“The Marine Isotope Stage 7: A relic of the 41-ka world?” by Legrain et al provides a valuable compilation and summary of sea surface temperature (SST) spatio-temporal variability during MIS 7, which after revision would make an excellent contribution to Climate of the Past. The comparison with the Clark et al (2024) SST compilation is particularly interesting. Below are some details I would like to see clarified in the manuscript before publication.

Major comments:

Methods:

Line 151: The LR04 benthic d18O curve is affected both by ice volume and deep water temperature. Due to a lag between temperature and ice volume, benthic d18O is not synchronous with ice volume change. The Spratt & Lisiecki (2016) sea level stack or the new Clark et al sea level reconstruction would be more suitable to use for ice-volume correction.

Lines 241-245: Similarity between the results of “selected” and “all” records is not a particularly good argument in favor of using the selected records compilations because the set of all records is acknowledged to be impacted by bias, particularly from the fact that many planktonic d18O records may be impacted by salinity changes. The compilation that excludes all planktonic d18O records produces a noticeably sharper and warmer peak for MIS 7e, especially in the SH stack. Is there anything particular about the spatial distribution of records that have been removed that makes you consider the d18O_p-excluded compilation inaccurate?  Would using the smaller compilation alter any of your main conclusions?

Chronologies:

To what extent is the relative timing of NH SST change and SH SST change set directly by the Greenland and Antarctic alignment targets? To help readers evaluate this, please add the GLT_syn time series to right panel of Fig. 1 and summarize the assumptions inherent in its construction. Are similar regional shifts in SST timing observed when SST and benthic d18O are compared in individual cores? (The timing of benthic d18O changes can vary by 2-4 kyr during terminations also, which would be useful to also mention.)

Are cores from the North Pacific aligned to the synthetic Greenland record? If so, the authors should discuss the degree to which North Pacific SST is expected to be synchronous with Greenland air temperature. For example, do they vary synchronously with one another during T1 and the Holocene?

Fig. S4 – Alignments to core U1429: I have concerns that U1429 is used as an alignment target for other cores given that it has a large gap immediately before (during?) TIII. Could the authors align those cores to a different core? Also, Fig S4 suggests that the age model for U1429 is based on alignment to Sanbao, which isn’t mentioned as an age model target in the main text.

Interpretation:

Line 446: Is the time resolution of the data sufficient to evaluate the SST response to a 2-kyr CO2 overshoot? Low temporal resolution in many records and the smoothing effect of bioturbation may prevent you from observing a short-lived warming response to the CO2 overshoot.

Lines 580-585: The manuscript discusses whether the mode of glacial climate dynamics shifted during MIS 7 due to the particularly strong obliquity forcing at the time. One way to evaluate whether the double peak in MIS 7 actually implies a change in dynamics is to analyze the outputs of simple models that fit the pattern of glacial cycles using a single set of equations and parameter values for the entire late Pleistocene. For example, is a double peak for MIS 7 but not other glacial cycles predicted by the Parrenin & Paillard (2012) model or others?  It might also be useful to compare the performance of models that are forced by 65N summer insolation with those that separately optimize sensitivity to precession and obliquity orbital parameters.

Minor comments:

Line 206: Rather than “inverse” (which often means 1/x), it would be better to say “multiplied by -1”

Line 256: awkward phrase – “display a very pronounced regional variability of the MIS 7”

Line 258: I think “low amplitude” would be clearer than “weakly amplified”

Line 307-308: “North of 23N” or “23-90N” would be clearer than “North to 23N” (same for south)

Line 309: This should be “Southern Hemisphere stack”

Line 564-565: Missing words? “a global synthesis evidence warmer deep ocean temperature during MIS 7C, similar to what observed during Holocene”

Line 565: Insert a paragraph break before “Regarding termination mechanisms…”

Line 614-624: English usage needs revision

The manuscript by Legrain et al. provides a comprehensive and valuable synthesis of sea-surface temperature changes during the relatively understudied interglacial Marine Isotope Stage 7 (MIS 7). I find this to be is an impressive piece of work, which makes a significant contribution to our understanding of climate variability during MIS 7. The study has some limitations that the authors acknowledge, but the main conclusions remain supported by the results. Most of my comments are therefore minor and relate to some points that in my opinion require some clarification.

Specific comments:

L.350: “In contrast, the atmospheric CO₂ record shows a higher concentration during MIS 7e (275 ppm) than during MIS 7c (245 ppm), highlighting a partial decoupling between radiative forcing and global surface temperature variations.” Yes, but the highest CO2 concentrations during MIS 7e only correspond to the overshoot. Mean CO₂ concentrations during MIS 7e are not higher than during MIS 7c but fall within a similar range.

