Review, Oveisgharan et al. "Snow Water Equivalent Retrieval over Idaho, Part A: Using Sentinel-1 Repeat-Pass Interferometry"

General comment: 

The manuscript performs an analysis of a 6-day repeat pass InSAR time series with the aim to retrieve snow water equivalent (SWE) from the InSAR phase. The theoretical foundation of this SWE-retrieval method is known for more than 20 years but common InSAR problems like coherence loss, phase ambiguities, and the choice of the best reference value to correct for unknown atmospheric phase delays still pose significant obstacles for the method, in addition to the limitation to dry snow. The analysis of a time series with one of the shortest currently (locally) available repeat intervals of 6-days at a relatively low frequency (C-band) is a valuable contribution to assess the best combination of repeat-pass interval and frequency.

However, in its current form the manuscript has several shortcomings that needs to be addressed before consideration for publication:

1) The linear approximation of the equation from Guneriussen (2001) has a methodological shortcoming: a linear approximation (y = mx + c) is performed and after the approximation the y-axis intersection c is neglected. Correct would be to first assume the y-axis intersection is zero, and then estimate the slope m. Even though the estimated slope changes by several percent, it would not significantly impact the results of the paper; however the authors claim to provide a more general approximation compared to existing literature which is simply not correct; furthermore, the comparison of their estimates with literature (Fig. 10a) shows a significant deviation due to the methodological fitting mistake. In addition, their approximation method is not reproducible due to the lack of given ranges for snow density and incidence angles (see specific comments on section 2.2 and the attached figure).

2) In section 5.1 the authors use the same data (average of all station's in-situ SWE measurements) for calibration of the InSAR based SWE estimate and for validation (local station in-situ SWE vs. local InSAR based SWE estimates). This means that the calibration data is not independent from the validation data (see specific comments on line 242-248/Figure 7a and b, 172a/b).

3) In section 1 and 2, several statements are supported by reference to literature, however, in a very vague, not correct way or misleading way. These references should be improved (see specific comments below).

4) In my opinion, low correlation coefficients (0.4...0.6) are often overrated by the authors as "very high/highly correlated/one of the best metrics". They need a more critical consideration.

Noteworthy, in section 5.2 the authors provide a reasonable correlation (0.51 and 0.62) between their spatially distributed SWE estimate and completely independent LiDAR data which supports the feasibility of SWE retrieval from 6-day repeat pass C-band data.

Specific comments:

Abstract:

4: "optimal": Before specifying what the optimal parameters are, I would not use the work "optimal". I suggest "suitable"

6: "long time series": In the sentence before, you talk about repeat intervals, therefore please specify if your time series has a 6-day or 12-day (or any more complex combination) repeat interval.

10: "highly correlated with LIDAR": The correlation with the SWE station data (r = 0.82) is much stronger than with LIDAR data (r = 0.5). Therefore I would not say "highly correlated" which indicates that also a very good relation between snow height and SWE exists. However, dependent on the snow pack, density variations can deteriorate SWE estimations from snow height. Writing "highly correlated" here implies that both, radar interferometry and LIDAR estimates are equally precise which is physically not correct, because radar interferometry shows a physics-based, almost linear relation to SWE while LIDAR estimates require a guess (or auxiliary information) of the average snow density (as written in line 29). I suggest something like "well correlated".

32-38: I suggest a more critical review of the listed papers. The references are given in a context that suggests that SWE estimation with active sensors is generally possible from space. I think that is  misleading and contradicts the abstract (line 3).  Did all authors use spaceborne sensors and did they really estimate SWE? I suggest to better detail and quantify where the authors of the listed papers have been successful and where not - i.e., where are still current gaps that have not been filled by the listed authors? 

