Dear Brian, We are resubmitting our paper "The Physical Properties and Effective Temperature Scale of O-type Star as a Function of Metallicity. II. Analysis of 20 More Magellanic Cloud Stars, and Results from the Complete Sample" (MS 61783) by Massey, Puls, Pauldrach, Bresolin, Kudritzki, & Simon in the hopes that it is now acceptable for publication. We have made changes in the paper where we thought it was appropriate. In some cases the referee misunderstood what we intended, and we used this opportunity to clarify the manuscript; in some cases there were legitimate errors, which we've now corrected. In other instances we disagree with the referee, as detailed below. I apologize for the length of the response attached below, but we felt it was important that we make it clear that we have carefully and fully considered each of the many issues he raised. cheers, phil Phil Massey, Astronomer Lowell Observatory 1400 W. Mars Hill Rd Flagstaff, AZ 86001 928-233-3264 FAX: 928-774-6296 ********************RESPONSE TO THE REFEREE'S REPORT**************** The referee's comments are prefaced with ">"; ours responses follow. > >General Comments to author: > >As promised in Paper I, this paper concludes the FASTWIND study of >field and cluster (R136) Magellanic Cloud O stars, and as such it >represents a substantial advancement in the subject of fundamental >parameters and wind properties of O stars. However, the present results >*are* rather overstated in the abstract and conclusions, in spite of >promises to the contrary. > >Some of the discussion is contradictory (esp. relating to spectral >types) and rather seeks to question previous results without proper >justification. Consequently, the following suggestions need to be >considered by the authors. > >Notably, the temperatures of the earliest O stars rely exclusively on >very weak HeI profiles from a heterogeneous sample of observations >(mixed aperture, S/N, resolution), in contrast with other studies in >this field based on uniform observational sample spanning UV to optical >diagnostics. Previous echelle resolution ground-based studies are >criticised for possible nebular contamination, which the present (lower >resolution) ground-based sample appears miraculously to be immune from >(NGC346 is not the only source of nebular emission in the Clouds), and >so there is the potential for in-filling of HeI/HI lines in the >intermediate dispersion CTIO observations >Specificially, *firm* conclusions regarding the systematically higher >(4K at the earliest subtypes) temperatures for SMC stars versus >Galactic counterparts seems rather premature, and problems with >NIII/NIV as a temperature diagnostic seem overstated. The data used for modeling comes from exactly two sources: very high S/N (400-500 per 1.4A spectral resolution element) CTIO 4-m RC spectrograph data all made with a 1.3 arcsec wide slit and sky-subtracted, and---for the R136 stars--- STIS HST data with a S/N of 100 per 0.4A spectral resolution element, obtained with a 0.2" aperture and sky-subtracted. We designed these observations specifically to optimize the detection of weak HeI 4471 with the spectral resolution of the ground-based data well-matched to the typical v sin i of these objects. We are unaware of a more homogeneous data set better suited for this modeling than ours. In order to make this clearer, we have modified the paper as follows: (1) We include the S/N per spectral resolution element in Table 2, as well as noting what data were used for what purpose (i.e., spectral classification vs modeling). (2) In section 4 ("The Earliest O Stars") we have added a short paragraph explicitly noting that a S/N of 400 per 1.4A resolution element implies that we should be able to reliably detect (at the 3-sigma level) a line whose equivalent width is about 10mA [i.e., 3 * (1/400) * 1.2A =0.009A]. This is quite consistent with our MEASUREMENTS of 20mA in the spectra of some stars (i.e., BI 237) noted in Table 7. For the R136 stars, where the STIS observations typically had a S/N of 100 per 0.4A, we expect to be able to reliably detect lines with a similar EW. (This was neither a coincidence, nor a miracle.) Hopefully, this will debunk any assertions that the HeI detections are marginal. When only an upper limit could be established on the EW of He I, we noted this as such in the Tables, and, accordingly, provide only upper lower limits on the effective temperatures. (3) Although we describe our data in some detail in Paper I, we have now added a couple of sentences in the second paragraph of Section 2 explaining our choice of instrumentation and dispersion (in contrast, e.g., to the Walborn et al. 2000 echelle data used by Bouret et al. and now Heap et al.). As for problems with the NIII/NIV diagnostics being "overstated", we admit that we did not approach this with a completely open mind, as from a theoretical point of view one would not expect this emission line ratio to be purely temperature dependent. And, that is what our modeling has shown: using the temperatures derived from our modeling of the Balmer and He lines, we find no significant correlation between the ratio and effective temperatures for the hottest stars (Fig 24b). However, the HeI/HeII ratio did not fair much better (Fig 24a), and we find that the reason for this is that for stars of the highest temperatures there is also a dependence of HeI 4471/HeII 4542 on the surface gravity as well as on the effective temperature, which becomes very significant for the hottest stars. This was finding was anticipated by the work of Kudritzki et al (1983 A&A 118, 245) and Simon et al (1983 A&A 125, 34). Our conclusion that no one spectroscopic diagnostic by itself will adequately predict the effective temperature is hardly new; it was emphasized by Sellmaier et al (1993 A&A, 273, 533), and was the motivation for the development on such model atmospheres as FASTWIND. The problem becomes more significant at the high temperatures and luminosities that characterize these extreme stars. To put this another way, whether one were to distinguish O2's from O3's on the basis of HeI/HeII or the NIII/NIV ratio, one would not have separated stars on the basis of effective temperatures. >The inclusion of so-called "slash" stars here seems rather ill-advised. >These stars are well on their way to developing WN winds such that >their optical spectra and parameters will be rather affected by a >strong wind. *If* you seek to compare Galactic and Magellanic Cloud O >stars, then you ought to adhere to morphologically normal dwarfs, >giants and supergiants, or else you will end up with