This paper presents a reasonable case study of microphysical evolution within a winter storm supported by ample observations and some well-considered idealized modeling. The authors do a good job at not over generalizing the observation evidence or reading too much into their simulations. I think this paper well highlights the prevalence of sublimation in this winter storm. IMPACTS as a project well showed how common sub saturated conditions really are.

I have concerns that the flight legs from this flight do not really create a good Langrangian view of the band of interest. I also think the idealized microphysical modeling experiments do not investigate variations in riming the way they should. However, because the authors do not over generalize and do not over interpret their evidence, the ultimate impacts are minor, and the investigation of sublimation stands as good and interesting work.

I recommend this paper be published with minor suggested changes that I trust the authors to consider without a subsequent round of review.

Below are suggestions in no particular order:

• The authors highlight the intended semi-Lagrangian nature of the flight sampling for this storm. However, there’s an implied assumption of near steady state conditions and consistency in the vertical structure along the storm’s direction of motion. There’s a deeper implied assumption that the banded feature of interest is contained within the extend of the flight legs. I think volumetric MRMS data or perhaps 3D EXRAD data (if available for this flight) as well as an examination of vertical wind profiles from soundings (or, as a last resort, HRRR or reanalysis) can demonstrate that the storm fits close enough to the implied structure and that shear isn't confounding the analysis.
• Paragraph starting at Line 164: A map and some time series plots would be of real benefit here. Moreover, the claim that the studied band produced locally high surface precipitation accumulations is never demonstrated to the reader.
• The authors stated that the two dominant microphysical processes at play for the bulk of the depth of the storm were sublimation and riming. I think the sensitivity tests for relative humidity were well considered. The variations in vertical velocity mainly influenced the fallout time of the particles and subjected them to more or less time to sublimate. Missing from the sensitivity tests was a variation in riming. The authors stated that they used a fixed LWC value to affect riming. I think that value should be subject to variation as well. The observed vertical velocity distributions (as well as time series of vertical velocity from which those distributions were derived) suggest that upward vertical velocity is brief and suggests that riming should happen in bursts. I don’t know if the McCool model allows for time-varying changes in ambient conditions, but I suggest investigating the possibility in order to better characterize the nature and role of riming. If the authors can reasonably fit some riming variations into the manuscript, they should. That said, I think the results of such variations should be obvious to most experts.
• Paragraph starting at Line 557: The authors are reading too much into the precipitation accumulation numbers here. Remember that a single rain gauge bucket tip is 0.254 mm. The authors state that 4 bucket tips in an hour is more than their simulations and 3 in an hour is more in line when the truth is that their numbers all fall within a rather large ballpark of measurement uncertainty.
• The radar colormaps don’t work at all in black and white.
• Table 1: Please include the obs for reference.

This case study leverages a Lagrangian particle model (McSnow) along with data from an HVPS cloud probe in order to understand the evolutionary pathway of snow properties and various microphysical processes in a midlatitude band. The authors constrain their model using environmental data from the P3 aircraft in situ instruments and the initial PSDs derived from the HVPS. The particular snowband that the authors targeted was subsaturated such that the estimated IWC decreased with decreasing altitudes. This behavior, along with the authors' arguments using PHIPS probe imagery, suggests that rapid sublimation was a driving factor for the decaying band. The authors conclude from their suite of simulations that sublimation provided greater than a 70% reduction of IWC and that small perturbations of RH can vary IWC by as much as 29%. The authors’ figures are simple, high quality, and I think they provide a cohesive and easily understandable narrative regarding their interpreted evolution of this decaying winter band.

I have three overall major concerns with this study that I think the authors need to address before publication. First, I think that there needs to be some discussion regarding how steady the band was during all four legs and how the location of the band changes at each of the P3 leg altitudes. The authors use MRMS composite reflectivity to show the P3 aircraft location with respect to the location of this decaying band. However, fallstreaks are often sloped in these winter storms. I’m not convinced that the composite reflectivity shown in Figure 1 properly illustrates the location of where the band was at each of the P3 levels. This information is quite important because the PSDs can vary quite a bit throughout each level which can be seen from the IMPACTS website quicklook figures; this PSD variability would naturally impact the authors’ constrained modeling results. Second, the authors rely on the HVPS to estimate ice water content (IWC) and the authors assume that the IWC predominantly results from the "prevalence of single crystals" that were "larger than 0.5 mm." The authors state on lines 347--350: "From imagery collected at all heights, relative to the prevalence of single crystals, very few aggregate particles were observed. This near absence of aggregation significantly contrasts with the high prevalence of aggregate particles observed within the southern region of enhanced reflectivity that lacked well-defined banding (DeLaFrance et al., 2024b)." I took a look at some of the example HVPS images and distributions available for the 04 Feb 2022 IOP on the IMPACTS 2022 website available publicly at https://catalog.eol.ucar.edu/impacts_2022. I don't really agree with the authors that aggregates were not common during these short time periods. You can see various pockets of moderate (mm sized) and even large sized (approaching cm sized) aggregates for each of these regions in the example HVPS distributions and images available on the IMPACTS website. It seems like there were moderate to large aggregates at some time periods such as 1617 UTC and 1710 UTC. I've added some HVPS buffer strips below to illustrate this.

