General comments

This paper is a major step forward for coupled ice sheet–climate modeling.  It presents results from the first simulations using a complex Earth system model with full two-way coupling of ice sheets to the atmosphere and ocean, for both the Greenland and Antarctic ice sheets (though Antarctica is the focus here).  Many earlier studies have argued for the importance of coupling and speculated on what might happen when feedbacks are included.  Here, these speculations are put to the test, in ensemble simulations to 2100 for both low-emission and high-emission scenarios.  The authors explain why their study is novel, while giving due credit to previous work.  The paper is well structured and clearly written, with figures and tables that effectively illustrate the main findings.

The results are both plausible and interesting.  For me, the most important findings are (1) the intrusion of warm water into the Ross and Filchner Ice Shelf cavities by the end of this century under a high-emission scenario, with consistent timing across ensemble members; (2) the absence of a strong response in the Amundsen Sea region, where warm water is already present in cavities; (3) the fact that increased snowfall (a near-term response to warming) adds more mass above flotation than the ice sheet dynamic response can remove by 2100, but with the likelihood that the dynamic response would accelerate in the 22^nd century.  There are many uncertainties – related, for example, to the coarse ocean resolution and the challenges of ice-sheet spin-up.  The authors acknowledge these uncertainties and are careful (except for a few minor cases noted below) not to draw conclusions that go beyond the data.

I have some suggestions to sharpen the text and to guide readers who may be unfamiliar with some of the details, but no major criticisms.

Specific comments

1. p. 5, l. 127: Here or below, it would be useful to say more about how NEMO computes basal melt rates. It would be good to know, for instance, whether the melt rate is a strictly linear function of the thermal forcing, or if it also depends on the speed of the sub-shelf ocean current.
2. p. 6, l. 162: “ice sheet model projections are typically initialized without any spinup”. I would say “often” instead of “typically”, because many ice sheet models (roughly half the models in the ISMIP6 projections) are spun up in some way.
3. p. 7, l. 211: Were basal melt rates assumed to be zero in the Cornford (2016) initialization? If so, please state this, since the tuned ice-shelf viscosity could be compensating for missing basal melt.
4. p. 8, l. 221: What is the magnitude of the steady value where the rms thickness rate settles? In what regions is the remaining drift largest?  Did you do multi-century standalone ice sheet runs, continuing with the same forcing?  Such runs would increase confidence that the drift is small enough to maintain stable grounding lines.
5. p. 9, Fig. 1: In general, the figures in the paper are informative and easy to interpret. However, many figures (including this one) use a rainbow color scale that could be problematic for color-blind readers. Please consider a different scale.
6. p. 11, Fig. 3: In Figs. 3a and 3b, there is good agreement with observations in the thinning of Pine Island and Thwaites Glaciers and thickening of the Kamb Ice Stream. My understanding is that this is largely the result of tuning basal coefficients to match observed ice speeds in the BISICLES spin-up.  We would expect the tuned velocities to change the thickness in places where ice flow has recently accelerated (for PIG and Thwaites) or decelerated (for Kamb).  This can be inferred from the text, but could be made more explicit for readers who are unfamiliar with tuning strategies.
7. Another notable feature of Fig. 3 is the general slowing and thinning of ice shelves.  The text (p. 12, l. 298) attributes the thinning to the SMB and basal melt forcing from the climate model.  Is basal melt primarily responsible for shelf thinning, or does SMB also play an important role?
8. p. 12, l. 297: Why would this slowing mostly occur during the first year of the standalone ice sheet initialization stage? I would expect it to occur more gradually as the shelf thins.
9. p. 12, l. 302: You refer to “the SMB and basal melting implicit in the inverted reference velocities”. I am not sure what this means.  My understanding is that the SMB and basal melting in the BISICLES spin-up are part of the input forcing, with SMB based on reanalysis and basal melting (possibly?) set to zero.  In that case, the shock could be attributed to the fact that the SMB and basal melt rates in the adjustment process (derived from the UKESM historical run and standalone ocean spin-up) are different from the SMB and basal melt rates in the spin-up.  It would be helpful to describe or plot the differences.
10. p. 15, Sect 3.2.1: The abrupt transition to warm water for the Filchner Ice Shelf is a very interesting result in an ESM, consistent with the recent regional studies.
11. p. 16, Fig. 6: Since the transition occurs near 2100, I suggest extending the x-axis to 2115, if possible.
12. p. 15, Sect 3.2.2: The transition to a warm Ross Ice Shelf cavity is another very interesting result, notwithstanding the fresh bias in the Ross Sea.
13. p. 29, l. 629: “These results may indicate the bigger potential that Ross/Weddell sectors have in becoming major sea level contributors in future warming scenarios.” Here, “bigger” seems to mean “bigger than PIG and Thwaites”.  It’s true that the Ross and Weddell sectors have the potential to become major sea level contributors, but it’s also true (based on present-day observations and published simulations) that PIG and especially Thwaites could be major contributors.  The Amundsen Sea contribution might not be captured by the model, for the reasons discussed in Section 4.3.  So I suggest rewording this claim.
14. p. 29, ll. 642ff: This paragraph is a good summary of the novelty and importance of the study.
15. p. 30, l. 666. The SROCC is cited several times, but I couldn’t find a citation of AR6. Please add AR6 citations where appropriate. For context, I suggest including the projected GMSL from Antarctica under low and high forcing scenarios, according to AR6.
16. p. 30, l. 667: It’s plausible that the AIS would have a positive mass balance in this century, but it’s misleading to call this a “rapid sea level fall”. The snowfall contribution is better described as a modest offset (~2 cm) to a robust global trend of rising sea level (28 to 55 cm by 2100 under SSP1-19, and 63 to 102 cm by 2100 under SSP5-85, according to AR6).
17. p. 31, l. 701: “… do not retreat.” Doesn’t Fig. 15 show some GL retreat for PIG and Thwaites?
18. p. 31, l. 705: “Nevertheless, the impact of a future strong climate change in Amundsen Sea cavities is unlikely to be larger than our modelled changes in the Ross/Weddell cavities. This is because the Amundsen continental shelf and ice shelf cavities are already filled with the warm Circumpolar Deep Water and hence there is less potential for further warming and strong ice response.” I think this is a bit too strong.  It may be true that the ASE cavities have less potential for further warming, but this does not imply less potential for strong ice response.  Because of its bed geometry, Thwaites might already be retreating unstably, or might be near a threshold such that it could be tipped into unstable retreat with a small amount of additional warming.
19. p. 32, l. 715: “do not appear to simulate”. I suggest “do not simulate”.
20. p. 33, Section 5: Many conclusions already appear in the Discussion section. Since some readers will look at only the Abstract and Conclusions, I suggest adding some content in Section 5.  For example:

