General remarks

In this study, the authors investigate how the applied present-day atmospheric climatology (specifically surface mass balance and air temperature) influences the simulated evolution of the Antarctic ice sheet. They employ outputs from four regional climate models (MAR, RACMO, COSMO, and HIRHAM), all boundary-forced by the ERA-interim climate reanalysis. To gauge the impact of the present-day climatology, the ice-sheet model PISM is used in two sets of experiments. In the first, the ice sheet evolves over 30 000 years under a constant present-day climate. In the second, Antarctic simulations spanning 1860 to 2300 are generated by adding HadGEM-ES anomalies to the respective RCM present-day climatologies. In both cases, for each RCM, an ensemble of simulations is run, covering uncertainties in model parameters such as enhancement factors, sliding parameters, and oceanic heat conductivity.

I appreciate the study’s focus on quantifying uncertainties related to the atmospheric boundary conditions (and especially the surface mass balance) derived by regional climate models. I also value the concept of applying an ensemble of simulations sampling uncertainties in model structure for each RCM. However, I have concerns about the methodology employed in the study, particularly regarding the model initialisation procedure.

In the PD-equilibrium experiment, the authors notably assess which RCM present-day climate triggers the greatest ice-sheet deviation from present-day observations. However, these results may be biased by the fact that the thermal spin-up is performed using RACMO’s surface air temperature field. In my view, a more robust approach would involve conducting the thermal spin-up individually for each RCM. Alternatively, the thermal spin-up could use ERA-interim as direct boundary conditions (similar to the approach by Li et al., 2023, where ERA5 is employed to approximate the present-day climate).

In their future projections experiment, the authors quantify the uncertainty arising from the choice in RCM baseline climatology and compare it with the spread observed in the ISMIP6 ensemble. However, I feel that the sea-level projections produced in this study are significantly influenced by the initialisation procedure. Based on my interpretation of Figure 2 and section 2.2 (if incorrect, I recommend clarifying the methods section), it appears that the simulations spanning 1860-2300 initiate directly from the fixed geometry thermal spin-up. If this is indeed the case, I believe it induces significant model drift, stemming from (i) the transition in the parameter-set model parameters for each ensemble member, (ii) the shift from the RACMO climatology used in the thermal spin-up to the present-day climatology of the respective investigated RCMs, and (iii) the abrupt imposition of pre-industrial anomalies derived from HadGEM-ES, while suddenly allowing the ice-sheet geometry to evolve. Model drift can be gauged by comparing control runs in Figure D1 (though it would be better approximated by a control run with a constant pre-industrial climate): the spread among the control runs from the four RCMs is similar to that observed in the RCP projections. Therefore, my impression is that the modelled responses stem more from model drift rather than from the climate forcing itself (especially given that the HadGEM anomalies are consistent across all simulations).

While I acknowledge that the study's aim is to quantify the influence of different forcings on future projections rather than to generate robust Antarctic sea-level projections, the results are nonetheless compared to such robust projections (i.e., the ISMIP6 ensemble). Given that current sea-level estimates prioritise minimal model drift by initialising the ice-sheet model with the starting climatology (whether pre-industrial, 1950, or present-day climatology, as seen in studies by, e.g.,  Seroussi et al., 2020; Reese et al., 2023; Coulon et al., 2023; Klose et al., 2023; Li et al., 2023), I find it challenging to grasp the value and interpretation of the numbers presented here.

If my understanding is accurate and the aforementioned points are applicable, I believe that the model initialisation procedure should be reconsidered, ensuring that the simulations start from an ice-sheet configuration in equilibrium with the initial pre-industrial boundary conditions (see, for example, the initialisation procedures in Li et al., 2023, Reese et al., 2023, Klose et al., 2023). It is worth noting, however, that even if such a strategy is applied to the present study’s investigation of the four RCM present-day climatologies + GCM anomalies, it may be that the spread in different projections would result more from geometry differences arising during initialisation (and therefore potentially considered as ‘initial state uncertainty’) rather than from variations in the different RCM climatologies, to which the ice-sheet initial state is equilibrated. This is because identical temperature and SMB anomalies are added to these respective RCM present-day climatologies. Instead, the authors may consider investigating the spread due to different RCMs projections forced at their boundaries by identical GCM projections. Alternatively, they could apply an approach similar to that of Li et al. 2023, Klose et al., 2023, or Coulon et al., 2023, where climate models air temperatures and precipitation rates (in the case of the latter two, anomalies are added to RCM present-day climatologies) are corrected for elevation changes and used as input to a positive degree day scheme which then calculates surface melt and runoff amounts.

