This manuscript describes a study to relate snow fall rate and W-band reflectivity based on two observational events. Overall, the results of this study may add some new incremental knowledge of mm-wavelength radar-based snowfall remote sensing. However, some revisions are needed.

Main comments.

1. You should, probably add some information about radar calibration. How well is the radar calibrated?
2. Did you account for the two-way radar signal attenuation by gases and hydrometers between the aircraft and the radar resolution gate, which was used?
3. What are the uncertainties of the hot plate for measuring snowfall rate? Given that sometimes you are getting negative snowfall rates as much as -0.3 mm/h (Fig.8), these uncertainties can be substantial.
4. As I understand your results are shown only by a couple of points representing mean Z and S values. Why do not you show more detailed information on the S-Z correspondence?
5. Note that the Matrosov (2007) relation was derived for Z > 0 dBZ. It needs to be stated in the paper and shown in Fig. 12 (like it is done in the PV11 paper).
6. How the reflectivities were averaged? Did you average them in linear scale (mm^6/m^-3) or in the logarithmic scale (i.e., in dBZ units)?
7. How well the snowfall rate and reflectivity measurements were collocated? What was the vertical separation between radar Z and hotplate S measurements used in analysis of Z -S pairs?
8. Section 2.3: How did you separate components of the Doppler velocities (i.e., the reflectivity-weighted fall speeds and vertical air motions)?
9. Was your assertion that particles were rimed based for the most part only on the analysis of the 2DP particle images?
10. Did you utilize 2DS particle measurements?
11. You suggest that the 2DP particle images are representative of those that fell from the flight level toward the hotplate. It might be not so since the height separation was very significant.

 Minor comments

1. Line 91: what are rho_ 1 and rho_3 ?
2. The manuscript could benefit from additional editing.
3. I wonder if you need any permission to reproduce the figure from PV11 paper (their Fig. 11), which is copyrighted by the AMS.

The manuscript presents a field experiment in which airborne W-band reflectivity is matched with ground measurements of snowfall rate to investigate the Z-S relationship for rimed particles. The topic is very important for the precipitation community because the uncertainties in the microphysics still lead to very big uncertainties in the precipitation retrievals. The authors follow up from a series of previous papers, but in particular from the Pokharel and Vali 2011 (PV11) in which a full range of particle types is assumed and the precipitation rate is calculated from particle density assumptions. In this manuscript the authors focus on a specific particle type, rimed particles, for which precipitation rate is usually underestimated using “conventional” Z-S relationships.

Despite the great importance of the topic, the manuscript doesn’t really provide a Z-S relationship for rimed particles as the title would suggest. Most of the manuscript is focused on the description of the methodology used to calculate the relationship, and very little space is dedicated to actual results. 4 points are really not enough to derive a Z-S relationship and the conclusions just state that the measurements of this field campaign fit within PV11 variability. The fact that rimed particles were not really well represented by published Z-S relationships was already known so the fact that this manuscript does not present a new Z-S relationship specific for rimed particles doesn’t match with what the title suggests.

Probably the use of a ground based W-band pointing radar would have helped with the availability of Z-S points, aided by the aircraft overpass to confirm the presence of riming with the cloud probes.

Given the availability of data (I assume no more aircraft overpasses are available at the site, otherwise they would have been used), I suggest to stress more the position of the Z-S points in fig. 12, trying to figure out what differentiates these 4 points from all the other points under the black best fit line or from the Matrosov 2011 range.

On the other hand, I understand that this journal is about atmospheric measurement techniques, so if the goal is to describe the methodology to match aircraft with ground based observations, that is not really clear from the title and the abstract. As I said earlier, my expectation here is to find a new Z-S relationship for rimed particles. Based on what you decide the goal of the manuscript is, please revise accordingly.

Also as a general comment, there are too many not needed figures in this manuscript, I provided some suggestions to consolidate them.

Specific comments:

• Section 2.1 and in general when you mention AF environmental data. It is not clear to me when you actually use this dataset in your analysis since HP already has the data needed to calculate precipitation rate. Probably I missed it, but I would suggest to be more clear so it could be more obvious. But on the other side, how far are the two sites? we know environmental conditions change a lot, especially in mountain environment, could the conditions be very different in this case? Is it actually reliable to use that data as it was at HP? And the same is for the SNOTEL site, would it actually reflect the HP situation?
• Section 2.4, you describe the hotplate and all the bias corrections needed, included a comparison with a fenced precipitation gauge. Why isn’t the HP inside a fence?
• Section 3.3, lines 287-291: why mentioning this previous attempt to compare wind speeds if data sets are difficult to interpret and they do not provide useful results for this work?
• What is the point to show up- and down-looking reflectivities? Up-ward ones are not needed for this work and actually these plots are a repetition of figures 9 and 10 (except for the up-ward reflectivities). Vertical winds can be consolidated into figs 9 and 10 too, focusing on the portion of the overpass that is actually of interest for the analysis.
• Line 433-434, the meaning of the slopes is not really clear if the reader hasn’t read the appendix yet. I would suggest to add a sentence explaining why the HP line is flat while the WCR one has a slope (and then refer to appendix for details).
• Figure 6: I am not sure this figure is needed or can probably be moved to the appendix. I find it a bit confusing.
• Figure 7b is the same as fig. 2, just extended to reflect the situation around the observation time. I would try to consolidate the figures.
• As I mentioned before, despite the presence of fig. 6, the averaging intervals are not clear and confusing. The appendix should be for details, not for the general understanding of what we are looking at. For example the difference between i=0 point being after t0 for HP and before for WCR should be stated somewhere in the text (not only in the appendix). Or the meaning of the WCR slope.