• You say here that these are the first AOGCM runs with full two-way ice-climate coupling; you could add a sentence or two (as in Section 4.1) about why this is important.
• You could point out that the Filchner warming is consistent with previous modeling studies, whereas the Ross warming is something new.
• You could mention the ASE non-response, with appropriate caveats about uncertainty.
• I would not end the paper with a sentence that refers to the Ross Ice Shelf alone.

Technical corrections

• p. 1, l. 21: “of the 21^st century”
• p. 5, l. 137: The phrasing is awkward, with two uses of “along with”
• p. 7, l. 189: “integration” without the “s”
• p. 7, l. 210: “caving” -> “calving”
• p. 13, Fig. 4 caption: “The white boxes”
• p. 14, l. 330: “where the SSP1-EM melt rates become”?
• p. 14, l. 334: “large cold” -> “large, cold”
• p. 16, l. 358: “on the ice front” -> “at the ice front”
• p. 16, l. 360: “The shelf” -> “Water on the continental shelf” or something similar.  In general, please be specific where the two meanings of “shelf” could be confused.
• p. 16, l. 361: “becomes” -> “is” (since the deep water is not becoming denser in an absolute sense, but only relative to the shelf)
• p. 16, Fig. 6i: In this panel the x-axis is different from the other panels.
• p. 18, Fig. 8a: The dashed lines in this panel are hard to see in the ice shelf and continental shelf regions.
• p. 18, l. 415: Add comma after “simulation”
• p. 20, l. 441: Delete “is” before “already”
• p. 23, l. 501, Fig. 11 caption: Typo in “SSP5-EM”
• p. 24, l. 516: “on Queen Maud Land” -> “in Queen Maud Land”
• p. 25, l. 539, Fig. 13 caption: It’s not accurate to describe the right-hand panels as “changes” like the left and middle panels.  Please reword, e.g. using “differences”.
• p. 26, l. 576: “end of the 2060s”
• p. 27, Fig. 14 caption: The descriptions of the middle and bottom rows are reversed.  In the fourth line, delete “the” before “West Antarctica”.  In the last line, “column” -> “columns”.
• p. 27, l. 588: “area-integrated” with a hyphen; delete “area” after “grounded ice sheet”
• p. 27, l. 591: “from the 2040s”
• p. 28, l. 598: Change “retreat up to 40 km takes place under southern Thwaites Glacier” to something like “the grounding line of Thwaites Glacier retreats southward by up to 40 km” (since the southern part of Thwaites Glacier lies far in the interior).  Similarly for PIG.
• p. 28, Fig. 15: It took me a few moments to get my bearings for the left and middle panels, which are rotated with respect to the standard view in a polar stereographic projection (e.g., Figs. 11-13).  Maybe rotate back to the standard view.  On the left panel, perhaps add labels pointing to the Thwaites and PIG ice shelves.
• p. 29, l. 639: Instead of “a while”, maybe “longer.
• p. 29, l. 647: “modern-day” with a hyphen, or just “modern”. Similarly, “present-day” at l. 652.
• p. 31, l. 696: “end of the 21^st century”
• p. 32, l. 726: I can’t tell if there is a paragraph break after “century”.  If not, please add one.
• p. 33, l. 757: “brings” -> “bring”
• p. 33, l. 759: Add a period.
• References: Please check for consistent capitalization in paper titles.