a confused, >inconsistent, set of comparisons. It appears you have selected >everything for which you have observations (witness a WN star Brey 58!) >rather than everything that meets the necessary comparison criteria. As >an example of your spectral type contractions, you suggest all O3If/WN >stars should be O2If stars (despite of their differences to O2If stars >in EW(HeII 4686)), and then claim Brey 58 should be an O3If/WN rather >than WN6+/-1 desipte EW(4686)=-30A or so. Much qualitative and >quantitative effort has previously gone into assigning OIf, OIf/WN and >WN distinctions - indeed EW(4686)=-10A is a fairly arbitrary division, >but one does have to draw the division somewhere, and this seems to be >a reasonable choice - you question this choice but don't offer a >jutification for a better criterion, and appear to select spectral >types that match your mood. Suggesting Of/WN for Brey 58 on the basis >that it has absorption features would also imply similar subtypes for >HD93162, HD93131, HD97950-A,B,C etc. Such a haphazard approach is not >acceptable, particularly when this is not central to the present study >- fundamental properties of O-type stars. This is an area where even the mightiest of pundits may disagree. Conti, for instances, has long argued that if a star CAN be classified on the basis of the absorption spectrum, then it SHOULD be---regardless of the strength of HeII 4686 emission, or that of any other emission line that is strongly affected by stellar wind parameters. The O2 class was introduced by Walborn et al. (2002, AJ, 123, 2754), a paper on which Massey is a co-author. I do not recall that we specified a cut-off in EW for a star to be considered an O2I rather than an O3If/WN star. Our point here is that it seems a curious nomenclature, if the NIV/NIII calls for an O2 classification, but the strength of the HeII 4686 emission line forces an O3/WN designation. In the present paper we have used only the published criteria in deciding to describe a star as O2. If these criteria can't be used by others (even a co-author on that study) to classify stars, then one might well question how good they are. In any event, the discovery of so many interesting extreme examples of hot luminous stars in the R136 cluster and other regions of recent star formation during the past few years has sparked the occasional discussion of this issue within the text. To Massey, who has classified a significant number of Magellanic Cloud O stars in his career (for instance, Conti, Garmany, & Massey 1986, AJ, 92, 48; Garmany, Conti, & Massey 1987 AJ, 93, 1070; Massey et al. 1995, ApJ, 438, 188; Massey & Hunter 1998 ApJ 493, 180; Massey et al. 2000 AJ, 119, 2214), the O3If/WN description of Br58, rather than WN, seemed reasonable given the strengths of the absorption features, and the general weakness of the emission. The type is not new to the present study, but the "reconsideration of Br 58 as a W-R star" was described in Massey, Waterhouse, & DeGioia-Eastwood (2000, AJ, 2214) near the end of Section 3.1.1. We are unaware of any other bona-fide Wolf-Rayet stars with NV 4603, 19 seen in absorption. However, as others have stressed (Walborn 1982, for example, or Conti & Bohannan 1989), there can be great difficulties in classifying such objects, and WE realize that other reasonable people might reach other conclusions. For that reason we have been very careful and detailed in stating how we reached the spectral types that we did. The referee obviously does not respect our opinions on the subject, and while he may have spent more time and effort worrying about this than others, there is actually room for differing opinions without the need for the insults that have characterized this and the report on Paper I. For the record, the EW of HeII 4686 in Br58 is -18A, not -30 (see the text). The inclusion of this star in the LMC Wolf-Rayet catalog of Breysacher et al. (1999) cannot be taken as proof of its WR nature; after all, Breysacher also includes Sk-67 22 in the catalog! We do now, however, suggest in the text that the high value of beta may suggest that Br58 is more similar to a WR star than to a normal O star. Be that as it may, the referee will be relieved to know that Br58 was never included in our derivation of the effective temperature scale: as is stated in the original text under our description of the star, "We do not include this star in our analysis in Sec. 5". Since apparently this was not clear enough, we have added an explicit statement that therefore it has had no effect on our effective temperature scale. However, in deference to sensibilities of the referee, we have now also removed this star from Fig. 24 in Section 4 to keep the comparisons of the NIII/NIV vs Teff and HeI/HeII vs Teff as clean as possible. We think this is justified not so much because of the spectral type issue, but rather because the temperature is poorly determined (i.e., not a lower limit but not a precise value either). We have added a footnote to its entry in Table 7 to make its exclusion in the figures clear; otherwise, its removal might seem arbitrary and biased, given the previous published discussions of this star (i.e., Massey et al (2000). >Specific comments: > >p.1 abstract: Your study follows exclusively from optical HeI/II >spectral fits, except that wind velocities are obtained from the UV and >far-UV wind lines, rather than "an independent check on the validity of >your derived parameters". Concequently this rather overstates what you >have done, Other studies (notably Crowther et al., Bouret et al., Heap >et al.) *do* actually use UV features as independent checks on the >optically derived parameters, whilst you do not. The FUSE OVI observations were used as a check on our derivation of v_infinity, while the NEAR-UV HST observations of 3187 and 3203 were used as an additional check on our modeling. We have reworded this sentence in the abstract to make our meaning clearer. In the following section, the referee uses our conclusions ("claims") in the abstract to criticize both the abstract and the work behind these conclusions as given in the text. We address both below, but note that it is impossible in the abstract to provide all of the caveats and details that are given in the paper. Simply because we do not feel that our study is the "last word" on the subject, does not mean we should refrain from drawing conclusions. We have been careful in wording in the abstract ("We find...", "The giants appear to have...") Although we have added material to the text, we have changed the wording in the abstract only slightly since our