Review for manuscript "Snowball Earth transitions from Last Glacial Maximum conditions provide an independent upper limit on Earth's climate sensitivity"

Authors: Martin Renoult, Navjit Sagoo, Johannes Hörner, Thorsten Mauritsen

General comments

In the presented manuscript, the authors study relevant climate feedbacks during the initiation of a snowball Earth from pre-industrial (PI) or Last Glacial Maximum (LGM) conditions using Earth system model (ESM) simulations. Furthermore, the authors present a novel way of contraining an upper bound of the Earth's equilibrium climate sensitivity (ECS), by deriving a relationship between an Earth system model's ECS and the simulated global mean (sea surface) temperature anomaly of the LGM compared to PI conditions. While I am not sure about the novelty and relevance of the analysis of climate feedbacks during snowball Earth initiation, the attempted contraint of ECS is very interesting and seems scientifically relevant. The chosen tool (ESMs) are a good way to approach this problem. However, there are some issues with the manuscript in its current state that, in my eyes, need to be resolved before publication of this work.

All potential issues are listed below under "specific comments", but I highlight the main ones here:

• The introduction and the method sections are a bit too short in my opinion: Some existing research about climate feedbacks during snowball Earth initiation is not discussed, the introduction fails to explain the reasoning behind the ECS constraint and the method section should go into a bit more detail about the used methods, instead of mostly referring to existing articles.
• It does not at all become clear, how the global mean temperature at which snowball Earth inception occurs is being derived from the individual simulations.
• My main concern is that the assumption that all models and setups would have a "snowball Earth inception temperature" of roughly 0 °C is too far fetched. This goes together with the above point that the derivation of this temperature is not clearly described and that even the results of the presented setup point to quite some uncertainty in my eyes (although a different derivation method could give a more precise, but model-specific number, as discussed below). This is especially worrying, as it seems that the uncertainty around the value of the inception temperature does not enter the calculation of the ECS constraint. If it would enter, the confidence on the reported value should be reduced significantly, unfortunately also reducing the significance of the findings reported in this manuscript.

Overall, the scientific idea, the chosen approach and the considerable amount of effort that went into conducting the simulations, make this manuscript a suitable contribution to ESD. However, the long list of issues and the potentially reduced certainty of the main finding of this work make me suggest that this manuscript should only be reconsidered after major revision.

