Predicting trends in atmospheric CO<sub>2</sub> across the Mid-Pleistocene Transition using existing climate archives

Martin, Jordan R. W.; Pedro, Joel B.; Vance, Tessa R.

doi:https://doi.org/10.5194/cp-20-2487-2024

Articles | Volume 20, issue 11

https://doi.org/10.5194/cp-20-2487-2024

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the Creative Commons Attribution 4.0 License.

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Oldest Ice: finding and interpreting climate proxies in ice...

https://doi.org/10.5194/cp-20-2487-2024

© Author(s) 2024. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 20, issue 11

Research article

|

12 Nov 2024

Research article |

| 12 Nov 2024

Predicting trends in atmospheric CO₂ across the Mid-Pleistocene Transition using existing climate archives

Jordan R. W. Martin, Joel B. Pedro, and Tessa R. Vance

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Final revised paper (published on 12 Nov 2024)
Preprint (discussion started on 14 Jul 2022)

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2022-574: Very simple analysis', Anonymous Referee #1, 12 Aug 2022

This manuscript presents a null hypothesis prediction for CO2 across the MPT based on generalized least squares regression between Late Pleistocene CO2 records from Antarctic ice and the LR04 global benthic d18O stack, a proxy for changes in global ice volume and deep water temperature. The regression-based predictions are then compared with sparse MPT CO2 estimates from blue ice (Higgins et al, 2015) and boron isotopes (Chalk et al, 2017) with respect to mean value and glacial-interglacial range and compared to trend in CO2 from an intermediate complexity model run across the MPT (Willeit et al, 2019). The authors argue that misfit between pre-MPT CO2 values and the regression-based predictions would be evidence for a change in climate-carbon cycle-cryosphere dynamics across the MPT.

The analysis appears to be performed well, and I have only a few concerns about the interpretation of the results. However, my main concern is that the work is too simple. I would encourage the authors to add more intellectual substance to the paper by exploring perhaps nonlinear regression between benthic d18O and CO2 or discussing in more depth the underlying mechanisms relating benthic d18O and CO2 to say more about the implications of potential misfit between CO2 and the regression-based estimate.

Additional Specific Concerns

Abstract, line 18: I think the authors meant benthic foraminiferal stable isotope (d18O). The d18O data used is from foraminiferal calcite, not “water.”

Line 118: It is not clear what the authors mean by “This trend is seen in our predicted record, and in the filtered BI-CO2 and BOR-CO2 data (Fig. 1C).” The previous sentence describes glacial stage CO2 draw-down and the absence of an interglacial draw-down. In Fig. 1C, it appears that this description holds for the predicted CO2 record (i.e., glacial draw-down but steady interglacial values). However, the BI-CO2 and BOR-CO2 data show a change in BOTH glacial and interglacial CO2 compared to the post-MPT average. The text should be revised to make clear which trends are similar between the predictions and observations and which are different.

Line 185-186: The authors need to explain why out-of-phase responses in northern and southern ice before the MPT (as proposed by Raymo et al., 2006) would lead them to expect “large discrepancies” between their regression-based CO2 prediction and the realized data. This inference seems to rely on the assumption of a certain relationship between CO2 and northern or southern ice sheets, but I’m not sure what relationship the authors are assuming. Section 4.2 overall is quite short and would benefit from a more in-depth, process-based discussion of implications of the anti-phased hemisphere hypothesis for pre-MPT CO2 variability.

Citation: https://doi.org/10.5194/egusphere-2022-574-RC1
- AC1: 'Reply on RC1', Jordan Martin, 24 Nov 2022
  
  Comment: “However, my main concern is that the work is too simple. I would encourage the authors to add more intellectual substance to the paper by exploring perhaps nonlinear regression between benthic d18O and CO2 or…”
  Response: We appreciate where this comment is coming from in terms of the simplicity of the model. However, we believe that in this case the simple generalised least squares model is adequate. A Pearson’s correlation test between d18O and CO2 yields a high correlation (r2) of 0.68 indicating fairly strong linearity between the two observed variables. The idea was not to model data to accurately predict CO2 past the MPT but to make a hypothetical CO2 history under the assumption that the climate-carbon-cryosphere system has remained unchanged over the past 1.5 Myr for a) comparison to realised 1.5 Myr records, and b) to compare to existing sparse data spanning the MPT. This simple model achieves this goal in that we can be confident the predicted values (outside of the current 800 kyr observable range) are accurate under an accepted null hypothesis. We acknowledge that non linearities may exist between the two datasets, however these are not constrained by any known mechanism.
  