conclusions have not changed. The exception is in point (4) concerning the NIII/NIV, about which the referee is particularly exercised; we have made it clear that while this ratio performs poorly for these hot stars, that HeI/HeII does not fair much better. >Claim (1) Although you indeed obtain substantially higher temperaures >for your O3-7V SMC stars than Repolust et al. did, the situation is >less clear when one considers other, equally valid, results based on >CMFGEN and/or TLUSTY. For example, Repoulst et al. obtained T=40.5kK >for HD15629 (O5V) whilst Martins et al. (in press) obtained T=40-41.5kK >for 3 O5V stars whilst Bouret et al. (and Heap et al. astro-ph/0412345) >obtain T=40kK for NGC346-MPG368 (O4-5V). Your results for 3 SMC O5V >stars stand out with T=42-45.5kK, though this may be due more to your >reliance on nebular contaminated intermediate dispersion long slit >datasets (Heap et al. indeed make this claim) than a genuine systematic >difference. One has to carefully compare similar techniques and >datasets in order to draw firm conclusions. Consequently, a systematic >difference of up to 4kK might indeed be genuine, but your qualitative >description of the cause is less convincing than the quantitative >comparison of Solar/SMC/Zero metallicity models in Fig.1 of Heap et al. >there is indeed an effect on HeI/II, but generally rather weak). > >Your place importance upon your derived temperature scale providing a >more coeval population of NGC346 stars, yet you did not analyse these >stars, whilst Bouret et al did, and with high quality observations and >models (including UV diagnostics!) such that they obtained ages of 3Myr >for several members. The coeval aspect is not necessarily in direct >support for your temperature scale (you also see cases of a >non-monotonic Sp-type vs Teff for O stars) as time will tell whether >all massive stars did form at the same time in this cluster. First, let us say that while we think Heap et al. (2005) did a very nice job with the data available, we find their Fig. 1 far less convincing than the effective temperatures derived from modeling real stars. Indeed, they did not intend their figure to show what the referee seems to think. Their Fig. 1 is intended ONLY to show the expected effects of line blanketing alone on the HeI and HeII profiles, and purposefully ignores the effects of stellar winds and mass-loss on the profiles! It has been known since Hummer & Abbott (1985) that "stellar wind blanketing" has a significant effect on the derived effective temperatures of Galactic stars. (This was a point that the referee for Paper I was also confused on.) There is considerable discussion of this in Sellmaier et al (1993), and more recently in both Repolust et al. (2004) and the introduction to Paper I, and we refer the referee there. Secondly, we have striven hard to be balanced and fair in what we say in the text in Section 5.1 where we have made extensive comparisons of our results to those of others (i.e., Fig. 29 and much of Section 5.1). For instance, we state explicitly in regards to the coeval argument that "While this doesn't prove our scale is right, and the Bouret et al. (2003) wrong, it does emphasize an often overlooked point, namely that changes in the effective temperature scale of O stars do have implications for the interpretation of H-R diagrams and star-formation in clusters; see discussion in Hanson (2003) and Massey (2003)." Also, as we note, if the physical parameters derived by Bouret et al. were correct, the O2 III star would have the YOUNGEST age of any star in the H-R diagram, and would have to physically be a dwarf, and not a giant. Thirdly the referee may be correct in the assertion that our "reliance on nebular contaminated intermediate dispersion long slit" has resulted problems in our effective temperature scale. We don't think so---in cases where there were strong nebulosity we also obtained high spatial resolution long-slit data with HST, and used that (particularly at Halpha). In general there was excellent agreement in our HST- and ground-based long-slit spectra. We can, however, be SURE that the Walborn et al (2000) echelle data (used by Bouret et al. and now Heap et al) DO suffer from some nebular and moonlight continuum contamination. After all, NGC 346 is the largest and strongest H~II region in the SMC, and the echelle's short slit was not optimal for sky or nebular subtraction. A careful reading of the text of Walborn et al. (2000) reveals that while these data were corrected in for the solar LINE spectrum (from moonlight), the ad hoc procedure they describe would not have corrected for any moonlight continuum contamination of the O star absorption lines. This would have the effect of making the lines weaker. While this would not have had much effect on the sort of qualatative discussion given by Walborn et al. (2000), it could have a serious effect on any modeling done with those data. We understand that John Hillier recognized this problem, and urged Chris Evans to re-reduce the data prior to Hillier's analysis of AV 83 (Hiller et al. 2003). Evans was able to perform approximate sky subtraction for some, but not all, of the stars, and in particular for the NGC 346, was not able to find sufficient sky pixels to correct correct either NGC346-368 or -487. For those two stars at least, some filling in of the O-star absorption lines by moonlight continuum is certainly possible. (We are indebted to Danny Lennon and Chris Evans for detailed correspondence on this subject, and providing us with a copy of the re-reduced version of their data.) How much this has affected the Bouret et al. and Heap et al. results, we don't know. Hopefully a competent referee will raise this issue with Heap et al, as it could be significant. We have now ourselves obtained very high S/N spectra of the NGC 346 stars themselves under excellent seeing (<0.5") and high plate scale from Magellan that have excellent sky subtraction. We will present our analysis of those data elsewhere, and if we are wrong, we will take our lumps then. Until then, we've done the best we can with what we believe is the best available data set. We have revised the text based upon our correspondence with Lennon and Evans, and included mention of the Heap et al. study, which appeared in unrefereed form in astro-ph a week after we submitted our paper. >Claim (2) Your results claim to support radiatively-driven wind theory, >yet from Fig.32 this does not seem so clear - there is little to >distinguish Gal/LMC stars (even after your tinkering with wind >densities to "correct" for clumping) whilst