Dear Paula,

Thanks very much for your prompt forwarding of the Nolan Walborn's
report on our paper "The Physical Properties and Effective Temperature
Scale of O-Type Stars as a Function of Metallicity. I. A Sample of 20
Stars in the Magellanic Clouds" ( MS# 59729).  I'll note that at the
time we submitted the paper, I also provided Nolan with a private copy
along with a note saying that while I knew that he would disagree with
many things about the paper, I wanted his comments nonetheless.   We
appreciate his positive report and constructive suggestions. In light
of the "philosophical and methodological differences", we also
appreciate his efforts to distinguish between differences of opinion
and what he considers to be errors. In a few cases we believe that he
has misunderstood the expected effects of mass loss on the atmospheres
of hot stars, as noted below.  Nevertheless, the paper has clearly been
improved as a result of his careful and thoughtful criticism.  We have
attempted to fully take his concerns into account, although as he
expected there were issues of "opinion" on which we will have to agree
to disagree.  Hopefully these will not necessitate a second round, as
they were labeled advisory.  We have detailed our changes and responses
below.  We are resubmitting the paper now in the hopes that it is
acceptable for publication in the ApJ.

We would much prefer for the paper to appear in the main journal,
despite it being a couple of pages over the 25-page limit you mention.
(I confess I had been unaware of this page limit. Is this something
new?) It is true that we have considered a larger sample of stars than
is typical for such studies, and this has required the paper to be a
bit longer.  However, as the referee notes, the paper presents
extensive analysis and discussion, and we fear that this might be lost
were it to be put in the supplement series.  The paper is by no means a
"data paper".  The conclusions about the effective temperature scale of
low-metallicity O stars is important to workers in a number of fields,
and we feel that this merits inclusion in the main journal.  Thanks for
your consideration.

Here are our specific responses to the referee.


> This paper is an important, new contribution to its field, presenting combined 
> optical and UV spectroscopic analyses of a sample of OB stars in the Magellanic 
> Clouds, most or all of them for the first time, with state-of-the-art 
> models.  It should be published in ApJ, following consideration of a number 
> of comments below.  It might be appropriate for the Supplement Series in view 
> of the large number of figures, but it also presents extensive analysis and 
> discussion, so I leave that to the discretion of the authors and editors.  
> Anonymity of the referee is neither required nor feasible in this case.  
> The first author and I have a well-established history of philosophical and
> methodological differences regarding the interpretation of early-type
> spectra (which has not prevented some fruitful collaborations, however),
> so I shall endeavor to distinguish between comments that I believe to
> refer to mistakes or misstatements of fact, which should be corrected,
> and those which are matters of opinion or interpretation, on which my
> comments are advisory.  I have also marked a fairly large number of
> typographical and minor grammatical errors in the manuscript, which are
> too numerous to list, so the marked copy is being sent to the first
> author. 
>

We have made most of the corrections indicated on the marked pages.  We
appreciate the thoroughness and effort of the referee. In a few cases
we disagreed with the changes (i.e., "majority of the data" does
require a single verb, we think, as "majority" is the subject), but
we'll leave any disputes to the very competent University of Chicago
Press copy editors.

> 1. Since UV data are available for the majority of the stars and were
> essential to the analysis, I'm disappointed not to see any of them
> displayed.  My preference would be to include the UV observation for each
> star, but at least one figure showing examples of the terminal-velocity 
> determinations should be added.
>

We do not believe much is to be gained by including all of the UV
spectra in this paper, as we use the data only for the determination of
the terminal velocities.  We have added a figure (Fig. 4) to provide an
example of the terminal velocity determinations; the figure is
described at the end of Section 3.1.


> 2. In the abstract and throughout the paper (e.g., p. 16), it is stated that 
> He II emission is due to the stellar wind, and that since the winds are 
> weaker in the MCs, the He II will also be weaker, especially in the SMC.
> However, no references are provided for the first part of the statement
> (should be Klein & Castor 1978, ApJ, 220, 902 and Gabler et al. 1989, I
> believe; the latter is listed in the very nice general introduction, but both 
> should be given at least for the first appearance of this specific statement
> in the text); and no systematic morphological or physical demonstration
> of the second part of the statement is offered (in contrast to the
> complaints about a lack of physical underpinning for the O2 spectral
> type!).  In fact, none could be, because the statement is incorrect: 
> He II 4686 and 1640 are STRONGER in SMC Of stars (see Sk 80 = AV 232 in
> PASP 107, 104, 1995, and AV 83 in Walborn et al. 2000), and 4686 is
> stronger in LMC WN stars (Lindsey Smith, IAU Symp. 143, p. 608 and references 
> there, including Conti & Massey 1989), than in Galactic counterparts.  The 
> reason may be that the lower metallicity winds, although weaker, are HOTTER.  
> So that statement should be omitted, or at least qualified with these 
> counterexamples.
> 

