This paper measures and analyses Mg/Ca-based deep ocean temperature (DOT) and d18O_benthic and the previously obtained DOT to determine d18O_seawater of the Iberian Margin site U1385 across the last 1.5 Ma covering the Mid-Pleistocene Transition (MPT) and sets results into context of others by (a) making basin- and global-wide averages using 4 other sites, and (b) discussing especially difference to the recent finding of Clark et al. (2025) on mean ocean temperature (MOT) and the deconvolution of d18O_benthic into temperature and seawater components. It concludes that while there is hardly any change in DOT across the MPT there is a drop in d18O_seawater around 900 ka, rather the opposite of what is proposed in Clark et al. (2025).

I cannot judge the methods, so my comments will solely be on the interpretation.

I think this is a solid piece of work on a new data set across the MPT. The discrepancy with the Clark et al interpretation somehow illustrates the state of knowledge that we are facing right now. So, more details here on what is compared and why things differ would help the reader to set things better into context. See my comments below for improvements:

Major issues:

- The used equations for calibration (Eq. 2-4) come with uncertainties, which are completely ignored here. For example, in Weldeab, Arce and Kasten (2016) the full equation is given as Mg/Ca [mmol/mol] = (0.36 ± 0.02) ∗ BWT [°C] + (2.22 ± 0.19). Furthermore, both the Mg/Ca-T calibrations are rather scatted in the temperature range used here (-1 to +6°C). Therefore I suggest to add discussions how these ignored uncertainties impact the results, at best recalculate propagated errors using uncertainties on all the parameters that go into the calibration curves. The 3 equations 2-4 should also be reworked to properly state units (so far it is only mentioned, that T comes as °C). 

- Several times Raymo et al. (2006) is discussed as an probably cause for the deduced salinity changes. However, the global SST compilation in Clark et al (2024) had no power in precession which is the dominant frequency in the Raymo et al (2006) hypothesis. This is discussed in part 3 of the Clark et al papers, just published in Science (doi: 10.1126/science.adv8389). I therefore think this hypothesis can be drop, or at least add this discussion point made in Clark et al to this idea.

- In the comparison to Clark et al (Figure 12) it is important to plot both, the own and the Clark data with uncertainties. Only then can we see if there is overlap or complete disagreement in certain periods. I actually see at least two main differences in T or both reconstructions. First, the drop in T across the MPT in Clark, missing here (discussed by the authors). Second, the much larger G/IG amplitudes in T after the MPT in the Clak data (not discussed). Thus, both T data sets never show similar things. For the part after the MPT Clark et al. used a ratio of GMSST:MOT=1.1, thus no information from deep ocean T are used which could explain the offset between both T. Furthermore, the d18O_sw from Clark contain the removal of a long-term increase of 0.083 permil/My in d18O_benthic, which is not included in d18O_sw of this study. Although this effect is small (1.5 Myr + 0.083 = 0.12 permil) it needs to be mentioned to understand the comparison.

- How can we learn even more from the comparison to the Clark et al. paper? Your stacked d18O_benthic compares very good to the Prob-stack d18O_benthic for the last 400 kyr, but differs somehow before (Fig. 9a). Maybe this illustrates, that for the last 400 kyr your stack is representative of the global signal, but not so much before. Maybe calculate the difference between both d18O_benthic time series to use as a proxy of global representativeness. If you plot this difference then together with the T and d18O_sw comparison to Clark (Figure 12), the reader would see, how much your stack are (or are not) global signals. Maybe this difference can also be exploided as a correction for d18O_sw and/or T, but I am not sure it will work or if it is a good idea. Furthermore, Fig 12 needs different y-axis labels. Your stack of d18O_sw is NOT a global stack (while d18O_sw of Clark is), it is a stack of globally distributed cores from waters below 2km. Actually, maybe at best you should not compare to the MOT from Clark but to the time series of T changes below 2km (Fig 16d in Clark et al., 2025, data should be available from the authors), which uses GMSST and a change in heat storage efficiency (=Delta MOT / Delta GMSST). This has large uncertainties 1.5-0.9 Myr, but basically allows(more or less) a long-term flat line across the MPT, similarly as here (no trend in temperatures).

- So all together, (a) considering if a long-term trend in d18O_benthic is included in plotted data or not, (b) which kind a T curves are compared, (c) highlighting that your approach is a least partially not representing global signals, (d) having some more emphasis on (missed) uncertainties, both your data and the Clark data seem to be not so much in disagreement as so far discussed.

Minor Details:

- Not all SI figures are cited in the main text. Either cite (and order the SI figures according to citation) them or delete them.

- Maybe I missed it, but why does Fig. 2 only show the time 700-1500 ka. Is this the only new part and 0-700 ka was already published elsewhere? Details can probably be extend in section 2.

- Line 435 or so: I believe Pacific bottom water temperature being near-freezing throughout the MPT and thereafter has first been shown in Siddall et al. (2010: doi:10.1016/j.quascirev.2009.05.011).

