Dear Authors,

Thank you for your replies. Both reviewers agree that this could be a valuable contribution to the field if you address their major concerns sufficiently. Some of your responses to the main points are rather brief and do not always completely resolve the underlying concerns. I am listing some of the issues below and would like to ask you for a more complete reply to the reviewer’s concerns.

It is good that you picked up the reviewer’s suggestion to run longer simulations, but you did not mention the results of these simulations in your response. Please add a discussion of these results and their implications in your revised manuscript.

The statement that BP leads to a 50% reduction compared to FS is a bit thin and I would encourage you to elaborate more on the model differences in case of BP and FS. It is also not clear whether you run BP until the year 2100 as well.

The major concern of reviewer 2 should be addressed more thoroughly. In your revision you merely state that you think that the differences in velocities derive from horizontal shear and that the ripples/oscillations in the differences between surface and basal speed are due to either rough terrain or basal friction coefficient. In figure 7 there is no sign of strong bedrock roughness/variability, and you don’t provide an explanation for the ripples in the basal friction coefficient which are derived from inversion. A more thorough explanation of these model results would be welcome. In your response you state: “The variation in basal friction coefficient is related with the variation in basal velocity”. While it is of course true that variability in the basal friction coefficient drives variability in basal sliding, no explanation is provided what the causes of the variations in basal friction are.

I agree with the reviewer that close to the grounding line and upstream (a few kilometers) velocity differences appear to be zero (at least your figure 7 suggests this for the “initial” case). It would probably help if you highlighted the grounding line position in panels a-f as well to make this clearer.
It is good that you fixed the python issues, but I am surprised by your statement that the oscillations in figure 7/8 are not relevant in figure 5. Figure 5 shows a transect and the ice speed along this transect through depth. Thus, both the surface as well as the basal ice speed is shown in Figure 5 and illustrated in Figure 7/8 in a different way. In your next reply to the reviewer you state that the variations in Figure 5 are indeed the ones you see in Figure 7/8. I would suggest that you address the reviewers’ comments more clearly both in your response as well as in the revised manuscript especially regarding the question why the inversion produces the undulating basal friction coefficient patterns in absence of strong bedrock relief variability and no evident drastic changes in ice thickness/surface slopes.

Please also make sure that you address the minor comments of both reviewers conclusively. Some examples below:

I agree with the reviewer’s comment that the formulation “their physics is more complete than the simplified models” is not necessary here. It is enough to state that Full Stokes models include all stress components as opposed to approximations such as SIA/SSA etc.
As suggested in the review process regarding the missing bedrock response to changes in ice load: it would be good to include some references which estimate the effect of e.g. 1D ELRA models or fully fledged GIA models on decadal to centennial ice sheet responses.
Please quantify the costs for the Full Stokes, BP simulations either in the methods or supplements.
As per the reviewers’ comments please use the term “significant” only where it applies to a quantifiable statistical estimate.

Best regards,

Johannes Sutter

Dear Ms. Yiliang Ma and Co-Authors,

thank you for submitting your revised manuscript. Both reviewers are supporting publication of your manuscript pending minor revisions. I would like to especially ask you to follow the suggestion to quantify the model drift and discuss how it affects your results and conclusions.

Kind regards and thank you for choosing TC,

Johannes Sutter

Dear Ms. Yiliang Ma and Co-Authors,

thank you for submitting your revised manuscript. Please find below my remaining comments and a re-iteration of the comment of Reviewer 1 and myself on the necessity of a reference simulation to quantify model sensitivity. As soon as you have adressed the remaining comments and corrections we can proceed with the publication procedure.

With kind regards,

Johannes Sutter

L281-282: i think you are confusing Gt/yr and m/yr in Rignot et al 2013. Totten average melt rates in Rignot et al. 2013 are ~10 m/yr NOT 63.2 m/yr.
L286-288: Same for Adusumilli et al., please be careful with the numbers you cite. The average basal melt rate for Adusumilli et al. 2020 is given as 11.5 m/a (see supplementary material table 1), thus very close to Rignot et al. and other publications. Please go through your manuscript carefully and double check any numbers you are citing from existing literature (e.g. line 327).
Given the remarks above, I’m unsure whether you assumed too high melt rates in your melt parameterization in general. Thus, please quantify average/bulk melt rates in the sub-shelf melt rate fields shown in figure 3 so a comparison with the literature is made easier for the reader.
L330 The sentence “and the sensitivity of Totten glacier dynamics to sub-shelf melt rate has been revealed in 35 years period.” is unclear. What do you mean by “has been revealed in a 35 years period”?

Quantifying the drift of the reference-control run. You have dismissed the comments of the reviewer and my own comments regarding a quantification of the drift/trend in your reference simulation/control simulation. I agree with Reviewer 1 that such an assessment is still missing in your study, and that the simulation would be relatively easy to run in a reasonable amount of time. The comment on the trend of Reviewer 1 might be motivated by your Figure 9, in which even for C_m0 the model responds with a linear and steady ice loss right from the beginning of the simulation implying model drift. This is fine but needs to be quantified and put into perspective with current trends in ice thickness changes in the region. If your thinning rates are higher(lower) than observations (e.g. Smith et al., 2020 or Nilsson et al., 2022 ESSD) suggest you can infer higher(lower) model sensitivity and quantify the trend.

