Winter Arctic sea ice thickness from ICESat-2: upgrades to freeboard and snow loading estimates and an assessment of the first three winters of data collection

Petty, Alek A.; Keeney, Nicole; Cabaj, Alex; Kushner, Paul; Bagnardi, Marco

doi:https://doi.org/10.5194/tc-17-127-2023

Articles | Volume 17, issue 1

https://doi.org/10.5194/tc-17-127-2023

© Author(s) 2023. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/tc-17-127-2023

© Author(s) 2023. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 17, issue 1

Research article

|

13 Jan 2023

Research article |

| 13 Jan 2023

Winter Arctic sea ice thickness from ICESat-2: upgrades to freeboard and snow loading estimates and an assessment of the first three winters of data collection

Alek A. Petty, Nicole Keeney, Alex Cabaj, Paul Kushner, and Marco Bagnardi

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Final revised paper (published on 13 Jan 2023)
Supplement to the final revised paper
Preprint (discussion started on 16 Feb 2022)
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Interactive discussion

Status: closed

RC1:
'Comment on tc-2022-39', Anonymous Referee #1, 06 Apr 2022

Review Petty et al, Winter Arctic sea ice thickness from ICESat-2:

upgrades to freeboard and snow loading estimates and an assessment

of the first three winters of data collection.

## General comments

The paper assesses the impacts of a number of changes to ICESat-2

ATL10 processing and to the NESOSIM snow model on estimates of

along-track and gridded sea ice freeboard and ice thickness. This

assessment is important for users of high level sea ice products such

as ATL20 gridded sea ice. Overall the paper is well conceived and

written. However, there are a nuber of issues that need to be

addressed before the paper is ready for publications. I list these

below. I also have a number of specific comments.

Overall, the quality of the figures is good. However, some of them

could be improved by adding descriptive titles/labels to each panel.

For example, figurure 7 has titles but these appear to be file

variable names. Rather than "ice_thickness_unc", it would be more

helpful to readers to have "Ice thickness uncertainty" spelled out.

Likewise with panel (i) "ice thickness int" would be better as

"Interpolated ice thickness". The authors might also want to think

about a better layout and if all panels are necessary.

The Jupyter notebook is an excellent addition as is making the code

available.

Different releases are used for different evaluations. The authors

show that there is little difference between releases 003 through 005

but it would make for a cleaner, and more up to date, analysis to use

release 005 throughout. The only exception being to show differences

between releases 002 and subsequent releases.

I would like to see a map in the main paper showing the "Inner Arctic

Ocean" region as the study region introduced as part of the methods.

This would focus readers attention on the analysis region up front.

Figure 8 is another example of a figure that would benefit from having

labels such as a) sea ice freeboard. Parameter names are on the

y-axes but they are small. Panels a, b, etc should be referenced in

the text.

There are a number of places in the text where important statements

are put in parentheses. I think it would improve readability to

rewrite these statements as part of the main text. Some of these

parenthetical statements are unnecessary.

## Specific comments

L60. "is *being* developed"

L63. Suggest "collected to estimate sea ice thickness"

Section 2. I think it would be helpful to summarise upgrades to IS2

processing, NESOSIM and ATL20 gridding in a simple table.

L111 prefer "km" to be consistent.

L124 "0-3 cm freeboard changes at basin scales". Does "basin-scales"

refer to the Inner Arctic region used in the current paper? Maybe say

"an increase in basin average freeboard of up to 3 cm.

L139 Suggest "New releases of ATL07 and ATL10 also reflect upgrades to

the underlying ATL03 processing, such as improvements in geolocation.

L141 and 110. ATBD for ATL07/10 use "surface reference" rather than

"reference sea surface". To avoid confusion it might be better to use

the same terminology as the ATBD.

Figure S1. Would it be better to have this figure in the main text?

Also, the point here is that the number of reference surfaces is

reduced from rel002 to rel003 because dark leads are not used.

However, the count difference is positive. It make more sense to me

to have this reduction as a negative number.

L190 Effectively the /beta and /gamma terms in equation 1 are

corrections to solid precipitation. It is not clear to me what the

difference is between the two terms. They could be combined into a

single loss coefficient.

L217 Do you mean "For each OIB snow depth product, snow depths are

binned into 100 km grid cells using a drop-in-the-bucket averaging

procedure. For each grid cell, the median snow depth of the three

products is then assigned as the grid cell snow depth". So in all

cases, you are taking the middle value. If the number of products was

larger, I can see this as an acceptable approach to

avoid outliers but for just three values, you can't really identify

an outlier. It would seem that the mean is a better estimator.

L 230. "within reason" This needs some clarification. Are there

limits you can set on depth or start date?

Figure 3. The left panel is busy. I suggest having a separate panel

for October and April. The horizontal grid-lines should be lighter or

removed.