In summary, I propose two key recommendations: (i) improve the initialisation procedure for the PD-equilibrium experiment, and (ii) reconsider the approach and methodology employed in the future projections experiment. These suggestions aim to positively contribute to refining the study's methodology for a more robust outcome. I align with the authors on the significance of elucidating and quantifying uncertainties in Antarctic projections related to surface mass balance, particularly those arising from regional climate models. Therefore, I believe that the study holds significant value for the scientific community and would be well suited for the scope of The Cryosphere. However, some major issues need to be addressed to make it a valuable contribution. Also, it is important to acknowledge that adequately addressing these recommendations would require rerunning the entire set of experiments, impacting not only the results but also reshaping the manuscript and its core findings.

Specific points

1. Abstract, l. 10: It is not clear here what is meant by ‘underlying ice sheet model parameterization’. Please clarify for better understanding.
2. Abstract, l.8-9: ‘Uncertainties in future sea-level predictions of 8.7 (7.3-9.5) cm …’ --> I find this sentence confusing, as uncertainties are mentioned, but it looks like the sea-level prediction and their uncertainties are presented. I think that it would be helpful to clarify what the numbers between brackets represent.
3. Introduction, l. 24: Include a reference to Goelzer et al. 2020 ISMIP6 projections when comparing GrIS and AIS sea-level projections by 2100.
4. Introduction, l.28: I’d suggest adding more references to the concept of calibration reducing uncertainties in sea-level projections, such as, e.g., Edwards et al., 2019, Coulon et al., 2023, Nias et al., 2019, Lowry et al., 2021.
5. Introduction, l.29: please check these numbers.
6. Introduction, l.31-32: I’d suggest adding a reference to Coulon et al. 2023 here, as they investigate uncertainties in ice-ocean and ice-atmosphere interactions.
7. Introduction, l.46: I’d suggest specifying that there is no specific reason to exclusively use one model given that other RCMs such as MAR are also designed to simulate polar regions by accounting for these processes.
8. Introduction, l.48: Seroussi et al. showed the influence of the choice of the GCM used to derive the forcing on Antarctic projections and not on its equilibrium state. Also, I don’t think that they isolated the specific influence on the SMB, as the oceanic forcings also vary for each GCM.
9. Methods, l. 65: refer to Mottram et al. 2021?
10. Figure 1: It is not clear to me from the caption what exactly is represented in the second line (figures f—j). I’d suggest clarifying this in the caption and maybe also in the figure itself.
11. Methods, l. 105: refer to Figure 2 here.
12. Methods, l. 112: an 8-km resolution was mentioned above, please clarify.
13. Methods, l. 117: when is this evaluated? At the end of the 30-ky run? Please clarify, as the calibration step remains a little bit unclear so far. Also, in Table 2, an ensemble of 54 simulations is presented, which ones are the 14 selected ones? Maybe highlight them in bold in the table? It could also be interesting to visualise the obtained equilibrium ice-sheet geometry for each, maybe in the supplementary material.
14. Methods, l. 138: I do not understand how the computation is rendered more cost-effective. Please clarify.
15. Methods, l. 143: was an 8-km resolution also used for the thermal spin-up?
16. Methods, l. 143: I am confused by the abrupt shift from the fixed geometry thermal spin-up under present-day RACMO climatology to the RCM + 1860 anomaly climate for the historical spin-up. Why not start from an equilibrated state, i.e., as in the PD-equilibrium experiment, but for the 1860 climate, as is performed in e.g., Reese et al., 2023, Li et al., 2023, or Klose et al., 2023? Could the authors comment on this, and ideally show the model drift when applying constant 1860 climate for the ensemble of simulations?
17. Methods, l. 145: Does HadGEM2-ES has projections outputs available until 2300 under RCP2.6, 4.5 and 8.5? If not, how are the projections extended to 2300?
18. Methods, l. 151: Could the authors comment on why the list of ensemble parameters in Table 2 differs from the ‘PD-equilibrium’ experiment and what guided this choice? Also, I understand that configurations without long-term stability are no longer excluded, it would be good to clarify which ones are the ones selected by the calibration procedure.
19. Methods, l. 151-152: What is meant by ‘model spin up’ here? Is the thermal spin up, or the short historical run? Please clarify.