Minor comments:

• In the abstract you refer to ‘published Z-S relationship’ which sound like a very specific one (I assume you are referring to PV11). It is probably good to mention it.
• line 309: add ‘forced through the origin, RED LINE’.
• Line 366: provide a time reference for the ridgeline as you did for the last 3 seconds.
• Figure 5, the plot at the end goes outside the axes (red line).
• Figures 7a and 8a are never mentioned in the text, either mention them or remove.
• Figures 9b and 10b, usually doppler velocity has a blue/red colormap, you might consider it for consistency with other publications or just for differentiating it from the reflectivity plot on figs 9a and 10a.
• Line 629: ‘within the variability’ – maybe in fig. 12 you can plot the PV11 variability to make it more clear.
• Line 693: in Kulie et al the threshold is 0 dBZ.

This manuscript advertises observational evidence from combined ground-based snowfall rate (S) and airborne W-band radar reflectivity (Z) measurements that rimed frozen hydrometeors are associated with somewhat unique Z-S relationships.   These types of studies are desperately need to more accurately characterize the sensitivity of W-band reflectivity to different particle microphysical characteristics, so I laud the authors on their attempts to constrain Z-S relationships for rimed situations using observational assets.    My main concern is the lack of data points presented in this analysis - are the results meaningful since the sample size is so small?    I am not sure how to suggest solving this issue other than collecting and analysing more data.    Conversely, I am very cognizant of how difficult it is to match spatiotemporally disparate datasets like airborne radar to point source measurements of precipitation rates at the ground, so I can appreciate how this study might still be valuable to the community by demonstrating the "atmospheric measurement technique" used so it can be replicated and improved in the future.    The manuscript could probably be improved greatly if the narrative leaned more heavily into this aspect of the study.   Addressing this issue might be as simple as more forcefully advertising how difficult it is to make such measurements combined with how important it is to collect observational Z-S evidence under rimed conditions in both the introduction and conclusions.   I might be able to offer more impactful suggestions in the future when I digest the manuscript again, but I encourage the authors to think about how to creatively make the narrative more impactful.

Specific comments:

1. Introduction:   I think it's important to note sooner in the introduction that some of the initial S/Z studies performed for W-band radars were purely modeling (i.e., using backscatter calculations from idealised models of frozen ice habits combined with parametrised particle size distributions) studies.    This is a very simple way to accentuate the methodological differences (and importance) of observationally-based studies to assess the veracity of idealised modeling studies.   
2. Two further studies of interest (and there are likely more) are Hiley et al. (2011) and Kneifel et al. (2015). Both highlight W-band radar applications for snowfall estimation and also provide analyses that either hint at or explicitly demonstrate how the existence of supercooled water and associated riming complicate Z-S relationships.   Battaglia and Delanoe (2013) and Battaglia and Panegrossi (2020) also demonstrate the global occurrence of snowfall events with supercooled liquid water and Z-S implications.   These studies might provide additional context to frame this study’s importance, including W-band attenuation.
3. I am not very familiar with the hotplate and its history of accurate snowfall rate measurements. While the authors provide some background on previous studies that have been published using hotplates, mostly related to various hotplate precipitation estimates due to various issues (e.g., catch efficiencies, wind speed measurement height, etc.), I still do not see any evidence that this instrument is effective at accurately measuring snowfall rates under various environmental conditions.   I would greatly appreciate at least a few more sentences that describe hotplate performance based on previous studies, including uncertainty estimates.   No snowfall rate measurement device is perfect, but it would nice to see more details regarding the hotplate since this instrument is such an important component of this study.
4. Somewhat related to the last point, can the authors further quantify (or at least qualitatively describe) the uncertainties related to their spatiotemporal averaging methodology for both airborne radar and ground-based snowfall rate measurements?  What is the sensitivity of the results for slight changes in averaging methodology?
5. The radar blind zone, and what happens within that layer, is incredibly important. The 200 m WCR blind zone is mentioned in this study in a few locations, but I think the authors need to mention more prominently that a tacit assumption used in this study (similar to a host of other airborne or spaceborne radar studies) is that microphysical evolution within the blind zone could be a major source of uncertainty.   I do not recall any studies that conclusively document how rimed particle density evolves in the lowest few hundred meters of the atmosphere – presumably not much – but this is an important to note within this manuscript.   It at least warrants a topic that should be studied in the future in the conclusion or discussion sections.   It would have been nice to have additional microphysical measurements at the surface to assess the microphysical evolution, but I completely understand how difficult it is to procure instrument suites for fieldwork.

I will likely add further comments later in the review cycle.   But I would like to see the above comments addressed by the authors before I devote more time to more specific comments.

I think this manuscript has potential and could be publishable.   But I encourage the authors to fine tune it further to make it more impactful.