The manuscript “The Antarctic contribution to 21st century sea-level rise predicted by the UK Earth System Model with an interactive ice sheet” by Siahaan et al. presents perhaps the first results of a climate model coupled to an ice-sheet model of the Antarctic Ice Sheet.  The paper presents a protocol for offline data coupling of UKESM and BISICLES and explains the initialization process for this complex configuration.  After this, results are presented for small ensembles of coupled simulations following both SSP1-1.9 and SSP5-8.5 greenhouse gas emission scenarios.  SSP1-1.9 shows small changes from initial conditions, while SSP5-8.5 leads to ice-shelf basal melt regime change beneath Ross and Filchner-Ronne ice shelves, and associated ice-shelf thinning and acceleration.  The manuscript discusses the major terms of the ice-sheet mass balance and considers unique aspects and limitations of the modeling approach presented.

The manuscripts presents a significant achievement of running coupled climate and ice-sheet models for Antarctica.  This has been a community goal for many years, and these results are the first to achieve it that I am aware of, even given the “offline” coupling method employed.  On the other hand, the methodology for achieving it includes a number of questionable choices with an unclear impact on the resulting simulation.  Most significantly, the initialization procedure for both the climate model and ice the ice-sheet model appears a bit ad hoc, with a number of details of the protocol not clearly described.  It appears there may be significant artifacts and model drift associated with the ice-sheet model initialization that have not been quantified.  The authors do a fair job of noting shortcomings, but more work could be done in quantifying the impacts of those choices.

On the whole, this is an impressive modeling achievement, but the scientific utility of the results is questionable without further substantiation.  The authors themselves note these limitations, and I wonder if this paper would not be better suited for a journal like GMD.  Below I focus on two major areas that require more work - description of the coupling and description and analysis of the initialization procedure.  I then list a number of smaller issues that require addressing.  Even after significant additional analysis, it may be that the initialization and coupling procedure leave the scientific intepretation of the results ambiguous.  The authors may wish to consider if a model description journal would be a more appropriate venue for this work, where it would be a significant contribution.

MAJOR CONCERNS

1. Better description of coupling. 

I recognize that the coupling methodology was previously described in the Smith et al. (2021) JAMES paper, but given the importance of the coupling to the science results, inclusion of more information here is warranted.  Some specific suggestions are:

142-6:  The description of the coupling protocol is vague.  Given this is a significant novelty of this work and coupled model results can be very sensitive to the coupling procedure, it should be described in much more detail.

Please provide evidence that the results are not sensitive to the chosen coupling interval.

130:  This sentence is unclear - please clarify or expand on this.  Also, please add a description of how retreat of the ice-sheet grounding line is handled by the ocean model.

126-146:  Please acknowledge in this section that the calving front restriction and the bilinear remapping prevent the system from conserving mass and heat, though these errors are not likely to be significant for the experiments being conducted.

2. Model initialization and its impacts.

Initialization of coupled climate and ice-sheet models is a very challenging problem.  Still, the procedure described here appears ad hoc, missing key information, and does not include an assessment of key initialization choices on the results.  The specific point below detail these concerns:

179: This paragraph is confusing and is missing key information.

182: 45 years seems like a short ocean spin-up time.  Can you provide justification that the most important transient behavior had reduced to small levels prior to creating the branch runs? 