We have added references to Klein & Castor and Gabler et al to support
the first part of the statement.  We do not agree that the second part
of the statement is demonstrably incorrect, but we do agree that the
matter is considerably more complex than what we originally stated.
The question is not whether there are SMC stars with strong HeII 4686
emission---we know there are, and Nolan cites two examples---but the
question is whether these stars have HeII emission that are stronger
than Galactic stars of the same bolometric luminosity and effective
temperature.  Such a comparison requires detailed modeling of a larger
sample of stars (both Galactic and SMC) to determine the physical
parameters. From a theory point of view, we agree with Nolan that the
issue is unclear at this time, and in fact a more detailed
consideration of the issue suggests we could make a good case for
either stronger or weaker emission in the SMC for stars of the same
spectral subtype. We simply do not understand the physics of the
formation of HeII 4686 in the same way that we understand (say) the
formation of Halpha.  The formation of Halpha will be largely
unaffected by blocking in the EUV, while HeII 4686 may be strongly
affected, due to the importance of the HeII 303 resonance line in the
formation of the 4686 line. We have modified our statements in the text
accordingly, both in the abstract and in paragraph 2 of Section 3.3.
We thank Nolan for helping us avoid any overstatement of what theory
shows.

We have added a reminder about Sk 80 and AV 83 (crediting Nolan) in the
second paragraph of Section 5.  We do, however, believe this may
SUPPORT our point that the f characteristics do not necessarily scale
with luminosity in the same way in SMC than in the Milky Way.  Perhaps
at lower metallicities there are examples both where the emission is
weaker or stronger depending upon the which of the many effects in the
formation of this line "win" under different physical conditions.
Further work will tell.


> 3. The last sentence of the abstract (further developed in Section 5) has
> so many grammatical issues that I'm uncertain of its meaning.  A possible
> grammatical rendition would be
> 
> "This temperature increase is presumably caused by the decreased
> importance of wind emission, wind blanketing, and metal-line blanketing
> at lower metallicities."
> 

There is no temperature "increase"---instead, the lessened importance
of blocking at lower metallicity means that there is LESS of a
DECREASE, as we had intended to make clear in our original sentence. We
have re-written it to make our meaning clearer. Perhaps this has
contributed  to the confusion that the referee seems to have over the
expected effects of mass-loss on the effective temperature scale.  What
we are saying is that the temperature decrease caused by including
wind- and line-blanketing is not as significant at lower metallicities
as they are at higher metallicities.  This does go the opposite as the
referee seems to expect:

> However, I believe that statement contains several conceptual errors.
> First, if wind blanketing heats the atmosphere, decreased importance
> would make the MC stars COOLER, not hotter as observed.  Moreover, the
> wind emission effect is only apparent (caused by emission filling in the
> He I lines) and should presumably be appropriately corrected at any
> metallicity by the unified models; and wind blanketing affects both the He 
> ionization ratio and Teff in the same sense, not the relation between them.  
> Only line blanketing affects the latter relation, because of flux 
> redistribution among different spectral regions, and would be relevant to 
> this (speculative) statement in the correct sense.  (I am not a modeling
> practitioner, and it is not out of the question that I could be missing
> something here, but I don't think so, so I urge the first author to
> seriously consider these points and discuss them with his coauthors, to
> prevent publication of incorrect statements in ApJ.)
> 

We appreciate your confusion on this topic, but all co-authors agree
that the sense is correct in our paper.  I will address the three
effects here, although in fact most of this simply parallels what is
already in the text (Section 1).

(a) Wind-blanketing. Refer to Table 1 of Abbott & Hummer (1985, ApJ,
294, 286).  There one will see the expected effects on the HeI/HeII
ratio (i.e., the spectral type) of mass-loss.  The log g=3.5 42,000
degree stellar atmosphere with NO mass-loss results in a log W'=-0.34,
and hence a spectral type of O5.5  Adding mass-loss decreases the
HeI/HeII ratio, resulting in a star of earlier spectral type.  In the
extreme (M-dot=1.5x10-5 Mo/yr) we see that the spectral type would be
O3 rather than O5.5.  This is equivalent to saying that for two stars
of the same spectra type but different mass-loss rates that the star
with the higher mass-loss rate will have a cooler Teff, all other
things being equal. So, our statement that at lower metallicity (and
hence a lower mass-loss rate) a star of a given spectral type will be
hotter is correct.  We already discuss this explicitly in item 2 of the
Introduction ("The introduction of mass-loss"...)

