Summary

The manuscript presents a study into ‘tipping points’ in the Antarctic ice-sheet system: climatic thresholds that, if crossed even briefly, lead to irreversible, large-scale retreat. Determining the existence and quantifying the thresholds of these tipping points can help understand the future evolution of the ice sheet. The authors study these tipping points from a palaeoclimate perspective. They have set up an ensemble of different realisations of the ice-sheet model Yelmo, and forced those realisations with output from a number of different climate models that have simulated the climate of the mid-Pliocene Warm Period. As that period represents the most recent time in Earth history that any significant retreat of the East Antarctic ice sheet might have occurred, it could help provide insight in the mechanics of these tipping points. The authors show that, depending on the amount of oceanic warming and the changes in precipitation predicted by the climate models, different sectors of the Antarctic ice sheet could have collapsed during this period. From this, they estimate the warming thresholds that represent the tipping points.

General comments

In general, I think the manuscript does a good job of presenting the work. The introduction provides a good context, the methodology generally gives a good picture of exactly how the work was executed, and the results are presented clearly.

However, aside from a number of small, technical comments (outlined below), I have a few more significant concerns with the adopted methodology.

1) Initialisation. The ice-sheet model in this study is initialised by a steady-state spin-up, with no inversion procedure for basal friction, viscosity, or basal melt. The consensus that has emerged in the last few years is that the biases this introduces into the dynamic response of the model to a climate forcing, are no longer acceptable. The (currently stated) aim of this study is to quantify warming threshold beyond which certain sectors of the ice sheet will collapse. I believe the current initialization strategy introduces major errors in these numbers. Either the initialization strategy needs to be revised (which I think should become standard practice for all palaeoglaciological applications, just as it already is for future projections), or the aims of the manuscript need to be changed.

2) Climate forcing. The method presented here, where the ice sheet is directly subjected to unchanging output from a GCM, is outdated. Even if setting up a coupled GCM-ISM is judged to be too expensive (which is probably the case for the multimillennial simulations presented here), there have been several papers in the last few years that describe more elaborate ways of forcing an ice-sheet model with pre-calculated GCM output. This way, the effects of the changing ice-sheet geometry on the climate, and the way these in turn feed back on the ice geometry, can be captured more accurately. Since the study involves major change in ice geometry (including the complete collapse of the West Antarctic ice sheet), these feedbacks should not be ignored.

3) Tipping points in dynamical systems. There have been a number of studies into tipping points from a dynamical systems point of view. These show, for example, that it matters for how long a threshold is crossed, or by how much, before a system tips. The steady-state approach adopted here excludes these temporal effects. For example, recently Stap et al. (2022, The Cryosphere) demonstrated that there are significant differences between the equilibrium response of the ice sheet (which is what is studied here), and the transient response (which is what occurs in reality). While they studied this in the even warmer Miocene, the conclusions apply to this study as well. The authors already mention that, in several of their simulations, the collapse of an ice-sheet sector can occur several thousand years after the onset of the climate forcing. Given the significant climate variability during the mid-Pliocene Warm Period, it is possible that this study significantly overestimates the ice-sheet retreat and the sea-level high stands during this period.

Specific comments

L12: “…a higher-order ice-sheet model.” DIVA is not a higher-order flow model. As Goldberg (2011) states, it is “a depth-integrated approximation to a higher-order flow model”. Please change this here and throughout the manuscript.

L15: “…related to initial topography…” Do you mean initial ice thickness, or bed topography?

L20: “…the likelihood of crossing them under future emission scenarios”. You have not done any simulations involving future scenarios though, so I think this is phrased too strongly here.

L22: “ocean expansion” change to “thermal expansion”.

L30-31: what is/are the source(s) for the different temperature thresholds you state here?

L39: “The thinning of ice shelves…” you mention hydrofracturing as a process causing this, but hydrofracturing causes shelves to disintegrate, not to thin. Choose a more appropriate phrasing.

L48: Is there no more recent data on Pliocene CO2 concentrations than Haywood 2016?

L106: “…similar to other 3D higher-order models.” Same as before.

L113: This need some more explanation. Provide the expressions for lambda and N, and explain what you mean when you say that “we will use it [c_f] for calibration of the model”.

L120-121: This is maybe a bit too cautious. Earlier work on sub-grid scaling of friction (Feldmann et al., 2014; Leguy et al., 2021; Berends et al., 2022), has quite clearly shown that you can get good results at much coarser resolutions than the <100 m numbers mentioned in the MISMIP papers.