179-194:  After reading the full paragraph, I am more confused. Replace the opening paragraph by clearly stating the initialization process is based on a hybrid state of the ice cavities from UKESM1.0-ice stitched onto the global ocean state of UKESM1.0.  Also, a schematic of the various runs and processing, would help communicate this process.

186: Emphasize for the reader that UKESM1.0 does not include ice shelves, e.g. add a parenthetical “(without ice shelves)” after “UKESM1.0”.

187: Which years were chosen?  Can you elaborate on what “a range of variability” means?  How many ensemble members were in the UKESM1.0 CMIP6 historical ensemble?  Also, do you have a reference for that ensemble, or a reference to the dataset on ESGF?  What does “end of the 20th century” mean?  What specific years were used?

189: What does “short” mean?  And what does “balance” mean on line 190?  Please show evidence of balance or behavior that is close to steady state, either in the form of a plot or some statistics.

196: Please explain why the ocean-sea ice simulations are regarded as beginning in 2000 if they were branched from specific times of UKESM and included a cavity state from perpetual 1970.

197: Are the atmospheric fluxes from the same runs that each was branched from?  Or one common set of atmospheric fluxes?

195-202: So the final initialization step is 1) not fully coupled to the atmosphere and 2) has temperature and salinity restoring applied.  Given that, it is unlikely that you can branch into a fully coupled projection without some shock and drift.  Please justify this choice.

195-202: Throughout this section, please clarify if every time you refer to UKESM1.0-ice, prognostic ice-shelf basal melt fluxes are on and what is happening with iceberg fluxes (if anything).

214: What is the thickness output of the inversion procedure?  In the previous sentence it is only said that basal drag coefficients and viscosity are adjusted.

216: Ice-shelf melting from what year(s) of each standalone run?

221: Referring to this ‘spike’ is vague, as is “about 20 years”.  Please report statistics or, better, show a time series of this RMS metric.

204-223:  It is entirely clear what year the ice sheet initial condition represents.  In line 212, it is stated the ice-sheet state starting the procedure represents “early 21st century”, but then it is relaxed for “about 20 years”.  How does the final state of each ensemble member compare to recent observed thinning rates, which have been highly variable in time?

Figure 3 and associated text (286-292):  The very large amount of noise (presumably transient flux divergence) in the ice-sheet elevation/thickness change deserves a few sentences of explanation.  While this is a well known and common challenge for ice-sheet models, the amount of spurious thickness change after 15 years of integration and 20 years of relaxation (if I followed the protocol correctly - it was confusing - see above) seems unacceptably large.  Also, what is the purpose of panel d?  It shows nearly the same information as panel b.

297: It is not obvious to me why ice shelves would slow so significantly in the first year just due to one year of thickness change coming from surface and basal mass balance, especially if further adjustment after one year is small.  Is it possible grounding line positions have shifted or the ice temperature field changed or something else is going on?  A more thorough explanation is warranted.

Section 3.4: It would be easier to interpret the changes presented if there was also a standalone BISICLES control  run that had constant 2015 forcing.  Presumably the speckly pattern of thinning and thickening in Fig. 13 panels a and b is due to unrealistic transient behavior in the initial condition.  That is a common problem in ice-sheet models, so it does not necessarily invalidate the results, but it should be clearly identified.  I would prefer to see additional results for an unforced control run.  Without it, it is difficult to assess what aspect of these results are an effect of the ice-sheet model initialization procedure and what is due to the climate forcing coming from UKESM.

Other Comments:

Abstract: Mentioning Greenland in the abstract is slightly misleading, because the Greenland results are not part of this paper.

47: Also cite the only paper that demonstrates this for the observational period that this sentence discusses:

Gudmundsson, G.H., Paolo, F.S., Adusumilli, S., Fricker, H.A., 2019. Instantaneous Antarctic ice sheet mass loss driven by thinning ice shelves. Geophys. Res. Lett. 46, 13903–13909. doi:10.1029/2019GL085027

48-55:  There are a lot of other important studies that would be appropriate to reference here, e.g.:

Spence, P., Holmes, R.M., Hogg, A.M., Griffies, S.M., Stewart, K.D., England, M.H., 2017. Localized rapid warming of West Antarctic subsurface waters by remote winds. Nat. Clim. Chang. 7, 595–603. doi:10.1038/nclimate3335

65: CMIP5 and CMIP6

68: One CMIP-class ESM recently published (since this manuscript was submitted) Antarctic subglacial melt rates (but those simulations were not part of CMIP6):

