Answers to comments by the reviewers. reviewer I - Bruno Bezard reviewer comment: The authors limit their analysis to 4 frequencies (4.86, 8.44, 14.94, 22.46 GHz) but indicate (p. 7) that "a much more complete data set including ... data from lower and higher frequencies is in hand and awaits full analysis." On the other hand, they commendably admit (p. 15) that their best fit model is probably not consistent with data at wavelengths longer than those analyzed here. So, it seems to me that a simultaneous analysis of all frequencies in hand would strengthen a lot the paper and bring more serious constraints on the atmospheric model. reply: There is no way to resolve (currently) the problem of fitting the long wavelength measurements. This is currently one of the outstanding problems/mysteries of Venus (and planetary?) radio science, and beyond the scope of this manuscript. We have reduced some ~1.4 GHz data and included that in the manuscript now. However, while more data has been taken at the VLA at many wavelengths, it is not all our own - it is either archival, in which case we must petition to obtain it (and in which case the data can be of dubious quality), or it is currently in the hands of other users. We should have been more careful about how we phrased that - by saying "in hand", we meant that the data had been taken, not that we had current access to it all. We hope that the full set of data taken at the VLA will become available in the near future, but cannot wait specifically for that to happen. In addition, there are still unresolved uncertainties about the flux density scale at higher frequencies, and until that situation improves there is little point in publishing new 43 GHz measurements. We have removed that sentence because it just serves to confuse the reader and a full explanation of the situation would require more space than it is worth. reviewer comment: Only an analysis of _disk-averaged brightness temperatures_ is presented while the VLA observations give access to spatially-resolved information. Because "the VLA does not measure total flux density well" (p. 11), the authors infer the disk-averaged brightness by extrapolating the measured _visibilities_ through a simple model. So my understanding is that they extract a parameter (disk-averaged brightness) not well constrained by their data while the strength of the VLA vs. single dish observations is not exploited. Again, the analysis of the brightness maps that can be derived from the VLA data is deferred to a subsequent publication. reply: We did not explain this very well at all, and thank the reviewer for pointing this out. We have fixed that section of the text to explain what is done more completely. The benefits of the VLA vs. single dish are implicitly exploited (confusion reduction, relative insensitivity to pointing errors, etc...), as they are in all interferometric observations. We didn't feel it necessary to explicitly point these out, and still do not. A final point - a distinction has to be made between long tracks which are amenable to imaging (like the K- and U-band data sets) and short tracks, which are not. I've explicitly pointed this out in the manuscript now. reviewer comment: The inferred disk-averaged temperatures are very consistent with those inferred from NRAO observations by Steffes et al. (1990). The error bars are a bit smaller, but the results presented here represent only a marginal improvement over those of Steffes et al., and I am not sure they would deserve publication by themselves. If the authors think so, they should have discussed their measurements against previous ones and show how they supersede them, which is not done in my opinion. reply: We think the observations described in this manuscript are significantly better than previous. The measurements are similar to those of Steffes et al., but use a single "telescope" (the VLA) and a single calibrator (3C286), and are interferometric, so are less liable to have systematic offset problems. The inclusion of the C-band and L-band data extends this to a wider frequency range than Steffes et al. Finally, the error bars in Steffes et al., when including the 5% quoted uncertainty in the flux density scale (p. 88 in that paper), are about 2-3 times what ours are. We have added a sentence to this effect. reviewer comment: Sophisticated radiative transfer models, taking into account the spatial inhomogeneity of Venus, are used to calculate disk brightness temperatures (Tb). It is not clear to me that such a complex model is superior to the usual homogeneous model (assuming that the surface and atmosphere do not vary with latitude/longitude) to analyze disk-averaged observations. A comparison of the two in terms of disk-averaged Tb is not given. Their elaborated model is _not_ used to infer disk brightness from the VLA data (p. 15), so I think there is some inconsistency in this procedure. Either the authors should use a simpler symmetric radiative model to derive the final Tb _and_ to model them. In this case, there is no need to describe their new radiative model in this paper. Or, they use their improved model to infer the observed Tb _and_ to model them. reply: The complex model is needed for the longer wavelength calculations. This is because there is a phase variation in the emission (tied to the surface emissivity features) which is significant relative to the uncertainty of the observations (at X-band, the phase variation is > 1% peak to peak). At the shortest wavelengths, the reviewer is right, a more simple model could be used. However, even at 15 GHz, the surface features are starting to show through (as shown in figure 2), and so we felt it better to just use the more complicated model at all of the frequencies. As to the inconsistencies in "models", we think we have clarified this in the revised manuscript. We have described more fully the fact that one "model" is just an idealistic one to allow for an analytical fit of the "data/measurement". That derivation (of V_o) is nearly independent of detailed model, because the measurements themselves (at short spacings, mostly) dominate the fit to the visibilities to find V_o. One could almost use any (well-behaved) function to fit the visibilities at short spacing to get V_o. Once we have an estimate of the total flux density (or brightness temperature, if you will), we then use the complete model to attempt to fit that by varying the atmospheric and surface/sub-surface parameters. reviewer comment: The authors provide an atmospheric model which fits their four data points. But they "merely adjusted parameters crudely ... to demonstrate that it could be done" (p. 15). The