L. 421: “In our ΔGMST reconstruction, MIS 7c emerges as the warmest phase of the MIS 7 sequence, with global mean surface temperatures 0.4 ±0.4°C warmer than during MIS 7e.” Here, the uncertainty is as large as the inferred temperature difference. While I am not calling this result into question, it should be treated more cautiously.

Taken together (i.e. CO2 values excluding overshoot values and uncertainties in the temperature difference between MIS 7c and 7e), the evidence for a strong decoupling between radiative forcing and temperature appears weaker than stated. 

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Caption Fig. 7: CO₂ values correspond to maximum concentrations. How is the “climate optimum” defined? Does it correspond to the time of maximum CO₂ or maximum temperature, even if these are not synchronous? Would MIS 7e and MIS 9e align more closely with other interglacials if mean values were considered instead of peak overshoot values?

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In my opinion Section 4.3 is less convincing than the rest of the manuscript. This section requires clearer explanations of the methodology and rationale behind using the entire MIS 7 interval, given that phasing with each orbital parameter varies greatly within the stage and that the processes leading to TIII and TIIIa are shown to be different. I strongly recommend adding a supplementary figure showing the global and regional SST stacks alongside orbital forcing. This is necessary to assess whether the reported correlations and lags are representative of both MIS 7e and MIS 7c. The method used to calculate the r-Pearson coefficient to estimate the lag must be more detailed in order to allow reproducibility.

L. 510: MIS 7e does occur during declining obliquity as do other interglacials, but its phasing relative to the obliquity maximum differs from most other interglacials. As noted by the Past Interglacials Working Group of PAGES (2016): “The minimum in δ18O also always occurs within or just later than a quarter of an obliquity cycle after the obliquity maximum, with the notable exception of MIS 7c and 7e.”

L. 520: “Regarding external orbital forcing, these analyses reveal a strong correlation with eccentricity (average r-pearson of 0.62), consistent with MIS 7 position within the 100-ka world.” The way this sentence is written implies that eccentricity is the main driver of the 100 ky cycle, which is inconsistent with the current debate. Eccentricity produces only weak insolation changes, so direct orbital forcing related to eccentricity of glacial-interglacial variability thought to be negligible and to influence glacial cycles mainly through modulation of precession (Raymo et al. 1997, Imbrie et al. 1984, Lisiecki, 2010). The physical significance of SST correlation with eccentricity, especially over a period of than one eccentricity cycle as in the case of MIS 7, may be discussed more cautiously.

L. 536: “A conceptual modelling approach identified both precession and obliquity as crucial to constrain the timing of glacial terminations over the past 800 ka (Parrenin and Paillard, 2012).” Additional key references should be cited in this section, such as Huybers (Science 2006, Nature 2011), Huybers and Wunsch (Nature 2004) and Bajo et al. (Science 2020) for the role of obliquity in driving the glacial-interglacial cycles in the 100-ky and 41-ky worlds and for the timing of termination relative to obliquity and precession forcing in the 100-ky world.

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Typos:

L.145: “Gray and Evans (2019)”

L.179: “benthic 18O record”

L. 198: “ΔGSST”

L. 564: “MIS 7c”

L. 565: “during the Holocene”

The centrepiece of this paper is a careful compilation of SSTs across MIS7. This is an excellent effort, very valuable for the community and presenting some interesting insights. There are always going to be issues with the methodologies of such a compilation (to do with choices of proxies, timescale alignments and averaging methods) but the authors here have generally chosen sensible compromises and have explained well the decisions they took. The rationale for reconstructing MIS7 by itself with the added resolution and number of useable datasets that this brings is well-taken. I am therefore confident that this paper should appear in CP. I do have a lot of comments (reflecting my interest and a wish to see everything explained precisely) and suggestions below but they are mainly minor.

There are perhaps two somewhat more overriding issues that the authors should think about (after I completed my review I found that they chimed with comments by rev 2):

1. While I agree that using their methods temperatures are slightly higher in 7c than in 7e at global scale, the difference is within the uncertainty, and is determined only by an increase in the north and equatorial Pacific (Fig 5). This seems quite tenuous to be one of the main conclusions highlighted in both the abstract and the conclusions. I think it should be downplayed somewhat and at least the fact that the two stages are within uncertainty should be mentioned.
2. I also found section 4.3 difficult, particularly with respect to orbital parameters that have very few degrees of freedom. I will discuss below but I think this section is overdone and should be reconsidered.

Provided these and other minor comments below are addressed I would recommend the paper should be published: it will be a very valuable resource for the community. The editor should ensure that the datasets forming various outputs (the stacks shown in Fig 4) are publicly available at the time of publication.

Detailed comments:

Line 27 “The warmest phase across MIS 7 occurs during the MIS 7c substage”. This should be caveated with something like “although the difference from the temperature of MIS7e is within uncertainty of the reconstruction, and the warmth is confined to the south and tropical Pacific.”