- Line 668: Raymo et al (2006) was published in Science, not Nature.

In a paper published yesterday in this journal

Thomas et al. present combined benthic foraminiferal Mg/Ca and oxygen isotope data from IODP Site U1385 at the Iberian Margin to reconstruct δ¹⁸O_sw (seawater oxygen isotopes) covering the past 1.5 Myrs. The record is compiled with similar datasets from the Atlantic and Pacific sectors of the Southern Ocean as well as from the North Pacific, allowing the authors to produce a deep-ocean δ¹⁸O_sw and temperature stack that reflects global changes. The study uses a (to my knowledge) novel approach by applying a volume-weighted averaging scheme to calculate the global δ¹⁸O_sw stack, that accounts for the relative sizes of the major ocean basins. This method is contrasted with previous approaches that did not include ocean volume-based corrections, providing new insights into the interpretation of global signals. The main findings of the study indicate increased salinity in the deep Pacific and reduced deep-water temperatures in the Atlantic during glacial periods after 900 ka, compared to the interval between 1.5 and 0.9 Ma. The authors interpret these results as evidence for enhanced glacial water mass stratification in the Pacific after 0.9 Ma, leading to a greater sequestration of atmospheric carbon dioxide in the deep ocean, as well as increased salinity in surface waters within regions of southern component water formation around the Antarctic margins.

The study draws on an extensive dataset, and the methodology appears sound and appropriate to the study’s objectives. The resulting dataset has the potential to make a valuable contribution to our understanding of global ocean temperature, salinity and ice volume changes across the Mid-Pleistocene Transition (MPT). However, the strength of the methodological and analytical work is not matched by the clarity and depth of the data presentation and interpretation. In its current form, the manuscript does not fully exploit the scientific potential of the dataset, and several key aspects of the analysis and discussion require revision and elaboration. Below I outline my major and minor points of criticism in the hope that the authors find them useful in improving and revising their manuscript.

In the following, I will first outline several broad, major concerns that affect the overall interpretation and structure of the manuscript. I will then provide detailed, section-by-section comments and suggestions aimed at improving the scientific robustness and overall comprehensiveness of the manuscript.

1. The manuscript warrants more transparency in the many nuances of the interpretation and should clearly outline the limitation of the data interpretation. For instance, the authors base their conclusion of an enhanced density stratification throughout the entire deep Pacific after 900 ka (compared to 1.5–0.9 Ma) primarily on data from only one Site in the South Pacific and one in the North Pacific. This interpretation is presented as a definitive conclusion, rather than as a working hypothesis supported by limited regional evidence. Potential variations in salinity throughout the entire water column—and their corresponding effects on vertical stratification—are not discussed, and possible regional hydrographic differences are insufficiently addressed in my opinion.
2. Throughout the manuscript, several sections lack a clear explanation and important arguments are presented in a way that they appear somewhat ambiguous. This occurs in multiple places and affects the overall clarity of the manuscript (e.g. comments on lines 42, 127, 172-177, 191, section 4.1). I recommend using more precise wording in many sections to avoid confusion. 
3. In the abstract and discussion, the authors attribute the observed increase in deep Pacific salinity after 900 ka to changes in the source regions of Southern Component Waters (SCW), i.e., Antarctic margin regions (e.g., the Weddell and Ross Seas). However, this interpretation (i.e. a key finding in the abstract) is not substantiated by any evidence presented in the study. In my view, the manuscript provides insufficent discussion of existing literature and data that would support such large-scale changes in SCW source regions during this interval. Revision is needed here.  Moreover, as PDW is a mixture of several water masses, the possibility of temporal changes in PDW end-member composition—and their influence on reconstructed salinity—should be addressed, to support the suggested changes in SCW across the MPT. The authors could consider potential variations in inter-basin connectivity within the Southern Ocean, e.g. using the Antarctic Circumpolar Current strength reconstruction of Lamy et al. (2024), which could help assess whether large-scale circulation changes—rather than solely local shifts in AABW formation—may contribute to the observed Atlantic–Pacific differences across the MPT.
4. Throughout the manuscript, statistical analyses are insufficiently applied when comparing different datasets and time intervals. Statements referring to “significant” differences are frequently made without presenting the results of any formal statistical tests. To substantiate these claims, appropriate statistical analyses (e.g., t-tests, ANOVA) should be conducted and reported. Including quantitative measures of variability and statistical significance would greatly strengthen the robustness of the interpretations and allow readers to assess whether observed differences between regions or time periods are statistically significant.