parameters of this model, such as the SO2 and H2SO4 abundance profiles, are indicated but there is no discussion of the error bars associated. The reader does not know how the authors can disentangle the opacities due to the two gases, how the assumed temperature lapse rate might affect their results... So the scientific content of this analysis is very poor. In particular, I do not understand how the authors can argue that their "inferred" SO2 abundance (at which level?) contradicts previous measurements (p.3, abstract) since no error bars are given. How does a spectrum calculated with 150 ppm of SO2 differ from one with 40 ppm? We don't know. reply: This is a good point, and that portion of the manuscript has been revised significantly, with additional material added in. The model has been run for a wider set of input parameters, and this is explained in much more detail. A representative set of models have been added into a table, with explanation. The proper reduced chi-square has been calculated and shown in a figure (and described), so the reader should be able to ascertain exactly how accurate the "fits" to the model inputs are. reviewer comment: I think that it might be best to have a single publication allowing the whole VLA data set, the radiative model used to analyze and model it, and the surface/atmospheric properties that can be reliably derived from the observations. reply: We prefer to keep the papers separate, since they really treat different problems to a degree. This manuscript treats more fully the observations at longer wavelength, which need a much better treatment of surface and subsurface emission, and (of course) only considers the disk-averaged brightness temperature. The "mapping paper" (Jenkins et al. 2001) treats in detail only the 22.46 and 14.94 GHz data, and specifically the brightness temperature maps that come from that data. There is a logical distinction between the two, and, again, we prefer to keep them separate. Other minor points: reviewer comment: p. 5: it should be "CO" instead of "CO2" in the list of gases "SO2, CO2, H2O, H2SO4." reply: Yes, indeed! Changed as recommended. reviewer comment: p. 13: I think you need to compare the retrieved Tb to previous measurements. reply: Addressed above. reviewer comment: Table III: I would like to see the error bars associated with "n" in the best fit algorithm. Another point: I would think that this "limb-darkening" could constrain the atmospheric model. Is this true? How does the best fit atmospheric model reproduce this parameter? I think it may deserve some discussion in the text. reply: The formal error bars associated with "n" are so small that I did not include them in the table. This is now described in the text. Yes, the limb-darkening parameter can be used to crudely constrain the atmospheric parameters (see e.g., Good, J.C., & F.P. Schloerb, Limits on Venus' SO2 abundance profile from interferometric observations at 3.4 mm wavelength, Icarus, 53, 538-547, 1983, or the referenced interferometric articles in our manuscript). However, the constraint on the atmosphere from that parameter is relatively weak - weaker than the disk-averaged brightness temperature constraint (see the discussion in Schloerb et al.). reviewer II - Gordon Pettengill reviewer comment: p.7: The jargon term AIPS needs to be explained -- or omitted (Same with AIPS and OMFIT on p. 12.). reply: I have added a web URL reference to the first mention of AIPS, and taken the reference to the specific task OMFIT out. reviewer comment: pp. 9 & 10: The development from eq (1) through (5) could be shortened by leaving out several of the rather elementary intermediate steps without losing most readers, in my opinion. Just define the new variables as you go along. reply: I have followed this recommendation and shortened that derivation. reviewer comment: p. 11, line before eq (9): Potential confusion exists here as to what "sky brightness" is: I suggest "planetary disk" be substituted for "sky," and "varies as" for "is like." reply: Changed as recommended (with some added words). reviewer comment: p. 13, I. 11: Isn't Tb obtained directly from eq (8), not by inversion? reply: Yes, this was a by-product of changing eq (8) during the writing of the manuscript, and not changing that reference to it. I've fixed it now. reviewer comment: p. 14, I. 3: Why use indirect occultation data from Mariner 5 as the model's temperature/pressure input, rather than Sieff's directly measured values from the Pioneer-Venus probes of 1978? reply: The problem is that the data are not fit well at all by the Sieff T/P profile. In answering the comments of the other reviewer, it became necessary to add some discussion of this in the "Results and Discussion" section, which I think answers this question directly. reviewer comment: p. 14, I. 7: Add "occultation of" between "by" and "the," to make clear that the measurements were from occultation of the MGN telemetry transmitter, and not from onboard remote sensing by the spacecraft per se. reply: Changed as recommended. reviewer comment: p. 14, lines 14-17: How about references for these assumed values? reply: The discussion of the subsurface parameters has been expanded, and references added. reviewer comment: p. 14, bottom line: "Assume" not "presume" -- please! reply: Changed as recommended. reviewer comment: p. 16, top of page: Would it be useful to mention here that the central disk brightness temperature would be expected to peak as the weighted emission moved down to within the lowest scale height, dropping back slightly (to ~ 630 K) as the finite emissivity of the surface itself comes to dominate longwards of 10 cm? reply: A sentence to this effect has been added. reviewer comment: p. 23, I. 8: Why should the subsurface temperature gradient be very small just because the atmosphere is insulating -- assuming that heat flow equilibrium has been established, as it most certainly has? The equilibrium gradient will be set by the temperature difference between great depth and the surface, where the fact that it is elevated to 740K (Venus) rather than 300K (Earth) is not all that important. reply: I apologize for not describing this very well, and it has been modified in the manuscript. The additional term in Tikkhonova and Troitskii is to account for the diurnal heat wave penetration into the upper layer of their 2-layer model. Because of the insulating atmosphere, the diurnal variation of subsurface temperature should be very small for Venus, and hence this term may be ignored. The temperature difference from great depth to surface is represented by the heat flow term (that involving 'q'), and is included in our model.