L254 One of the arguments for not using the Warren climatology for

snow depth is that it is not represenative of the present day

conditions. The previous paragraph and Figure 3 have been used to

argue that recent years snow depth are also lower than average and may

be declining. So why would you use a climatology of NESOSIM.

Wouldn't using output from an operation product or low latency

reanalysis be a better option?

L266. The redistribution method needs a reference.

L296 The smoothing/gridding procedure needs more explanation. It

would be helpful to say why each of the steps are done. Why use

Delaunay triangulation - generally this method is used to interpolate

unstructured data? Presumably the KDTree algorithm is to speed

up the search for neighboring cells.

Figure 4, L343. How do these look for other months and for other years? No need to show

them but a comment in the text would be helpful.

L354. Significant or major?

L356. Prefer peak rather than mode. Mode could be confused with

operating mode.

Figure 4. How many segments are used to generate these plots? Are

dark leads more common in November?

L370. The name NESOSIMv1.1clim has not been introduced yet.

L389. Suggest "In Figure 6, we show the correlation coefficients,

mean bias and standard deviations of ICESat-2 monthly gridded ice

thickness from rel002 and rel003 compared with ESAs CryoSat-2."

What are the standard deviations of?

Why mask data less than 0.25 m?

Figure 6. I suggest removing the shading and, for each month, plot

release 002 and release 003 as separate columns. That way you can see

the ovelap. The shading suggests the data is continuous rather than

discrete monthly data.

L445. NESOSIM presecribes snow density for new and old snow. The

bulk density is a weighted average of these two values. How much can

be read into variations in density?

Figure 8. Why is sea ice concentration lowest in October? Is this an

artifact of averaging.

Figure 9. The flow vectors obscure the thickness data. They are not

really discussed. Are they necessary? Could they be relegated to

supplemental material?

Line 535. Care needs to be taken with ERA5 (or any reanalysis)

near-surface variables over snow. ERA5 snow parameterisation is still

a single layer, which does not produce realistic surface fluxes

(Arduini et al 2019).

L540. Are three years of data enough to make a statement about

strength of coupling?

L591. This seems to contradict what is shown in Figure 4.

Figure 12 and 13. The multi-year ice fraction panel is not needed.

Arduini, G., Balsamo, G., Dutra, E., Day, J. J., Sandu, I., Boussetta,

S., & Haiden, T. (2019). Impact of a Multi-Layer Snow Scheme on

Near-Surface Weather Forecasts. Journal of Advances in Modeling Earth

Systems, 11(12), 4687–4710. https://doi.org/10.1029/2019MS

Citation: https://doi.org/10.5194/tc-2022-39-RC1
- AC2: 'Reply on RC1', Alek Petty, 12 May 2022
  
  The comment was uploaded in the form of a supplement: https://tc.copernicus.org/preprints/tc-2022-39/tc-2022-39-AC2-supplement.pdf
  
  Citation: https://doi.org/10.5194/tc-2022-39-AC2
AC1: 'Comment on tc-2022-39', Alek Petty, 08 Apr 2022

We would like to note that after submission of our preprint, a paper that analyzed at threee years of winter Arctic thickness with ICESat-2 but using CryoSat-2 radar freebaord measurements to infer snow depth was published in GRL: https://agupubs.onlinelibrary.wiley.com/doi/10.1029/2021GL097448. A different approach to our method of using a snow accumulation model to constrain the time-varying snow depth (and density too in our case).
Our preliminary analysis has indiciated a very high degree of agreement between those estimates and the final rel005, gridded monthly mean results reported in our study in terms of mean snow depth, thickness and the ~50 cm multiyear ice thinning.
We expect to add a note on this to the revised manuscript.
Alek Petty

Citation: https://doi.org/10.5194/tc-2022-39-AC1
RC2:
'Comment on tc-2022-39', Anonymous Referee #2, 14 Apr 2022

This paper discusses improvements in the ICESat-2 (IS2) processing of sea ice thickness retrievals from different releases of the IS2 products. As such it feels more like a NASA technical report that discusses how the different versions change the thickness retrievals. The author previous published in 2020 on the processing chain to IS2 and I do not find that with the changes this now warrants an updated assessment of thickness changes and a new publication. The question is what do we really gain from this paper vs. having a NASA technical report on the changes in data processing?