Comeau, D., Asay-Davis, X. S., Begeman, C., Hoffman, M. J., Lin, W., Petersen, M. R., et al. (2022). The DOE E3SM v1.2 Cryosphere Configuration: Description and Simulated Antarctic Ice-Shelf Basal Melting. Journal of Advances in Modeling Earth Systems, 14, e2021MS002468. https://doi.org/10.1029/2021MS002468

69-74: There also is recently published (since this manuscript was submitted) regional model that includes all physical climate components (atmosphere, ocean, sea ice, land, ice sheet):

Pelletier, C., Fichefet, T., Goosse, H., Haubner, K., Helsen, S., Huot, P.-V., Kittel, C., Klein, F., Le clec’h, S., van Lipzig, N.P.M., Marchi, S., Massonnet, F., Mathiot, P., Moravveji, E., Moreno-Chamarro, E., Ortega, P., Pattyn, F., Souverijns, N., Van Achter, G., Vanden Broucke, S., Vanhulle, A., Verfaillie, D., Zipf, L., 2022. PARASO, a circum-Antarctic fully coupled ice-sheet–ocean–sea-ice–atmosphere–land model involving f.ETISh1.7, NEMO3.6, LIM3.6, COSMO5.0 and CLM4.5. Geosci. Model Dev. 15, 553–594. doi:10.5194/gmd-15-553-2022

58-81: Somewhere in here you should also acknowledge the fully coupled configuration of CESM with the Greenland Ice Sheet.

104: Can you report the approximate horizontal resolution of the 1 degree ocean grid at the typical latitude of Antarctic ice shelves?

111: It is worth pointing out that this adaptivity is dynamic in time.

117: Can you briefly summarize the impact of choosing 2 km as your finest resolution instead of 1 km or 0.5 km as is sometimes used for BISICLES?

162: I would say most ice-sheet models follow this practice, but it is not ‘typically’ the case - there are a number of ice-sheet models that do a paleo or steady state spinup.

169-171: These comments make me wonder if this manuscript would be more appropriate for GMD or JAMES.

Figure 1a,b and associated text in 3.1: It is rather awkward to compare these plots to referenced observational data without showing those observations or model biases relative to them.  As presented, these comparisons are not useful.

264: Would not surface restoring bring properties closer to observations?

249-271:  This discussion of water mass properties, especially at depth, based on mixed layer depth is obtuse.  It would be much better to show T&S diagrams for the regions of interest compared to observations.  Many global ocean models struggle with the formation of Dense Shelf Water, even with realistic mixed layer depths, so that in and of itself is not a guarantee of good water mass properties.  It would also be quite important to see maps of ocean bottom temperature and salinity, as those matter more for ice-shelf basal melting than surface properties.

271-2:  Please provide evidence for this statement (e.g. the bias value for UKESM and other CMIP models).  Are you basing this statement off of the version of UKESM in Heuze (2020) or the simulations presented here?

278:  Do you mean *near-shore* fresh bias here?  Over most of the Southern Ocean, Fig. 1 shows a saline bias.

Figure 4: Similar to figure 1, this figure should include the observational references fields (or show an anomaly).  Simply saying “shows a similar spatial pattern to present day observations (Rignot et al., 2013; Adusumilli et al., 2020)” and expecting a reader to pull those up and make comparisons across different colorbars is not sufficient.  Also the linear colorbar is inadequate for showing the high melt rates in the Amundsen Sea - presumably the ice shelves in that entire sector are well above 5 m/yr.  Similarly, the colorbar in panel e and f saturates in areas of interest (e.g., Ross and Larsen ice shelves).

Table 1: Presumably in your model analysis you can separate Ross and FRIS into the two halves that the observational data uses. 

309: While the modeled melt might be within the range, I suspect a t-test would indicate a significant difference.  That is not necessarily unacceptable, but please report a more careful comparison.

Figure 5: Please also show present-day observational estimates for reference.

Section 3.2.1: This section demonstrates the melt regime change at FRIS very clearly, but the causal mechanism is left only hinted at.  There is a plot and mention of declining sea ice volume and its possible relation to declining density.  There also is a mention of increasing freshwater flux.  This is already a long, dense paper, but if it were possible to tease out the mechanism(s) leading to WDW increase, that would be a valuable contribution.  Have you looked at changes in wind stress?  The previous papers you cite also discuss that as a potential mechanism for the WDW intrusion at FRIS. 