I believe the source of the referee's confusion is the common use of
the phrase ``back-warming effect".  What is happening physically is
that the stellar wind is backscattering radiation into the photosphere,
warming it, and thus producing a smaller HeI/HeII ratio. The result is
that to produce the SAME HeI/HeII ratio requires a COOLER effective
temperature that would be the case if this effect weren't present. See
for instance Voels et al. (1989, ApJ, 340, 1073) where they find that
the effective temperature of a wind-blanketed model that fits Alpha Cam
is 2000 deg cooler than that of a model that neglects the effect of
wind blanketing.

(b) Wind emission.  The presence of mass loss results in some filling
in of the HeI lines by emission produced in the stellar wind, as
described in Sellmaier et al. (1993).  So, again consider two stars of
the same Teff.  The star with the stronger stellar wind will have less
HeI compared to HeII, and hence will be classified as an earlier type
star.  Thus for two stars of the same spectral type but different
mass-loss rates, the star with the stronger stellar wind will have a
cooler effective temperature.  This is in the same sense as (1), and we
would thus expect stars in the lower metallicity SMC to be somewhat
hotter than their Galactic counterparts, just as we state.  This is
already described explicitly in item 3 of the Introduction ("The
inclusion of hydrodynamics and metals"...)

(c) Metal line blanketing.  The inclusion of metal line blanketing has
been shown to lower the effective temperatures; see Martins, Schaerer,
& Hillier (2002, A&A, 382, 999) among the other references we provide
in the text.  Again, this goes in the same sense.  As to why, let me
also refer you to the detailed discussion in Repolust, Puls, & Herrero
(2004, A&A, 415, 349;  Puls says he has also sent you a copy), which
includes all the above topics and includes also a discussion of the
importance of the change in gravity which has to go along with the
reduction of temperature, an effect which is usually forgotten.

In summary, then, all three of these effects go in the same sense, and
in the way we say in the text. We have not modified the text.


> 4. A general criticism of the paper, related to the previous two, is that
> while most relevant recent references are cited in the nice introduction,
> their results are virtually ignored in the remainder of the paper, which
> focuses almost exclusively on these particular 20 stars and the present
> analysis, to the detriment of the discussion at several points.  As
> additional examples, Crowther et al. 2002, Hillier et al. 2003, and
> Bouret et al. 2003 all derive lower Teff's from line-blanketed analyses of 
> MC stars; are their results incompatible with the present ones?   From
> similar analyses, Repolust et al. 2004 and Herrero (IAU Symp. 212 and
> references there) conclude that the mass discrepancy between
> spectroscopic and evolutionary determinations has been nearly resolved,
> in contrast to the huge discrepancies in Table 4 here; e.g., the first
> author determined 72 Mo for LH64-16 in Walborn et al. 2002, but 26 Mo
> here!  The same issue applies to the discussions of individual stars, in
> which global inferences about MC spectra are made from one or two cases,
> while published observations of other similar stars that disagree with
> those inferences are ignored; specific examples will be noted below.  It
> is not reasonable to expect that all these issues can be resolved in this
> paper, but they should at least be mentioned.
> 

Our original intent was to defer a comparison with others until we had
the second sample of stars analyzed in the next paper.  However, in
fairness to all we now include these data in our Figure 26 and
explicitly discuss the comparison in paragraph 7 of Section 5.  In
point of fact, there have simply not been enough stars analyzed with
CMFGEN to see if there is agreement or not.

As for the mass of LH64-16, the "spectroscopic" mass simply comes about
from Newton's second law; i.e., g/go = (M/Mo)/(R/Ro)^2.   Walborn et
al. (2004) models my spectrum of the star using CMFGEN and assuming a
similar gravity (log g=4.0 rather than our fit 3.9).  Since their
derived effective temperature is nearly the same (55K vs 54.5K), and
their bolometric luminosity is the same (log L = 5.90 vs 5.89) I would
have to guess that the stellar radii are similar as well, although
Walborn et al (2004) do not actually quote a value.  But this would
suggest that that the mass implied by Walborn et al.  (2004)'s modeling
must be about the same as ours.  So, really the question must be why is
the mass given by Walborn et al (2002a) so different?  Walborn et al
(2004) do not address this point either, possibly because they do not
quote a mass, and did not themselves realize there was a discrepency.

