Felikson et al. perform Bayesian calibration using different types of observational datasets as priors for an ensemble of model runs of the Greenland ice sheet under constant present-day climate. In general, better understanding the effect of calibration on the posterior probabilities is a very valuable endeavor. The study presented in the paper sheds some light on that task by showing that using different datasets for calibration of the prior distribution influences the posterior distribution quite substantially. In general, I recommend publishing the paper in TC, however, some comments have been addressed before doing so.

Entire manuscript:

-The underlying model ensemble is called “projections” in many places which will likely cause a misinterpretation of their results. I had to read to the methods to actually understand that the experiments underlying the calibration model the evolution of the Greenland ice sheet under current climate and are not informed by future SSP scenarios. A less careful reader could think that the numbers presented are sea-level projections. Make sure to change your wording, e.g. by adding “commitment under current climate” or “under constant present-day climate”. Also add a timeframe over which this commitment is calculated earlier than in the methods (2100 or later?). This includes changing the title, the abstract and checking the rest of the manuscript.

Abstract:

- line 6-9: What do you mean with “maximum a posteriori ice sheet mass change”?

- end of abstract: what do you propose as a way forward?

Introduction:

- line 23: a “likelihood” of what? And “update” to what? The explanation of Bayesian calibration is quite cryptic, reformulate.

Methods:

- Data/Model output processing: More detail is required on how you handle cells at the margins in your processing and regridding since those show most changes and hence are probably most important for you calibration. For example, is the ice front retreat that you impose part of the “dynamic thinning signal” or is this removed from the signal? And how does this compare to the observational dataset? How is this for the other datasets?

- line 134-136: apparently, mass changes are aggregated at a basin-scale, but figure 1 does not show this. You should update Figure 1 to show the basin-scale values you actually used, otherwise this is confusing. That you use basin-scale makes your results for mass changes comparable to other studies mentioned in the introduction that usually use aggregated values of mass change – extend on this in your discussion. If I misunderstood this comment here, and you did not do the calibration using the aggregated values, I suggest you to do this as this is a commonly used methodology and it would be interesting to compare with this.

- lines 155 and following: definitively more detail is required on the Bayesian calibration, implicit assumptions you make and how it is applied here. This methods is maybe not clear to all readers from The Cryosphere and this paper should hence make a better effort to introduce the methodology to their reader. Moreover a reference to a standard book that described the methodology should be given. Lines 156-162 need clarification, i.e., that m stands EITHER for model parameters, forgings OR mass change in 2100, and just one of them, and that m does not lump all these together. Lines 163 and following: what is the reasoning behind using these terms to calculate the likelihood terms? What are the underlying assumptions, e.g., on the distribution of the priors? A definition of sigma_{o,i} is missing (is this based on the uncertainties shown in Fig. 1?). Furthermore, you should give the exact numerical form of the equations, for example in an appendix, that you use to calculate the respective terms used, i.e., the sigma, the likelihood, the posterior distribution (do you fit this in Figs 2 and 3 to the histogram resulting from weighting the prior histogram? Which method is used for fitting the curve?).

- Line 173: Does this manual adjustment of k influence anything else?

Results:

-Table 2: Add to the description that the “Prior” is of course not a “posterior”.

- Figure 4: Why are there “holes” in the residual plots for dv and dh? Description of RSS missing in legend. Do positive numbers mean that the ensemble member is faster / ticker than the observational dataset or is it the other way around? Why did you flip the colormap in the central pannels in comparison to the other panels (would be easier if they were similar)?

- line 185: “maximum a posterior sea-level” can be misunderstood to mean an upper bound on the sea-level contribution, not the value with maximum probability (if this is a correct assumption from my side?).

- lines 184-197: I wonder if these large differences between the calibration methods are also partly due to the fact that overall numbers are not very large. Or putting the question the other way around, would you expect similar large percentage differences when calibrating SSP5-8.5 projections instead of “committed mass loss”?

- line 207-8: clarify sentence.

- line 220: should it be “which overestimates thickness changes around Jacobshaven”?

- line 224 and following: Not sure what you can learn from this exercise of comparing the RSS for these three simulations.

Discussion:

- From your discussion I get the impression that you do not believe in the thickness change calibration because it is very dependent on the firn thickness change that is hard to constrain. If this is correct, I suggest that you make this one clear conclusion from your study, e.g., by suggesting to rather use the velocity or mass change calibration as these are less prone to these uncertainties.

- line 273-278: You mention that open questions remain, but in the sentences following this, I cannot see any open questions that remain from Aschwanden and Brinkerhoff (2022). Is one open question whether it is better to use ice speed data or change in ice speed for calibration (why? Also the model initialisation in their study is different from the inversion used here, so maybe adding the direct velocity data information in their calibration is more like the step of using the velocity data for inversion done here)? Is it a bad that “the second step of calibration using mass change in Aschwanden and Brinkerhoff (2022) does not shift the posterior median estimate of ice sheet mass change” – because you make it sounds like this not a wanted result?

- line 278: Selling that you account for model uncertainty in contrast to this study is a bit too much, as you only use a very ad-hoc way of including it.

- line 288-294: Not sure I understand what you want to imply with this part of the discussion.

- How much does adding the structural uncertainty in the ad-hoc manner (proportional to the observational uncertainty) affect your results, i.e., how would your results look like without accounting for this term?

Conclusion:

- line 315: I suggest rewording here, because it is not only the mass change calibration that leads to highest scoring members with undesired behavior, you found the same also for the other calibrations. I would rather write “As we show, using the mass change calibration – or any other single dataset for calibration - does not necessarily mean …”

- line 318: “right answer” to what question?

- line 328: you claim that you have shown that“utilizing different observation types in separate calibrations can yield additional insight into biases in the model ensemble”, but the paragraph on that in the discussion (lines 261 and following) contains only once sentence on this (“For example, the highest-weighted ensemble member from the mass change ensemble overestimates acceleration (Fig. 4c) and underestimates dynamic thinning along almost the entirety of the GrIS margin (Fig. 4f).”) and this appears to be more a problem of the observational dataset (the firn correction uncertainty) rather than a bias in the mode ensemble?

- What do you recommend, based on your results, to the modeling community to make meaningful model calibration in the future?