These aggregate regions also seem to show up in HVPS distributions themselves from what I can tell from the available figures on the IMPACTS website. While I don't think that the presence of aggregates necessarily changes the authors' results or interpretation, I do think that the presence of aggregates as seen in the HVPS buffer strips should be mentioned and some HVPS strips should be shown as a figure. Finally, I also think that the authors need to demonstrate that the 2D-S is not needed here to fully resolve the ice water mass distribution. I suggest that the authors utilize a separate IMPACTS case such as the 07 Feb 2020 IOP to investigate how much ice mass, on average, would be from particles smaller than 0.5 mm. Since many of these winter systems have bimodal particle distributions, it’s possible that the IWC values from these smaller size particles are appreciable and could change the interpretation of the McSnow sensitivity tests. The authors could easily calculate IWC using the HVPS and the combined 2DS-HVPS size distributions (which are already available online) for another IOP.

Specific concerns/comments:

• Figure 1: The authors use composite reflectivity from the MRMS product here. However, wouldn't it make more sense to use the MRMS reflectivity at levels corresponding to the rough P3 altitudes for each leg? I don't think the composite reflectivity is really appropriate if we are to be convinced that the P3 is truly following a decaying winter band in a Lagrangian or semi-Lagrangian sense.
• I like how the authors show PHIPS images for each leg. However, it would be better from an analysis perspective to show the HVPS buffer strips as well throughout each leg. This would be a better way to demonstrate whether or not the particles were generally unaggregated and also whether the HVPS is good enough to resolve the mass distribution. Also, the authors should consider using CPI images as well as those were also available throughout the IOP.

• Section 4: It isn't obvious to me how McSnow was configured. The authors say that the model is a "columnar model" where there were 500 grid cells. This is giving me the impression that the model is 3D and that each grid cell represents some 3D column in space. However, I think this is actually referring to the vertical spacing alone. The authors should specify here what they mean by each grid cell.
• Table 1: It wasn’t clear at all to me what the bracketed percentages represent. I tried reading the caption and the text and I couldn’t find that information. From the text, I was able to infer that this probably refers to the change from the control simulation, but this should be explicitly stated in the table caption.

Suggestions:

• Figures 1,2,3: It would be really beneficial if the authors provided the times as well, in addition to the along-track distances. I like to utilize the NASA IMPACTS field catalog to verify some of the authors' claims and so I can understand the authors’ arguments a bit better. For example, readers could be pointed to the IMPACTS website for additional images from, for example, the CPI measurements. However, it wasn’t clear to me throughout what the time periods were in each figure. I think that the start/end periods are represented in the first and last PHIPS image panels in Figure 4 but this wasn’t stated anywhere in the text from what I can tell. The authors should provide these time details somewhere in either the text or the figures.
• Figure 8: I think the authors should make the histogram stairs dashed or dotted for their simulated particles less than 0.5 mm. This would help readers better compare panels a and b while maintaining the simulated PSD at smaller sizes.

Authors present a case study and associated microphysical modeling study of a case during IMPACTS. This study presents an interesting look at a decaying storm, and how structures – particularly enhanced reflectivity/banding – is impacted by an otherwise dying system. The article is generally well-written, and represents a worthwhile contribution to the body of knowledge. I have a number of issues with the article, that I think addressing would make the article stronger.

The major issue I have is with the overall storytelling of the paper. There are some parts of the paper that jump around, for instance going from lit review, to describing the case, and then back to the lit review. In addition, I think the modeling portion of the paper could use some more tying back to the observations portion. For instance, there’s a lot of sensitivity plots (e.g. Fig. 11) for model runs. While the “control” should be close to observations, it would be helpful to ground some of these plots with observations where possible.



It would also be helpful to think a bit about how the assumptions of the Lagrangian framework are or are not met - are the individual layers moving with the system as a whole? Are the particles sampled in the top leg substantially the same ones sampled in the lowest leg? If you don't capture the same layers/particles, does it matter?

Line-by-line comments below:



Ln. 27-28: Are bands a radar feature? That’s usually how they are defined. But then they can’t produce precipitation – they correspond to intensified precipitation rates.