Specific comments

• The analysis of what feedbacks are important in the snowball Earth transition is not something completely new. For example, the contribution of Pierrehumbert et al. (2011) in the "Snowmip" activity is not mentioned at all (which is odd considering that the authors write about scientifc discussions with Raymond Pierrehumbert and other involved persons in their acknowledgements). Pierrehumbert et al. (2011) specifically discuss that snow and sea-ice albedos together with clouds and atmospheric circulation have a major control of the models behaviour during snowball Earth initiation. There is a short introduction to the topic in the very first paragraph, but I would strongly suggest to add more discussion of the existing literature here.
• l. 31: After the introduction, it is still not clear how the logic behind the ECS constraint works. I would suggest to elaborate on the approach, i.e. that you constrain ECS ultimately by fitting a line for the relationship between a models ECS and the simulated LGM temperature anomaly, and then assume that there is a fixed value of the anomaly at which a snowball Earth would be initiated (in all models). Since a snowball Earth did not happen, you have a new and independent limit on ECS. This reasoning is completely missing in the introduction, so the reader has to guess how this should work. I would suggest to add a bit more explanation in the abstract too, since this is the main point of the paper.
• l. 47-50: How is the growing sea ice problem then treated in MPI-ESM? The reasoning behind having the limit is to avoid numerical artefacts or model crashes as the surface layer runs dry. After reading the rest of the manuscript, it seems like this is just ignored and only the 50 ppm-simulation crashes after 1848 years because of this problem. But why is this not a problem earlier and in the other simulations? This limiter was included, because even pre-industrial states sometimes got too thick ice and crashed. Why are your much colder simulations not crashing quickly?
• Methods generally: The authors refer to other papers for their methods, but I think some more explanation should enter also here, to let the reader understand what is being done without having to read up in other papers.
• Table 1: It does not really become clear why all the different runs are being done. A bit more thourough explanation of why the individual sets of simulations are being done would make it easier to understand from the beginning, and not after reading the whole manuscrpt.
• When first looking at Fig. 1, I assumed all dots correspond to stable climate states, but later it became clear that these were taken out of transient simulations that are in the middle of approaching a snowball Earth. Over which time periods where they averaged and should these numbers really be produced from non-equlibrium climate states? There generally needs to be more explanation which goes together with the fact that the method section is quite short. There is a similar issue with Fig. 2. These maps are all from one simulation, so over which time periods were they created? A figure with some simple time series of the runs would be very helpful.
• l. 106-108: First, it is said that positive cloud feedbacks at the sea-ice edge decrease the temperature of instability, then it is said that cloud feedbacks substantially increase the threshold CO2 level, which are opposing statements. I can imagine this dicrepancy comes from comparing local to global effects of the cloud feedback or because neglecting the cloud feedback would decrease global mean temperatures at a reference CO2 level, but please explain in more detail what is the cause of the discrepancy here.
• Fig. 3 description: Terming some phrases "stable climate" even though some of the runs are in the middle of a transition towards a snowball Earth seems incorrect to me. Please elaborate and be more specific about what is actually meant here.
• l. 115: To me Fig. 3 does not really show that the different runs transit towards a snowball Earth at roughly the same (transient) global mean temperature. Again, a simple figure with time series of global mean temperature in all the runs would be helpful to support these kind of statements.
• Fig. 4: Generally, schematics are nice, but this one is hardly telling a story. Could it be a bit more elaborate or just left out? If you want to keep this in, I am not going to oppose.
• Chapter 4: I am having a hard time believing that the temperature at which the climate transits to a snowball Earth state is similar across CO2 forcings, setups and even supposedly climate models (l. 118). First of all, what temperature is even meant here? These are all transient simulations, so I assume it is not the global mean temperature of the last stable pre-snowball equilibrium climate (which would surely be highly dependent on the climate model). Is it the (global mean) temperature at which the TOA radiative imbalance starts to grow over time again, as marked by the different phases in Figs. 3 and A1? But then, this is all but a clearly defined temperature range, as can be seen from the large ranges where the imbalance goes sideways in some runs, and even if taking the shown different colors as markers, there is still a range of ~10 K between the different runs. Does this count as "broadly similar"? Especially the statement that this temperature will still be the same even with other climate models seems dubios to me. Again, some of this issue could potentially be resolved by simply explaining more thourougly the procedure that was taken.
• l. 127: Now it sounds like the "inception temperature" is actually the global mean temperature of the last stable pre-snowball climate state? A clear definition of what you mean by this temperature is highly desirable. Also, the final global mean temperature of the 50 ppm run (assuming it reached climatic equilibrium and that a further lowering of CO2 would drive the climate into a snowball state) IS probably the "inception temperature", when defined as above. I don't think that the other transient simulations can give any more reliable input. Hence, simply finding the last stable pre-snowball climate by iteratively changing the CO2 concentration of individual runs would give a more reliable and more precise estimate of the "inception temperature" for a given model setup.
• l. 142: I find it very problematic to make such statements. First of all, what is the uncertainty range here? It seems to be in the order of at least 5 K. Second, it should be made clear that if this would be a sound statement, it would only be valid for the modern arrangement of continents and not for the setup during the Neoproterozoic, where the snowball Earth actually occurred. This needs to be specified. Lastly, this temperature is in fact highly model dependent. From personal experience, I can say that parameterisations like the sea-ice and snow albedos or even small changes in parameters of sea-ice dynamics can shift the transition towards snowball Earth inception substantially.
• l. 151: how does Fig. 5 show that the instability is around 0°C?
• l. 162: How are the critical ECS and the confidence interval computed? It seems like the values just come from the fit of the regression line in Fig. 6. But how does this account for the uncertainty in the "inception temperature", which surely has an uncertainty range of several degrees, maybe up to 5 K or more. This would substantially increase the uncertainty in the calculated upper limit of ECS.
• l. 179: Point 3 is not really part of the recipe from the points above, but rather a general proposal, hence it doesn't really fit into the list.

Overall text:

• Quite often simply the term temperature is used for "global mean temperature", which could lead to confusion. I'd suggest to be more precise with the wording.
• The sentence structure is not always sensible (e.g. l. 15: it is not the geological evidence that supports the formation of sea ice within tropical regions, but there is geological evidence that supports the hypothesis that there was sea ice in tropical regions).
• Sometimes unclear and weak use of the english language, like in l.127: "...the inception temperature happens at a temperature...". Not the inception temperature happens at a specific temperature, but snowball Earth inception does.

Technical corrections

- l.15 and other locations: To my knowledge, it should generally be "sea ice" without the hyphen, but then "sea-ice albedo", i.e. including a hyphen when combined with a following noun.