all the non-supergiant SMC >stars appear to upper limits - doesn't this indicate that the winds of >SMC dwarfs/giants are much weaker than predicted (in accordance with >Bouret et al.). We believe that the plot shows a clear effect between Galaxy and LMC along the lines predicted by theory. If the upper limits are close to the true values, then the SMC seems also to be ok, with the exception of two objects. A detailed analysis of the of the UV spectra (to be done in the future) might provide better constraints on the wind momenta in those cases, where Halpha provides upper limits only. We have modified the text in Section 5.2 and the conclusions to make our interpretation clearer. We have not modified the wording of the abstract. >Claim (3) You question your derived gravities or radii, yet a problem >with the latter would indicate a problem with the derived Teff that >affects claim (1) and (4). A systematic error in log g or the radii at high temperatures could explain the mass discrepancy; It is our own feeling that the log g's produced by the models may have some systematic problem, but this would not require the effective temperatures to be wrong. Even if the radii were a problem, it would not necessarily mean an error in effective temperatures, as an error in the BC leading to an incorrect bolometric luminosity could also explain an erroneous radius. In general, we do feel that resolving the mass discrepancy poses a significant challenge to stellar atmospheres and interiors. Heap et al. found a similar problem in their analysis, but circumvented it by claiming that their stars must be viewed pole on and thus have intrinsically huge rotation velocities! >Claim (4) Spectral types are designed to reflect a physical sequence, >intricately coupled with ionization, and hopefully with temperature. >Consequently, the previous morphological introduction of O2-3.5 >subtypes to break the O3 degeneracy remains "legitimate", even if there >is little evidence for a uniformity of Teff at each subtype. Indeed, by >the same logic you night question the definition of O3-5V subtypes on >the basis that one of your O5V stars appears (see however above) to >have a higher Teff than one of your O4V and O3V stars (admitted in your >Sect 5.1). >In fact, you do not make a very strong case to discredit NIII/NIV as an >ionization/Teff crieteria (Fig 24 contains few actual data "points") >since you do not actually consider models containing these lines, >whilst others (notably Heap et al. in their Fig.8) do seem to indicate >a robust sensitivity of NIII/NIV to Teff at logg=4. >Either soften your claim, or actually carry out calculations in which >you can back up your statements. Our effort was not to "discredit" NIII/NIV as a temperature indicator (although as noted above, we did not understand why this would necessarily work), but to to investigate the interesting and provocative suggestion made by Walborn et al (2002) that it could be used as such. Our FASTWIND models do not yet include an exact NLTE/CMF solution for nitrogen that is needed to derive NIII/NIV ratios, but including this in the future is a high priority, as we state in the text. For now, we derive temperatures via modeling of the strengths of the Balmer and He~II and He~I lines, and compare those temperatures to the measured NIII/NIV ratios. This places the totally qualitative assertions of Walborn et al. (2002) on a quantitative scale for the first time. What we find is, we feel, both interesting and significant: at high temperatures the NIII/NIV ratio do not accurately predict the effective temperatures, but then neither does the HeI/HeII ratio. This is because the physics of the highest temperature stars is quite complicated, with even the HeI/HeII ratio dependent upon the surface gravity of the star, as discussed in Section 4, and illustrated in Figs. 24 and 25. It is true that CMFGEN could right now model the NIII/NIV behavior, and Massey has proposed a project to model a large Galactic sample. If funded, he will use FASTWIND on the complete sample, with CMFGEN used to analyze an interesting subset; John Hillier has agreed to provide expertise for the CMFGEN. In the meanwhile, a few of my spectra have apparently been passed on---explicitly against my wishes---by Nolan Walborn to other CMFGEN users in "the spirit of independent analyses." So, results may soon be available on the black market. >p.3, Sect 1, para 1, Since L scales with Teff^4, doesn't a 10% error in >Teff lead to a larger error in L than 30%? No, that would be true only if the radius were somehow known a priori, which it is not. Instead, what IS known is M_V, the absolute visual magnitude. So, the question becomes how much of an error in the BC (and hence in L) comes from a 10% error in Teff. The referee is referred to our equation 2, where we find that the BC goes as -6.9 log Teff; a similar value was found by Vacca et al. (1996). A 10% error in Teff thus leads to roughly a 30% error in L. We have added an additional reference to Massey (1998), where all this is explicitly discussed. >p.3, Sect 1, para 3, "more exact treatment" - reword. DONE. >p.5, last para of Sect 1, To reiterate, whilst you follow a common >technique to Repolust et al., you do not use uniform optical datasets >with common S/N, resolution, potentially leading to systematic >differences. Let us make two points: first, other recent studies (such as Heap et al) do not compare their derived temperature scale to those of other modern Galactic studies, but rather to the Vacca et al (1996) scale, which is based upon a variety of different models drawn from the literature with very different data sets; those older models were pure hydrogen and helium, and lacked much of the modern physics possible today. So, by using the SAME models in our study as that used by Repolust et al. we at least are doing much better than some others. Secondly, how different ARE the datasets? Repolust et al. reanalyzed the Galactic sample of Puls et al (1996), which is derived from the data described by Herrero et al. (1992) and Herrero (1994). Those spectra are described as having a S/N of 300 per 0.6A spectral resolution element, quite comparable to the data used in our study. We now note this in the introduction when we first explain our use of the Repolust et al. results. >p.6, para 3. The FUSE data are presumably large aperture (you should >state this), and so may be significantly contaminated by nearby stars - >you should state if this is true or not. The aperture size was always given in Table 2. We have, however, added a sentence in the text also quoting the