  Comment: “…discussing in more depth the underlying mechanisms relating benthic d18O and CO2 to say more about the implications of potential misfit between CO2 and the regression-based estimate.”
  Response: According to another review comment we revised at lines 58-59 to “The rationale in using the LR04 stack as an input parameter to predict CO₂is based on the relationship of ocean temperature (of which ẟ¹⁸O is a proxy measure) with its ability to absorb CO₂from the atmosphere. The solubility of CO₂in the ocean decreases with increasing temperature meaning when the ocean temperature is warmer there is a lower concentration of CO₂ in the atmosphere.” We will also tie in approaches by N Shackleton in the original EPICA challenge, and Berends et al. 2021 (https://doi. org/10.1029/2020RG000727) who both have used a d18O to predict CO2.
  We will discuss the implications of potential misfit between CO2 and the regression-based estimate further in section 4.1.
  
  Comment: Abstract, line 18
  Response: Accepted and revised.
  
  Comment: Line 118
  Response: Accepted and revised:
  Various studies conclude that glacial stage draw-down of CO₂occurs across the MPT in the absence of interglacial draw-down (e.g., Chalk et al., 2017; Hönisch et al., 2009). This trend is seen in our predicted record. The filtered BOR-CO₂ and BI-CO₂ data shows a strong glacial stage draw-down across the MPT when comparing the two sets of data: 238.69 ppm. and 226.2 ppm respectively. However, the data also exhibits a slight interglacial stage draw-down: 274.23 ppm., and 271.33 ppm resp. (Fig. 1C). The latter seemingly contradicts the studies that suggest an absence of interglacial draw-down but could also be due uncertainty in the data.
  
  Comment: Line 185-186
  Response: Accepted and revised:
  “The hypothesis states that prior to the MPT, local, precession-driven changes to Northern and Southern Hemisphere ice volume was out–of–phase between the two hemispheres resulting in the suppression of these changes in the global marine sediment record, and domination by the obliquity paced changes in ice volume that were in-phase at the time (Raymo & Huybers, 2008). In terms of the MPT, the theory states that terrestrial–based ice sheet margins in East Antarctica were replaced by marine margins at the onset of the transition; and that this resulted in a change from out–of–phase to in–phase Northern and Southern Hemisphere ice sheets at the precession frequency. If this were the case, then a spectral analysis of a 1.5 myr CO₂record (once sampled) should show significant power at the 23 kyr precession frequency prior to the MPT. Our predicted record, having inherited the spectral characteristics of the LR04 benthic stack, does not display any significant power at this frequency (Fig. A).”
  
  Citation: https://doi.org/10.5194/egusphere-2022-574-AC1
- AC4: 'Reply on RC1', Jordan Martin, 02 Dec 2022
  
  An earlier incomplete version of the review response was uploaded on 24/11. We expect to upload the full and final response by 09 Dec. Please wait for the full response. Apologies for the inconvenience.
  
  Citation: https://doi.org/10.5194/egusphere-2022-574-AC4
- AC7: 'Reply on RC1', Jordan Martin, 15 Dec 2022
  
  The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2022/egusphere-2022-574/egusphere-2022-574-AC7-supplement.pdf
  
  Citation: https://doi.org/10.5194/egusphere-2022-574-AC7
RC2:
'Comment on egusphere-2022-574', Anonymous Referee #2, 16 Aug 2022

Review „Predicting trends in atmospheric CO2 ...” by Martin et al.

Overall assessment

The paper by Martin et al. represents a very simple, statistical (further on loosely called regression) model to estimate past atmospheric CO2 from the LR05 stack of benthic d18O. As LR05 is a combined record of deep ocean temperature and ocean volume (not of CO2) the regression of CO2 with LR05 is only statistical in nature and does not include a direct causal connection. Accordingly, a good predictive skill of LR05 to calculate CO2 beyond its calibration period (the last 800 kyr) cannot be expected. Not surprisingly, the predicted CO2 does not closely reflect the limited data we already have about CO2 in the MPT from blue ice snap shots and CO2 reconstructions based on d11B in foraminifera.