But let me offer an opinion.  I think that the relatively low mass of
LH64-16 derived from the spectrum is correct, and that it is telling us
something very significant about the evolution of this star.  We derive
a He/H number ratio of 1, and although Walborn et al (2004) do not find
quite as large a value, they do find evidence that the star shows
highly processed material at the surface.  In Paper II of our series we
are going to do a detailed comparison for the entire sample of stars
between the spectroscopic mass and the "evolutionary" mass. I believe
that we will find LH64-16 will stand out as discrepant there, and that
this may not support Walborn et al's (2004) theory that this star is an
example of "chemically homogeneous" evolution.  The assumptions that
went in my calculation of the evolutionary mass for the Walborn et al
(2002a) paper were clearly stated at the time (at least in email), and
included the assumption that this star was in this part of the H-R
diagram for the first time.  If instead LH64-64 is a highly evolved
object---as the surface composition would seem to suggest---then this
assumption would be wrong.

In other words, I don't think that this star resurrects the so-called
"mass discrepancy".  I think the discrepancy between the current mass
estimates (ours, and that **implied** by Walborn et al 2004) with that
from the simple evolutionary considerations of Walborn et al 2002a
reveals something quite interesting about the star's evolutionary
status.  I've long argued to the referee that this star may be the
result of some sort of binary evolution, or that the star is visiting
this region of the H-R diagram for the second time.  Our mass estimates
would be consistent with either interpretation.

We do agree with the referee that we shouldn't totally ignore this
point in the present paper.  Although we will do the detailed
comparison between the evolutionary masses and spectroscopic masses in
Paper II, we have added two sentences to our discussion of LH64-16
pointing out the contradition with Walborn et al (2002a) and offering
our own interpretation.  Perhaps Nolan will want to offer his own
interpretation for the discrepancy in Walborn et al (2004).

> 5. In the first paragraph of the Introduction, mention that observations
> below the Lyman limit are prevented by ISM absorption, for the benefit of
> nonspecialists.
> 

DONE.


> 6. In the first paragraph of Section 2, say "...steepness OF THE VELOCITY
> LAW of the stellar wind...
> 

DONE.


> 7. The notation for the names of the LMC LH association stars should be
> made consistent--three different versions are given, e.g., pp. 8 vs. 9
> vs. 15, one of which is called "unwise" in footnote 8!
>

We believe you are referring to footnote 10, where we eschew the HYBRID
terminology "LH64-W8".  If the Westerlund (1961) notation is used, it
really has to be W16-8.  We have tried to be consistent thoughout the
text: the first form of the name given in Table 1 is what we use both
in the text, tables, and figures, with the cross-reference provided in
Table 1. I could find only one instance where we goofed (referring to
LH64-W8 rather than LH64-16), and I have corrected this.  What we have
done is used the Lucke (1972) designation if it exists, and the
Westerlund (1961) notation if it does not.  Neither LH81:W28-5 nor
LH101:W3-24 were cataloged in Lucke's thesis, and therefore we have
used the Westerlund notation.   We do include the Lucke-Hodge OB
association number, as not many are familiar with where Westerlund
field 28 or field 3 are.  We do not see any inconsistency in this.

The alternative approach would be to use the Westerlund designation for
all three stars.  However, many are familiar with the star "LH64-16"
(from Massey et al 2000 and Walborn et al. 2002a), and we believe that
now referring to this star as W16-8 would create confusion.

I will note that both the Westerlund numbers and the LH numbers appear
in SIMBAD (i.e., "[LH72] LH64-16" is cross referenced as "W61 16-8"),
and that both W28-5 and W3-24 appear as well.  So, we fail to
understand that the problem that the referee has with this.  It is only
the hybrid form, LH64-W8, which does not appear in SIMBAD, and we do
not use this form.  


> 8. Re footnote 4, at the recent CNO Workshop (ASP Conf Ser 304), I was
> surprised to learn that the pundits no longer believe that the solar
> neighborhood CNO abundances are lower than solar; the problem was with
> the solar abundances, which have now been revised downward!  See paper by
> Asplund, p. 275.
> 

We have added a reference in the footnote 6.


> 9. At the bottom of p. 14, clarify that R136-024 is one of the three
> stars for which no adequate fit could be achieved.
> 

DONE.


