This paper improves an exisiting conceptual model on global ice volume changes as function of orbital forcing and some internal feedbacks which is then applied to the last 2.6 Ma in order to understand the Mid-Pleistocene Transition (MPT).

In my view this is a solid piece of work, but misses one important piece of discussion. All sea level (=global ice volume) reconstructions used here as target are some sort of deconvolution of the LR04 benthic d18O stack into sea level and temperature. However, a most recent approach by Clark et al., published some weeks ago in Climate of the Past (doi: 10.5194/cp-21-973-2025) doing the same thing supported by SST and deep ocean data comes to a significantly different deconvolution with larger glacial/interglacial amplitudes in the sea level component throughout the Quaternary than the sea level records used here. 

In an ideal world, this new record (data to figure 10b in Clark et al., 2025 available in the SI there) would as an alternative be used here as tuning target, but I understand that this would be a major effort and leave it up to the authors if they want to jump on this challenge. However, I noted that the authors referred to another discussion paper (Scherrenberg et al., 2024), so it is not clear to me why they not also included in their discussion of the MPT the Clark et al paper, whose discussion version was also available since September 2024. What should be and needs to be done is that this difference between the sea level component in the new Clark et al 2025 paper and those used here needs to be discussed. This is in my view important for two reasons. 

    1. The Clark paper is simply one of the newest papers published on MPT sea level changes (although only indirectly contained in the contribution to the benthic d18O stack) and should be considered/discussed in any upcoming paper on the same topic. 

    2. The regolith hypothesis, formulated some decades ago, also by Clark and others, was trying to explain that there were ice sheets in North America, that were reaching as far south as 39-40°N around 2.5 Ma ago (e.g. Balco & Royery, 2010, doi: 10.1130/G30946.1). However, more complex models are not yet able to simulate these ice sheet extends. The Utrecht model (in the version of de Boer et al 2014, doi:10.1038/ncomms3999) was failing to do so, as has been shown in Köhler & van de Wal 2020 (doi: 10.1038/s41467-020-18897-5), which plotted in their Fig. 2b the latitudinal ice sheet extend of the Utrecht model as function of time. 

(Side note: Köhler & van de Wal 2020 is to some extend a reinterpretation of Tzedakis et al 2017 on the appearance of interglacials during the Quaternary and might for that content also be discussed here as one recent study on the understanding of the MPT.)

The sea level of Berends et al (2021) used here is a follow-up study of the de Boer et al 2014, both using a model to deconvolve benthic d18O into sea level and temperature, thus both results differ in detail, but rely on the same approach and give in principle comparable results. Also the 3 Ma long simulations of the CLIMBER model (Willeit et al., 2019, doi: 10.1126/sciadv.aav7337), which is a more complex climate model than in the Utrecht approach, and which does not use benthic d18O as input, do not get large ice sheets down to 40°N at 2.5 Ma BP.

That said, these interpretations of the benthic d18O stack are still failing to explain the terrestrial evidence of Balco and others. These shortcomings are also worth mentioning in the discussion.

With this two contrasting deconvolutions of the benthic d18O stack - one based on ice sheet model, one based on an ocean temperature data compilation - such a simple model as used here might be able to give ideas how to understand them. Eg if completely different conceptual models are necessary to satisfy both data sets, but again, maybe this is a task for a future study, especially since a final interpretation of the sea level related changes in benthic d18O from Clark et al is still not published. Nevertheless, I would say it is a missed opportunity if the authors decide not jump on this issue here and now.

Minor issues:

- Barker et al. 2025, explaining the role of orbital parameters for the 100k-world after the MPT also gives a glimpse on their roles in the 41k-world (their SI Figure 8). Thus, I believe this paper is one of the most recent studies discussing underlying processes of the MPT and should already be discussed widely in the introduction.

- Please update the reference to Scherrenberg et al., 2024 to the now available final version:  https://doi.org/10.5194/cp-21-1061-2025).

- Figure 4: purple and red dots look the same. Make one symbol differently, eg squares.

- lines 520ff: Somehow now „glacial inception“ is shortened to „gl. inception“. Please use full words.

- line 614: The most recent review on MPT SST changes is in Clark et al. 2024 (doi:10.1126/science.adi1908). please revise your discussion here based on that paper, instead of using the older study by McCymont et al 2013.  

- line 618: d^{13}C instead of d_{13}C

- Section 4.5. The starting sentence should already say that such a future exercise would be one which would ignore anthropogenic impacts. 

- line 688:“… would reach a maximum rate“. A rate of what? Glacial inception can hardly be a rate.

- The content of the Appendices (Tables A1-A2, Figures B1-B6) are in my view actually Supplementary Figures which should appear in an SI (in the final format an extra PDF) and not as Appendices (added extra figures in the main PDF).

Review of Pollak et al., 2025: “An improved conceptual model of Quaternary global ice volume and the Mid-Pleistocene Transition”

By Tijn Berends

Summary

The Mid-Pleistocene Transition (MPT) remains one of the most important unexplained phenomena in the Earth’s climate system of the past few million years. Explanations for the observed change in glacial cycle periodicity often involve interactions between different components of the Earth system. Explicit physical models of these physical systems are often too computationally expensive to feasible simulate the multi-million-year timescales involved. This means that conceptual models, while by necessity less detailed than physical models, can provide valuable insights.