47-49: These lines imply that FMCW radars cannot be used in space because of their wide bandwidth. That is not correct. FMCW radars are cheaper because they do not require temporal pulse compression (that needs high-power electronics) but because they transmit and receive at the same time, they are limited to a range of a few km because the signal travel time limits the pulse repetition frequency. And it would even be simpler to build them with a narrow bandwidth, but a benefit of these experimental and locally installed systems is the possibility to explore wide bandwidths. It is more, that wide-band system cannot be used in space because of limited frequency allocation. Possibly, I misunderstood your point: Did you mean nadir-looking radar altimeters (that could be FMCW from air or pulse-systems from space). Please clarify.

50: "specularly reflected": that is not correct in the context of the given references. "specularly reflected" means "like on a mirror", according to the law of reflection. However, the listed authors observe the snow/ground surface from the same point as the illumination source (monostatic or almost monostatic radar system).

52: "in wet snow the phase center is normally at the snow surface": that might be true for X-band and above, but the cited papers used P-band where I would expect a significant penetration into the wet snow pack. Did the cited authors really show that the phase center is at the surface? Please clarify or correct.

53: "the phase unwrapping (...) increases at higher frequency." That does not make sense. Either "the effort for successful phase unwrapping increases at higher frequencies" or "the phase wraps more frequently at higher frequencies."

55: "the theory behind this method": Could you first concisely describe the method you are referring to? What's the core idea of the method (see Guneriussen 2001)? After that, you can outline successful applications and limitations of the method as attempted in line 50-54.

56: snow stratigraphy and grain size: you are citing Yueh(2017) here, but consider also citing Leinss(2015) who did an error analysis on the impact on SWE estimates from layers with different density. 

80: Please provide a reference after "dual-pol dual-frequency retrieval algorithm". Are you sure that this algorithm relies on the assumption of non-scattering, non-absorbing dry snow, so that microwaves penetrate to the ground?

90: "highly correlated": Please quantify by providing a correlation coefficient.

95: "works well": Could briefly you point out how you solved the problem of phase reference and how you corrected for atmosphere?

106: "a high temporal coherence is observed...with a month temporal baseline": Could you provide some quantification or statistics from the cited paper? Was this "high coherence" observed in a single observation or was it generally high over a certain time series? Under which snow conditions? 

109: What do you mean with "controlled system"? What snow conditions did the authors observe?

110: "the ... temporal coherence... Leinss (2014)": The cited paper does not deal with temporal coherence. Please check. I guess, you mean Leinss(2015).

114: "the temperature was shown to be the most critical variable ...": In which sense? There are strong differences between positive and negative temperatures. Variations in negative temperatures should not significantly affect the coherence.

120: I would drop the complete sentence "More studies are needed..." because it is very general.

Section 2.2:

Comment for section 2.2: The described method seems to contain a few methodological shortcomings, misses values of parameters that are needed for reproducibility and is, in my opinion, less general than the approximation of Leinss (2015). Even though I do not expect any major impact on the results, I would like to urge the authors to improve this section and to set it in proper context with existing literature, specifically Gunneriussen (2001) and Leinss (2015) but also Mätzler (1996) and Wiesmann (1999) [reference below, comment on l.128]. An interesting idea of the described method is to fit a function for every incidence angle - this idea is, however, almost identical to the introduction of the fit parameter \alpha in Leinss (2015) to provide an optimal numeric approximation for every chosen incidence angle, because the incidence angle is very often precisely known - in contrast to the snow density, for which only a reasonable range can be estimated. In contrast to Leinss (2015), where a density range from 0 to a maximum snow density (rho_max) was assumed, a slightly improved approximation could possibly be achieved by assuming/selecting/limiting snow density to a more realistic range, e.g. rho = 0.1...0.5 g/cm^3, or whatever the authors expect for their specific region.

Specific comments for section 2.2:  

125: "related the interferometric phase directly": Could you be more specific? I suggest "related the interferometric phase with a linear approximation directly to SWE changes"

126: "depends on the range of incidence angles and snow density": That is not exactly correct. I suggest:  "depends on the chosen incidence angles and the maximum expected snow density"

126: Could you specify what exactly you mean with "more generalized"? In my opinion, your method is less general then the approximation by Leinss (2015), because it is limited to snow densities up to 0.5 g/cm^3 and incidence angles between 20 and 50 degree.