> 10. I believe that in the equation on p. 16, the sign of the exponent on
> Z is incorrect, since it implies that the mass-loss rate varies inversely
> with the metallicity, contrary to what is implied throughout.
>

The referee is correct that there was a typo in this equation.
However, the equation has now been eliminated as part of the rewrite of
paragraph 2 of Section 3.3 as per item (2) above.


> 11. In the last paragraph of Section 3.3, the adoption of Mv as a
> spectral-classification criterion is indeed abhorrent!  Have you ever
> heard of the Mt. Wilson system of spectral classification?  I didn't
> think so!  In this system, developed by Joy circa 1930's, the spectral
> type was determined from line ratios, but the luminosity class was
> assigned on the basis of Mv determined from cluster moduli.
> Subsequently, the latter turned out to have large random and systematic
> errors, so the spectral types became useless and were forgotten.  In
> contrast, MK spectral types retain their validity in the face of
> calibration revisions.  Why repeat an error from the 1930's?  On p. 14, a
> 35% spectroscopic-binary incidence is cited to excuse fitting problems,
> but it appears to have been forgotten here.  Even worse, the issue of the
> linear spatial scale at the MCs is not mentioned in either context, and it 
> should be.  At the LMC, 0.1 arcsec subtends 5000 AU, plenty of room for 
> entire Trapezium systems with no detectable radial-velocity variations.
> Such systems must exist and are likely relevant in some specific cases
> discussed below.  This is a point on which I cannot insist that the
> approach be changed, but it is ill-advised and I strongly recommend that
> it be!  These multiple systems will eventually be resolved, perhaps
> sooner than you think...
> 

The referee is certainly one of the world's greatest experts on
spectral classification of early-type stars, and has spent far more
time than ourselves in considering the "right" way to do things.
Nevertheless, to us, ideally, one would like spectral classification
and luminosity criteria that identify physically similar objects in a
variety of environments, i.e., that are fairly independent of whether a
star is located in our own Milky Way, the Magellanic Clouds, or in the
Andromeda Galaxy, regions that span nearly a dex in metallicity.  Conti
originally proposed using the relative strength of SiIV to HeI as the
primary luminosity indicator in O-type stars; this eventually gave way
to the use of the "f" characteristics (NIII 4634, 42 emission and HeII
emission) to define the luminosity class.  Unfortunately neither of
these are expected to be independent of metallicity.  In this paper we
call attention to two issues that have not received the attention they
deserve:  first, that the formation mechanism of NIII and HeII 4686
emission are DIFFERENT and therefore from a theoretical point of view
should not be expected to track the same way as they do in Galactic
stars, and two, that there MAY be systematic differences in the
emission-line properties with stellar luminosity.  To us then, it can
only make sense to also consider other factors such as the absolute
visual magnitude.  As described above (2), we have softened our
statements on this topic given that we lack confidence in our ability
to predict the behavior of HeII 4686.  (The converse of this is that
there is no theoretical support for the contention that the behavior
will scale the same with luminosity in the low metallicity SMC.) We
note three cases in this paper (and additional ones in the second paper
of this series) where the SMC stars show "f" characteristics that do
not appear to be consistent with the absolute visual luminosity of the
stars.  I think it would be irresponsible not to point these out, given
the lack of theoretical support for the commonly accepted scheme so
loyally defended by the referee.  The referee apparently wants to
disregard all of these, arguing that they are binaries or multiple
system. We might then be faced with the very interesting result that
the incidence of multiple systems in the SMC is much greater than in
the LMC, as **we do not see this sort of discrepancy in the LMC stars
in our sample**.  In the absence of radial velocity variations or high
spatial imaging data to support the referee's contention, we will for
now keep with the answer to us that appears to be simpler, and not
unexpected from a theoretical point of view.

We also are curious why this binary argument goes only one way.
Couldn't Sk80 and AV 83 have enhanced HeII 4686 emission due to
wind/wind interactions in close binary systems? I'm unaware of any
radial velocity studies of these stars, and because of that would be
reluctant to just blithely invoke a binary explanation.

We further note that we are the first group to graciously admit defeat
in modeling some of the stars---in some cases no good fit could be
achieved, and in general these stars show some other evidence of being
binaries (such as eclipses!).  We do not see a similar problem with
the stars that show inconsistent "f" characteristics.  The reader may draw
his/her own conclusions.