I want to point out here, that it is a usual and useful procedure in both model projection studies as well as sensitivity studies (such as yours) to define a baseline/reference/control simulation in which you simulate the evolution of the glacier/ice-sheet assuming no change in forcing (e.g. fixed CESM2 + present day ocean forcing e.g. similar to the ISMIP6 ocean reference field.). The response of your model against such a control scenario then provides an idea of the sensitivity of the model setup against which you can compare the perturbations in melt rate and SMB. This important aspect is still missing in your study. So far it is not possible to differentiate between already ongoing non-linearities in the ice sheet response vs. differences in the response triggered by different assumptions of basal sliding etc. Your study would be much more impactful if such an assessment where possible. As you employ an inversion in your model initialization, one useful simulation to quantify model behavior and sensitivity is to simulate (reg. Coulomb) the response of the catchment to present day constant forcing (with a bulk basal melt rate field optimally fitted to present day bulk melt rates, i.e. ~10m/yr from Rignot et al., 2013 or Adusumilli et al., 2020) and compare the ice sheet thinning rates with satellite observations
So to re-iterate: please provide an additional reference run (reg. Coulomb) in which you prescribe a sub-shelf basal melt rate with an average rate similar to what the literature suggests (seems to be in the ballpark of 10 m/a) and present-day reference SMB and surface air temperatures (e.g. in your case a historical or present day mean of CESM2). You can include this run in figure 9 as e.g. “present day reference simulation”.
It would be also interesting to see how different the CESM2 SMB field looks like for present day compared to tailored regional climate models such as RACMO as often in ice sheet modelling studies the climate forcing is constructed with climate anomalies from a GCM added to a regional climate model to alleviate any regional model biases in globally tuned circulation models.
Additionally, please provide a timeseries (supplementary material) of CESM2 SSP5-85 SMB over the Totten catchment from 2015 – 2100, otherwise it is not possible to assess the influence of changing accumulation in the region. While you mention that CESM2 SMB does not vary much over the period from 2015 – 2100 it would be better to quantify this via the timeseries plot over both floating and grounded ice.

Please rephrase the second sentence in the abstract
“It has the third highest annual ice discharge, 71.4±2.6 Gt yr-1, among East Antarctic outlet glaciers”
as you cannot cite literature in the abstract and the number you give is probably from a specific study while there is a range of estimates. You could e.g. write something along the lines of
“It features very large discharge rates among the highest for East Antarctic outlet glaciers and has been losing mass over recent decades.”

Dear Ms. Yiliang Ma and Co-Authors,

thank you for submitting your revised manuscript and including an extended run until the year 2100 of the "control" experiment which now illustrates the general sensitivity of the model setup. There are some last very minor points I would like to see adressed before proceeeding (see below).

With kind regards,

Johannes Sutter

L394+: How come that both the C_m80 and C_m40 exhibit the exact same grl retreat until 2100? Maybe a mix up in the numbers? Please confirm whether these numbers are correct. -> "Along the main trunk FL1 both the regularized Coulomb (C_m80) and linear Weertman (LW_m80) sliding parameterizations produce comparable grounding line retreat rates of 0.14 km yr-1 over 2015-2100 (Fig. 7). By 2050, this results in 8.08 km of retreat, increasing to 12.20 km by 2100. In contrast, with nonlinear Weertman sliding, retreats are 5.94 km by 2050 along FL1 followed by then stabilization (Fig. 6). Meanwhile, the drift control experiment (C_m40) shows a grounding line retreat of 8.08 km along FL1 by 2100."

Can you please structure the paragraph below (L400+) such that the annual retreat rates are followed by the integrated retreat until 2100 so the reader does not have to jump from one to the other through the parapgraph : -> approximately 0.42 km/yr (35.7 km until 2100) using linear Weertman (LW_m80) etc.
I also was confused that you quantify 0.27km/yr or C_m80 but 23.29 unti 2100. If I multiply 0.27 km/yr with 85 years I get 22.95km. The difference is small but should be zero if you compute the average retreat rate.
L400-406: "Along FL2, the retreat rates differ significantly across parameterizations (Fig. 8): approximately 0.42 km yr-1 using linear Weertman (LW_m80), 0.27 km yr-1 using regularised Coulomb (C_m80) from 2015 to 2100, 0.04 km yr-1 from 2015 to 2050 followed by near-stabilization using non-linear Weertman sliding parameterization (NW_m80). Along FL2, the grounding line retreats 12.09 km by 2050 and 35.85 km by 2100 using linear Weertman; 10.83 km by 2050 and 23.29 km by 2100 using regularised Coulomb; and only 1.32 km by 2050 followed by near-stabilization using nonlinear Weertman sliding parameterizations (Fig. 6). Meanwhile, the drift control experiment (C_m40) shows a grounding line retreat of 12.33 km along FL2 by 2100. "

L598 please correct the sentence.

Figure 5: I would suggest adding the grounding line position at the year 2100 of the drift_ctrl experiment in figure 5b and 5c as well as in the transects (e.g. as a black or white line) so the relative positioning of the other runs with respect to the ctrl are accessible from the figure.