20. Methods, l. 153: What initial ice-sheet configuration is referred to here? If my understanding is correct, the ice-sheet initial state obtained from the thermal spin-up was produced with fixed ice-sheet geometry. Deviations with respect to ice thickness should therefore be zero.
21. Methods, l. 155: ‘have often been used in the past’ --> I’d suggest adding some references to support this. I would also suggest clarifying what exactly is meant by ‘simple spin-up’ routines, is it the thermal spin-up?
22. Figure 2, caption: ‘First the model is initialized from present-day ice sheet observations. Then a 200-ka thermal spin up is performed.’ à My understanding was that the initialisation was the thermal spin up itself. Here, it is implied that the spin-up is performed after a first initialisation procedure. Please clarify.
23. Figure 2: The figure says ‘BEDMAP topography’ while Bedmachine is mentioned in the manuscript, please correct. Also, I would suggest specifically writing on the figure that the thermal spin up is performed with a fixed ice-sheet geometry.
24. Figure 3: I’d suggest clarifying in the figure caption that these are the timeseries under constant present-day conditions, i.e., the PD-equilibrium experiment. In addition, please clarify what change rate is meant in figures (e-h). Also, I suppose from the figures that (i-l) represent the change in ice fraction area? Finally, please clarify how the total ice mass change is translated in m s.l.e? Is only the ice above floatation accounted for here?
25. Results, l.168: Could this be influenced by the fact that the thermal spin up was performed with RACMO only? The trend would hence not be influenced by the RCM itself, but rather by the difference between the RCM surface temperature field and RACMO’s one. Why not performing a thermal spin up for each RCM to exclude this possibility?
26. Results, l.176: I’d refer to Figure 1 here.
27. Figure B3: Why not simply combine figures 3 and B3?
28. Results, l.183-184: What is meant by ‘mainly driven by ice-sheet model parameterisation’ here? I think that this requires more clarification.
29. Results, l.188: ‘(effect of ice sheet model spin up and parameter choices)’ --> Again, I think that this requires a bit more explanation.
30. Results, l.190-193: Alternatively, a control run under constant present-day climate conditions used for the thermal spin up could be deduced from each simulation from the ensemble, allowing to isolate changes in the AIS due to the evolving climate for each configuration.
31. Results, l.195: It could be interesting/helpful to the reader to highlight, on one or several figures, some of the regions/locations that you refer to in the text.
32. Figure B4: It is not clear to me what exactly is represented in Figure B4.
33. Results, l.205: Why were these specific simulations selected? Where do they lie compared to the rest of the ensemble?
34. Figure 5: Writing the parameter values in each of the subfigures is confusing as it gives the impression that each parameter value is associated with the panel itself, I would suggest removing it. In addition, please clarify in the caption what experiment is represented in the figure.
35. Results, l.212: please clarify what is meant by ‘similar’ here.
36. Results, l.216-219: in which figures can we see this? Please clarify. It would also probably be easier to indicate the parameter-set subset on the figure directly.
37. Results, l.213-219: as a few of these simulations do not seem to have reached a steady state nor a quasi-steady-state yet, one could wonder whether running these simulations for more than 30kyr would lead to a WAIS collapse in all of the configurations, implying that the committed ice-sheet state is mainly driven by the parameter set itself, while the RCM climatology modulates the timing of the potential collapse? This is only a guess, but it could be interesting to discuss this somewhere?
38. Results, l.223-224: Figure D1 seems like an important figure which, I believe, has its place (along with its discussion) in the main manuscript.
39. Results, l.242-243: SMB over the ice shelves has no direct contribution to sea-level rise, but it does indirectly influence the ice-shelves stability and hence buttressing effect on the ice-sheet flow. Maybe it is worth briefly commenting on this?
40. Figures 7, D2-D3: I see no purple line on these figures. Also, the grey line does not seem to be the observed present-day grounding-line position. Are these the median grounding line positions? Also, are these the ice-sheet configurations by the end of the simulations, i.e., 2300? Please clarify.