L123-125: The last word has not yet been said on the problem of sub-shelf melt at the grounding line. It is not automatically so that the NMP scheme is the best choice at coarse resolutions (see e.g. Berends et al., 2023, Journal of Glaciology), so I’d like to see a bit more discussion on how this affects your results.

L133: “lambda_srf and c are parameters used to calibrate the AIS” What do you mean by this? Do you calibrate to achieve an SMB similar to observations/regional climate models when forced with reanalysis climate? Or do you calibrate to produce a steady-state ice sheet similar to observed? Both could be seen as appropriate for this work, but you should explain what you do and why.

L140: More often, people adjust precipitation by ratios rather than differences (e.g. P = P_pd * (P_mod_Plio / P_mod_PD). Explain why you deviate from this practice.

L142: There are more recent RACMO simulations of Antarctica than this.

L146-147: “…a lapse rate correction factor is applied…” What do you use as the reference surface elevation? RACMO uses a different elevation than the GCMs you used, how do you account for this difference?

L162: “PD fields are obtained from the ISMIP6 protocol” Technically, this protocol only dictates how to extrapolate any ocean temperature dataset into the sub-shelf cavities, and into the space currently occupied by ice or bedrock. I assume you mean you applied this protocol to the World Ocean Atlas dataset? If so, mention this.

L162-163: “For computing the basal-melting rates at the mPWP, the Tf and So fields are changed with an anomaly method analogous to equation 4”. The GCMs only provide temperatures for the open ocean. How do you compute the anomalies in the sub-shelf cavity? Do you apply the same ISMIP6 extrapolation protocol to the GCM data?

L165: “For those cases, a spatially homogeneous temperature anomaly field of one fourth of the atmospheric anomaly was applied, following work by Golledge et al. (2015) and Taylor et al. (2012).” This seems rather ad-hoc. If you were to apply this method to the GCMs where you do have ocean data, how would the result compare to the actual GCM ocean temperatures?

L169-170: “First we perform an ensemble of 180 ice-sheet simulations for the AIS with different dynamic configurations under steady PD climatic conditions using the .” Using the what? Oh, the suspense!

L177-180: How do your initialized geometries compare to the present-day in terms of root-mean-square errors in thickness and velocity? Having an approximately correct volume is a nice start, but in theory this could also be achieved by collapsing the Wilkes basin but grounding the Ross.

L197: “Ice extension ranges from 9.2 times 10^6 km2” Why spell out the word “times”? I’ve not seen this notation anywhere else.

L215: “The ice thickness is practically always negative” I assume you mean the thickness anomaly.

L222-224: “This spread in the EAIS and more specifically in the Wilkes basin points to an important role of the applied boundary conditions in the model response.” What boundary conditions do you mean?

L228: “Since an increase in oceanic forcing is thought to be the main driver of MISI…” Thought by whom? Also, consider a different phrasing than “driver” – by definition, an instability will result in a retreat that continues even in the absence of continued forcing, which only needs to act as a trigger.

L229: “the ice extension” I think you mean ice extent, here and in other places throughout the manuscript.

L231: “this model result does not show realism in terms of sea-level equivalent” What do you mean by this?

L235-236: “we focus on the four models that do not exceed 1 degree of oceanic anomaly” How do you define this anomaly? Global, Southern Ocean, Amundsen Sea, sub-shelf cavity? Sea surface or vertical average?

L237-243: This section is unclear. What do you mean when you say that the “precipitation anomaly lies around 85% of PD precipitation”? Do you mean that (P_mod_Plio - P_mod_PD) / P_PD = 0.85? Or that P_mod_Plio / P_mod_PD = 0.85? Or 1.85? The phrase “Thus, we see that a thermal forcing below 0.5 K can lead to a collapse of the WAIS if precipitation stays below 80% of PD” seems to suggest that the WAIS will collapse if the ocean is warmer than present, AND the precipitation is lower than present. Please rewrite this in a more understandable manner.

L245: “we assume that thermal forcing is the main trigger” Do you mean oceanic or atmospheric thermal forcing?

L248-250: Again, your treatment of precipitation anomalies is very confusing. You state that a precipitation “three times more than PD rates” is similar to an anomaly of “around 130% of PD rates”. I see no way for those numbers to be similar.