aperture size, and noting that we had picked isolated targets for the FUSE observations. >p.8, first complete para. The statement about Of stars scaling witn >hluminosity seems rather obtuse. NIII and HeII emission implies Of, but >this does not necessarily imply OIf (witness AV220, Of?p). There are >nevertheless genuine examples of OIaf stars in the SMC (AV83, AV232), >with strong winds, so your statement seems rather puzzling. Two stars with the same luminosity and effective temperatures but differing metallicity will have different mass-loss rates and hence it would be naive to expect that they would have identical HeII 4686 and NIII 4634,42 emission strengths given the formation mechanisms of these lines. (This is fundamental.) We have reworded the text to say this explicitly. >p.10 - AV440 was not clasified by Walborn in that or any other >reference. The referee is correct; the star had been previously classified by Garmany, Conti, & Massey (1987). We have corrected this mistake in the text. >p.11 - Sk-67 22 Your spectral type arguments are poorly made. If >HD93129A is O2If with EW(4686)=-2A?, isn't EW(4686)=-10A or so or Sk-67 >22, close to the generally adopted division 10-12A above with a star is >a bona-fide WN star? Certainly, Brey 58 is not intermediate (see >below), so Sk-67 22 DOES represents a sensible prototype of the "hot" >intermediate slash stars. You are of course entitled to your opinion, >but such rearrangement of generally accepted divisions cannot be >accepted unchallenged - for this reason your choice of O2If for R136a5 >(#20) in Paper I seems unwise (again EW(HeII) circa 10A), since it had >previously been accepted as a hot slash star by Heap et al. (1994) and >Massey & Hunter (1998). > >You bring up the binarity of HD93129A, yet correction for the presumed >dwarf companion (with 4686 in absorption) would only marginally affect >the EW of 4686. > >Your need for Sk-67 22 to be so He rich (He/H=0.3) further supports its >intermediate spectral type between normal O stars (He/H=0.1-0.2) and WN >stars (typically He/H>0.5, though some have He/H=0.3). >p.13 Brey 58 - You measure EW(4686)=-18 for Brey 58 (other measurements >are closer to -30A), such that this alone distinguishes Brey 58 as a >bona fide WN star (HD93162, WN6ha has a similar strength). Your >revision is certainly unwarranted. We are sorry that the referee finds our spectral type arguments "poorly made" but we've done the best we can, and tried to lay out our reasoning in some detail. Walborn et al. (2002) does not specify any sort of EW litmus test for a star to be considered an O2If* vs a O3If/WN. We understand that the referee feels STRONGLY that Br58 is a bona-fide Wolf-Rayet star. Yet, the absorption spectrum would argue (using the Conti principle) that we classify the star as an O star. ("If you CAN classify the spectrum from the absorption spectrum, you SHOULD.") We argue in the text that Sk-67 22 has a high He/H ratio due to mixing. A similar argument was used by Walborn et al (2004, ApJ, 608, 1028) to explain how the star LH64-16 could have a He/H ratio of 1. Walborn et al consider LH64-16 as a prototype of the ON2 III class, and I think no one would argue that IT is a Wolf-Rayet star, despite its high He/H ratio. (We ourselves argue in Paper I that it is the product of binary evolution.) As stated above, we understand that other reasonable people might disagree, but we have spelt out our arguments to the best of our abilities for the reader to accept or reject. However, while we respect the opinion of the referee on this difficult matter, let us again emphasize that it has no impact on the science of the paper, since we are not happy with the fits for Br58 and did not use this star for either the effective temperature scale or in our comparison of NIII/NIV vs HeI/HeII. In addition, in deriving our effective temperature scale we do not consider O2 and O3 separately, but simply lump the values under "O3", since we conclude that this division is not justified. Similarly, our evaluation of the NIII/NIV line ratio is NOT dependent upon spectral types (other than the fact that the star is O3.5 or earlier), but is done differentially with respect to HeI/HeII and the temperatures derived from our modeling of the hydrogen and helium spectrum. >p.14 ST2-22 "somewhat redundant" - rather impolite We have removed "somewhat". >p.14 - BI237 (and BI253). Both have very weak (if present at all) HeI >4471, which you rely upon for a temperature determination. However, >from the spectral fits presented the case for HeI being present is not >so clear (LH64-16 suffered from a similar problem in Paper I) despite >claims that EW(HeI)=0.02A in BI237 and <0.025A in BI253. Whilst your >high S/N is not in doubt, your rectification may be questionable - >witness the poor match between the observed "continuum" and model in >Fig.12 - which would affect the measured EW and derived temperature. We have normalized the spectra as best we could before proceeding with our analysis. We find the referee's comments here quite curious; perhaps he has used a printer in which the red and black ink jets are misaligned? In our versions of the figures the agreement in the model and normalized spectrum is excellent. To further investigate this odd claim, we have looked at the original data used in the modeling and in making the figure. For BI 237, the average value of the normalized spectrum in the range 4450.5A to 4460.5A (35 points) is 1.00044. On the red side, from 4485.5A to 4495.5A (26 points) is 0.99953. So, the normalization appears to be good to 0.05%! This is, I'm sure, fortuitous, but it does suggest some problem with how the referee is looking at the figures. The normalization of BI 253 is probably more typical, where the agreement is closer to 0.3%. How much of a differences does this make in the determination of the equivalent widths for these weak lines? If the line width is similar to the spectral resolution (which is the case here), then a 20mA EW line will have an average line depth of 20/1400, or about 1.5%. If we are mistaken in the continuum level by 0.5% (which, we believe, would be extreme), then if we did not compensate in any way when we did the modeling, the 20mA line could be as strong as 28mA. Recall that our S/N of 400 introduces a 3-sigma error of 10mA, so in fact our normalization procedure cannot be a significant source of error. We thank the referee for raising this interesting point; we have added several sentences discussing the normalization and the resulting affect on our EW measurements in paragraph 2 of Section 4 in the revised text. >p.15 - LH101 W3-14 was already re-classified as O3V + OB by Walborn et >al. 2002 (see also Table 2/Sect 3.2.5) We have added a sentence saying that Walborn et al. (2002) came to the same conclusion as we did based upon the same data. Historically one must keep in mind that much of the data in Walborn et al. (2002) were obtained as part of the present study; the extensive use of these data and descriptions given in that paper may be considered as preliminary to those of Paper I and the present paper. >p.16, W3-14: Note that your inability to model a star does not >necessarily indicate that it is a binary (witness Brey 58 above, and >AV469 that you failed to model in Paper I yet Evans et al. 2004 had no >problem). Of course, at the distance of the Mag Clouds many binaries >will be present, yet one does not *automatically* follow from the >other. Since the modeling process involves reproducing not just line RATIOS but also line STRENGTHS, it is hard to have a composite spectrum and successfully model it as a single star. As Kudritzki has often noted, binarity usually has an effect on the observed spectrum when examined carefully. (Perhaps the referee will recall the insightful description of HDE 228766 by Walborn 1973; his realization that this star was a binary based upon very subtle spectral signatures led to Massey's first paper as a graduate student giving an orbit solution for this star.) Radial velocity studies by Morrell and collaborators are underway currently for the stars we identify from our modeling as composite, and so time will tell. In the case of AV 469, we could have declared success as well, but were bothered both by the small emission bump we observed on the Halpha profile, which the models did not predict; in addition, there was a shift of the synthetic HeII 4686 shift to the blue that we did not observe, as described in detail in Paper I. Possibly we were being too fussy and careful! But, the fits were worse than what we typically obtained. Evans et al were apparently better satisfied with their fits than we were with ours. >p.16 LH101 W3-19 - the NIV/NIII ratio indicates O3 If not O2 If Perhaps. The difficulty again comes to the fact that there are no quantitative criteria in Walborn et al. (2002) where the new O2 If spectral class is defined. What is the difference between "NIV >> NIII" and "NIV > NIII"? 10%? 100%?? 300%??? And, should we rely solely on the EWs, or should we also use the peak intensity? Again, see our point above that if the stated criteria are not good enough to allow even a co-author to classify a star, how well described is the scheme? Since the only "representative" star listed for the O2 If* class is HD93129A, now a known composite spectrum, we did the best we could. But, if the NIV/NIII ratio really does indicate an O3 If type, rather than O2 If, then what do we make of the CIV 4658 emission? Although Walborn et al.\ (2002) does not explicitly LIST this as a spectral criterion, the presence of this line is used in that paper to distinguish "particularly hot" O2 stars. Again we emphasize that if the star WERE classified as an O3 If rather than an O2 If, it would have NO EFFECT on the derived effective temperature scale OR on our evaluation of the NIII/NIV as a temperature indicator. >p.17, first line: "made checked" FIXED. >p.18 R136-007 (alias Mk39) - "arbitrary and unnecessary division" >between Of and Of/WN - to reiterate, you favour dispensing with the /WN >nomentclature, yet Mk39, Sk-67 22 are much closer in appearance to >HD93162 (WN6ha) than HD93129A (O2If), so the existing nomenclature >seems reasonable (followed by Walborn & Blades, Massey & Hunter). As a >further argument, since EW(4686)=-7A yet the system might be multiple, >so the emission line star might well have EW(4686)=-10A or so, right at >the boundary between WN and OIf (hence not really so "well short" of >the boundary). The referee reiterates the fact that our opinions differ on the issue of the slash nomenclature. We agree. However, since the spectral type of this star is composite (the star is a light variable, and recent Las Campanas data has established both the period and delta m), it is moot. We have added a sentence noting this recent result. >p.20 - End of Sect 3.2.1, you ought to include Crowther et al., Heap et >al. (astro-ph) here who have attempted what you suggest, namely fitting >the UV *and* optical. We have added the Heap et al. (2005) study; however, a careful reading of the Crowther et al. (2002, ApJ, 579, 774) study reveals that they did NOT fit the UV and the optical. Instead, they fit the optical, and then compared the synthetic model spectrum to the UV to see if there was general agreement or not: no actual fitting in the UV was done. The referee is referred in particular to Section 4.3.2 of Crowther et al. What we have planned is more comprehensive than that. >p.20, Sect 3.2.2, Your "consistent fits" are demonstrated only for HeII >3203, and not for HeI 3187 - the latter is too weak to see in all cases >presented. Fits to non-neglibible HeII and HeI would be needed to >really add "reassurance". We believe that the referee overlooks the fact that the HeII line strengths vary with the physical parameters of the star; i.e., it is NOT just the HeI/HeII ratios that the models predict, but the absolute line strengths of each line. Since the HeII 3203 line comes from a different level than the lines in the blue/optical, this is additionally reassuring. As we say in the text, "None of the stars were sufficiently late for HeI 3187 to be detected at our S/N, consistent with the output of the stellar atmosphere models. Since HeI 4471 and, in some cases, even He~I 4387 is measurable in all of these stars (with the possible exception of LH101:W3-19; see Sec 3.1), we note that while the NUV region provides reassurance on our fitting procedure, the additional information added is limited." >p.21 Replace "staring at" (used pejoratively) with "visual inspection >of" The phrase may have been used whimsically, but not pejoratively; the first author, anyway, spent much of his graduate days "staring at photographic plates" (at least, prior to his measuring them on a microdensitometer). We have, however, reworded the sentence. >p.23 Refer to discussion of NIII/NIV vs HeI/HeII above. To reiterate, >your criticism of a scheme in which not all stars of the same spectral >type/luminosity class do not share identical properties is >unwarranted. The spectral type is morphological in nature, such that >e.g. O2III stars share certain characteristics. Certainly, winds do >play a role, especially in stronger lined systems such