Dear Authors,

thanks for uploading your responses-to-review. Both reviewers have raised in parts substantial criticism. Therefore, I decided to send the paper out to re-review. Please make sure that you submit the revised version together with a track changes version. Note that I will be out doing fieldwork in December to mid-January. I apologize in advance if this should cause delays.

Kind regards, Reinhard Drews

P. S: I concur with one remark of RV2 that it was not easy to distill clear take-away messages in the initial version. It is ok that you follow the standard TC guidelines, but still make sure that, e.g., results and discussion are clearly distinguishable.

Dear Authors, thanks for handing in your revisions. As indicated earlier I will now send the paper out to re-review. Kind regards, Reinhard Drews

Dear Authors,

Thank you for submitting the revisions tc-2021-168. In the meantime, I have received two re-reviews. Both reviewers acknowledge your responses and note corresponding improvements in the revised version. I add to this, that the paper presents a strong observational dataset of airborne and ground-based IPR with much scientific potential.

Unfortunately, a number of critical comments have been raised again and the overall impression of the paper from both reviewers remains weak. I concur with the majority of the concerns raised, and below I also provide some additional thoughts from my own reading. There is a lack of clear take-away messages and some claims made in the paper are not fully substantiated by the data analysis.

Hence, the manuscript is not ready for publication in The Cryosphere. Substantial revisions are required including data analysis. If you decide to address this in another round at TCD, I will send out the paper for another review including at least one new reviewer. Alternatively you may want to consider to fully restructure the paper with a clearer research focus and make it a new submission. Both options require a significant amount of work, but given the reviews and my own reading I don’t see a way around this. I hope that you perceive the remarks as constructive and helpful for improvements.

Kind regards,

Reinhard Drews

The comments mentioned below are in addition to the two reviews, they are not intended to replace any of the comments from the reviewers.


Lack of basal radar reflections:
I am not convinced that frazil ice accumulation is the only explanation for the lacking ice-ocean boundary in the radar data. Did you consider the basal slope? In Figure 6d I cannot estimate the slope because the x-label is given in Trace number (should be ‘distance’) and the y label in traveltime (should be ‘depth’). Do you have an example where the lack of signal occurs in both airborne and ground-based IPR? This could be helpful to investigate effects of the different radar systems. (Fig 6a suggests that the lack of basal reflections does not occur in the spatially more extensive airborne dataset. Is this linked to the different radar systems used?).

Flux gate analysis:
Why not close the gates (i.e. consider the flux into and out of a box)? Given that the flux differences between some gates are small, it seems important to exclude influx/outflux of ice between the two main gates. Neckel et al., 2012, J. Glac. would be an example for this (no need to cite this paper of which I am a co-author).

From thickness change to basal/surface melting:
I stumbled across section l. 252f because at first I didn’t grasp the meaning of ‘vertical melt rates’. I believe it is a lumped term that should include either basal or surface melting, but this was not clear to me at first and others may feel the same way.

I am not convinced that the points marked in Fig. 3 belong to the same draft apexes and keels (i.e. that they are part of one feature). More radar lines would be needed to trace this coherently. Therefore, I am unsure about the inferences drawn starting l 252f. Later on, I miss a number of details about how the mass budget was closed. Do you assume steady state and is that justified given current dH/dt estimates for the NIS? Very likely many of the smaller-scale features such as the head of ice-shelf channels or basal fractures are not steady-state features in an Eulerian sense an so I don’t quite understand how the analysis works. I was entirely lost at the statement that “..100% of the thickness change in the suture zone center can be attributed to surface ablation processes.” (l. 281). How is it possible that strain thinning plays apparently now role in the thickness change for an ice shelf?