Based on this disagreement, the authors conclude that the null hypothesis of "a common global climate - carbon cycle - cryosphere feedback across the MPT" must be rejected. This is correct in a purely statistical sense, however, without laying out what exactly the causal relationship is between the three Earth System components and why these could be imprinted in the LR05/CO2 regression, the null hypothesis appears to be not well justified. Accordingly, I think the minimum the author have to do to their manuscript is to discuss this connection and to bolster the justification of the null hypothesis. Another point of criticism could be raised that also the existing CO2 from blue ice and d11B may contribute to the difference between observed and predicted CO2. For example, the very old ice from the bottom of blue ice areas may be subject to diffusional smoothing of CO2. This could explain that the minimum (glacial?) values found in the blue ice are higher than the true atmospheric values, however, it would not be in line with the (interglacial?) blue ice maxima in CO2 being also higher than the prediction. Also the limits of the d11B reconstructions have to be better laid out as they are strongly dependent on the input parameters that are used to calculate CO2 from d11B and also from the CO2 saturation state at the marine drilling site in the past, as also illustrated by the relatively large uncertainty of the d11B reconstructions compared to ice core records.

In summary, while the study by Martin et al represents an interesting exercise (as was the initial EPICA challenge published in a non-peer reviewed journal), the question remains, whether this contribution in its present from provides sufficient new insight to justify publication in CP.

Specific comments:

line 16 : "is to make"

line 17 and throughout the manuscript: Myr instead of myr

line 25: the authors state that the null hypothesis should be rejected, however, without laying out the causal relationship between the regression parameters and potential reasons why the regression may not hold back in time, this statement is not entirely satisfying.

line 58-59: d18O is not just a sea level proxy but also influenced by deep ocean temperature. A process-based discussion of why LR05 is a viable input parameter to predict CO2 is required.

line 66: please include also the record by Dyez et al., Paleoceanography 2018

line 68: The very old ice at Allan Hills is not really from the surface but from a shallow ice drilling of more than 100 m depth

Methods: the uncertainty in the regression connected to the independent age scales should be discussed

line 85: not clear what r(226) means, please explain. Did you allow for lag correlation? (see also comment on age scales above)

line 89: the limitations of blue ice CO2 reconstructions and d11B reconstructions of CO2 should be discussed as well

Citation: https://doi.org/10.5194/egusphere-2022-574-RC2
- AC2: 'Reply on RC2', Jordan Martin, 24 Nov 2022
  
  Comment: Line 16
  Response: Accepted and revised
  
  Comment: Line 17
  Response: Accepted and revised. kyr – thousand years, kya thousand years ago, Myr – million years, Mya – million years ago
  Comment: Line 25
  Response: Revised in abstract: “…Further, discrete measurements and proxy data of atmospheric CO₂indicate more stable interglacial concentrations during interglacial periods when compared to the glacial periods across the MPT. This supports the theories that changes in factors governing the stability of ice sheets over time (namely the removal of sub-glacial regolith, or phase locking of the Northern and Southern Hemisphere ice sheets at the precession orbital frequency) has resulted in the change from 41 kyr to 100 kyr ice age periodicity…”
  
  Comment: Line 58-59
  Response: Revised to: “The rational in using the LR04 stack as an input parameter to predict CO₂is based on the relationship of ocean temperature (of which ẟ¹⁸O is a proxy measure) with its ability to absorb CO₂from the atmosphere. The solubility of CO₂in the ocean decreases with increasing temperature meaning when the ocean temperature is warmer there is a lower concentration of CO₂ in the atmosphere.”
  
  Comment: Line 66
  Response: This record, while not providing any insight to the trends across the MPT (1250 – 800 kya), supports our general conclusion of a predicted upward departure of CO2 values from our LR04 based predictions. The record presented by Dyez et al., displays significantly higher IG CO2 values than our predicted models, whereas glacial CO2 is more in agreement. We will include this record on Fig02 in our discussion.
  
  Comment: Line 68
  Response: Accepted and revised
  
  Comment: Line 85
  Response: Revised to r2. The test is between our predicted record of CO2 and the observed composite ice core record. As the model we used was a generalised least square model, it accounted for autocorrelation/lag between the predictor (d18O) and CO2 using an AR correlation factor (see methods).
  
  Comment: Line 89
  Response: We will further discuss the limitations of blue ice CO2 reconstructions and d11B reconstructions of CO2 in our discussion.
  
  Citation: https://doi.org/10.5194/egusphere-2022-574-AC2
- AC5: 'Reply on RC2', Jordan Martin, 02 Dec 2022
  
  An earlier incomplete version of the review response was uploaded on 24/11. We expect to upload the full and final response by 09 Dec. Please wait for the full response. Apologies for the inconvenience.
  