127: What are the units that you use for density? kg/m^3 or g/cm^3 or volume fraction (unitless)?

 

128: "We use Matzler’s model for calculating epsilon in equation 1 (Mätzler, 1987).": Could you provide a more specific reference (e.g. equation number or show the used equation for epsilon)? The cited dissertation has 130 pages and contains many different models for the permittivity of snow. Note, that there are more recent equations for the permittivity of snow from Mätzler, e.g.:

 - C. Mätzler, “Microwave permittivity of dry snow,” IEEE Trans. Geosci. Remote Sens., vol. 34, no. 2, pp. 573–581, 1996-03, doi: https://doi.org/10.1109/36.485133.

 - A. Wiesmann and C. Mätzler, “Microwave Emission Model of Layered Snowpacks,” Remote Sens. Environ., vol. 70, no. 3, pp. 307–316, 1999, doi: http://dx.doi.org/10.1016/S0034-4257(99)00046-2 (Note, that Eq. 46 misses an exponent of 1/3 for eps_s which becomes apparent when comparing with Eq. 10, Sect. IV-F in Mätzler 1996).

129: Please specify what units you use for SWE: kg/m^2, mm w.e.q., m^3/m^2=m (w.e.q)? Make sure, that the equation returns the correct values when entering SWE, rho, k_i, and C in the specified units.

Figure 1a: What units has C(theta, rho)? Could you verify if you really plotted C(theta, rho) as defined in Eq. (2). When I compute C from equation 2, I obtain the data shown in Fig. 1a, but only when not dividing by snow density rho. That means, currently, Fig. 1a is identical to Figure 8left, in Leinss (2015), and C(theta, rho) == xi(theta, rho_s); an overlay of both figures confirms this. I think the division by rho in the definition of C should be removed.

132: "we fit a line to C for different incidence angles": Could you specify the interval of densities rho that was used for fitting? Depending on the chosen interval, the fitting parameters can vary by several percent (see attached figure).

132: Could you specify the interval of theta for that lines-slopes were obtained by fitting? In the attached figure I assumed 20..50°, similar to Figure 1b and 1c.

135: I cannot reproduce the equation in line 135. When following the described approach (assuming a density range of rho = 0.15..0.5 g/cm^3) my values for the parameter A deviate by 1-2% from eq. 135. (see attached figure, dashed red line vs. solid blue line). Also note that for a different density interval of rho = 0.1..0.4, the values of A deviate 3-4% from eq. 135 (dashed purple line).

136: "Assuming B(theta) = 0": I see this as the main shortcoming in this section: Why do you first fit a line including an y-axis intersection, and then assume that the y-axis intersection is zero? As shown in the attached figure, you obtain more accurate results when first assuming "B(theta) = 0" and then fit a line C = A(theta)*rho where the y-axis intersection is zero by definition (solid teal line). The difference to eq. 135 is about 5% at incidence angles of 20°.

136: "B is very close to zero": (See also comment above). How close? Neglecting terms makes only sense when putting them into relation to larger terms. Could you put B in relation to A * rho? The ratio of B/A is up to 1.5%, depending on the chosen fitting interval; however, you need to consider the equation C = A(theta)*rho + B(theta) where the snow density (assuming units of g(cm^3)) can be very small, again, depending on the chosen interval. With rho = 0.15, B is as large as 16% of (A*rho) which can have - and has - a significant impact on the fitting results.

139: What's the advantage of using eq. (4) vs. Eq. (18) from Leinss 2015? Considering the above described shortcomings, I do not see any advantage of using this equation. But a proper linear fit as suggested two comments above would do it.

Section 3.1:

143-151a: This paragraph reads than a general description about Sentinel-1 and the ASF. Could you describe which data and which processing workflow you use for your input data?

143-151b: Which incidence angle (range) did the acquisitions have that you processed? 

152-172: same as above: I would expect an introducing sentence to motivate why you discuss the SnowEx2021 campaign(s) and the SNOTEL data. The reason why these campaigns are discussed is given at the end of the section, line 171-172. It would be easier to read if these sentence appear as a motivation/reason at the beginning of the paragraph. (see also next comment).