Derivation of the hydrostatic ice thickness:
This has been done many times and I understand the desire to not dwell on this topic for longer than needed. However, given that you compare the hydrostatic ice thickness with IPR thickness and you use it to derive basal melt rate fields, it suggest to get both relative and absolute error estimates. Your estimate of \pm 10 m (l. 114) contains only a \pm 1 error in surface elevation. There are other sources of uncertainties such as:

• What about the uncertainty of ice density? A marginal difference (let’s say 915 instead of 917 kg m^(-3)) already translates into 4 m for a freeboard height of 20 m. a. s. l. . Similar for the ocean water density.

• It appears that firn thickness at NIS increases with decreasing distance to the grounding-line. This will result in relative errors which may play into your basal melt rate calculations with similar arguments for the density as mentioned above.

• How good approximates the GL04C sea level in this area?

• Other studies (e.g., Shean et al., 2019, https://doi.org/10.5194/tc-13-2633-2019; Griggs & Bamber (2009, https://doi.org/10.3189/002214311796905659) consider effects of mean dynamic topography and inverse barometer effects. Is this irrelevant for the NIS?

Derivation & interpretation of strain rates:
Figs 4b,c show a fairly noisy structure (no surprise when deriving strain rates at such high spatial resolution) with some coherent bands in the along- and across-flow directions. The fast-ice/thin ice/sea ice zone that is clearly evident in the surface elevation (Fig 4a) has surprisingly no correspondence in the strain rate fields. Fig 2c shows masked velocities in this area. Somehow I don’t manage to bring this information together. I would feel more comfortable if the strain rate fields would more clearly show some first-order signatures (e.g., compression near inexpressible island) for orientation prior to going into details on scales <500 m.

The statement that when calculating the strain rate fields on a 600 m grid “..produced similar results in both spatial pattern and magnitude of strain rates, but with smaller strain rate magnitudes in the suture zone on the order of ~0.08 [per] year” is confusing. 0.08 per year is almost the maximum values shown in Fig 4b,c. This seems like a substantial difference that should be investigated. How do your results compare to Antarctic wide estimates, e.g., from Alley et al., 2018 (J. Glac.)?

Calculating strain rates on <500 m assumes a very high quality of the surface velocities both in terms of magnitude and direction. Another figure (maybe in the Appendix) that clearly shows that the strain-rates adequately capture ice dynamic signals rather than measurement noise can strengthen your arguments. It might also be worthwhile to check if the smaller scale surface undulations could lead to errors in the satellite-derived velocities which may not have used such highly resolved DEMs (e.g., using InSAR with a more coarsely resolved DEM to correct for the topographic phase).

Terminology:
To me the term ‘fracture’ suggests a basal or surficial crack that emerged because some strain/stress limit was reached. However, some of the features discussed (e.g., the longitudinal features that are directed along-flow) could also have an oceanographic origin. Maybe consider first using a more general term such as ‘basal undulations’ and then more specific terms once you circled in on a possible formation mechanism.


Editorial remarks:

I don’t see how eq (3) is actually used. Vertical strain rates are not shown. Also, is it necessary to introduce a variable (\varepsilon_1) that is always zero?

L 185: Wrong internal reference? Fig 1c does not show the slope.

L 300: What does gain of 0.5 mean ? There are many different types of gains and I don’t see how a single number would characterize this.

Fig 4d y label should be strain rate (not strain)

Fig 5 maybe a red-blue color scale with white at 0? It is difficult to differentiate between melting and re-freezing which should be a first-order outcome of this Figure.

Fig 6 trace number should be distance, y label depth.

Figure 6 b/c should detail viewing direction relative to ice-flow direction.

(A1) should have a v^2

Dear Authors,

let me apologize for the long time that it has taken to get back to me. One reason was that I couldn't easily find new reviewers. The old ones declined to continue with the review, in parts because they found that initial revisions have not improved the paper to the degree required. Because of this I decided for one new reviewer and to complement this review with an editor review. This took me much longer than expected (mostly due to teaching obligations with field mapping courses). Please accept my apologies for the delay.

Unfortunately, the evaluation of the new reviewer is weak, which means that we now have five external evaluations which have raised substantial criticism. A number of points have improved (i.e. the strain rates are more convincingly displayed, and the mass budget between Site 1 and Site 3 is now closed), but take away messages still remain in parts inconclusive.