as WN stars in >which stars of identical ionization (e.g. WN6) may have quite different >temperatures based on the strengths of their winds (strong wind - high >temperature; weak wind - low temperature). Such an effect does not >discredit the spectral type scheme, since only ionization claims to be >in common. The issue is whether or not O2 stars are, on the average, hotter than O3 stars within a given luminosity class. We find that the situation is more complicated than that, and that a full-blown analysis is needed to derive physical parameters. Even the HeI/HeII ratio suffers from a log g effect at these high temperatures, as we demonstrate. See discussion above. >p.23 It is implied that "wind criteria" are not reliable logg/L >diagnostics, but the selective emission lines are NOT >primarily/entirely wind features (ditto p.27). We have reworded the phrase to make it "more exact". >p.23 You make the sensible statement that careful modeling of NIII/NIV >will provide useful diagnostics (following Taresch et al. AND Heap et >al.) but your reliance on HeI/HeII severely hinders your conclusions. Including NIII and NIV in the FASTWIND models is a high priority; however, what we can do for now is derive physical parameters from the HeI, HeII, and Balmer lines, and then compare THOSE effective temperatures to the measured NIII/NIV ratios. The referee feels that our reliance on HeI/HeII "severely hinders" our conclusions, but we disagree. Still, we make it clear in the text that there is room for improvements, which we plan. >p.24 - Sect 5, the 7 stars you failed to fit were either composite, had stronger WN signatures or you may have just been unable to fit the data >(recall AV469 in Evans et al. vs Massey et al.) Yes, it's possible in some cases that we were were just too darn careful and fussy, but since our goal was to derive an effective temperature scale, this seemed to us to be a better approach. We have added a footnote to the statement noting that Evans et al (2004) succeeded where we had failed. >p.24, second para - in parenthesis you comment on potentially much >higher errors on dM/dt should your assumption of a common beta law be >invalid - how much larger if 0.7 < beta < 2? Isn't this one difference >insufficiently highlighted with respect to Repolust et al. who derived >beta for some stars? In general, beta can be fit if Halpha is in emission, and then the determinations are typically 20%. When Halpha is in absorption (which is true for most of the stars in our sample), beta values between 0.7 and 1.3 are reasonable. Values of 1.5 through 2 would have a large impact on the fits, and one could see it from central emission features if v sin i is not too large. This range (beta=0.7 to 1.3) is also the maximum range of O star betas (irrespective of luminosity class) which have been found so far, consistent with theoretical expectations. The typical uncertainties introduced by this are 20-30%, although they could be larger in some instances. We have now added a footnote explicitly describing this. As we say in the text, we began with a beta=0.8 and varied it only if we felt we had to. We were satisfied with our fits with beta=0.8 for all of our stars, except for Br58, where a very large beta seemed indicated, but where we were unsatisfied with our fits. Since a beta=0.8 was found for nearly all the stars by Repolust et al., we do not see what difference needs to be "highlighted". >p.25 - Don't Maeder & Meynet (2001) show all SMC metallicity tracks >with Vrot(initial)=300 km/s? Yes, there are SMC metallicity tracks available with Vrot=300 km/s, but not for other low metallicities (i.e, LMC-like). In addition, they do not yet have a set for non-rotating tracks available with the new opacities. We had searched for both of these on their Web site as we prepared the paper, and when we were unable to find them, corresponded directly with Georges Meynet, who said they were still working on these. >p.25 Sect 5.1 - you should be more cautious in your claims - recall >above discussion. Comparing early Of supergiants in the LMC and Milky >Way, Repolust et al. (2004) find that zeta Pup (O4If) has an identical >temperature to HDE269698 (O4If) in Crowther et al. (2002). At late O >supergiants, there are more examples in the literature with which you >can make comparisons (e.g. Evans et al 2004). We now include Evans et al (2004) in our comparisons. In making our effective temperature scale, and describing our conclusions, we have both averaged and smoothed, as is typically done (Conti 1973, 1987). This is only proper, as the Teff determination for any one star has some error associated it. >p.27 in para 3, The ranges of mass and luminosities of O2-3 stars was >amply discussed by Walborn et al. (2002) and are not newly recognised >here. The masses and luminosities in Walborn (2002) were very approximately computed by his co-author Massey, who was forced to make several gross assumptions, including one of a single temperature (50000) and correspondingly a single bolometric correction. Such estimates should not be confused with the values derived from the modeling here. >p.27/28, You quote the disagrement between CMFGEN studies of Crowther >and Hillier for two O7 Iaf+ stars as AV232 (39kK) and AV83 (32.8kK), >respectively. However, the former derivation was actually 32kK, so >there is no inconsistency within the errors for these two - almost >certainly on the low side due to the extreme nature of their winds >(recall both were Ia+) versus normal supergiants. This was our error; we misread Table 6 in Crowther et al, in which both values are cited as CMFGEN but one is actually from Puls' et al work. We have corrected the text and the figures. We do however stand by our point, though, that some of the CMFGEN data agrees with our now scale (Crowther et al's analysis of the O9.7 I star Sk-66 169), while other do not (Evans et al's study of the O9.7 I star HD 269896). >p.29 - You are critical of the study by Bouret et al., yet FASTWIND >compares well with CMFGEN for studies in common, and they combined high >quality UV and optical observations of their targets (supported by Heap >et al.). It appears inappropriate to favour a generic Teff scale for O >stars (of queestionable significance given your problems for SMC O3-5V >stars as discussed earlier) than one specificially derived from >observations. In fairness to Bouret et al., 3 of their sample were >derived to have an age of 3Myr (in accord with Mssey et al 1989 based >on an old Teff scale independent of metallicity!). MPG 355 and 487 >differed (though were commented on specifically by