L270-279: This section is unclear. Did you use a different initial ice thickness, or (also) a different bed topography? Did you use that as the initial state for your spin-up simulations, or only for your GCM-forced simulations? What do you mean by “the parameters from the ensemble that produced results closest to the mean value for every AOGCM forcing”?

L305-307: This work by Richards et al. (2022) really should already be mentioned in the introduction.

L315: “this threshold is highly sensitive to structural dependence” What do you mean by “structural dependence”?

L304-316: This section contains a number of spelling/grammar errors.

L318: “This might seem counterintuitive…” It does. Your suggested explanation that “ice does not flow 320 sufficiently fast to readvance again” contradicts the findings of the MISMIP experiments, which are founded on basic ice dynamics.

L323-324: “Such an analysis of structural dependence allows us to assess the sea-level uncertainties that arise from dynamical configuration and climatologies.” Unclear what you mean by this.

L328-329: “Thus, a large ensemble parameter constraint like in our study, helps considerably to reduce uncertainty from ice-sheet models.” No, you only used one ice-sheet model. Dolan et al. (2018) used three completely different models (ANICE, Sicopolis, and BASISM). It’s not at all surprising that they find a larger spread.

L331-333: “Consistent with our results, ISMIP6 simulations forced with these and other climate models predict that Antarctic tipping points could be reached within this century” Your results do not support this at all. You have performed no future simulations.

L335-336: “Two of the models employed here (EC-Earth3.3, HadGEM3, see Table S1) belong to CMIP6 whereas the rest belong to CMIP5” What does that imply for your results?

L339-245: This section is vague, but I think it tries summarise one of my major concerns mentioned before: that there is a difference between equilibrium response and transient response, and that tipping points concern the latter rather than the former.

L348: “an ensemble large enough to be statistically significant (more than 30 simulations)” How many simulations would you define as “statistically significant”? I find it hard to believe that you can put a number on this.

L352: “the transient evolution of Berends et al. (2019) allowed only for a WAIS collapse, avoiding other tipping points” Untrue. This model set-up “allowed” for ice-sheet collapse anywhere. That the climate forcing applied there did not result in a collapse is another matter.

L357-358: “their results also show that starting from PRISM4 conditions leads to higher sea-level contributions and a less extended AIS during the mPWP. This result is expected” Those results were obtained with ice-sheet models that did not yet include any grounding-line treatment. Any hysteresis they found could well be a model artefact rather than a physically meaningful result.

L358-360: the arguments after “the one hand” and “the other hand” seem to point in the same direction?

L362-363: “before the mPWP, CO2 concentrations were below the pre-Industrial period, with sea-level estimates also below PD” Do you mean the M2 cold excursion? Be specific.

L366-367: “only 3 out of 12 AOGCM models can be considered to realistically simulate warm

Pliocene conditions, according to our simulations” I do not think your results are strong enough to discredit the results of any of the GCMs. Phrase this less strongly.

L373-383: Unclear where you are going with this. Comparing to the Abumip results is meaningless here, as in those simulations all floating ice is destroyed in the models. The flux condition is not something you use, nor something you need – Alex Robinson already showed in the original Yelmo paper that your sub-grid friction scaling scheme works just fine.

L385: “the particular melting implementation at the grounding line is somewhat arbitrary” A strange way to phrase this. The fact that no perfect solution exists yet does not make the existing imperfect solutions “arbitrary”.

L391-392: “Given that we do not apply flux conditions or grounding-line melting, our results are more conservative than other studies” I’d argue that it is the other way round. Your model includes a sub-grid friction scaling scheme, which has been shown to work well. The models you compare with did not have any special grounding-line treatment, so that they likely would have severely underestimated any grounding-line retreat.

L393-398: Ah, here is the detail I was missing earlier. This should already be explained in your methodology section.

L410-411: “Consequently, the model initialized with the PRISM4 ice-sheet thickness displayed persistent differences in simulated AIS characteristics compared to other initializations.” That begs the question of how the ice sheet came to be so small in the first place, which I think needs to be discussed somewhere.

L417: “a lowering of PD precipitation could lead to such an irreversible retreat.” Do you think a future decrease in precipitation is realistic?

L419: “our simulated sea-level contributions ranged from -1.8 mSLE to -9.6 mSLE considering the whole ensemble.” A negative contribution indicates a sea-level drop.

L423: “as well as grounding-line migrations” Unclear what you mean here.

L424: “sea-level standings” = sea-level high stands?