For now, we have added a few sentences at the end of Section 3.3 to
explicitly remind the reader of the possible effects of binarity and
the spatial scale of the MCs in this case. We have also added a
paragraph (2) to Section 5 restating our concerns about the "f"
characteristics.


> 12. Individual Stars
> 
> AV 26: The discussion is "fair", even explicitly acknowledging my
> previous private communication, but I'm confident that it is wrong.
> Despite arguments to the contrary, the spectrum could easily be and is
> most likely a composite of something like HD 64568 or LH10-3058 (Walborn
> et al. 2002) and AV 15 (Walborn et al. 2000) or Sk -66 100 (PASP 107, 104).
> Weak N V absorption as in the former pair is consistent with the noise
> level here plus dilution by the continuum from the other star.  I
> challenge you to produce a model spectrum of a single star that contains 
> N IV emission and He I 4387 absorption with the strengths observed here!  
> Moreover, a multiple system explains the bright Mv simultaneously.  The
> inference from this single case that SMC mid-O supergiants have He II 4686
> in absorption is completely unjustified, given the other spectral anomalies
> and the existence of Sk 80 and AV 83, in which the emission is even
> stronger than in LMC and Galactic counterparts!  What does the UV
> spectrum of this star show?--not mentioned.  Again, I cannot insist that
> this discussion be changed, but it is ill-advised and I hope the above
> specific points will be seriously considered.
> 

We assure the referee that we have SERIOUSLY CONSIDERED his points, as
we did when he wrote an even more detailed argument several months
months ago, which we acknowledge in the paper.

(a) If we had a composite spectrum of an O3 V ((f*)) star [such as
HD64568 or LH10-3058] and and an O6-O6.5 II star [such as AV 15 or Sk
-66 100], it is HIGHLY UNLIKELY that we would have been able to fit the
HeI line strengths AND the HeII line strengths with a single model.
Remember that with this modeling exercise one is not trying to simply
match the HeI/HeII line ratios (in which a composite early and late
type O star can mimic the line ratios of an intermediate type), but
that one is attempting to achieve good fits to the HeI and HeII line
strengths (and profiles) simultaneously.  Thus modeling is a very
sensitive detector of composite spectra.  The fits shown for AV 26 are
excellent, with good agreement between all of the HeI and HeII lines
with a single model.  FASTWIND does not yet include the atomic physics
of the nitrogen atom, so we will have to defer the referee's challenge
to see whether NIV is in emission in such a model.

(b) Secondly, in such a composite the NIV 4058 emission would not be as
strong as seen in AV 26.  We measure an EW of -70 mA.  Although none of
the above cited Walborn papers contain any quantitative information on
the spectral features (such as equivalent width), we can measure the
strength of this line ourselves in the several O3V's in our program,
and none of them have NIV emission that is that strong by itself! So,
given the need to "dilute" NIV emission with a companion, either an O3
giant or supergiant is needed as a member of any putative pair.

(c) However, if the companion is an O3 giant or O3 supergiant, then the
referee's assertion that NV absorption would produce "weak N V
absorption...consistent with the noise level here plus dilution by the
continuum from the other star" is demonstratively FALSE.  Let us take
Pis24-17 as a typical case.  The absolute magnitudes of an O3 III and
O6 I are roughly equal, and so with a dilution effect of a factor of 2
we would expect such a line to have an EW of 200mA AT LEAST in our
spectrum.  The S/N of our spectrum of AV 26 is 350 per 1.2A spectral
resolution element, and we can place an upper limit on the strength of
any feature at NV 4603 of 12mA at the 3 sigma level.

(d) We note that the star AV 75 provides a very similar example of
strong HeII 4686 absorption coupled to a high luminosity.

So,  I am not inclined to accept the referee's argument.  If he
provides quantitative examples that he could make such a composite, we
would certainly reconsider this point. For now, we have added a
sentence to the text to further debunk the composite spectral type
argument along the lines given here.


> AV 372: Give numbers to substantiate statement that He I is broader than 
> He II--not at all apparent in the figure.  Classified in ApJS 141, 443,
> 2002 and FUSE spectrogram illustrated.

I'm not sure how numbers "substantiate" the statement, but we now
provide numbers.  Most readers, we hope, will assume that we have
examined the spectra more closely than they can do from eye from our
figures.  We have added a reference to the FUSE atlas by Walborn et al
(2002b).