I understand that this is an unsatisfactory result, and below I mention some points which are hopefully constructive and helpful. If you decide to revise the paper, I will have to send it out to re-review again. We need at least one positive external review to move on to TC.

Kind regards, Reinhard Drews


EC1: Derivation of basal melt rates from discharge
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The comments from previous reviewers and myself have been incorporated, and the mass budget between Site 1 and Site 3 is now closed. However, I disagree with multiple statements in the paper that basal melt in the suture zone was calculated from in-situ data (e.g. l. 295; l. 447; l. 483). It wasn't. Analysis around l. 268f explains the observed thickness change with strain thinning, basal melting and surface melting. But it doesn't "derive" basal melting per se. Instead it uses existing basal melt rate estimates (Adsumuili et al.) and puts those into an ice dynamic context. Derived are maybe the surface melting rates, b/c 0.5 m/a explain the thickness change better than 0.25 m/a.

The glider data may support existing basal melt rate estimates, but they also don't derive them. Language according to this should be changed throughout the manuscript.


EC2: Interpretation of enhanced melting at the flanks vs keel.
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Section 5.5. suggests that the Adsumuili data indicates that basal melting is in some parts stronger at the flanks than at the keels. This point is interesting, but not rigorously evaluated. If melting is stronger at the flanks, then the zone should widen downstream. If the Coriolis force leads to stronger melting at one flank, then the suture zone should deviate from flowlines (cf. Drews et al., 2021 -- no need to cite this paper). Is this the case? Without this kind of analysis, degree of novelty of these findings is limited as they have been mentioned in the previous studies cited in the paper.

EC3: Hydrostatic equilibrium.
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This point is technically well done, but it takes up a lot of space in section 5.2 for what is known already. It is not new that narrow surface expressions in REMA are not well represented in the basal morphology. The arguably new point (i.e. also features larger than one ice thickness show signs of bridging, l.368) appears buried. I suggest to significantly shorten this section (e.g., in order to provide more space for EC2) and to highlight this new point more clearly.

EC4: Integration of glider data
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I now well understand that you argue that the glider data may pick up zones of localized ice-shelf melt. However, I don't find this convincing. Figure 7a detected ice-shelf water in most areas apart from two more localized (white) zones where no such water was detected. Do you suggest that that the higher basal melt rates in the suture zone (up until the ice-shelf center) are somehow flushed out localized at the front? If so, could you indicated the pathways on the Figure?

Also, basal melting 15 km upstream from the ice-shelf front is absent and the freeze-on rates appear unrelated to the suture zone. How would that change the presence/absence of ISW in the glider data?

EC5: Detection of marine ice
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From what I understand (I may not have) you suggest that the suture zone has some fractures which go through the entire ice shelf, and which are filled with marine ice. This would be a nice new finding for me. However the radar data analysis is not fully clear in that regard. It is correct that marine ice attenuates radar waves rapidly, but then you would still expect a marine--meteoric ice interface in the radar data (cf. Kulessa et al. -- research at the Larsen Ice Shelf). This doesn't seem to be the case. Is this because the marine ice structures are vertical and not horizontal? If so, how would this imprint on the radio-wave propagation? Do you see any internal signatures in the zones where the basal returns drop out, if so, how do they related to your hypothesis of vertical marine ice?

EC6: Features in the transverse strain rates in the suture zone
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The elongated red-blue stripes (transverse compression and extension) in the suture zone are a nice signal in the strain rate maps. I believe one explanation for this could be linked to secondary flow of ice into from areas of thick ice into areas of thin ice although, then we would need two zones for transverse extension which are not observed. Nevertheless, I suggest to put this observation into the context of the study from Wearing et al. (GRL, Secondary flow of ice shelf channels).