424-6:  From Figure 9, it looks like a missing piece of this explanation is that Dense Shelf Water (cold and saline) on the continental shelf is present at the start of the simulation, but becomes significantly fresher by 2060 (Fig. 9e).  This is consistent with the sea-ice decline mentioned and shown in Fig. 8b to become more substantial around that time.  Similar to the FRIS case, the reduction in the continental shelf density barrier facilitates the intrusion of mCDW.   This series of events is alluded to in this paragraph, but the sentences at 426-7 implies that the driving mechanism is warming of the mCDW, which is not apparent in Figure 9.  Maybe this just requires some rewording.

432: As you say, I think the relative model fresh bias in each of these regions is critical.  To further illustrate that point, could you follow up with a quantitative metric of the salinity bias in each region at the start of the simulation?  (e.g. averaged over the region or at the shelf break analysis point used in each region.

440: You haven’t shown that the regional climate is warming during this period.  Maybe reword to “While the changing climate”.

441: Remove “is”.

Fig. 10: What year and simulation are these draft values from?

Section 3.2.3:  Initially I was skeptical of even discussing results from an ice shelf represented by 11 grid cells, but I appreciate the honest assessment of what is happening in the model here, given the importance of this region.  Better to acknowledge the limitations of interpreting these results than ignore it and risk readers reading their own interpretation into it.

491: Similar to previous comments, simply stating your results look similar to your observational reference is insufficient.  Please include a panel in the figure showing the reference dataset (or the difference from it).

Table 2:  Please also include a present-day estimate (e.g. from RACMO).

525: Another relevant reference here: Trusel, L.D., Frey, K.E., Das, S.B., Karnauskas, K.B., Munneke, P.K., Meijgaard, E. Van, Broeke, M.R. Van Den, 2015. Divergent trajectories of Antarctic surface melt under two twenty-first-century climate scenarios. doi:10.1038/NGEO2563

541: The Thwaites and Pine Island inland thinning goes away when you difference the two scenarios, and there is in fact less thinning in the SSP5 scenario.  Please discuss this.  Having a control run for context (previous comment) would likely help here.

Figure 14: Typo in ‘cumulative’  in title above panel b.

574: Consider rewording this sentence to avoid the possible interpretation that the thinning of Ross Ice Shelf has a direct impact on MAF.

580: This goes back to my earlier comment about what Thwaites and Pine Island are doing in the control run.

Figure 15: Consider using the same color scheme for the two scenarios here as in the previous figure.

642. 655-8: Maybe GMD/JAMES is a better fit?

Section 4.2: A short comparison of the results to those of ISMIP6-AIS is warranted, as that set of experiments is perhaps the closest point of reference to this work.  In addition to considering the overall behavior of each region, it would be interesting to look at the threshold for surface hydrofracture employed by ISMIP6 and if/when that is passed in your simulations.  Similarly, comparing your simulated basal melt rates to the parameterization they employ might help explain differences in response.

ISMIP6: Seroussi, H., Nowicki, S., Payne, A.J., Goelzer, H., Lipscomb, W.H., Abe-Ouchi, A., Agosta, C., Albrecht, T., Asay-Davis, X., Barthel, A., Calov, R., Cullather, R., Dumas, C., Galton-Fenzi, B.K., Gladstone, R., Golledge, N.R., Gregory, J.M., Greve, R., Hattermann, T., Hoffman, M.J., Humbert, A., Huybrechts, P., Jourdain, N.C., Kleiner, T., Larour, E., Leguy, G.R., Lowry, D.P., Little, C.M., Morlighem, M., Pattyn, F., Pelle, T., Price, S.F., Quiquet, A., Reese, R., Schlegel, N.-J., Shepherd, A., Simon, E., Smith, R.S., Straneo, F., Sun, S., Trusel, L.D., Van Breedam, J., van de Wal, R.S.W., Winkelmann, R., Zhao, C., Zhang, T., Zwinger, T., 2020. ISMIP6 Antarctica: a multi-model ensemble of the Antarctic ice sheet evolution over the 21st century. Cryosph. 14, 3033–3070. doi:10.5194/tc-14-3033-2020

705-708: This is a very speculative statement.  The water in warm cavities can certainly get warmer, as it is modified CDW and not unadulterated CDW.  Please remove or rephrase this statement with supporting information.

Section 4.3:  A major limitation not mentioned is the lack of iceberg calving and dynamic calving front position.  Other missing physical processes that might be important are subglacial hydrology/basal physics and the impact on ice rheology of fractures and damage.

Section 5: The conclusion would benefit from an additional couple sentences about the technical achievements and limitations of the model.