Line 72. “MIS 7c may or may not be classified as an interglacial period”. I am a bit confused by this. Under what kind of definition would you not classify it when it is (by your own analysis) a little warmer than 7E and separated from it by a -80 m SL stand (in Spratt and Lisiecki at least).  I think you are creating a controversy that doesn’t really exist here.

Line 130 and around. I was a bit surprised that you used del18O_P as a temperature proxy, but I appreciate that you do consider removing it later. I wonder if you should add a sentence though explaining that it is considered a proxy of temperature and hydrography (salinity) so should be treated with caution (which is why people go to so much trouble to derive specific T-proxies such as Mg/Ca).

Same area and Table S1. Generally you treat MAT as seasonal and all others as annual. But then for ODP8982 you give UK37 as seasonal even though it is treated as annual at all other sites. Is this an error? If not you should probably justify it.

Line 173. While I appreciate the point being made about methane I think in general it’s been shown that the sharp transitions in methane do correspond rather well to millennial variability and Greenland temperature within a very small time lag. I suggest you show GL-SYN on the same figure as methane so we can judge for ourselves whether GL-SYN is acceptable for this purpose.

Line 194. “the randomly gridded SSTs (2-5°) and then the randomly latitudinal SSTs (2.5-10°)”. I don’t understand what this means, please explain what you have done.

Line 196 “weighted mean”. Do you mean that they were weighted by area or by uncertainty? I assume the former but you should explain. For completeness. should you also mention that there are no sites north or south of 60 degrees so polar amplification is only represented in the derived GMST record, while the GSST records are only extrapolar averages.

Line 207-8. I think this is not quite expressed right. It is not impossible for one of your stacks to be negatively correlated with an orbital parameter (for example one can imagine that SH temperature could be negatively correlated with NH summer insolation). But of course it’s interesting to ee whether the correlation is positive or negative so this is the reason to show us r and r^2.

Page 10. Just a presentational point but I would have found it helpful to be pointed at sections of Fig 4 regularly on this page, while at the top of the page the much less interesting Fig 5 is pointed at.

Line 281. “TIIIa is characterized by a more gradual”. Is it? It doesn’t look more gradual to me, it’s certainly smaller in amplitude but the gradient with time looks if anything steeper in TIIIa than in the early parts of TIII.  Either give numbers to back this or alter the text.

Line 310: Again point to Fig 4?

Line 315 More precise would be “with the Northern Hemisphere starting to warm last”. The tropics actually continue to warm after the others reach their peak.

Line 338. “MIS 7c stands out as the warmest interval over the MIS 7 sequence”. Again needs a caveat about the uncertainty.

Line 348. “MIS 7c emerges as the warmest period of MIS 7 (+0.4 ±0.4°C and +0.2 ±0.2°C, respectively)”. You need to clarify that those numbers are the difference between 7c and 7e not the absolute temperatures.

Line 425. “sea-level reconstructions suggest higher stands during MIS 7c than during MIS 7e”. I agree, but this is perhaps a slightly different case compared to the temperature reconstructions, because one would expect radiative forcing or temperature to lead to loss of ice, and because we start from a higher glacial SL stand in 7d than in 8, the same radiative forcing would of course lead to a higher SL stand in 7c than 7e. I don’t think this is surprising.

Page 16. I didn’t find this discussion convincing. Earlier on you explain that the CO2 high in 7e and 9 is transient, with the very high concentrations lasting only centuries. While your data have an average resolution of 1.7 ka. Isn’t it possible that you just aren’t seeing rapid SST excursions, or that the CO2 increase was too short for the SSTs to reach any equilibrium.? Your explanation involving sea ice and obliquity seems very tenuous and speculative.

Line 510. “average r-pearson of 0.84 and 0.89”. Please explain what you mean by the average, do you mean the average r value for the maximum correlation of each stack? Seems a slightly strange thing to average…

Line 513. This says the optimum is at 4100 years but on the figure it shows 3.4 kyr.

Line 520 and following paragraph. I am not at all convinced by this comparison with orbital parameters. You get a strong r with eccentricity across all lags and yet it is obvious that this is because ecc changes very slowly and weakly and is essentially just a single sine curve . No-one looking at ecc and the data in Figs 1 and 4 would see a meaningful correlation, and I think the same more or less applies to the other orbital comparisons though it is less clear. I would honestly remove this part completely to avoid diluting the paper with a rather meaningless analysis (but I don’t insist as long as it is clarified whether the correlations are actually significant given the very few degrees of freedom in the insolation curves).

Page 20. The discussion is OK but I would tend to phrase it differently. Surely in the 100 kyr world we are in a state where the internal timescale of the system is long and it takes a huge amplitude of insolation to overcome that and melt an ice sheet.

Line 641. Again you need to caveat the statement about 7c being warmer than 7e.