This is in part because any sea ice thickness (SIT) assessment depends strongly on the choice of snow loading used. It also depends strongly on the choice of snow depth processing applied to OIB data for validation of your snow loading, and the seasonality of this validation period. It seems that with the changes presented to NESOSIM there are minimal changes anyway to the snow loading and thus it is the changes to the lad detection that seem to have the largest influence. To make this paper more impactful and not just a technical report on updates to IS2 data processing, one way forward could be to assess the choice of snow loading in the IS2 SIT retrievals. Since Zhou et al. (2020) already showed how different these data products can be, and other studies such as Mallett et al. (2021) and Glissenaar et al. (2021) detailed how using different snow loading can lead to different trends, one really cannot trust any assessment of thickness changes over the 3 years evaluated here without addressing the uncertainty in the snow loading. How would Figures 8-10 look using different snow data sets for example? You state that it’s the freeboard processing that results in the largest changes (again indicative that this should be a technical report), but given the wide variety of snow depth data sets out there, the 3 years analysed here may be quite different depending on data set applied. And is analysing 3 years of data really useful for assessing drivers of SIT variability? At the moment I really do not see much value in having this as a publication in The Cryopshere for an incremental update to the IS2 processing chain. That doesn’t mean it shouldn’t be published someplace, but The Cryosphere should be for more impactful papers.

More specific major comments:

It is stated that NESOSIM is updated to use ERA5 calibrated against CloudSat and a new blowing snow term. However, there is no validation of this blowing snow loss term, or discussion on how the coefficients, i.e. wind action threshold, blowing snow loss coefficient and atmosphere snow loss coefficients are derived and validated. There is no in situ evidence that a significant amount of snow is lost to leads in the winter (any lead in winter quickly refreezes in a matter of a few hours), and there is no assessment here of the magnitude of this new snow loss term, and comparison to the old (and presumably still used) snow loss term to leads. Since SIT retrievals depend very strongly on the snow loading, at a minimum some quantitative analysis is needed on what these changes represent in terms of the overall snow mass, and some science justification is needed for doing this in the first place. It seems that some artificial tuning is based on trying to reduce the mean difference with OIB snow depths, but of course those are not perfect either. And they are done only in the springtime, and the question is how valid this bias-correction is for other months during the winter season?

The author is wrong about what SM-LG does at the end of summer as it keeps the snow cover in places where it doesn’t entirely melt out. Also, snow can start to accumulate before September in the Arctic, and thus it seems these changes are made purely to reduce your bias but there is no physical reason to justify these changes. I do not think that because NESOSIM matches mW99 in October that you can conclude you have “good” snow depths. In fact given delays in freeze-up, I would expect much thinner snow in October compared to mW99 based on the fact that ice is forming later than it used to.

Zhou et al. (2020) showed large differences between the various atmospheric reanalysis-based approaches to snow loading as well as the remote sensing-based retrievals, with the SM-LG (Liston et al. 2020) providing more spatial structure to the snow depth/density distributions, whereas products such as NESOSIM are artificially smoothed products. I see you get around this by taking your smoothed products and then adding some artifical spatial structure to match IS2 resolution, but why regrid to 100km in the first palce? Anyone who has spent time on sea ice knows the snow is very heterogeneous and thus the artificially smoothed 100km NESOSIM product seems unrealistic. Some justification for regridding the snow depth to 100km is needed and why you think this artificially smoothed data set is a good representation of snow over sea ice. Also, the impact of the redistribution then to 30m resolution is needed.

Some assessment of the impact of using different ice motion products is also needed. It is not true that updated ice motion from NSIDC is not available, and the author could have contacted the data provider for updated ice motion fields. Since OSI SAF and NSIDC ice motion vectors to not agree, how does this influence your results? It is also unclear now how the Warren et al. climatology is used, are you assigning MYI snow depths on September 1 based on W99 and then accumulating snow? And finally, I’m not sure why so much smoothing is applied to both the snow and SIT retrievals, and some justification for this is needed. What does your SIT data product really give us if so much smoothing is applied? Snow and ice are highly spatially variable and thus is this a data product that is really useful to the community if it is artificially smoothed? Wanting “pretty” maps is not a reason to do this.

I do not find much value in the CS2 to IS2 comparison. In particular, now suddenly the mW99 climatology is applied after spending much time discussing updates to NESOSIM. This seems to be only because you want to use existing products out there, which we already know are not realistic because they do not have a realistic snow loading representations. Instead, maybe comparison of the freeboards would be a better thing to do, as you can convert the IS2 snow freeboards to ice freeboards with your snow loading from NESOSIM. Then we can better understand differences on the ice freeboard level, and may be get some insights into where the dominant scattering surface from CS2 is located as well as the influence of surface roughness on the freeboard retrievals. The use of PIOMAS is also not useful in my opinion, it’s a model and has known biases, so adding it here just distracts from the overall paper.

The abstract is too long and reads more like a technical report.