162/Figure 3b: Could you add to the caption in Figure 3b that for Delta SWE the first date of the differenced dates is shown? 

163: "located in remote, high elevated mountainous regions": Figure 3a shows strongly variable SWE values. Is that due to altitude differences of the stations? Could you specify the altitude range of the stations? 

170: "As seen in this figure [3a], there is a one 6-day repeat data acquisition gap in Sentinel-1 data on 2/5/21": Figure 3a shows two gaps as if there would be no acquisition on 2021-01-30 which is not true (Figure 4/5 show the pair 2021-01-24 vs. 2021-01-30).

172a: "we used these in situ data for SWE retrievals performance": what do you mean? To tweak the performance? Or to validate the performance?

172b: [used for] "the InSAR reference points": Could you clarify which data you used for InSAR phase reference points and which data for validation of InSAR-based SWE results? 

174-175: "LIDAR...are reliable sources of validation data, particularly a powerful constraint for InSAR retrieval of SWE": same as comment above: Could you clarify if you used the data for validation or to constrain the results?

175: "The "SnowEx20-21 QSI LIDAR DEM 0.5m" data set is part of the SnowEx 2020 and SnowEx 2021 campaigns (Adebisi et al., 2022). The data includes digital elevation models, snow depth, and vegetation height with 5m spatial resolution." - Could you clarify which data had 0.5m resolution and which 5.0 meters? 

185: Could you explain why you selected the period from 2020-12-01 to 2021-03-30? Did you limit the period to dry snow conditions?

185-186: Do you have any information about (or did any correction for) the height-(or air pressure) dependent phase contribution? It seems yes, maybe add a reference to Section 4.1.

189/191: "In this study, any pixel with less than 0.35 temporal coherence  is not considered reliable (...) However, in .. 5.1.2 and 5.2 we used all ... data even with low coherence to calculate total SWE": Why do you consider it as an advantage to use all data, even though you consider the data as unreliable due to low coherence? Or is there something specific about these two sections that the reader has not yet been informed yet? Would it not be more of advantage to set unreliable data to some assumed SWE change, e.g. zero? (see also comment on line 197)

192: "The ionospheric error ... is much smaller than other sources of error .. and considered negligible": Could you distinguish tropospheric error and ionospheric error? Or is the ionospheric error removed together with tropospheric phase delays? 

197: "similar to correlation filtering, for ... 5.1.2 and 5.2 we used all the ... data": why? (see comment 189/191)

201-203: For choosing the phase reference point, Tarricone et al. (2023) point out a promising idea for mountainous terrain: They suggest snow free areas, derived from optical data (fractional snow cover maps), as phase reference. I think it's worth to cite this paper here.

 - Tarricone, J., Webb, R. W., Marshall, H.-P., Nolin, A. W., and Meyer, F. J.: Estimating snow accumulation and ablation with L-band interferometric synthetic aperture radar (InSAR), The Cryosphere, 17, 1997–2019, https://doi.org/10.5194/tc-17-1997-2023, 2023. 

204-206. "we used the average of all in situ Delta SWE ... to calibrate the retrieved [InSAR] Delta SWE images": Figure 4 (and also Figure 3) shows strongly variable SWE values across all stations. Why would a correction with the average improve the estimates? Would a correction using stations with small/no SWE change (I would assume, these are the stations at lower altitude) not be more beneficial (see also Tarricone TC 2023)? 

210-211: Could you provide the given information (Delta SWE, and the information that there was no SWE change and two storms) (also) in the caption of Figure 4? 

242/244: "all the retrieved Delta SWE" / "all the retrieved Delta SWE time series": It seems you plotted Delta SWE between each two S1 acquisition for all SNOTEL stations. Even though you analyzed data from the whole time series of images, the shown data does not contain any specific time-series characteristics (in contrast to section 5.1.2). Is that correct? If so, clearly indicate this.