- l. 18 "referred to as"

- l.38 bad punctuation around MPI-ESM1.2

- l. 69-70: Example of weak language, making it hard to follow the text. "... the highest value of the Earth's ECS that does not lead to an unstable LGM state represents an upper limit..."

- l. 93 "snow ball"?

- l. 125: 50 ppm is rather 1/5 to 1/6 and not 1/4 of PI CO2, why not be precise?

- l. 140: "involve"

- l. 150 "as MPI-ESM1.2"

- l. 156-158: bad punctuation or sentence structure

- l.176 "surface"

- l. 184 "...model Earth's climate sensitivity." What does this man?

- l. 290: The doi in the reference does not go to the actual article, but to an eossar link. Please link the actual article.

References

Pierrehumbert, R. T., Abbot, D. S., Voigt, A., & Koll, D. (2011). Climate of the Neoproterozoic. Annual Review of Earth and Planetary Sciences, 39(1), 417-460, doi: 10.1146/annurev-earth-040809-152447

The study addresses the role of cloud feedback in the transition to a snowball Earth state, and provides an upper bound on equilibrium climate sensitivity (ECS).

The authors use a suite of MPI-ESM simulations with negative CO2 forcing, including one set of simulations where feedbacks are locked by hiding changes in cloud/humidity/albedo fields from the radiation code. They show that while ice albedo feedback is the one that causes the snowball runaway, clouds play a crucial role in initiating this process. With additional support from CESM simulations, the authors argue that a transition to snowball Earth occurs around 0 degrees Celsius. They use this to develop an emergent constraint for an upper limit to ECS, which they quantify to be around 5.5 K. The justification for this emergent constraint arises from the fact that the Earth was not completely frozen during the LGM. The authors furthermore call upon modeling centers to replicate reduced-CO2 simulations to find thresholds for the transition to a snowball Earth in other models.

Overall, I find the simulations and the reported results enlightening, and I have learned interesting aspects from the paper. In particular, I enjoyed learning about the results from the feedback-locked simulations, which I think are well designed. However, I think that the study lacks rigor in important points, and I do not buy some of the main conclusions because of hand-wavy arguments.

Major comments

1. There are a few inconsistencies and a lack of clarity related to the transition temperature, which I summarize here:

   1. How is the transition temperature defined? I assume when the feedback becomes zero?

   2. If my interpretation is correct, how is the value and the uncertainty determined? E.g. looking at Fig. 3A in the 1/64 x CO2 line, I could see why one would argue the transition temperature to be at -20 K, but at the same time -33 K also seems reasonable. Similar reasonable ranges seem to exist for many other simulations.

   3. How does this uncertainty affect the uncertainty of the emergent constraint?

2. My second set of comments refers to the emergent constraint:

   1. Fig. 6: Taking out all the CESM-2 points (the blue ones and, as I read from the text, the upper left white one) leaves no relationship at all. In fact, the authors write that “the relationship lacks robustness” (caption Fig. 6). Considering only the remaining PMIP models, there seems to be no linear relationship at all, which seems to indicate that all the emergent constraint actually comes from CESM2.

   2. The instability threshold was previously argued to be around 0 degC, in this figure it starts around -8 K SST anomaly relative to preindustrial. Given that pre-industrial SST were around 15 degC or so, how does this go together?

   3. How is the emergent constraint different from simply excluding models that freeze over in the LGM when estimating ECS on the grounds that they would be too sensitive? Would that method lead to the same results?

3. The third set of comments refers to the threshold of snowball transition at 0 degC:

   1. Some arguments are very hand-wavy. For example, the argument that this supposedly generalizes across models (l. 118-119) and the “geometric argument” in l.122-124.

   2. In particular, I am not sure that the transition temperature would be 0 degC across all models. Already in Fig. 3A) I can see a transition temperature range of ~ 15 K across simulations performed with the same model. Similarly, in Fig. 5, the transition temperature seems to be at or below -20 K anomaly to pre-industrial, which would be well below 0 degC, too. The statement that all models share a similar transition temperature to snowball Earth also seems to be at odds with the statement in l. 28-29, which points towards different models having different transition temperatures. Also the statement in l. 147-148 points toward different transition types and temperatures even within the CESM model family.