> 
> AV 378: Definitely luminosity class III from the strength of He II 4686 
> absorption, and Mv agrees!  Criteria seem to be selected on an ad hoc
> basis...  The lack of stellar-wind lines also shows that it is not a
> supergiant, since SMC late-O supergiants have strong wind lines.  At the
> beginning of the discussion of the next star, the type of this one is in
> fact given as O9.5 III!  
> 

As the text clearly indicates, we were on the fence in classifying this
star as an O9.5 III or an O9.5 I.  We defer to Walborn's "III",
although to us the HeII 4686 absorption is more typical of a dwarf. The
value M_V=-5.5 is intermediate between III (-5.1) and I (-6.0).  We
find a log g = 3.25, which seems awfully low for a giant, doesn't it?
Perhaps this should carry the same weight in the spectral classification
as does the lack of a stellar wind?


> AV 396: The statement that the presence of He II at B0 is partly due to
> "some re-shuffling of the spectral standards by Walborn (1971a)"
> necessarily implies that that author moved some previous O9.5 standards
> to B0.  Can you give an example?  I don't think so.  Thus, that statement
> is incorrect and should be removed.
> 

We have removed the statement.


> AV 469: He II 4686 is NOT in emission in Galactic O8 Ib(f) spectra; see 
> HD 225160 in Fig. 7 of Walborn (1971a), as well as HD 192639, O7 Ib(f), in
> Plate II of AJ 78, 1067, 1973.  AV 469 was also classified in ApJS 141, 443.  
> Note typo in HD 151804.
> 

Let me take these three items in term. 

(a) First, is it surprising that  AV 469 shows  HeII in absorption?
The star has an Mv=-6.2, and a spectral type of O8.5I.  

We note that the "f" characteristics in AV 469 were so weak that Walborn
et al (2002a) actually called it an O8.5 II((f)).  The "((f))" of course
simply emphasizes the fact that HeII is in ABSORPTION rather than
filled in by emission ["(f)"] or in emission ["f"].  So, really this
disagreement could be recast as the fact that the luminosity of the
star is typical for a "I" (Mv=-6.2) but that the "f" characteristics are
more in keeping with a less luminous star.

Both HD 225160 (O8) and HD 192639 (O7) are of slightly earlier type,
and therefore may not be the best comparison.  In addition, HD 225160
is a field star and therefore lacks a reliable distance, and so there's
nothing more than a morphological basis for referring to its luminosity
class as a very precise "Ib".  HD 192639 is a member of Cyg OB1, and
has an M_v=-5.9 (Markova, Puls, et al. 2004, A&A 413, 693), about 0.3
mag fainter than our star.  Finally, in our opinion neither star has
HeII 4686 as strongly in absorption as seen in AV 469, as can be seen
even from the photographs published in the two above references.  Of
course, it is hard to do a quantitative comparison using reproductions
of these photographs, but the fact that Walborn refers to both of these
stars as "(f)" rather than "((f))" means he must feel that the HeII
4686 line is partially filled in by emission as well.  In contrast,
AV 469 had a HeII 4686 line is just slightly less than the neighboring
HeI 4713 line (our Fig 15a), and very similar to that of HeII 4200 and
4542, which led to Walborn's description of the star as "((f))"!
Walborn goes further than we go, as we feel that there is SOME filling
in of the 4686 line in AV 469, which is why we call it "(f)".

A better analog might be HD 17603.  This star has the same spectral
type (O8.5 If), and the identical absolute visual magnitude (M_V=-6.3),
and no detected absorption at HeII 4686 (see Tables 1 and 2 of Conti &
Alschuler 1971, ApJ 170, 325).  We note that the distance modulus for h
and Chi used by Conti & Alschuler (11.8) is in excellent agreement with
more modern studies (i.e., Slesnick, Hillenbrand, & Massey 2002, ApJ,
576, 880).

However, we do agree that our wording can be improved. Rather than
saying "in emission" we now say "filled in by emission", and cite HD
17603 as an analog.  We have also introduced qualifying statements when
we refer to this star as a potential problem; i.e., "However, below we
find several examples (AV 14, AV 26, AV 75, and possibly AV 469) where the
"f" characteristics are not consistent with the star's $M_V$ in the SMC..."
(Section 3.3).

b) We have added a reference to the Walborn et al. (2002b, ApJS 141,
443) paper.

c) We have corrected the typo.
 