Citation: https://doi.org/10.5194/tc-2022-39-RC2
- AC3: 'Reply on RC2', Alek Petty, 12 May 2022
  
  The comment was uploaded in the form of a supplement: https://tc.copernicus.org/preprints/tc-2022-39/tc-2022-39-AC3-supplement.pdf
  
  Citation: https://doi.org/10.5194/tc-2022-39-AC3

Peer review completion

AR: Author's response | RR: Referee report | ED: Editor decision | EF: Editorial file upload

ED: Reconsider after major revisions (further review by editor and referees) (07 Jun 2022) by Yevgeny Aksenov

AR by Alek Petty on behalf of the Authors (10 Jun 2022) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (11 Jul 2022) by Yevgeny Aksenov

RR by Anonymous Referee #3 (29 Jul 2022)

Suggestions for revision or reasons for rejection

Review of

Winter Arcticc sea ice thickness from ICESat-2: upgrades to freeboard and snow loading estimates and an assessment of the first three winters of data collection

by

Petty, A. A.

Summary: With the ICESat-2 satellite laser altimeter launched in September 2018 the sea ice community has access to very high resolution observations of the sea ice topography and hence novel means to retrieve the sea ice thickness distribution. This manuscript details the impact of recent changes in the processing of the ICESat-2 data relevant for such retrieval. It details further the impact of updates of an important data set of ancillary information required for this retrieval: the snow loading. The manuscript convinces with comparably clear messages of these impacts mentioned and comes up with a presentation, interpretation and discussion of the seasonal development of the freeboard, snow and sea ice thickness values at basin scale.

The present manuscript falls into the category of work typically connected to new satellite missions when the (raw) processing is still ramping up and updates in the derived products are issued at a comparably high frequency. It is therefore of a quite technical nature - albeit it has a considerable fraction of geophysical interpretation. I was wondering therefore, whether the authors have considered to hand in this manuscript also into the journal "Earth System Science Data"? I'd say it is at the verge between both journals.

I should note that I read this manuscript in the second round of reviews - which explains why I refer to comments of the previous review at a few occasions.

General comments:
GC1: The authors need - throughout the manuscript - clarify and correct the usage of "total (sea ice plus snow) freeboard" and "sea ice freeboard". Currently, these terms appear to be mixed and they are in part misleading the discussion of the results. A laser altimeter observes the total freeboard. A radar altimeter is supposed to observe the sea ice freeboard. This must be corrected in the manuscript both in the text as well as in all figures and tables where this applies. You will find repeated notion of this in my specific comments. This is the main reason why I suggest that this manuscript requires another round of major revisions because it might require some time to correct this in an appropriate way.

GC2: Despite a high fraction of technical details there are a few technical and/or methodological issues that, to my opinion, are not laid out sufficiently well. To these belong i) the calibration of the parameter gamma, ii) the evaluation of the NESOSIMv1.1 product for other months than April, and iii) the description of how you derived the sea-ice thickness uncertainties.

Specific comments:
L19-21: Is an enhanced agreement with CS-2 based sea-ice thickness data that desirable given the fact that penetration depth of the radar signal into snow plus ice-snow interface processes and properties play a much larger role therein?

L35-46: In this paragraph you speak of "sea ice freeboard" in the context of laser altimetry. I strongly recommend to clearly differentiate between sea ice freeboard and total (sea ice plus snow) freeboard which is the quantity derived from the ICESat-2 elevation measurements first. Any conversion into sea ice freeboard (if need be) requires knowledge of snow thickness and density. It could be the that product you are using is named "sea ice freeboard" but physically it is not.

- What I am missing in front of this paragraph is that classical paragraph that tells us why satellite altimeters are such an important tool to observe the polar regions and why this is important. This would move your paper away from the impression one of the reviewers had that this is merely a technical report. In other words: So far the paper is not put into a larger context sufficiently well.

L51-53: "Additional .... procedure" --> You could stress perhaps, that this is a high skill for daylight, clearsky conditions.

L108: "Sea ice freeboard" --> I assume this is in fact the total (sea ice plus snow) freeboard and should be referenced like this in the paper.

Section 2.1.1: I can understand that one of the previous reviewers got the impression to read a technical report rather than a scientific paper. This section appears to be quite long given the comparably little information that appears to be relevant for the content of the paper. To my opinion, this section could be condensed such that the main changes that determine the differences between rel002 and rel005 are highlighted while the reader is referred to the (regularly updated) technical documentation and change log associated with every release for the less relevant changes.

L195: How is the calibration of gamma carried out?

L212/213: "Here we choose instead ..." --> This recalibration has the disadvantage that is is only valid for April snow conditions. Is that correct? How reliable can NESOSIM v1.1 then be for the rest of the freezing season. How is this period evaluated?

L232-241: It is still not clear to me after these lines what the initial snow thickness on the sea ice on September 1 is.

L232: It is still not clear how you tuned gamma.

L251: "declining trend" --> Is suggest to either write "decline" or "decrease" or "negative trend". A declining trend is a trend which is not stable over time but where the change of the parameter with time is decreasing over time.

- I am sure you are aware that this decline in snow thickness has several causes, beginning with the change in ice age, over changes in snow accumulation (period), actual ice drift vectors and retrieved ice drift vectors, to potential inconsistencies and spurious trends in the input data to NESOSOM v1.1. Because of these it might be a good idea to not overinterpret this decline. In addition: The tuning / evaluation of the NESOSIM v1.1 is limited to April ... and hence the time series shown for October could be less credible / reliable than the time series shown for April.