242-248/Figure 7a and b: What is the correlation coefficient between the mean Delta SWE values of all stations (that was used as reference for the Delta SWE images - see line 204-206) vs. the Delta SWE of all individual stations?  - The contrast of the good correlation between 0.6 and 1.0 (with a mean around 0.82) in Figure 7b (and the mean in Fig. 7a) and the low correlation (between at least -0.5 and +0.8, median correlation at approximately 0.4) is a hint that the major part of the correlations is due to the fact that validation data was used for calibration.

For estimating a lower limit for the expected error in your data: how large is the standard deviation for certainly snow free areas (if there are any)?

252: I would not call an correlation coefficient of 0.4 and higher "very good" (See examples on https://en.wikipedia.org/wiki/Pearson_correlation_coefficient). I would call a correlation of 0.8 good, and a correlation of 0.4 poor.

Figure 7c: What is the correlation of the first acquisition at 12/01? Could you scale the y-axis so that all datapoints are shown? 

Figure 7c: Could you add to the caption in Figure 7c that for correlation and the first date of the correlated date pair is shown? 

250-262: Here, you discuss reasons why you could expect a low correlation. If you select only acquisitions pairs with SWE changes (average over all station) larger than a certain threshold (according to Figure 3a) how would the correlation coefficient look like? For example, you could have the average SWE change per acquisition pair (sorted by magnitude) on the x-axis and the correlation coefficient of all SNOTEL stations vs. InSAR Delta SWE on the y-axis, would the correlation show an increasing trend with increasing SWE change? I would expect that if there's a clear correlation between Delta SWE and the station data. In contrast to Figure 7a, such a plot would be independent on the choice of the reference phase (or reference Delta SWE).

Section 5.1.2: Note, that the methodology in this section might suffer from the same calibration problem as commented on 242-248. (validation data used for calibration). If you plot the SWE error at the end of the season (03/31) over total SWE, I would expect that for stations with a large total SWE the S1 data show a negative bias, while for stations with  a small total SWE, S1 shows a positive bias.

277/281: "we think the main reason for divergence is the ... phase ambiguity" vs. "The divergence is mainly due to phase ambiguity": These two statements are not compatible with each other. Do you assume/think that that's the main reason? - then you can't make the second statement. Or do you have sufficient evidence that that's the reason? - than provide the evidence it, instead of "thinking" it's the reason.

Figure 10a: I think the main reason for the discrepancy between the approximation from Oveisgharan (2023) and Leinss (2015) is the shortcoming of correct approximation of the equation from Guneriussen (2001). See attached figure (blue line vs. thin black line; even more accurate: blue line vs. thick black line). See comment on line 136.

304-309 vs. 314-318: These two paragraphs show a very high redundancy of text. Consider writing it more concise, e.g. first a single paragraph describing both figures (11 and 12), then a second paragraph describing the differences.

308-309: "The high correlation of 0.51 shows the success of this method": I would say "there's likely some correlation supporting that SWE estimation with InSAR from space is feasible."

318-319 "The correlation ...is 0.62. This high correlation is one of the best validation metric for SWE retrieval using the InSAR techniques". First, I would not consider a correlation of 0.62 has high. It basically shows that there is likely some correlation. Considering that the comparison of the spatial snow height distribution from LIDAR is a completely independent dataset from the spatial distribution of the InSAR estimate (that includes calibration by in-situ data from SNOTEL station) makes this correlation, more correctly, the two correlations shown in Figure 11c and 12c, currently the most convincing correlations in this manuscript.

326: "highly correlated (0.82) with in situ values" - as commented above, there might be a calibration problem as commented on 242-248. (validation data used for calibration).

327: "The retrieved total SWE has less than 2 cm RMSE compared with in situ values in 16 stations" - you neglect here, that it is worse for the other 34 stations of the in total 50 stations.

328-329: "We show ... that SWE retrieval using spaceborne InSAR timeseries is a very promising candidate for future SWE missions": It might be true that the analysis of InSAR time series is a promising candidate for future SWE missions. However, your paper shows that the method is likely feasible, but it also shows that several problems of the method, like phase unwrapping, loss of coherence, choice of reference phase, are still not sufficiently solved and that even with a 6 day repeat interval at C-band it is not easy to retrieve reliable SWE estimates.