> LH64-16: The thought experiment about two O stars of different
> temperatures but the same bolometric luminosity is rather eccentric.
> How could that come about?  A blackbody of higher temperature is
> brighter than one of lower temperature AT ALL WAVELENGTHS.  The only way
> a cooler star can be brighter than a hotter one at any wavelength 
> (neglecting blanketing effects) is if it has a LARGER RADIUS.  Thus, this
> discussion, although correct in principle, seems of dubious relevance.
> The authors may wish to reconsider it.
> 

There is nothing eccentric about two stars of the same luminosity
having different effective temperatures and hence different radii. In
fact, given that stars evolve primarily at the same bolometric
luminosity, with decreasing effective temperature, this thought
experiment could easily describe the same star at two slightly
different ages!  So, we disagree that this is any way irrelevant.
We've added a sentence to that effect:  "(Since stars evolve at fairly
constant $M_{\rm bol}$ this situation could apply simply to the same
star at two slightly different ages; the fainter, hotter star would be
the younger.)"


> LH81:W28-5: This star is classified (somewhat obscurely) in Table 3 of
> Walborn et al. 2002, in agreement with the present result.
> 

We have added this reference.


> R136-020: The fact that this star is not included in Walborn et al.
> (2002) is not "odd", since slash stars were explicitly excluded from that
> paper, as discussed.  There are several others in 30 Dor, as well as
> elsewhere.
> 

CORRECTED.


> R136-024: "...lack of He I" stated, but 4471 identified in the figure.
> 

CORRECTED.


> R136-040: Given the quality of the FOS data, the spectrum is quite
> consistent with the O3.5 V category illustrated in Walborn et al. (2002).
> 

The criteria listed in Table 3 of Walborn et al (2002a) are as follows:

O2V((f*)): NIV>NIII, no HeI
O3V((f*)): NIV>=NIII, weak HeI
O3.5V((f+)): NIV < NIII, weak HeI
O4V((f+)): No NIV, weak HeI.

So, given that we can detect neither NIV nor NIII, how would one go
about distinguishing the O3V and the O3.5 class?  Apparently the
referee can do this by eyeball on our spectrum, but I can not---given
that neither line is visible, how do you decide which is stronger?

Similarly, does the lack of He I mean that it's an O2? Or an O4?
Without some representative equivalent widths given for the different
spectral classes proposed by Walborn et al (2002a), one is [as we say
in the text] hard pressed to classify this spectrum by those criteria.
Afterall, the SNR of our FOS spectrum isn't that shabby: about 60 per
quarter-pixel, or 90 per 1.5A spectral resolution element.

We have modified our wording to hopefully make our meaning clearer.


> 13. In Section 5, surely the agreement of the line-blanketed Teff scale
> with the early results of Conti is a coincidence.  I don't think the
> statement is a cogent tribute to his pioneering efforts.
> 

Peter liked the sentence fine when we ran it by him.  But, several
readers have been unclear what we are implying by this statement. We
now explain that the Conti (1988) temperature scale is the preferred
one to use at the moment, rather than (say) that of Vacca et al (1996).
Hopefully work over the next few years will result in an improved
effective temperature scale with the effects of metallicity taken into
account. That will be the real tribute to his pioneering -- and
continuing! -- efforts.


> 14. In Table 1, why isn't the individual photometry of MH 1998 used for
> the R136 stars?
> 

As we say in the last sentence of Section 2.1, the Mv's for the R136
stars come from the photometry of Hunter et al (1997, AJ, 113, 1691).
The Mv's derived by Massey & Hunter (1998) were based upon the WFPC2
F336W, F555W, and F814W photometry of Hunter et al.  (1997, AJ, 113,
1691).  As Holtzman et al (1995) has emphasized, any reddening
corrections must be applied to the F336W, F555W, and F814W filters
BEFORE conversion to the standard U, V, I system, and the procedure was
described in Section 4.1.2 of Massey & Hunter.  So, the situation is a
little more complex than just throwing a few numbers into Table 1,
as I'm sure the referee realizes, having published his own de-reddened
WPFC2 photometry of LMC objects (Walborn et al. 1999, AJ, 118, 1684).

Perhaps the referee was confused by the fact that footnote "j" fell off
the bottom of Table 1. That footnote refereed to the fact that the
photometry for the R136 objects came from Hunter et al. (1997) rather
than Massey & Hunter (1998). We have reformatted the table to make
things easier to read.   We have also corrected the impression given by
footnote "e" to Table 1 that we have rederived the MV for the R136
stars here.   Instead, we say that the values for the R136 stars come
from Massey & Hunter (1998). Finally, we have corrected the reddening
values from the average values to those which we did use, and modified
the last sentence of Section 2.1 to take this into account.