L272-276 / Figure S3: Please check these lines; it seems they contain two times almost the same sentence.

- How much ice is in the Kara Sea in October? I am not overly convinced that this particular region is well suited looking at October snow thickness on sea ice. I am wondering where the ice edge drawn in the Kara Sea for October comes from.

- Figure S3 units are cms. Is this correct?

- The color table used in the snow thickness maps on the left does not convince me that there is "measurable" snow thickness on Kara Sea sea ice. It looks white.

- Apart from these comments, I guess I have a conceptual problem with on the one hand striving to produce a temporally reasonably fine resolved snow thickness data set for proper sea-ice thickness retrieval and on the other hand generating (again) kind of a climatology.
Shouldn't the strategy be to use the auxiliary data sets when these are fully available? I mean, you also switched to a different daily sea-ice motion product for the time period that NSIDC drift is not available. You are not computing a climatology. Also, since you don't show these NRT products in your paper and only deal with the winter season 2020-2021 as the most recent, I believe you could condense this part of the investigation considerably. Perhaps you could mention at the side that a climatology based on NESOSIMv1.1 based on the 2010s (which would exclude 2020 by the way) provides an October snow thickness which is about 1 cm smaller than mW99 and an April snow thickness which is about 5 cm larger than mW99 for the inner-Arctic region you selected. You could then argue that most likely - if one still wants to use a climatology - then the NESOSIMv1.1 climatology might be a better choice ... but your results in fact only show the difference but do not indicate which of the two data sets is the more accurate one. I therefore find this comparison between mW99 and the 2010s snow thickness climatology not overly useful and I cannot recommend to keep this in the manuscript. To my opinion this sets the wrong signal.

- Did you try to compute a similar time series as shown in Figure 4 using W99 / mW99 and available multiyear ice areal fractions for "your" Inner Arctic region to see whether the negative trend in NESOSIM snow thickness is also visible in W99 snow thickness (simply via the change of the multiyear ice versus first-year ice partition)?

L279-298: Given the coarseness of the NESOSIM snow thickness data I am wondering whether from the view point of spatial scales involved it would make much more sense to discard the interpolation from 100 km x 100 km over more than 4 orders of magnitude to 30 meters and instead work with 10 km along track mean freeboard estimates. With that the interpolation would just be about one order of magnitude - at least into one direction.
But lets see what you will write about this in your discussion section.

- I note that your description of the error estimation in Lines 284/285 is not overly specific. If there are no further details given elsewhere I recommend to specify better how you carried out this step.

L307: So in the monthly sea ice thickness data you use the CDR version 4 but in NESOSIMv1.1 you use version 3. This difference in versions is possibly not dramatic, isn't it?

L326-332: I am sorry, I don't get why you prefer to compare ICESat-2 sea ice thickness data based on rel005 of ATL10 with the four CS-2 sea ice thickness products using THEIR snow loading. What is the motivation? What are you aiming to show here? It seems you are using the CS-2 sea-ice thickness products as a benchmark against which you would like to reference your product. Is this a viable approach given the difficulties / assumptions these radar altimeter products need to deal with? If you find a large bias / RMSD ... I'd say this is fine ...
In addition, you only use data of strong beam #1 here - to be consistent with your previous work. Are you not interested in how your updated sea-ice thickness product (see the many updates you wrote about so far in the manuscript!) compares to all these other products?

Section 2.6: This section appears to need some more work at it seems not to be complete. Also, it is not clear what the ERA5 data are for here. "To assess the winter Arctic atmospheric conditions" reads as if you made an investigation of the atmospheric conditions such as comparing ERA5 with rawinsonde and in-situ observations or the like. You need to work on your wording. Also, the last sentence does not fit quite well. I guess you merely perform a consistency check whether ERA5 2-m air temperatures support your assumptions about the physics and conditions but the nature of what you do is far away from an "assessment". It is an inter-comparison.

L362-365: The derivation of individual freeboard values from surface heights and approximated sea surface level implies that there are negative freeboard values as well. What is their fraction and what did you do with these?

L366: The results shown in Figure 6 are for your inner Arctic region or the entire Arctic?

L399: I see the "performance" of the v1.1_2010s snow thickness climatology in a slightly different way than you. I would state that in April it appears to be a good representation of what Nv1.0 and Nv1.1 provide. But in January and particularly in November the distributions differ considerably, casting doubts about the credibility of this climatology; these doubts are justified looking at the sea-ice thickness distributions where usage of the climatology provides a substantially smaller modal (1st mode) sea ice thickness. If used for model initialization, assimilation or intercomparison studies the sea ice thickness data based on the climatology are certainly more problematic - especially at this critical time of the freezing season. I cordially invite you to tone your statements about the climatology into this direction rather than saying, well, all data sets look just fine with some minor differences.