I'm looking very much forward to the first SWE time series from NISAR :)

Technical comments: 

Please check the paper against the submission guidelines https://www.the-cryosphere.net/submission.html, specifically dates should be written as "dd month yyyy" (https://www.the-cryosphere.net/submission.html#math) rather than in American notation. I know that sometimes (e.g. in figures or tables) the date can be given according to the international ISO 8601 standard (https://en.wikipedia.org/wiki/ISO_8601) but that needs to be confirmed with the editors.

189: You might want to change double negation to a positive formulation "less than .. not considered reliable" -> "higher than ... considered reliable"

Figure 4 and 5: It might make sense to combine both figures into a six-panel image with a top row of the three Delta SWE images and a bottom row with the three correlation images.

The manuscript from Oveisgharan et al presents the results of the analysis of Sentinel1, C-band, InSAR timeseries over Idaho for Snow Water Equivalent (SWE). The generation of the InSAR derived SWE timeseries over the SNOTEL stations was demonstrated using them as reference for phase. Additionally, the total SWE retrieved over several months showed great agreement with SWE when compared to LIDAR snow depth. The work is of interest for the snow community focusing on InSAR SWE retrievals. The results presented in this manuscript would be useful for future satellite missions such as NISAR or ROSE-L. Furthermore, it also demonstrates the technique using Sentinel1, that will operate along ROSE-L. Congratulations to the authors for the great work. I have some concerns I think should be addressed before publication.

General Comments:

1. I think an interesting addition would be a figure (maybe in the annex) with the time series of in situ vs retrieved SWE for all stations. This is at your consideration. Also, in Figure 2.b add the number of the stations, at least the ones you used for Figure 9.
2. Regarding the calibration, while I agree that the large number of stations reduce the bias, I am a bit concerned that this method can “mask” unreliable phase measurements. Take as an example the interferogram presented in Figure 5 (c), where most of the stations have very low coherence. If you do an averaging around the low coherence stations (considering homogeneity and a sufficient large number of pixels), phase is noisy and the expected value should be zero, which translates to 0 DeltaSWE. If now you add the mean DeltaSWE from the stations, you’ll probably get something closer to the in situ value for that station, although the phase had no usable information. I’m not asking to change the methodology, just comment on this. Additionally, adding error bars with standard deviation in Figure 9 would be useful to assess the effect.
3. See comments regarding Section 6.
4. Perhaps it is a bit picky but be more consistent with coherence and correlation along the manuscript (e.g., lines 196, 205, F5 caption, 213… these could be coherence or temporal coherence). I am also missing some explanations why you neglect other sources of decorrelation and assume that the product is just the temporal component. Also, when discussing temperatures, I’d use 0°C over zero.

Specific Comments:

Section 1: Good introduction. I am missing perhaps some mentions to co-polar phase difference for snow height estimation.

Line 15: wouldn’t mass be more precise than cover here?

Line 50-56: perhaps add a few details. Phase center at the snow surface or the volume. I got a bit lost in this paragraph, when you say this method do you refer to the method for dry or wet snow? A sentence clarifying this could be useful.

Line 55: remove second “this method”.

Line 57: remove small.

Section 2:

In Section 2.1 you could add that snow is a thermal insulator and it reduces temporal changes in the underlaying layers. Is this relevant for mountainous areas?

Line 68: I think the idea is clear without “very” and “small”

Line 72: higher than what? or relatively high frequencies.

Line 75: Extend the equation to include . I guess makes some sense since you are focusing on SWE in the manuscript. Also details that snow permittivity depends on its density and can be approximated from the density and that the complex part is negligible for dry snow.

Line 93 to 96: is this the correct place for explaining what you have done, or should it go in the introduction?

Line 101: two different times, for generality.

Line 102 to 103: maybe make this idea about decorrelation more general, not just for vegetation.