41. Figures 7, D2-D5: I find the use of the difference to the common mean hard to read and interpret. Alternatively, a control run under constant pre-industrial climate conditions could be deduced from each simulation, allowing to isolate changes in the AIS due to the evolving climate for each configuration (something similar is performed in Li et al.’s Exp. CMIP6_RAW_1850-2100).
42. Results, l.267-269: I think that this makes sense, given that the parameters included in the ensemble do not have a strong impact in this region, which is instead strongly influenced by the SMB.
43. Results, l.276: What about the control (i.e., constant present-day as of 2005) simulations? It could be interesting to show these as well to have a better grasp of the influence of this signal.
44. Figures D4-D5: It should be clarified in the figures' captions that these represent the ensemble member 10 only. Also, what do the different coloured lines represent in these figures? Overall, it would be good to clarify figure captions throughout the manuscript.
45. Results, l.281-282: I don’t think that I would say that the RCM baseline will ‘significantly affect the onset and pacing of a marine ice sheet instability’. First, I don’t believe that Figure 8, given that it is a snapshot at year 2300, allows us to draw conclusions about the pacing itself. In addition, except for the 5 and 95 percentiles, the grounding line positions are overall relatively similar. I think that it is more correct to say that the choice of the RCM baseline modulates the grounding line retreat. Also, I don’t think that it makes sense to refer to a marine ice sheet instability mechanism here. We do not know whether a self-reenforcing retreat has been triggered. I would simply refer to a grounding-line retreat.
46. Figure 8: It is not clear to me how the percentiles of grounding-line positions are calculated. Could the authors specify it in the caption?
47. Results, l.287: Here it is referred to ensemble member n°10 while before the ensemble members were referenced using letters (AY, etc.), maybe consider using either letters or numbers for both for consistency?
48. Results, l.288-289:’similar to the already observed patterns in the present-day equilibrium runs’ à I am not sure which figure I should refer to for the comparison, I am guessing Figure 4, but it would be good to specify.
49. Discussion, l.304-305: I think that this formulation is clearer than the one used in the abstract, maybe use an equivalent sentence as this one for the abstract as well? Also, I think that it is important to specify that these are the maximum differences between two RCM configurations.
50. Discussion, l.306-308: I find that how both (different) numbers are compared is confusing, as, e.g., 8.7(7.3 – 9.5) represents a spread in sea-level contribution, while 9.6 +- 7.2 represents the sea-level contribution itself. I’d suggest presenting the spread of the ISMIP6 ensemble instead. The authors may also consider calculating an equivalent indicator as the ‘mean maximum sea level contribution difference’ on the ISMIP6 ensemble for a more robust comparison.
51. Discussion, l.311: My impression is that the uncertainty presented here is instead mainly driven by the initialisation procedure. I think that this requires a more thorough discussion and presentation of control (i.e., constant pre-industrial climate) simulations.
52. Discussion, l.352: ‘may be simulated’. It is in fact only for specific RCM and parameter set that divergences appear. Your median grounding line positions are in fact relatively similar.
53. Discussion, l.329: what is meant by ‘unforced’ grounding-line retreat here?
54. Discussion, l.341&345: Grounding-line retreat does not necessarily imply reduced buttressing and hence acceleration in ice flow…
55. Discussion, l.355: I don’t understand what is meant by ‘the ice sheet gradually responds to the SMB forcing’, please clarify.
56. Discussion, l.358-359: I don’t understand this. The evolution of the ice flow can be investigated with the evolution of the ice velocities through time.
57. Discussion, l. 360: I find this title a little confusing. I would suggest reformulating it.
58. Conclusion, l.377-378: I don’t think that the differences in thickness and grounding line positions that are presented here may be considered as ‘considerable’ (see, especially, Figure B1)
59. Figure D1: How come that Figure D1 shows only one curve for the control runs? What parameter values are used for these control runs? For consistency, control simulations should be performed for each parameter configuration.
60. Appendix D, l.399: ‘minor ice loss’ --> I am not sure that the 1860-2005 ice loss (of several dm) can be considered ‘minor’. It is the same order of magnitude as the sea-level contribution between 2100 and present under RCP8.5, as shown in Figure 6. Also, as mentioned above, I suggest moving this entire section to the main manuscript.