This is a review of the submission “Antarctic Tipping points triggered by the mid-Pliocene warm climate” of Blasco et al to Climate of the Past.

The paper is an interesting contribution to the body of work utilising the Pliocene Model Intercomparison Project Phase 2 simulations.  It builds on a number of ice-sheet modelling experiments conducted for this period and takes some elements of its experimental design from previous ice sheet model Intercomparison efforts (e.g. PLISMIP). The paper is well written in terms of language and readability.  The figures are clear and of high quality. 

The study takes a perturbed parameter approach to considering the configuration of the Antarctic Ice Sheet (AIS) during the mid-Piacenzian. Results in the study are used to make inferences of potential tipping point thresholds that may have been passed in the mid-Piacenzian, leading to retreat of large sectors of the AIS.  The study provides a step forward on the work of Dolan et al, and De Boer et al, who use a similar modelling framework for exploring uncertainty, in that it considers more thoroughly parameter uncertainty within one ice sheet model.

General comments:

The authors make good use of the data available through PlioMIP and provide a good overview of their results.   My general feeling is that the results presented here present a pragmatic approach to understanding uncertainties in ice sheet predictions for this time period. I am less convinced that the overall model set up is sufficient to draw strong conclusions around Antarctic tipping points.  Through necessity, the modelling framework needs to ignore certain climate-ice sheet feedbacks, but I think a more thorough assessment of these would be needed to draw robust conclusions on tipping points.  It would be useful for the authors to elaborate further on the other ways of considering/modelling tipping points, and the limitations of their current study.  This does not question the overall results of the study, which in my view are sound, but there is a reflection required on how these results are interpreted when considering future Antarctic ice sheet changes.

The authors make very few comments about the comparison of their results for PlioMIP2 and those already published for PlioMIP1 in terms of any significant changes between the climatological forcing.  This is possibly beyond the scope of this study, but it would be interesting to try and assess the impact of the changes to boundary conditions between PlioMIP1 and 2 and their effect on Antarctica.  While the ice sheet boundary condition remained the same, others (e.g. topography, ocean gateways) did not. Are there any systematic changes within the climatologies that would have an impact on the spread of sea-level predictions here?

Finally, it would be beneficial for the authors to provide a brief summary of non-sea level related records that could help assess whether or not ice-retreat in certain areas would be expected during the mPWP.

Specific comments:

L4: the use of mid-Pliocene Warm Period is no longer the most up-to-date way of referring to this time interval (see the note on terminology in Dowsett et al 2023, Stratigraphy). Please also refer to Haywood et al (2020) for the definition of the time period used for PlioMIP2 - mid-Piacenzian warm period (3.264 to 3.025 million years ago).

L37: Such rather than Suc

L50: Sea-level estimates noted here are inconsistent with those in the abstract.

L170: Sentence missing ending

L185: Do all simulations used or tried reach the steady-state condition required? It would be useful to note this as it is unclear from Figure S2 - were any excluded if they did not reach a steady-state?

L195 onwards: use X rather than times.

L214: perhaps use ‘assess the spatial origin’

L246: can you clarify what defines ‘high probability’ in this context?

L274: missing end bracket

L325: Comparison with Dolan et al is useful, but it is unclear from the way it is written if the authors infer that they agree or disagree with the overall conclusion of a high climate model dependency of AIS reconstructions.  Please consider alternative phrasing.  The quoted sea level figures for ‘simulations which are not close to tip’ needs further elaboration.

L331: the statement that ISMIP6 simulations around tipping points over the next century being consistent with the results presented here seems a little ungrounded, given that these results are for a steady state following thousands of years.

L364: Regarding the note around cooler conditions prevailing before the mPWP, it would be useful to provide some further context on this. Do you mean the MIS M2 event? Throughout this period there will have been orbital forcing that is not taken into account here.

L417: use of “irreversible retreat” terminology should perhaps be reconsidered here in reference to the Pliocene, as WAIS has clearly advanced since then. However, I am not clear if this sentence does refer to the mPWP or PD – it would benefit from rephrasing I think.

L419: Is this Pliocene only here, and does it include both ice-sheet initial conditions?

Fig 6: Just for clarity, does 100% probability mean that all simulations agreed? Do any of the results presented reach that 100% mark, or are they mostly between 80% and 100%. It could be useful to have a distinction in colour for when they do all agree.

Table S1: additional comma in caption