  Citation: https://doi.org/10.5194/egusphere-2022-574-AC5
- AC8: 'Reply on RC2', Jordan Martin, 15 Dec 2022
  
  The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2022/egusphere-2022-574/egusphere-2022-574-AC8-supplement.pdf
  
  Citation: https://doi.org/10.5194/egusphere-2022-574-AC8
CC1:
'Comment on egusphere-2022-574', Peter Köhler, 18 Aug 2022

This is a potentially interesting study, which might gain from some more discussions of what has already been done with respect to CO2 across the MPT. Some comments, which might be of interest to the authors:
1. To be transparant in what has been done, the equation which calculates CO2 out of the LR04 benthic d18O stack is missing. Plotting of the LR04 benthic d18O, which is at the core of the approach is also missing.

2. Blue ice CO2 data from Allan Hills have been extended in Yan et al (2019), now also containing snapshots of CO2 at 1.5 and 2.0 Ma.

3. A recent paper by Yamamoto et al (2022) calculates CO2 over the MPT from leaf wax d13C and finds that smaller glacial/interglacial amplitudes in CO2 before the MPT are based on stable glacial CO2, but smaller interglacial CO2 before the MPT. This differs to the d11B-based CO2, and if I got it right might support the here defined Null Hypothesis, which then cannot easily be dissmissed.

4. New CO2 data based on d11B from Pacific cores have recently been published (Guillermic et al., 2022). Ok, data coverage across the last 1.5Ma might be weak, but worth discussing it.

5. CO2 as function of benthic d18O has in an inverse modelling approach already been calculated by Stap et al (2016). This approach has been updateded by Berends et al. (2021a). So comparison to their results might tell, how (if at all) this study shows something new.

6. Maybe also discuss other approaches of CO2 across the MPT, eg C cycle simulation results (apart from those in Willeit et al, 2020, which are cited) of Köhler & Bintanja (2006), or the compilation of at that time available CO2 data and the calculation of a continous high-resolution CO2 record in van de Wal et al. (2011), updated in Stap et al. (2018).

7. The recent review on the MPT (Berends et al., 2021b) gives also an idea about processes including a collection of CO2 data and discusses a potential influence of the carbon cycle on the climate transition.

8. While mentioning the call for the EPICA challenge, maybe also cite / discuss its results (Wolff et al., 2005). They have been shown on 2 posters at AGU fall meeting in 2004 (PDFs for download at: https://epic.awi.de/id/eprint/11721/, https://epic.awi.de/id/eprint/11722/), on which you see, that one of the participants to the challange (N Shackleton) also used d18O to predict CO2 for the 400-800 ky time window.

References:
Berends, C. J., de Boer, B., & van de Wal, R. S. W. (2021a). Reconstructing the evolution of ice sheets, sea level, and atmospheric CO2 during the past 3.6 million years. Climate of the Past, 17, 361–377. https://doi.org/10.5194/cp-17-361-2021
Berends, C. J., Köhler, P., Lourens, L. J., & van de Wal, R. S. W. (2021b). On the cause of the mid-Pleistocene transition. Reviews of Geophysics, 59, e2020RG000727. https://doi. org/10.1029/2020RG000727  
Guillermic, M., S. Misra, R. Eagle, and A. Tripati (2022), Atmospheric CO2 estimates for the Miocene to Pleistocene based on foraminiferal 𝛿11B at Ocean Drilling Program Sites 806 and 807 in the Western Equatorial Pacific, Climate of the Past, 18(2), 183–207, doi:10.5194/cp-18-183-2022. 
Köhler, P., and R. Bintanja (2008), The carbon cycle during the Mid Pleistocene Transition: the Southern Ocean Decoupling Hypothesis, Climate of the Past, 4, 311–332, doi:10.5194/cp-4-311-2008.
Stap, L. B., de Boer, B., Ziegler, M., Bintanja, R., Lourens, L. J., & van de Wal, R. S. W. (2016). CO2 over the past 5 million years: Continuous simulation and new 𝛿11 B-based proxy data. Earth and Planetary Science Letters, 439, 1 – 10, doi: 10.1016/j.epsl.2016.01.022
Stap, L. B., van de Wal, R. S. W., de Boer, B., Köhler, P., Hoencamp, J. H., Lohmann, G., et al. (2018). Modeled influence of land ice and CO2 on polar amplification and paleoclimate sensitivity during the past 5 million years. Paleoceanography and Paleoclimatology, 33, 381–394. https://doi.org/10.1002/2017pa003313
van de Wal, R. S. W., de Boer, B., Lourens, L. J., Köhler, P., & Bintanja, R. (2011). Reconstruction of a continuous high-resolution CO2 record over the past 20 million years. Climate of the Past, 7, 1459–1469. https://doi.org/10.5194/cp-7-1459-2011 
Wolff, E. W.; Kull, C.; Chappellaz, J.; Fischer, H.; Miller, H.; Stocker, T. F.; Watson, A. J.; Flower, B.; Joos, F.; Köhler, P.; Matsumoto, K.; Monnin, E.; Mudelsee, M.; Paillard, D. & Shackleton, N.Modeling past atmospheric CO2: results of a challenge EOS, 2005, 86 (38), 341, 345, doi: 10.1029/2005EO380003
Yamamoto, M., S. C. Clemens, O. Seki, Y. Tsuchiya, Y. Huang, R. O’ishi, and A. Abe-Ouchi (2022), Increased interglacial atmospheric CO2 levels followed the mid-Pleistocene Transition, Nature Geoscience, 15(4), 307–313, doi: 10.1038/s41561-022-00918-1.
Yan, Y., M. L. Bender, E. J. Brook, H. M. Clifford, P. C. Kemeny, A. V. Kurbatov, S. Mackay, P. A. Mayewski, J. Ng, J. P. Severinghaus, and J. A. Higgins (2019), Two-million-year-old snapshots of atmospheric gases from Antarctic ice, Na- ture, 574(7780), 663–666, doi:10.1038/s41586-019-1692-3.