Overall,

1. the methodology, particularly outlined in Section 2.2, is unclear. The inconsistent use of terms such as 'spin up' and 'initialisation' makes it challenging to comprehend the precise procedures, even with the aid of Figure 2, especially for the ‘Future projections’ experiment (section 2.2.2). Similarly, the calibration procedure, and how it varies between experiments (resulting in different parameter values) remains unclear. To enhance clarity, the study would benefit from a clear list of experiments, similar to Table 1 in Li et al. (2023), where climate forcing, initial conditions, and objectives are explicitly stated.
2. the figure captions should be enhanced for consistency, providing clear information on the represented experiments, years, and the significance of various elements (e.g., grounding-line position). Improved consistency and clarity in figure captions would enhance the overall understanding of the figures and contribute to a more straightforward interpretation of the study's findings.
3. the discussion lacks consideration and comparison with related works (other than ISMIP6).

Minor comments/Typos

1. Abstract, l.1: remove coma after ‘impacts’.
2. Abstract, l.7: ‘constant forcing quasi-equilibrium state’ --> I find this formulation confusing, try to rephrase?
3. Abstract, l.8: ‘uncertainties of’ --> uncertainties in?
4. Abstract, last sentence: remove coma after ‘importance’.
5. Introduction, l. 17: add come after ‘Until the end of this century’
6. Introduction, l. 17: ‘see level rise’
7. Introduction, l. 25: ‘century’s’ --> centuries
8. Introduction, l. 32: ‘The latter, estimates’ --> ‘Uncertainties in estimates of’?
9. Introduction, l.38-41: I’d suggest splitting this sentence in two.
10. Introduction, l.50: I’d suggest splitting this sentence in two: ‘We address the following questions:…’
11. Methods, l. 70: ‘drainage basis’
12. Methods, l. 70: remove come after ‘All four models’
13. Methods, l. 83: ‘togeher’
14. Methods, l. 86: ‘Antarctic Ice sheet’ --> ‘Antarctic Ice Sheet’ for consistency. I believe that this is the case at other places in the text, please check.
15. Methods, l. 90: ‘shelf’s’
16. Methods, l. 100: to improve the readability of this sentence, consider using ‘two model set ups: (i) …, and (ii) …’.
17. Methods, l. 102: ‘scenario’ --> ‘scenarios’.
18. Methods, l. 102: ‘BedMachine’.
19. Methods, l. 104: remove come after (2004).
20. Methods, l. 112: ‘on 16 km resolution’ à ‘at 16 km resolution’.
21. Methods, l. 113: ‘RCM-‘
22. Methods, l. 113: ‘we employ’ --> ‘we run/produce’?
23. Methods, l. 118: ‘An additional constrained’
24. Results, l. 165 and l.172: ‘initialization shock’ --> ‘initial shock’?
25. Results, l. 229: ‘maxmimum’
26. Results, l. 244: ‘SMB The accumulated…’
27. Figure 8, caption: ‘siumaltions’
28. Results, l. 285-286: remove comes after ‘both’ and ‘forcing sets’
29. Results, l. 286: ‘chosen ice sheet model parameter choice’.
30. Discussion, l.300: ‘onto’ --> ‘on’?
31. Discussion, l.322: ‘forcing data’ --> ‘baseline climatology’?
32. Discussion l.341&345: ‘butsstressing’
33. Discussion l.345: ‘In these simulation’

References

Coulon et al.: Disentangling the drivers of future Antarctic ice loss with a historically-calibrated ice-sheet model, EGUsphere [preprint], https://doi.org/10.5194/egusphere-2023-1532, 2023.

Goelzer, H., Nowicki, S., Payne, A., Larour, E., Seroussi, H., Lipscomb, W. H., Gregory, J., Abe-Ouchi, A., Shepherd, A., Simon, E., Agosta, C., Alexander, P., Aschwanden, A., Barthel, A., Calov, R., Chambers, C., Choi, Y., Cuzzone, J., Dumas, C., Edwards, T., Felikson, D., Fettweis, X., Golledge, N. R., Greve, R., Humbert, A., Huybrechts, P., Le clec'h, S., Lee, V., Leguy, G., Little, C., Lowry, D. P., Morlighem, M., Nias, I., Quiquet, A., Rückamp, M., Schlegel, N.-J., Slater, D. A., Smith, R. S., Straneo, F., Tarasov, L., van de Wal, R., and van den Broeke, M.: The future sea-level contribution of the Greenland ice sheet: a multi-model ensemble study of ISMIP6, The Cryosphere, 14, 3071–3096, https://doi.org/10.5194/tc-14-3071-2020, 2020.



Li et al.: Climate model differences contribute deep uncertainty in future Antarctic ice loss. Sci. Adv. 9, eadd7082 (2023). DOI:10.1126/sciadv.add7082



Nias, I. J., Cornford, S. L., Edwards, T. L., Gourmelen, N., & Payne, A. J. (2019). Assessing uncertainty in the dynamical ice response to ocean warming in the Amundsen Sea Embayment, West Antarctica. Geophysical Research Letters, 46, 11253–11260. https://doi.org/10.1029/2019GL084941



Klose, A. K., Coulon, V., Pattyn, F., and Winkelmann, R.: The long–term sea–level commitment from Antarctica, The Cryosphere Discuss. [preprint], https://doi.org/10.5194/tc-2023-156, in review, 2023.