4. l. 28 – 29: I found this surprising, and from skimming through Zhu et al. 2021a, I didn’t find that information. From my understanding, they look at only one climate model family (CESM), albeit in different configurations. While CESM2 definitely goes to a snowball state, I can’t see at what temperature the transition would happen, as their Gregory plot (Fig. 2 (d)) seems to indicate a stable regime throughout (with small, but nevertheless negative feedback). Furthermore, I was under the impression that cloud feedback accelerates the transition to the snowball state, or, as stated in l.95-97, doesn’t change the transition temperature. All of these statements seem to be inconsistent with each other. A similar statement is found in l.107. How do these conflicting statements go together?

5. l. 32: independent from what? If the intended meaning is “independent from models”, then I think independence is a strong claim, which should be further justified

6. l. 99-100: This is almost exactly the same finding as in Abbot 2014 (https://doi.org/10.1175/JCLI-D-13-00738.1), please cite

7. l. 145: “universal”: I suggest rewording, given that it was tested on only two selected models

8. Why is there no summary, conclusions, or discussions section? I don’t want to insist on the traditional structure, but some wrap-up and putting-into-context at the end of the paper might be helpful.

Minor comments

1. The authors did a great job motivating the study in the introduction. A few additional sentences about ECS and its uncertainty would be helpful, since the emergent constraint on ECS is one of the main purposes of the study. Also, the emergent constraint could already be clearly set as a goal for the paper, as well as the logic that is behind it.

2. l.99 I suggest “locked clouds” rather than “locked cloud feedbacks”. I find “locked cloud feedbacks” not wrong but misleading, because with locked clouds there is actually zero cloud feedback.

3. l. 130: “state” here refers to temperature, not CO2 concentration, I guess? If so, then I suggest making this clearer, since the CO2 concentration technically belongs to the state.

4. l.156-158: I am not sure the sentence is correct grammatically, at least it’s hard to digest

5. l. 171 and following: I suggest to implement the call for the new experiments to the abstract.

Summary

In summary, when looking at the abstract:

l. 1-5 are intro

l. 6-8 seem sound and could be an interesting contribution, but I am genuinely not sure about their novelty.

l. 9-13: These statements are unconvincing.

I suggest major revisions in which the authors provide more rigorous arguments addressing the comments. In case that in the revision no convincing arguments for the constancy of the transition temperature and the justification of the emergent constraint can be made, and if the findings about the role of cloud feedback in the transition to a snowball Earth are not novel, I recommend rejection of the paper; otherwise it should be accepted.

The concept of the manuscript content is novel. I think that the central scientific concepts (e.g. snowball Earth, climate sensitivity, and exploration of forcings) can be described more clearly so that the value of this approach to the community can be fully understood. The manuscript considers a model response that is somewhat unphysical and is perhaps related to model-deficiencies (e.g., falling into a snowball Earth state during a Quaternary glacial stage), so I think more clarity here would encourage other modelling groups to maybe take onboard these concepts. Similarly, I question whether new insights can be attained on Earth’s climate sensitivity using climate model runs with boundary conditions that are not temporally coincident in this extreme case (e.g. fixed LGM and PI boundary conditions with Precambrian levels of solar insolation or CO2).

Nevertheless, there is a lot of good work here. I believe that if these points are addressed, the manuscript has the potential to expand upon the derivation of climate sensitivity and could also provide insight into the role of climate feedbacks (e.g. surface albedo and clouds) during Precambrian Snowball Earth states.

General Comments (by line number).

L15 The authors state “During the Neoproterozoic (>635 million years ago) …”, here the Neoproterozoic ran from ca. 1000 - 538 Mya, and the Cryogenian stage (encompassed the two episodes of the Snowball Earth) ran from ca. 720 – 635 Mya. Your phrasing just needs to be tightened as this would get picked up by someone working in the Precambrian.

What defines your snowball Earth State? The definition of Snowball Earth generally falls into two camps, the Hard Snowball Earth in which the ocean is fully glaciated with marine terminating tropical glaciers, and a Soft Snowball Earth scenario in which sea ice reached into and perhaps beyond the sub-tropics (extending to approx. 10 - 25 degree latitude, sometimes referred to as waterbelt or slushbelt ). Within the manuscript is snowball Earth inception when the tropical ocean has >0% sea ice fraction (as shown in Figure B3). My apologies if I have missed your definition of snowball Earth inception.

L25-29 If some PMIP4 models do indeed attain a snowball Earth state in the modelling of the LGM, is this more likely due to deficiencies in model parameterisations? If so, are we really deriving insight into the Earth’s climate sensitivity? If my thinking here is logical, this needs a brief discussion in the text.