Ln 34: remove “recently” – it may not be recent to the reader.

Ln 52-55: These are a lot of words that may or may not be true, but don’t really say anything of value.

Ln 58: Are bands always readily diagnosed? You provide one definition, but there are others. Automated band detection algorithms are relatively recent (e.g. Fairman et al. 2016), as the problem has been fairly tricky.



Ln 61-65: Are you predicting or diagnosing? Different problems.

Ln 66-81: This is out of place, surrounded by lit review

Ln 100 and elsewhere: “natural particles” are mentioned several times; is this supposed to be in opposition to cloud seeding or something? Is this setting this paper separate from SNOWIE findings?

Ln 104-114: Again, a description of the campaign seems out of place sandwiched in the lit review.

Ln 168-170: I don’t understand the point here. Are you saying a banded snow project selected a band to sample? Would something else ever be selected?

Ln 171-178: How many of these sites are human-augmented? P-type observations from ASOS depend on that – for instance, unaugmented sites can’t detect ice pellets.



Also, what is the point of discussing surface p-type? Does it matter to your conclusions? Bands are features aloft.

Ln 182-184: Were the passes sampling the bands calculated to be truly Lagrangian – that is, was the actual band/storm motion used to select the location of the next flight leg? Or is it quasi-Lagrangian with just an estimate of motion used/were legs constrained by things like ATC?

Ln. 191: Reflectivity maxima in the along-track direction, right? Not the most intense part of the band in the along-band direction? And this is presumably on a composite reflectivity image, right? Not intensity at a particular altitude?

Ln 202-205: In winter, changes in reflectivity can also be due to brightbanding. Do you know that the drop in reflectivity is due to weakening and not thermal profile changes (e.g. the freezing level moving relative to radar coverage)?



Also, those are very high reflectivites for winter outside of convection!

Ln 214: It would seem that the prior IMPACTS-specific text intermixed in the intro would fit better here.

Ln 230-232: You have the data you have. But what does this mean for the reliability of measurements you wanted to use the 2D-S for? If the HVPS were reliable in the 2D-S’ size range, why have the 2D-S at all?

Ln. 283-285: Does the frontal position correspond exactly to the freezing level?

Ln 308:313: You’re discussing a frontal boundary quite a bit, but don’t actually show where you are saying it is. Can you add your analysis on Fig 2 or a new figure here?

Ln 314-315: Is this a coincidence? I’m not sure what you’re saying here. There is a maximum at the north? Or the north end was chosen because of the maximum?

Ln. 319-326: I like this analysis. However, I do need to ask: how steady-state is the aircraft motion? That is, when you calculate derivatives, are your measurements actually on the same x/y plane – or close enough? I think 1 Hz measurements take care of it, and I don’t think the underlying fields vary that much even if turbulence change your altitude.

Ln 329: I think I get it – “observational domain” here is the analysis domain for this work, not observational domain for IMPACTS. But when talking about a field campaign, observational domain often means the latter.

Ln 332-334: Why these points vs other points in the leg?

Ln 344 (and elsewhere): Are the observed habits unusual for this temperature? If so, what does this mean? If there’s nothing truly remarkable or unique, avoid those words in formal papers.

Ln 352: Presumably RH w.r.t. liquid water? Just checking since the paper is discussing ice phase processes.

Ln 352-353: Advected from other higher RH areas outside the flight track perhaps?

Ln 359-360: Is this the southern region in this study? You may want to name your regions and indicate them on a figure.

Ln 369-370: This is basically stating the next section header.

Ln 375: Liquid equivalent precipitation rates, right? Snow rates depend on more than mass.

Ln 378-380: These are presumably IWC values averaged over a certain time frame (the whole leg), right? That’s where the distribution in Fig. 5 comes from? Would shorter averaging change the story for parts of the legs?

Ln 386-388: Probably should have a cite here to support this claim, particularly in light of trying to use HVPS to get around the lack of 2D-S.

Ln 414: Is it really unique?

Ln 437-439: Did you sample these supersaturated environments? Do you think these SLW drops are being advected in from off the cross-section? If you didn’t sample them, where are the supersaturated environments?

Ln 455-456: If the uncertainty in the instrument is 0.2 m/s, these values are indistinguishable from zero – that is, the sign (ascent/decent) is unknown, right?

Ln 460-461: Did you measure this colocation of updraft and supersaturation?

Ln 496-499: Is there a chance that an important layer (e.g. sloping frontal inversion/theta-e max) is washed out with this methodology of averaging and interpolating?

Ln 743-745: Given the slow V_t, do we know that the generating cell particles are the same ones in the band, or are they advected elsewhere during their long fall?