L403/404: "In general ..." --> I suggest to refer to a table or figure in your manuscript which supports this very general comment.

L468-470: How do the W99 snow densities compare to your densities? Can you identify hotspots in space and/or time where the W99 snow density would be considerably off compared to your results?

L478-481: "For example: thinner ... mean thickness." --> consider revisiting and perhaps correcting these statements in light of so far failing to adequately discriminate between total (sea ice plus snow) freeboard and sea ice freeboard in your manuscript.

L486-510: I am sorry, but I do not see the added value of anomalies computed from three winters of data. To my opinion this Figure 12 and this paragraph can be deleted without substantially changing the relevance of the manuscript.

If you decide to keep both, then I recommend to condense the text considerably and focus on those highlights that seem most obvious to be related with each other. Please keep in mind that a positive snow thickness anomaly in April does not need to coincide with a negative sea ice thickness anomaly - simply because the snow thickness during earlier in the winter determine how much the ice had the chance to grow thermodynamically. There is a temporal dimension involved which cannot be interpreted from the maps shown. Also consider to mention the retrieval noise of the parameters presented to foster readers to disentangle what is noise from what is a real signal.

L514-516: "In general ... thicker" --> Does this intercomparison result fit to other results where, e.g. PIOMAS data were compared to in-situ, sub-marine and ICESat data? In my mind there is this result from somerwhere in the published literature that PIOMAS over-estimates thinner ice and under-estimates thicker ice - a result that is not that well confirmed by your results - particularly not for the second winter period.

L545-551: "These ice type .. this limited record" --> What I am clearly missing here in the discussion is the role of different snow thickness conditions. And this discussion could be also linked better with the 2m-air temperature and longwave radiation data from ERA5.

- What is interesting to see, for instance, is that the sea ice thickness increase between November and February is larger in 2018/19 than in 2019/20 despite a) the sea ice itself being thicker and b) the snow thickness being larger by about 5 cm. Wouldnt' one expect that thicker ice with a thicker snow load grows less thermodynamically than comparably thin ice with a thinner snow load - provided the oceanic and atmospheric forcings are roughly the same?

- Another observations is that from November through January the freeboard values are the same for 2019/20 and 2020/21. At the same time snow thickness is about 5 cm larger for 2020/21. This means the sea-ice freeboard which is your total (sea ice plus snow) freeboard minus snow thickness is actually smaller by 5 cm for 2020/21 than 2019/20 which would point to about 40 cm thinner sea ice during these months in 2020/21 than 2019/20 and is actually confirmed by the respective panel. So here your observations are consistent in themselves. The fact that over these 3 months there is 20 cm more ice growth in 2020/21 compared to 2019/20 despite a more or less constant snow load could be discussed more specifically in light of the balance between thicker snow isolating better while thinner sea ice isolates less and the ancillary data used (drift, ERA5).

- I guess my recommendation is to discuss specific observations in your data time series in a comprehensive way, taking ERA5 and drift information of Fig. 11 into account instead of kind of listing what is shown in the respective panels without connecting the information well to your observations.

- Did you check, by the way, how ERA5 treats sea ice and its snow cover? How well is the snow thickness on top of sea ice resolved and is the sea ice allowed to grow and melt? Has it a variable thickness that would support discussions about feedback between 2m-air temperatures and ice and snow thickness?

L562-564: "For example ... " --> As always the interpretation of such maps offers potential for subjectivity and might depend stongly on the observer. I for my part rather see that the 2019/20 winter is different in terms of the strength and extent of the Beaufort Gyre - including the drift speed of its southern limb - as compared to the other two winters considered. Since the anomaly maps of these two other winters do not provide consistent information, i.e. exhibit different spatial patterns and signs of the anomalies, I am not convinced that the possible relationship between these anomalies and the ice drift pattern should be discussed the way you did. I note in this context, that the anomalies you are referring to here are mostly below 0.5 m in magnitude. How large an anomaly needs to be to be larger than the retrieval noise?

L615-617: This statement is not sufficiently well supported by the results given in the manuscript.

L619/620: "although ... scales." --> Also this part is not sufficiently backed up by the results presented in your manuscript.

L638-644: I am wondering whether you perhaps could be a bit more specific here because there are snow depth observations from several sovjet drift stations and in addition the N-ICE2015 and the MOSAiC campaigns provided quite a lot of useful snow thickness data to be used for a better calibration and/or evaluation of NESOSIM.