Citation: https://doi.org/10.5194/egusphere-2022-574-CC1
- AC3: 'Reply on CC1', Jordan Martin, 24 Nov 2022
  
  Comment 1:
  Response:
  We will include the form of the equation as:
  CO2 = -33.37 x d18O + 365.16, autoregressive correlation factor (AR): 1
  We will also include the lr04 stack in fig 1
  
  Comment 2:
  Response: The blue ice data at 1.5 Mya does not offer any information as to the CO2 trends across the MPT. It may be argued that the higher (assumably interglacial) CO2 concentrations at this time may offer support to our theories upward departure of the CO2 records from our LR04 based predictions, but the extremely large age uncertainty (~213 kyrs) means we don’t feel we can draw any meaningful conclusions from its inclusion in this paper.
  
  Comment 3:
  Response: This paper certainly was very interesting. It is amazing how well the pattern in the CO2FA match up with the observed CO2 record over the past 800 kyrs. In fig. 1b of Yamamoto et al., the trend in their reconstructed CO2 record from the fatty acid record appears to *in part* affirm what we deduced.
  Overall, the reconstruction shows a departure from the LR04 benthic stack over and preceding the MPT. However, the departure is not in the direction we deduce through our comparison to the d11B and blue ice data and therefore doesn’t support the idea of stable interglacial with declining glacials. But this was not our null hypothesis, simply a deduction based on the data we used and the current studies of CO2 across the MPT. This paper concludes that “These results suggest that the CO₂–ice interaction was reorganized during the MPT” - This agrees with the general rejection of our null hypothesis which states that no change had occurred in the CO2-ice relationship between the observable and currently non-observable CO2 record. In a way, it is another proxy record that differs from our predicted record indicating the relationships between the carbon-climate-cryosphere from 0-800 kya are not consistent 800 + kya.
  
  Comment 4:
  Response: You’re right, average coverage across the MPT, it’s not enough to filter into G/IG averages as we have done with d11N and the blue ice. But the data does seem to support our conclusion of a gradual “upwards” departure of CO2 from the LR04 benthic stack across and prior to the MPT (800 kyr +). Thank you, we will add some discussion on this.
  
  Comment 5:
  Response: This paper (Berends et al., 2021a) does have a similar point to ours in which “Our results 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, we believe they should be viewed as scenarios which can help in interpreting an expected new ice-core record.” Our record was also constructed under the currently observed conditions to act as a comparison to the upcoming million+ year records. Our simple model in comparison yields a high correlation to the same observed CO2 record by Bereiter et al. (r2 0.68). We differ in that we have taken it a step further in the comparison to the discrete d11B and blue ice data over the MPT; by treating the available data we have as snapshots of the future continuous record we were able to make a (low-resolution) but reasonable conclusion that a change in carbon-climate-ice sheet relationship has occurred in the time prior to the current continuous records. From what I understand, this paper does not attempt to draw potential conclusions of CO2 trends across the MPT.
  