The authors present results from a simple conceptual, zero-dimensional model of the cryosphere, where the net ice mass balance is determined by insolation, plus some generic climate feedback terms which depend on the total ice mass. It additionally includes an artificial switch between “glacial” and “deglacial” states, which allows the model to reproduce the general features of the Pleistocene glacial cycles, including the MPT. The authors performed some experiments where they include a temporal change in some of the model’s parameters, which could be interpreted to represent both the hypothesized change in subglacial substrate (i.e. the regolith hypothesis), as well as the background CO2 concentration (i.e. the gradual cooling hypothesis). They show that this increases the match between their model results, and different d18O-based sea-level reconstructions.

While I think this work has potential, I believe it requires some substantial revisions.

Major comments

My main issue with this manuscript is that it is a continuation of the work by Legrain et al. (2023), but it is difficult to understand from the manuscript how the new model and its results differ from those by Legrain et al. Right now, a reader who is not familiar with Legrain et al. could be given the false impression that the model and the experiments are entirely novel. (In fact, even for me it is difficult to spot the differences, and I actually reviewed the Legrain et al. paper!). To prevent this, when presenting the model equations, it should be made clear how and why they are different from those already published. Similarly, since three of the four experiments (ORB, ABR, and GRAD) were also performed by Legrain et al., the results of those experiments with the earlier model version should be shown for comparison, to illustrate the effect of the changes to the model.

My second issue regards the way the performance of the different model versions is assessed, namely by comparing to the sea-level curve from my 2021 paper (Berends et al., 2021a). I hesitate to call it a reconstruction (despite the rather optimistic title of that publication!), because, as I cautioned readers in that paper, that curve is based on a model-based deconvolution of the LR04 benthic d18O stack, and includes major uncertainties. For example, at the last glacial maximum, I simulated a sea-level drop of only ~100 m, well below the accepted value of ~130 m. As I stated in the discussion section of that paper, the results presented there “…should not be interpreted as a realistic reconstruction of what the world looked like in terms of global climate, ice-sheet geometry, sea level, and CO2 during these periods of geological history. Rather, … they should be viewed as scenarios which can help in interpreting an expected new ice-core record.” Considering the magnitude of the errors and uncertainties in this curve (i.e. up to 30 m), I do not think it can be used to (in)validate the results of the conceptual models presented here, which all lie well within this uncertainty (i.e. RMSE’s of less than 20 m). Given that other sea-level curves (like the different ones from Rohling et al., which are also cited in the manuscript) suffer from similar uncertainties, in my view this means that the currently available sea-level data is insufficient to choose one of the author’s models over another. This implies that the conclusion of the manuscript should be that, “until more accurate observations become available, both abrupt and gradual changes in the Earth system can explain the available (inaccurate) observations equally well”. Of course, that does not mean it is not worthwhile to study the implications of abrupt vs. gradual changes, or of introducing non-linearities such as the ice-volume feedback in the RAMP-l model. But at present, such studies are, by necessity, exploratory in nature.

The authors also apply their different model versions to the future. I do not immediately see the relevance of such experiments, given that present-day CO2 concentration far exceeds the Pleistocene range. The results presented here should, as far as I understand, be interpreted as “possible future patterns of glaciation in the absence of any anthropogenic CO2 emissions” – i.e., a thought experiment. Since such a thought experiment lies quite far from the scope of the rest of the manuscript, I think it might be best to leave it out altogether.

Lastly, I believe that, with thirty pages of body (plus ten pages of bibliography and appendices) the manuscript is too long, especially considering the rather simple model and limited number of experiments. There is a lot of repetition going on, with e.g. the nature of the four different experiments being described in the experimental set-up, in the results, and then again in the discussion. A lot of text could, and therefore should, be removed without losing information or coherence.

Minor comments

Sect. 2.1: Please add a few lines explaining why it is physically justified to assign different weights to the different orbital signals (eccentricity, obliquity, and precession) in the different experiments. A flake of snow lying on top of an ice sheet cannot know the eccentricity of Earth’s orbit or the tilt of its axis; it can only feel how much solar heat it is receiving at that moment (which is a simple mathematical result of those orbital parameters, with no room for “optimization”). Of course, it has to do with the asymmetry in the sensitivity of the mass balance to summer vs. winter changes; that fact deserves to be mentioned.

Fig. 2: it looks like the ORB and ABR models produce higher-than-present sea levels between 2.6 and 2.2 Myr. Should I interpret this as retreat of the Antarctic ice sheet? How does your model handle negative values for the ice volume?

Fig. 3 and other places: I’d like to suggest again (as I did to Legrain et al. before) to use a wavelet transform (or something similar) to show the temporal changes in frequency content. This is much more intuitive and informative than showing time-averaged power spectra for two different blocks of time.

Table 2: Please explain why running the models over different lengths of time (2.0 Myr, 2.6 Myr, or 3.6 Myr) can yield such different results. Are the models also optimized separately?