Bouret et al.), >suggesting an age spread of 4Myr (1-5Myr) not 5Myr, whilst the Walborn >et al. result for MPG 12 not being coeval *was* discussed by Bouret et >al. First, let us again emphasize that both Bouret et al and Heap et al relied upon the same optical data for their "independent" analyses of these stars, and that these data were not sky (nebular) subtracted. See our remarks above about the possible effects not only of nebular contamination, but the effect that moonlight contamination might make on the absorption line strengths in the stars. But, even if their data wasn't suspect, it would still be an interesting test to see what effect applying our effective temperature scale would be to the NGC 346 stars. We find a much more coeval placement in the HRD, and the O2 III star is actually sitting where a giant should be, and not where one would expect a ZAMS star to be. Coincidence? Maybe! As we say in the text, this doesn't prove us right and Bouret et al wrong, but it does illustrate that changes in the effective temperature scale has broader implications for star-formation and evolutionary theory, a point which Hanson (2003) in particular has recently emphasized. The placement of the NGC 346 stars using the Bouret et al. analysis results in an age spread of 5 Myr as we say in the text; the referee is referred to our Fig. 30a, where the dashed lines indicate isochrones at 1 Myr intervals. (5.8 Myr - 0.8 Myr = 5 Myr, not 4 Myr). >p.31 - The correction for "clumpiness" is rather artificial. Repolust >et al. merely adopted this factor (for their Galactic stars with strong >winds) in order to find a common wind momentum for their sample, so it >does not physically correct for clumpiness. Further, one might question >a Galactic clumping factor for non-Galactic stars, especially given the >notorious uncertainties in distance (hence form of the wind momentum >fit) to Galactic O stars. Clumpiness is a controversial issue. The underlying assumption of Repolust et al [first explained by Puls et al 2003 at the Lanzarote conference] is that any kind of instability needs some time to grow, and thus the lower part of the wind should be barely affected by clumping. Thus, only those Halpha profiles should be affected which are formed in a major volume of the wind, i.e., the emission profiles. If Halpha is in absorption, this immediately suggests that the only wind contribution is from layers very close to the sonic point, and thus absorption type profiles should be little affected. The way the correction by Repolust et al has been performed then is somewhat arbitrary, as pointed out by the referee, in the sense that it adopts the hypothesis that radiatively driven wind theory is generally correct. If that is the case, then there should be no dependence of the WLR on luminosity class, and that was the way that the correction was determined for the Repolust et al. data. In the present paper, we present our mass-loss rates without the correction, but in describing the WLR, we show the results both without (Fig 32a) and with (Fig 32b) the correction. For the Magellanic Cloud data, the correction only applies to the few LMC supergiants with Halpha in emission, as shown in Table 9. Applying the Repolust et al. correction then greatly reduces the scatter for these stars. Coincidence again? Perhaps! We have added some additional text describing the basis for the clumpiness correction, and an informed reader can draw his/her own conclusions. >p.33 - last para of Sect 5.3, ON2 III FIXED >Conclusions - see major comments as for abstract. See our replies above. >Table 4 - compare your derived Vinf with previous studies (Prinja & >Crowther?) In Paper I we were able to compare our Vinf values to those of Prinja & Crowther 1998 and de Koter et al 1998. However, in the new sample there is no overlap; the data presented in Paper I had existing UV spectra, while the ones presented here are new, as we describe in the text. See Table 2: all of the UV spectra used in the current study were obtained as part GO-9412 with STIS. >Fig.6 - Your observations appears to comtain an emission feature >blueward of 4471. There is an apparent problem with the RV of H-alpha >(model blue shifted relative to obs.) We have carefully examined our data for this star. First, the "emission feature" at 4471 is below 10mA in EW, and hence is not significant; in this case, we believe it actually IS a normalization problem, caused by the adjacent 4430 IS feature, which is relatively strong. We have chosen not to re-normalize the data, as this would be purely cosmetic---we do not detect HeI in this star. Secondly, we have examined both the ground-based and HST data. We agree that there was a problem in the RV of the Halpha data resulting in a mis-match. We now use the HST data, which gives good agreement, and have modified the text accordingly. >Fig.12 - HeII 4200 problem "presumably" due to reduction - how so? The 4200 line is flat-bottomed; a number of glitches could have caused this problem. The line was ignored in the fit, as stated in the figure caption. >Fig.20 - R136-033 appears to show a P Cyg HeI 4471. The EW of this emission feature is 15mA; we would ourselves not call a line P Cygni with that weak an emission component. >Fig.26 - better to show M_bol range from -8 to -11.5 or so, since >nothing less luminous than Mbol -8 (ditto for Fig.30 where you >presumably mean Z=0.004 (1/5Solar) rather than Z=0.04 (2Solar) in >caption) We have changed the scale of Fig. 26 to make it agree with Fig 30; however, it is important to see what part of the HRD these data do NOT cover. We have corrected the typo in the figure caption. ********************************************************** We apologize for the length of our response, but we do want to make it clear to the referee that we have SERIOUSLY CONSIDERED his many concerns. We do disagree with the referee over a few of the spectral nomenclature issues, but we note that this discussion is peripheral to the science (i.e., Br58 being a O3If*/WN6 star vs a WN6 star, or whether a particular star should be called O2 I or O3 I), since our arguments are based upon the NIII/NIV ratios vs Teff and not upon the assignment of spectral types. We also disagree as to whether our detailed analysis of our sample of 40 stars is sufficient to draw any "firm" conclusions---others seem happy to do this with two or three stars in their sample! We do realize that the referee spent considerable time and effort in preparing an exceptionally detailed report, which includes constructive remarks, and we feel that the revised paper is the better for this.