L556-674: I am not sure this "sea ice thickness reconciliation" paragraph should be kept as is. My impression is that it could be potentially misleading. What I am missing is i) a more clearly formulated statement that ICESat-2 could perhaps be the benchmark sensor for sea-ice thickness retrieval rather than CryoSat-2 - simply because of the more well defined main reflection horizon and the smaller number of snow processes and properties influencing already the freeboard retrieval. ii) What could also be more in the focus of future developments is a better handling of the different spatio-temporal scales involved - both in the retrieval process but also in the evaluation of the products. All parameters, freeboard, snow and ice thickness have their specific distributions. Two issues that I do not find solved satisfactorily is the error propagation of the downscaling approach from 100 km to 30 m and the propagation of the influence of substantial difference in the acquisition time of ICESat-2 data within one grid cell. These (and others) would be enough material for further improvement and I currently do not see the need to write that much about the potential of radar altimetry. But this is clearly my personal view based on this manuscript and on the results presented in similar papers.

Figure 1: I don't find this figure particularly well developed. Neither is clear that sea ice comprises level and ridged parts nor is clear that a radar measures sea ice freeboard while a laser measures total (sea ice plus snow) freeboard. The fact that the laser signal might also penetrate into the snow a bit is neglected. The role of the "internal ice stresses" is not clear, neither is mentioning of keel depth for satellite altimetry of sea ice. Not represented well is that radar waves may in fact be reflected at the snow-ice interface or even from within the sea ice but that they may also not reach to that interface at all. While the figure is for winter, which is good, the caption refers to the key challenges and one of these definitely is to measure freeboard during summer in the presence of melt ponds. So there is in fact a lot more one could and potentially should include into this schematic figure.

Figure 2: Particularly in the bottommost row the white circular area is not a well defined circle. What is the reason for that? Is there a higher probability for data drop-outs near the pole?
The main aim of the paper is to show the differences between rel002 used Petty et al. 2020 and rel005 used in this paper. I am wondering what can learn in terms of science from the many other panels and whether it wouldn't be sufficient and more straightforward to concentrate on the differences between rel002 and rel005 only.

Figure 3: What about the median biases for both cases? I note that (b) shows more cases than (a). Why?

- Personally, I would make the lengths of x- and y-axes the same when the data range is the same - here 80 cm for both quantities shown.

Figure 4 c) What is the reason for the violins for Oct. through Jan. to look cut off at the side facing higher snow thickness values?

Figure 5: This map contains many regions that are not used in the paper. It might make sense to color all regions not used in the same color as open water, only explain the acronyms / names of the regions actually used, and add that this map is "adopted" from a region mask provided by ...

Figure 6: The x-axis title needs to be changed into "total freeboard". Please provide the meaning of the dashed lines in the caption.

- I strongly recommend to be consistent in the notation between the figure and the caption. You write r002, r003 and so forth in the figure but write "rel002" and "rel005" in the caption text; this is inconsistent. Similarly, in the figure you write "bnum1", "bnum3" and so on, in the caption text you write "beam #1, #3" and so on. This is inconsistent as well.

Figure 9: I note that the sea ice thickess uncertainty seems not to be influenced by the substantial differences in the "mean day of the month" varying over a very short distance the ICESat-2 data. Hence in one 25 km grid cell ICESat-2 might come (on average) from the first few days of a month while in the adjacent grid cell this data might stem from the end of the month. I would expect that thermodynamic sea ice growth and dynamic processes can add substantially to the uncertainty - most likely especially during months October through January. Did you check this?

Figure 14: I guess it would make sense to not show values for September but rather begin with October as this is when the freezing season commences. There is room for one more panel in which you could put the fraction of the FYI relative to the total sea ice area of your Inner Arctic region. The same comment applies to Figure 15, but here for the MYI fraction of course.

Pure typos / editoral comments:
A general editoral comment upfront: Since you advertize at the end that basically all your results and the processing is available as jupyter notebook you might want to scan you paper and reduce the number of repeated mentioning of this. I think you overdo it a little bit.

L28/29: "Mean first-year ... negligible" --> possibly you refer to changes or differences?

L139: "2we" --> "2, we"

L218: "consensus" --> In the modeling world one would speak of an ensemble mean - or in your case apparently an ensemble median. I would find this a better expression because "consensus" is something that usually involves some discussion, some weighing perhaps, some additional constraints. What you do, however, is taking mean and median, i.e. use a statistical tool. Hence, I would recommend to change the wording accordingly - here and later in the text.

L231: "halving the blowing snow open water coefficient" --> would you mind to show the respective equation in this paper as well so that everybody immediately understand the effect of what you stated here?

L247-249: You are providing enough information about this region map in the context of Figure 5 I guess and can delete the sentence "Out Inner ... Figure 5" and instead refer to this figure at the end of the previous sentence.

L304-306: "Our monthly ... ATL10 data" --> namely what ancillary data?

L309: "on to" --> "onto"

L311-317: This reads a lot like again being in a technical report. Have you thought about publishing this manuscript in the journal Earth System Science Data? Would that be a more adequate journal for your manuscript being comparably rich in processing and product details, bug fixes, novel masks, and so forth? I slowly begin to second that other reviewer who had difficulties to see the merit of this manuscript in The Cryosphere.