Kind regards, Reinhard Drews

Minor Comments:
1. There are no results pertaining to the glider data in the abstract. This is another sign that the glider data is not yet sufficiently connected to the analysis on the ice shelf

l 58 What is "active basal melt"? Is there something like "passive basal melt"? Do you maybe mean "localized basal melt"?

l 133 "an \rho_i is the f" ?

l 140 ".,"

l 149 "plotted in Euro? " ?

l. 152 another Euro

Figure 5: I don't get the caption (b) and (c). If both show longitudinal strain rate they should look the same. I guess (c) refers to the horizontal shear strain rates as suggested by the title of that subfigure?

Equation 2: I understand what is done here, but the notation is sub-optimal. "i" is both an index and a distance. Maybe better use dl_i or something like this to indicate that you multiply with a length

l. 160 "REMA hydrostatic product" better "we use the hydrostatic ice thickness derived in section 3.2" (otherwise it sounds as if the thickness product is delivered by the REMA team.)

l. 176 Instead of "high-resolution" better quantify what the resolution is in meters.

l. 180 Which are the transverse and which are the along-flow directions? I believe you define this all locally, meaning that transverse and along-flow are defined with the local velocity vector. A few words will make this clear.

l 313 I find it uncommon to mention processing steps of the radar data in the figure caption.

In general: Always be specific which component of the strain rate tensor is shown,e. g., is the profile in 4d transverse or longitudinal? The y-label is unspecific.

l 267 Much of this paragraph sounds like as if it belongs into the methods, but I don't insist on this.

l 273 v should be bold, also the divergence operator is missing, it is written as a gradient.

The equation near l. 273 is unnumbered. Also, in essence, this integral is an integral over space rather than time (because no datasets are available for t_1 and t_2). Wouldn't it be easier to mark this accordingly?

l 284 Can you state what impact the smoothing has (i.e. compare the results for smoothed and unsmoothed).

l 304 Can you differntiate more? There is no active (do you mean localized?) melt in the suture zone near the ice shelf front. How would that imprint on the distributiion of ISW?

l 311 "icec)"

l 355 Not sure what the take away of section 5.2 is. This hydrostatic thickness is a damped version fo the real thickness, but this is known. It appears that features larger than one ice thickness are also damped, but why not. From what I understand this has never been fully formalized and will be a function of the specific strain regime. I suggest to significantly shorten this section.


Which strain rates are shown in Fig 8? I guess it is transverse.

l 543 "marine Ice" -> "marine ice"

Dear Authors,

thank you for another revision of this manuscript. Fortunately, we now have a positive review that suggests publication with minor revisions. I concur with this assessment and added some additional remarks which you should address prior to typesetting. This paper has had an usually long review history, but I believe in the end this has improved the paper to the degree required. I hope you feel the same way in spite of all the criticism that was raised.

We can now essentially move on with publishing this paper in The Cryosphere. Congratulations!
-- Reinhard Drews




l 18 missing comma "ice shelf draft, the cause and ..."

l 24 "The combination of thinner ice ...." this is a long sentence which I found hard to digest. Split in two sentences? Also, can you find a better word than "complex" strain rates and "complex" morphology? I believe in terms of morphology you mean that it is "spatially variable on sub-kilometer scales". In terms of strain rates, do you refer to the "along-flow banding" seen in Fig 4b? I don't think I found the best words either, but "complex" by itself doesn't really contain useful information.

l 55 "thinning rates .. "

l 62 to you mean "topography" or "thickness"? My guess is the latter.

l 99 "bed reflection" do you mean "reflection from the ice-ocean interface" or "ice base". Bed suggests sediments/bedrock to me.

l 144 "demonstrate I consistency " what does the "I" do in there ?

l 201 I don't think "if" is the right wording but "how".

l 205 "horizontal compression" --> "transverse compression" to be consistent with what is described in the legend of Fig. 4.

eq (3) make sure that that the divergence is adequately done in typesetting. Currently it is not.

l 263 "from horizontal" incomplete sentence

Please check the possibility of one column vs. two column Figures. Some Figs (e.g. Fig 3,7) are somehow in-between both options.