  Comment 6:
  Response: We are happy to include discussions of Kolhler and Bintanja (2006); from our understanding the paper also creates a model based on the LR04 benthic stack as a null hypothesis, which sets precedence to our method. We only used the model by Willeit et al., as an example of the trajectory we expect CO2 to depart from the LR04 based predictions, while the main focus of this paper was to compare our model to realised proxy data. So comparing our hypothetical model to another hypothetical model might not offer much by the way of our conclusions, however we will explore the paper by van de Wal et al., but inclusion will be dependent on relevance.
  
  Comment 7:
  Response: Thank you for the reference, it will be used to bolster some of the mechanisms behind the MPT.
  
  Comment 8:
  Response: Thank you. We will add references and discuss the precedence in using d18O to predict CO2 according to N. Shackleton and Berends et al., 2021a
  
  Citation: https://doi.org/10.5194/egusphere-2022-574-AC3
- AC6: 'Reply on CC1', Jordan Martin, 02 Dec 2022
  
  An earlier incomplete version of the review response was uploaded on 24/11. We expect to upload the full and final response by 09 Dec. Please wait for the full response. Apologies for the inconvenience.
  
  Citation: https://doi.org/10.5194/egusphere-2022-574-AC6
- AC9: 'Reply on CC1', Jordan Martin, 15 Dec 2022
  
  The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2022/egusphere-2022-574/egusphere-2022-574-AC9-supplement.pdf
  
  Citation: https://doi.org/10.5194/egusphere-2022-574-AC9

Peer review completion

AR: Author's response | RR: Referee report | ED: Editor decision | EF: Editorial file upload

ED: Reconsider after major revisions (20 Dec 2022) by Erin McClymont

AR by Jordan Martin on behalf of the Authors (30 Jan 2024) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (20 Feb 2024) by Erin McClymont

RR by Tijn Berends (11 Mar 2024)

Suggestions for revision or reasons for rejection

Review of Martin et al., “Predicting trends in atmospheric CO2 across the Mid-Pleistocene Transition using existing climate archives”
By Tijn Berends

The Mid-Pleistocene Transition (MPT) is one of the major challenges in palaeoclimatology, representing a poorly-understood transition in the duration and amplitude of glacial cycles that does not appear to be accompanied by any significant change in orbital forcing. Looking ahead to the expected publication of new ice core CO2 data covering the MPT, the authors present a prediction of these concentrations, based on a very simple statistical model that translates benthic oxygen isotope data into CO2 concentrations. They show that this simple model is able to reproduce the known ice core CO2 record reasonably well, and does not seem to produce significant mismatches with available CO2 data beyond the ice core record, such as (geo)chemical proxies, and blue ice data.

My main concern is that these results are similar to the point of being identical to those I published myself three years ago (Berends et al., 2021, Clim. Past). While the authors do cite this paper, they seem to have looked only at the reconstruction based on physical ice-sheet modelling therein, not at the simple statistical model I presented as well (which I didn’t mention in the abstract, but it’s in the text and in the results, particularly Table 1). That model is arguably identical to the one presented here: a linear regression based on the LR04 d18O stack, producing an R^2 of 0.70 relative to the Bereiter ice core record (versus 0.68 for the authors; possibly a small difference due to different time binning?). My analysis of the results there found pretty much the same conclusions as the authors find here: no appreciable change in interglacial CO2 across the MPT, but a marked drop in glacial values. In that paper, I also compared to the ice core records, boron and alkenone proxies, and blue ice data, although some of the more recent boron proxy data and the Yamamoto leaf-wax d13C reconstruction weren’t available yet then, so that part of this paper is new.

In case the editor decides that this is still enough novelty to warrant publication, I have only a few minor comments on the manuscript, as I generally find it well-written and easy enough to follow.

Minor comments

Lines 73-74: “Emergence of … after the MPT (Fig. 1A)” While the spectral power in Fig. 1 does indeed show a peak around 100 kyr, which coincides with the eccentricity cycle, this kind of analysis is problematic. The “skipped obliquity cycle hypothesis” posits that the post-MPT glacial cycles are mostly alternating 80/120-kyr. Such a signal shows up in a spectral analysis as a single 100-kyr peak, not as separate 80 and 120-kyr peaks (try it out if you like!), so that this result by itself is not conclusive. Please discuss this.