L374-376: Since you do not consider June I suggest to remove June and the respective value from this sentence.

L407: Here you write rel003, in L413++ you write rel005. What is correct?

L413-424: I am wondering whether you need to list all ranges for all parameters shown in Figure 8. Do you see a chance to simply let speak Figure 8 for itself and perhaps only put the highlights here - perhaps along the lines that correlation coefficients in general increased by around 0.1, that biases change (not necessarily reduce) by about 30 cm and that standard deviations reduce by, on average, 0.2 m. This might make this part of the paper easier to read.

L417: "58" --> "0.58"

L434: "i-j" --> "i-k"

L450/451: "The data within this domain ... Figure 10e)" --> You need to put labels a) to f) to the panels in Figure 10 if you want to refer to them.

- I cannot see any sea-ice concentrations within the range given here (40-60%) in your Figure 10 e; something needs to be corrected here.

L533: "snow depth in November ... winters" --> you could denote in addition, that in Feb to April, however, differences in the snow thickness on the sea ice are between 2 cm and 4 cm.

L611: I suggest to use "significant" only in the context of statistical tests which I could not see in your manuscript. Hence "considerable", "notable", or "substantial" might be a better wording here.

L654/655: "The extension ... estimates" --> While this is true it would require first and foremost that we have (more) accurate freeboard estimates during summer from ICESat-2?

L920: "now depths" --> "snow depths"

L958/959: Perhaps better (and more correct): "The background dark grey shading in panels a to k is the CDR sea ice concentration shown in panel l."

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ED: Reconsider after major revisions (further review by editor and referees) (17 Aug 2022) by Yevgeny Aksenov

AR by Alek Petty on behalf of the Authors (05 Oct 2022) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (28 Nov 2022) by Yevgeny Aksenov

RR by Anonymous Referee #3 (02 Dec 2022)

Suggestions for revision or reasons for rejection

Review of

Winter Arctic sea ice thickness from ICESat-2: upgrades to
freeboard and snow loading estimates and an assessment of the first
three winters of data collection - Revision

by Petty, A. A., et al.

I am not providing a summary of this manuscript, refering to my previous review.

What I found here now is a remarkably well to read paper which I like to see published soon. The authors spent a lot of effort responding to my comments and amending their manuscript where these comments could result in an improvement or clarification of the presentation. Thank you for considering the comments the way you did; this is a good appreciation of my work.

I have neither general nor specific comments that would point to issues with the content. I only have two handful of editoral comments which are to your descretion and a final careful check by the editor.

L176 and L221: How was the regridding done? Nearest-neighbor interpolation? Bilinear?

L388: Which snow depth is added here?

L411-415: I am a bit puzzled to read that a "decrease of 1.2 cm in November 2018 " is in line with "October 2019 ... and 2 cm increases" . Did I understand something wrong here?

L433/434: "are thinner than ... 17.7 cm to 15.5 cm)" ... --> Could it be that you should switch the two figures such that it reads "15.5 cm to 17.7 cm"?

L521-523: Please check your writing here. In Line 521 you refer to Figure 10 ... but I guess you mean Figure 12?
Then you refer to "is generally lower concentration ... Figure 10e" ... but I don't get what concentration you mean here ... I assume sea ice concentration. But Figure 10e does not exist ... so this has to be Fig. 12e, right?

L578/579: "limited to October onwards ... lack of ... data in this month" --> From Fig. 15 I can see that you include October ... I guess it is semantics but it might be more clear if you write "before October" or "before this month" instead of "in this month"?

L594: "thicker" --> "thinner" ... assuming that you are referring to sea ice thickness in Nov/Dec 2020/21 in comparison to Nov/Dec of the previous two winters.

L698: Suggest to replace "shown in" by "by" to avoid the double mentioning of "shown".

L713: Would it make sense to cite the respective paper by Farrell et al. in this context?

L730/731: Just as a comment: Given the fact that there are attempts to combine Ku- and Ka-Band radar altimetry to infer snow thickness on sea ice I am not sure mentioning Ka-Band radar altimeter returns being considered to come from the ice-snow interface is a good idea.

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ED: Publish subject to technical corrections (02 Dec 2022) by Yevgeny Aksenov

AR by Alek Petty on behalf of the Authors (04 Dec 2022) Author's response Manuscript

Short summary

We present upgrades to winter Arctic sea ice thickness estimates from NASA's ICESat-2. Our new thickness results show better agreement with independent data from ESA's CryoSat-2 compared to our first data release, as well as new, very strong comparisons with data collected by moorings in the Beaufort Sea. We analyse three winters of thickness data across the Arctic, including 50 cm thinning of the multiyear ice over this 3-year period.