Line 105: Consider changing faster sampling for shorter temporal baseline, sounds more connected to repeat pass interferometry.

Section 3:

Would be nice to explain that at the time of the study, Sentinel-1 operated a constellation of two satellites. You can mention that each of these satellites had a repeat pass of 12 days, but due to the orbit offset between them, the effective temporal baseline is 6 days.

I think Figure 2 deserved better visualization. The caption should mention that the green frame is the S1 image (as you did in Line 160), and what are red and green diamonds.

Line 143: … at a central frequency of 5.405 GHz

Line 145: comment that you can get S1 data at the Copernicus Open Access Hub :)

Line 167: … for each of the SNOTEL stations.

Line 209: change squares to diamonds?

Figure 3, (a): Change x label to “Day from 12/01”.

Section 4:

Line 185: are these sources of error general for all applications or just particular to snow?

Line 195: be more specific specifying that it is data from SNOTEL stations and that this data is snow measurements.

Line 213: this idea about temporal coherence being a limitation of InSAR is repeated a couple of times in the paper. Consider removing this one.

Line 214-215: I don’t understand the point of this sentence. Isn’t it as short as possible? Or would you discuss limitations related to satellite capabilities?

Line 221: water vapor content between passes.

Section 5:

Line 239: is results the correct word here? Or LIDAR data/scan?

Somewhere in this section you should state what is the window (number of pixels) used to extract the values of coherence and phase for the stations.

Line 255: change discovered to observed?

Section 5.1.1: I would like to read some discussion about the points with error=0

Figure 7,c): are the dots placed on the reference acquisition?

One thing that comes to mind is if you can say something before the 12/25/20 acquisition (as it is the common one between the two interferograms you show) that could explain the noisy phase. E.g. wet snow, a storm…

Line 261: Do you mean observations 5 and 4? Otherwise, I don’t think we know where stations 5 or 4 are…

Section 5.1.2:

Line 269: As mentioned in Section 5.1.1? or in Section 4? But check this sentence if I understood correctly you use DeltaSWE values when temporal coherence is below 0.35 and temperature higher than 0°. So, does this mean all values?

Please indicate that you set SWE_t1 as 0. Some stations have snow already for the first acquisition. I think you need a comment on this.

Figure 9: Do the timeseries expand the same time span. I think they do but the x axis is different for the three subfigures… Also, drop some of the decimal precision? See comment about std for each acquisition.

Line 295: could you be a bit more precise about how a station is labeled as red or green? What is the threshold for it? I see this is explained in the caption of Figure 10, but shouldn’t it be in the text also?

Section 5.2:

I think the analysis here could be extended. Is there anything that is increasing the error like steep slopes or vegetation (although from figure 2 seems there is not much vegetation)? Could you add some comments about coherence for those images? Was it generally conserved? Another point just out of curiosity, are the results similar if you compare the LIDAR map to S1 SWE map from 03/13/21? Looking to Figure 3.b) does not seem there were much SWE accumulated between the pass dates.

Line 303: Add the complete date of the LIDAR scan.

Line 305: isn’t the closest date the 03/13/21?

Line 311: total SWE accumulated rather than change?

Perhaps indicate in the text that in Figures 11 and 12, (c) what does color represent?

Section 6:

I think this section is a bit short and does not discuss important aspects of the work. You could emphasize that the total SWE vs LIDAR was done accumulating the contribution from many interferograms, and the great spatial match. This to me is a truly impressive result. On the other hand, you should also need to discuss the calibration strategy, in my opinion this plays a crucial role in your results you cannot overlook commenting on it.

Line 324: Not completely sure about this. Definitely short temporal baselines will help with coherence but if between passes there is a snowstorm most likely coherence will drop significantly.

Technical Comments:

Line 191: Section 5.12, I think

Line 196: Section 5.1.2, I think

Line 214: InSAR (capitalization)

Figure 7. (a): Path:71. Why 2021? Should not be from 2020 to 2021?

Line 256: InSAR(capitalization)

Line 333: NISAR acronym already introduced.