Line 112: “the LR04 benthic stack” Why did you use this one, instead of the more recent, larger stack of 180 records by Ahn et al. (2017)?

Line 158: “van de Wal et al., 2011” Roderik van de Wal and I try to discourage people from using this reconstruction, but instead to use the more recent one by Berends et al. (2021, Clim. Past), which is based on the same method but using newer versions of the ice-sheet and climate models.

Line 171: I cannot understand from the text what this “autoregressive factor” represents.

Line 190: “after removing 50% of data” I’d like to see a bit more explanation about how this works, and what the results are. If your data is significantly auto-correlated (which with a 3-kyr time step I think it is) then I’d think it’s not very surprising that removing some of the data points (which essentially don’t contain any new information) doesn’t affect the least-squares fit.

Lines 261-262: “In the following section … interval” Why do you compare to some data in the Results section, and then to some other data in the Discussion section?

Hide

ED: Reconsider after major revisions (25 Mar 2024) by Erin McClymont

Dear authors,

Thank you for the detailed replies to the reviewers and submitting a corrected manuscript. These have been reviewed by the Editor and an additional reviewer. Although the manuscript has significantly improved from the earlier version, some concerns remain regarding how you might highlight the novelty of the work and ensure that the statistical analysis is clear.

Specifically, please can you comment on how you will address the following:

1. Now that you show the details of the d18O-CO2 regression more clearly, and the improved comparison to CO2 records, the results of this study are near-identical to the work of Berends et al. (2021), which also included a statistical model for prediction. To ensure that this new work has novelty, please highlight in the main text whether this work extends or replicates Berends et al. (2021) and explain how the approaches may have been different, or not.
2. Why did you use the LR04 benthic stack rather than the more recent stack by Ahn et al. (2017)? (Line 112)

Minor comments from the Editor and Reviewer:
Lines 73-74: “Emergence of … after the MPT (Fig. 1A)” While the spectral power in Fig. 1 does indeed show a peak around 100 kyr, which coincides with the eccentricity cycle, this kind of analysis is problematic. The “skipped obliquity cycle hypothesis” posits that the post-MPT glacial cycles are mostly alternating 80/120-kyr. Such a signal shows up in a spectral analysis as a single 100-kyr peak, not as separate 80 and 120-kyr peaks (try it out if you like!), so that this result by itself is not conclusive. Please discuss this.

Lines 113-115: please add some additional text regarding the combined record of bottom water temperature and global ice volume. For the 0-800 ka time interval the proxy record of Elderfield et al. (2012) showed that the shape of the glacial-interglacial changes are quite different between these two components, which may also impact your premise that Southern Ocean is an important link. It’s not a linear relationship between ice volume and ocean temperature.

Line 158 presents the reconstruction by van de Wal et al. (2011) but the more recent version by Berends et al. (2021) should be presented since it has updated ice sheet and climate models.

Line 171: there needs to be some additional text to explain what this “autoregressive factor” represents.

Line 190: “after removing 50% of data”. Please provide additional explanation on how this works, and what the results are. If your data is significantly auto-correlated (which with a 3-kyr time step I think it is) then I’d think it’s not very surprising that removing some of the data points (which essentially don’t contain any new information) doesn’t affect the least-squares fit.

Lines 261-262: “In the following section … interval” Why do you compare to some data in the Results section, and then to some other data in the Discussion section?

Line 325: this statement is not supported by a citation, please include reference to the evidence that boron isotopes over-estimate CO2.

Lines 350-351: clarify here whether you are referring to the whole time interval shown on your figures (0-1.5 Ma), or a narrower period? Figure 3 seems to suggest that glacial CO2 was fairly constant >1 Ma, then declined through ~1000 to ~650 ka. The text currently doesn’t distinguish between these scenarios, which have quite different implications for climate forcing.

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AR by Jordan Martin on behalf of the Authors (07 Jul 2024) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (17 Jul 2024) by Erin McClymont

RR by Tijn Berends (22 Jul 2024)

RR by Lorraine Lisiecki (05 Aug 2024)

Suggestions for revision or reasons for rejection

The revised manuscript is much improved and should be suitable for publication in Climate of the Past with a few small changes to the text to improve accuracy and clarity. -Lorraine Lisiecki

Minor revisions
1. Line 81: Use (Raymo et al., 2006) citation throughout text for hypothesis #3. Raymo & Huybers (2008) was a short review of several existing hypotheses. It didn’t present any new details about the antiphase hypothesis.