L15 geological evidences

L28 what models are you referring to when you say these models start transitioning to a snowball state (the PMIP4 models that fail to model the LGM?)

L38-40. You state that you are using an ESM. It would be beneficial to the reader if you briefly described which sub-models are included (e.g., is there an interactive Ice Sheet Model incorporated? If so is it a global model or just GIS & AIS domains) or are you referring to an atmosphere-ocean coupled model. I assume the latter. I would also write a sentence or two on the sea ice model as the physics and parameterisations would be important to a reader looking to understand and compare your modelling results with their own. It is also relevant to discuss the snow-albedo parametrisation within the model (e.g., deep snow albedo), I am assuming in these simulations that year-round persistent terrestrial snow cover advances equatorward, so a discussion of snow cover within the model is pertinent.

L41-43 You state that you use the “coarse” T31 truncated model for PI and the “low resolution” T63 model for LGM. I would be more consistent with your description of resolution, as T63 is higher resolution that T31. Or drop the terms “coarse resolution” and “low resolution” and use “low resolution” and “higher resolution”.

Are there any differences in other relevant parameterisations between MPI-ESM1.2-CR (T31 31L) and MPI-ESM1.2-LR (T63 47L) that could impact the outcomes of the study? For example, do both models share the same ocean model (in terms of spatial resolution and sea ice model parameters)?

It would be useful for the study if the same run (of Table 1.) was conducted for both CR and LR versions of the model. I understand from Table 1 that some of this is an opportunistic ensemble, and so I understand if this isn't possible in a reasonable time frame.

L47 A bit unclear here for the reader – are you saying that the act of limiting sea ice growth generates latent heat or does thick sea ice itself generate latent heat?

Table 1. 1/2056x CO2 should be 1/2048x CO2?

L56 Why does the length of the run vary with forcing? Could you have run each simulation long enough so that you didn’t have to use (linear?) regression of TOA radiation imbalance.

L55–57 This is a little bit unclear so needs clarifying- are you computing the climate feedback by determining the change in TOA imbalance over a 5 C temperature change?

L59-60 It would be helpful to the reader if you could succinctly describe how these are locked (1-2 sentences) L60 mentions that these are imposed on the radiation parameterization, but this is still not that clear to someone not experienced in locking feedbacks.

L64-69 So are you saying that you are comparing the snowball transition state to the modelled LGM state to derive the Equilibrium climate state?

L81 be slightly more specific here and say these all relate to global mean surface air temperature.

L91 “southern sea ice edge” I think you mean something like “equatorward sea ice edge” unless you are just considering the northern hemisphere sea ice extent here.

L114 It is not entirely clear from Fig 3. how the climate transition is broadly similar. What feature am I looking at in Figure 3? (is this where TOA radiative imbalance is most +ve?). Do you need to show on Fig 3 the global temperature in which your criteria for snowball Earth is met?

Figures 3 and A1 have the 2X CO2 in the upper right quadrant extending beyond the numbered parts of the y-axis. I would adjust the x- and y-axis numbering so that they extend into the +ve values.

L115 Appendix A should this instead be Figure A1

L125 50 ppm is closer to 1/6 of pre-industrial than ¼

L144 I believe this statement depends upon how tightly you are defining the transition / inception into a snowball Earth state, definition of this transition would clarify this.

L161. I am a little uncertain how this 5.5 K (4.4 -6.6, 90% confidence interval) statement relates to the data within Figure 6 – I guess this where your linear fit intercepts with the upper bounds of your instability threshold. Could this be identified within Figure 6.

L301, You state that your model is numerically unstable at low CO2 concentrations and so compare solar-forced snowball Earth transitions instead. Given that you are running at low CO2 levels, has this numerical instability impacted your work?

In the text, be consistent with the term “snow ball” or “snowball”

Some instances of informal scientific language used. 36 “notoriously difficult” or L145 “notoriously performed” are not scientific terms (notorious often means something bad or unfavourable that is somewhat common knowledge). Modify also L46 “few simulations” and L88 “All in all”.

Equilibrium climate sensitivity (ECS) is the temperature change to a doubling of CO2 once the atmosphere and ocean (including deep ocean) has equilibrated to that change in energy. I believe here you are in fact just considering only atmospheric changes. I think you therefore need to reconcile this ECS with your definition of climate sensitivity. Here also the definition of your snowball Earth is important (sea ice at the equator? I assume you are holding terrestrial boundary conditions fixed – no expansion of terrestrial glaciation).