitive than MEG below about 3A (though it is of no significance for the current investigation)" Yes. Fixed. p.4, L, 49: ""just the normalization": is this equivalent to the line flux? then for consistency with the following text, give the parameter a name: "the normalization, f_{line}, ..." OK. Done. "p.4, R, 39: "... propotional to \kappa, the atomic": add "bound-free opacity" (or continuum opacity) (to clearly distinguish from a line opacity)." OK; the wording of that paragraph has already been changed in any case. "p.5, L, 13: "normalization factor", is the line flux? (i.e., not the continuum normalization, which is frozen?)" Yes, we've clarified with the new notation the referee suggested. "p.5, L, 23: Regarding line-of-sight velocities, was xi Per velocity significant because of the magnitude, or good signal in the line? Perhaps line-of-sight velocities could be included in Table 1." Because of its magnitude. We have noted in the text that this is the only sample star with a geocentric radial velocity that high during the time of the Chandra observations. "p.5, L, 37ff: were any wavelengths free parameters? were line groups constrained to have fixed wavelength offsets?" Early in the project we tested this extensively and found no evidence for significant shifts and more importantly, perhaps, when we did force a shift of 100 or 200 km/s, to correspond to (bigger than expected) wavelength calibration errors for example, we found very little change to the derived tau_star and R_o parameters. "p.5, R, 49: The paragraph beginning "The actual wind abundances" is awkwardly phrased. It sounds like "uncertainties in and updates to" our knowledge will affect the *observed* profile. Instead, something like: "Elemental abundances determine the wind opacity and hence, in principle, affect the line profile. Abundances are somewhat uncertain and represent a source of uncertainty in derived parameters. However..." Yes, it was awkward, and we have improved it now. "p.6, L, 35ff: Please comment also on dependence of the LDI mechanism on metallicity (and the velocity law), which, if important, would introduce a non-linear dependence in the determination of \dot M (i.e., one affect of metallicity is a scale factor; can the other be ruled out?)" None of these stars have metallicities that vary significantly from solar - maybe by a factor of two. The metallicity dependence of Mdot is slightly sublinear, so we'd be talking about a factor of two in mass-loss rate due to metallicity effects, which is dwarfed by the actual variation in mass-loss rate among the sample stars (not to mention the scatter in the literature values for Mdot for nearly every star in the sample). Metallicity dependence on wind shock properties is purely speculative at this point (no theoretical predictions exist). And the overall level of X-ray emission (the F_line parameter, or line normalizations) aren't a topic for this paper in any case. "p.6, , 30: in the figure caption, "is therefore even narrower, in an absolute sense" would be more simply put as: "is unresolved, and therefore narrower than the instrumental profile which is about 0.02 A (FWHM) or ... km/s ...." No, the line is in fact resolved. The point is that the x-axes in these plots are all scaled to the wind terminal velocity of the relevant star, and since zeta Oph's terminal velocity is the lowest of the three, the line width looks stretched in a sense. However, this point isn't important and since it may lead to some mild confusion, we have removed the sentence. "p.7, L, 50: it is not clear how the extra opacity is applied. The function range is 0 to 1. Is it added, times some scale factor?" Yes, exactly. We've clarified this. "p.7, R, 49: while it is fairly obvious from context and the citation to Asplund, it wouldn't hurt to qualify abundances as "solar photospheric"." OK, added. "p.8, L, 33: Better to say that the lines are unresolved and thus show the instrumental profile, which is close to Gaussian." But that's not what we're saying. Only that the subtle profile shape differences between a wind profile and a Gaussian are indistinguishable at the resolution of Chandra, the wind velocities of these stars, and the S/N of the observations. "p.11, R, 54: Regarding point 3: here is where other mass loss rate determinations are relevant, as well as theory. Also, it might be noted that while current X-ray results rely on the profile fitting, there is also information in the overall X-ray emission normalization not accounted for here (i.e., if you know geometry and emission measure you can get N_e and another X-ray-derived \dot M) and that is where the complementary approach of broad-band fitting can be useful." We would prefer not to muddy the waters with this. Such an EM-based mass-loss rate determination is subject to very large density-squared clumping uncertainties for one thing. "p.12, R, 31: Q: What is the relevance of the phase of 9 Sgr being such that the primary has zero orbital radial velocity?" Just that we didn't have to include any orbital motion based X-ray line shifts into account when doing the profile fitting (as we did for xi Per). "p.15, R, 30: Regarding systematic errors, this term usually refers to unknown effects, which if you knew what they were, would be removed. "Systematic effects" (instead of errors) is a fairer term here, since they represent known terms which can be included and assessed with some effort." OK, changed. "p.15, R, 58: The argument about consistency is extremely weak, to the point of being meaningless. The only way to know if the consistency is significant is to repeat the analysis with a different velocity law, in which case, different but consistent values might also have been obtained. If that could not be done, then one could conclude something about the kinematics. Is there any verifiable, quantitative conclusion which can be made? But as described briefly at the end of sec. 4, we did fit models to quite a few high S/N lines in which we allowed the terminal velocity to be a free parameter. And we found consistency with the UV and H-alpha derived values (of the bulk, unshocked wind). But even aside from this quantitative fitting, we do think it's meaningful that we simply get good fits with models that assume both v_infinity and beta are the same for the X-ray plasma as for the cold, bulk wind. This isn't true for example for most early B and many late O main sequence stars. So the fact that it is true for these O stars with strong winds does mean something. And we don't believe we've over-sold this; we're not claiming to rule anything else out. "p.16, L, 62: In what sense are the determined mass loss rates "reliable"? One would need an independent assessment, i.e., the truth, against which to judge. Or a theoretical study showing that fits with one model against simulations with another can definitively show that models are inconsistent. Perhaps simply omit the word, "reliable". (Or is the intent of the statement that rates are consistent from line-to-line for a given stellar spectrum?)" Our intent wasn't so much to focus on the global, line ensemble, consistency, but more on the lack of dependence on unknown clumping factors (hence X-ray Mdots are more reliable than an H-alpha analysis that doesn't constrain the clumping factor using information from other wavelength regions. But the referee's implication that our statement is overly broad is taken; and we have changed this statement to be specifically about clumping. We thank the referee for the many thoughtful and useful comments. David Cohen and co-authors