2. Line 97: Whether a decrease in CO2 is expected during both glacials and interglacials depends on assumptions about the causes and effects of CO2 change as demonstrated by the authors’ later explanation of why CO2 might decrease only during glacial stages (lines 99-105). Therefore, I recommend changing the wording here to say “reduction in CO2 might be expected in both” or “reduction in CO2 has been proposed in both...”

3. Line 216: This description of the LR04 age model development is unclear because it suggests that each individual core’s age model was based on that core’s sedimentation rate. I recommend revising it to “The age models for these cores are constructed by alignment of their d18O signals, followed by tuning of the stack to a simple ice model based on 21 June insolation at 65°N in a way which maintains relatively stable global mean sedimentation rates.”

4. Line 225: Please clarify the meaning of “(median, 2 sigma, 5.78 ppm).” I think this is supposed to indicate that the 2-sigma value for all bootstrap analyses has a median of 5.78 ppm, but it isn’t clear from the current notation.

5. Line 243-244 (and throughout the results section): It’s not clear to me how the blue ice time window of 1.5 Mya +/- 213 kya is compared to the PRED-CO2 values which appear to only extend to 1.5 Mya. Do the authors only use the PRED-CO2 values from 1.287 to 1.5 Mya? That wouldn’t be a completely fair comparison because the blue ice may be affected by higher or lower atmospheric CO2 levels during the older half of the time window (1.5 to 1.713 Mya). The authors should clarify whether they analyze PRED-CO2 older than 1.5 Mya without showing it in their figures or use different time windows for calculating the average CO2 values from the blue ice and predicted CO2. If they use different time windows, the text should include a caveat that this presents a potential source of bias in the comparison.

6. Line 295: How do the authors conclude that glacial CO2 levels of 217.6 +/- 2.3 and 226.2 +/- 4.0 ppm are NOT significantly different from each other? The 95% confidence intervals for the two estimates do not overlap (if the uncertainties quoted are 95% confidence intervals as described on line 240). Perhaps there is a typo here?

7. Line 421-422: There is an issue here with how the authors describe the antiphase hypothesis proposed by Raymo et al (2006). That publication did not propose an explanation for decreased obliquity sensitivity specifically, rather a change from local (insolation) forcing for a terrestrial ice margin to global (sea level/ice volume) forcing for a marine ice margin. Less total Antarctic ice volume change after the MPT resulted in less Antarctic ice volume sensitivity to all orbital cycles because Late Pleistocene Antarctic temperatures were consistently too cold for significant ice melt in East Antarctic. Therefore, I recommend changing this sentence to “is then proposed to remove sensitivity of Antarctic ice volume to local precession forcing in favor of quasi-100 kyr ice volume changes that are in phase between the hemispheres (Raymo et al., 2006).”

Punctuation, typos, etc:
8. Line 56: Change comma to semicolon “forcing; therefore, the mechanisms”
9. Line 58: Omit comma “A common element in many of these is internal…”
10. Line 82: Omit “to” so that the text says “changes fall into phase”
11. Line 116: “52” should instead be “57 globally-distributed records…” in the LR04 stack
12. Line 204: A negative sign appears to be missing in front of the slope of 33.37 because CO2 is lower when d18O is high (as shown in Fig. 2).
13. Figure 3: The 95% confidence interval shading is very hard to see. I recommend making both the line color and shading color darker.
14. Line 338: I think “date” should be “data”
15. Line 356: Remove extra “and” at the end of the sentence.
16. Line 402: Change “That fact that…” to “The fact that…”
17. Line 404: Insert “the” to say “that the LR04 benthic stack”

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ED: Publish subject to minor revisions (review by editor) (07 Aug 2024) by Erin McClymont

AR by Jordan Martin on behalf of the Authors (28 Aug 2024) Author's response Author's tracked changes Manuscript

ED: Publish as is (10 Sep 2024) by Erin McClymont

AR by Jordan Martin on behalf of the Authors (18 Sep 2024) Manuscript

Short summary

We use existing palaeoclimate data and a statistical model to predict atmospheric CO₂ concentrations across the Mid-Pleistocene Transition. Our prediction assumes that the relationship between CO₂ and benthic ẟ¹⁸O_calcite over the past 800 000 years can be extended over the last 1.8 million years. We find no clear evidence from existing blue ice or proxy-based CO₂ data to reject the predictedrecord. A definitive test awaits analysis of continuous oldest ice core records from Antarctica.