Lowry, D.P., Krapp, M., Golledge, N.R. et al. The influence of emissions scenarios on future Antarctic ice loss is unlikely to emerge this century. Commun Earth Environ 2, 221 (2021). https://doi.org/10.1038/s43247-021-00289-2

Reese, R., Garbe, J., Hill, E. A., Urruty, B., Naughten, K. A., Gagliardini, O., Durand, G., Gillet-Chaulet, F., Gudmundsson, G. H., Chandler, D., Langebroek, P. M., and Winkelmann, R.: The stability of present-day Antarctic grounding lines – Part 2: Onset of irreversible retreat of Amundsen Sea glaciers under current climate on centennial timescales cannot be excluded, The Cryosphere, 17, 3761–3783, https://doi.org/10.5194/tc-17-3761-2023, 2023.

The influence of present-day regional surface mass balance uncertainties on the future evolution of the Antarctic Ice Sheet by Wirths et al., 2023

This study focuses on the impact of anthropogenic global warming on rising sea levels, specifically examining the Antarctic Ice Sheet (AIS). It underscores the crucial role of selecting appropriate regional climate model (RCM) references for predicting future sea level rise contributions from ice sheets. By using the Parallel Ice Sheet Model (PISM), the researchers find that the choice of RCM reference forcing introduces uncertainties in sea level rise predictions. Additionally, the study highlights how the choice of RCM reference influences grounding line retreat in West Antarctica. Overall the manuscript is clear but some sections could be improved (notably the Methods). The topic is interesting as the influence of the SMB baseline has not yet been assessed. Differences of less than 100Gt/yr ie lower than the annual variability  (for instance between MAR and RACMO whose results are really close to the observations following Mottram et al., 2021) seem to lead to large mass differences.

Major comments

The paper is worth publishing, but I'm particularly concerned about the initialisation method and wonder to what extent the results are influenced by it. Like most models, PISM was originally calibrated to RACMO over Antarctica, and its development was based on this forcing. We can already assume that part of the model's behaviour is linked to RACMO (or at least a similar SMB field). The idea of redoing calibrations with other parameters seems to me to be an interesting way of overcoming this problem, but I have the impression that the results are still essentially influenced by RACMO and PISM's intrinsic behaviour, and therefore favour differences as soon as another forcing is applied. Only “good” calibrations for RACMO (or giving correct results and stability under the RACMO forcing) are conserved while other combinations could work for other models but not for the RACMO forcing. My concern is that the authors want to analyse the influence of the SMB between different models, but that they rely heavily on one of the models in question.



The ensemble set could be enlarged by keeping the combinations that also work for another forcing, and a comparison of the best combinations for each forcing would also allow us to see how a less good combination influences the results. It would also be possible to take the ideal calibration for one forcing and apply it to the others, to see how PISM responds in this case. What about PISM bias? Despite the different calibrations, isn't there a PISM component in the results? If PISM has a tendency to discharge the ice too slowly or too quickly (poor discharge due to poor basal or dynamic ) obviously a "better adapted" SMB will always work better, especially when only the parameters that fit a model are kept. 

Similarly, what is the impact of model drift? From figure d1 (a,b,c) (*which should be in the main text), only one simulation seems to have no drift. What happens to these differences if we remove the drift from PISM? For the scenarios with little warming, apart from MAR it looks like most of the differences could be caused by drift alone. Is it the drift of the model itself or also the result of an ice sheet that was out of balance at the start of the simulation because of another shape? This drift or imbalance would then be less significant in the simulation with a stronger anthropogenic forcing (rcp8.5).

Specific and minor comments

P3L66 : Please refer to Mottram et al., 2021 where MAR is described and not the dataset on Zenodo. I also encourage the authors to respect the data usage notice concerning MAR outputs that are available on Zenodo.



The authors use models with the same forcing (ERA-Interim), which is a good point. They refer to Mottram et al., 2021 (P4 L75- L76) for the comparison between these models. However, RACMO2.3p2 is a more recent version of RACMO than the one use in Mottram et al., 2021. I won't say that the conclusions remain valid.

Figure 1f: This is not SMB ERAint vs the Ensemble Mean, but rather the SMB from ERAinterim. Please check your caption as some of them are not clear. 

Generally speaking, I recognise that a lot of work has been done to free ourselves from the problems of initialisation and calibration depending on a single model, which is already a good thing, but I'm not convinced that we're free enough. I hope that the authors can improve this aspect of their study because I really think that this article is interesting and highlights the importance of multi-model studies.

Best regards,

C. Kittel