5. In my opinion, the introduction lacks a clear structure and does not fully establish the central research question. Integrating relevant key studies (e.g. Quin et al., 2022)—many of which are discussed in the discussion (e.g. Hines et al., 2024; Pena and Goldstein 2014, Farmer et al., 2019; Lear et al., 2016) —more prominently at the start would help frame the topic, clarify existing knowledge gaps, and better motivate the study within its scientific context. Moreover, a concise overview of the main hypotheses proposed to explain the MPT—including e.g. the regolith hypothesis (e.g. Clark and Pollard, 1998, Clark et al., 2006), the expansion of North American and/or East Antarctic ice sheets (e.g. An et al., 2024; Bintanja and van de Wal, 2008; Raymo et al., 2006), or feedback mechanisms involving changes of the marine carbon cycle (e.g. Chalk et al., 2017; Willeit et al., 2019)—would provide important context and more clearly situate the study within the broader landscape of MPT research.

6. Overall, the figures would benefit from improved clarity and more explicit information to help the reader follow the comparisons and interpretations of the many timeseries presented. It would be helpful to include the location of each record directly in the figure, for instance by labelling the regions (e.g., Pacific, Southern Ocean, Atlantic…) in the figures. For the Iberian Margin record, it should be clearly indicated which data were generated in this study and which were compiled from previous publications (different symbols or colours). Finally, it would be beneficial to show key time intervals discussed in the manuscript at higher temporal resolution, rather than referring exclusively to the long composite records. This would allow for a clearer evaluation of the main features and transitions emphasised in the text. If feasible, reducing the overall number of figures may improve the readability of the manuscript, as the large number of time series and figures can be somewhat overwhelming for the reader.
7. Salinity on the Practical Salinity Scale (PSS-78) is a dimensionless quantity, and the use of the unit “PSU” (Practical Salinity Unit) is therefore incorrect. The authors should avoid using “PSU” throughout the manuscript. Instead, it should be stated upon first mention that all salinity values are reported on the Practical Salinity Scale (PSS-78) and are thus unitless. It would be preferable to adopt the TEOS-10 (Thermodynamic Equation of Seawater, since 2009) scale and thus report Absolute Salinity in g/kg. However, given that global datasets such as GLODAP and WOA report salinity on the PSS-78 scale, calculated from conductivity, temperature and pressure, clarification in the text that values are dimensionless and follow PSS-78 are sufficient.

Detailed comments:

Line 13, 14: The study would benefit from more cautious wording, as it presents no direct evidence for changes in the carbon storage capacity.

Line 23: One of the main conclusions of the study concerns a salinity change across the entire deep Pacific after 900 ka based on two Sites. However, the text states that δ¹⁸O_sw only reflects variations in global ice volume and local hydrographic effects. This phrasing is somewhat ambiguous and should be clarified.

Line 32: This statement is too vague. Since this appears to be one of the main motivations of the present study, the divergent interpretations should be clearly introduced in the Introduction.

Line 40-43: Please specify what specific concerns are being referred to here and clarify whether “previous findings” refers to Yu & Broecker (2010) or Sosdian & Rosenthal (2009).

Table 1: Please use a consistent coordinate format. The authors should also cite the sources or datasets from which present-day temperature and salinity data were obtained.

Fig. 1: Please indicate in panel (a) where the transects shown in panels (b) and (c) were taken. Given potential differences between the eastern and western Atlantic, this spatial context is important. It would also be useful to include a single transect (covering the Pacific, Southern Ocean, and Atlantic) directly in the main manuscript rather than in the Supplement, as temperature gradients between these basins are a key aspect of the study.

Fig. 3: Please use a consistent capitalisation for “Marine Isotope Stage” throughout the manuscript (either always “Marine isotope stage” as in line 81 or “Marine Isotope Stage,” as in line 103). In addition, clarify the basis of the 2σ error bars mentioned in lines 82-83; are these derived from replicate measurements or represent analytical uncertainty or both?

Line 89 and 92: The phrase “and have similar seawater physical properties” is somewhat vague. Please specify which properties are referred to (e.g., temperature, salinity, density) or include a reference to Table 1 for clarification.

Line 107-109: Do all studies use the same approach for their age model?

Line 122-123: To my knowledge the MD01-2444 record spans ~50–35 ka, which does not include the LGM.

Line 123-124: Please Specify whether this offset is based on overlapping intervals between the cores or on modern temperature differences (which are not listed in Table 1). 

Line 127: I cannot fully understand this sentence. If the text refers to a specific taxonomic level, please use the term “species” to avoid confusion.

Line 128: Please clarify how comparable the results are between the two genera when both were measured.

Line 143-144: Please specify which error the authors are referring to. No corresponding uncertainty is shown in Fig. 2a, so it is unclear what uncertainty estimate is referred to or how it was derived.

Line 146: It seems likely that the intended method was inductively coupled plasma–optical emission spectrometry (ICP OES), rather than "spectrophotometry".

Line 166: I think the intention was to refer to the excluded samples when using the term “the remaining samples.” However, lines 166–169 read as if this refers to the samples actually used in the dataset. Please replace “remaining” with “excluded” to avoid confusion.

Line 168: Please remove the “<” before 0.03 mol/mol⁻¹ or instead use “< 0.1 mol/mol⁻¹,” as Barker et al. (2003) only rejected samples with Fe/Mg < 0.1 mol/mol⁻¹, whereas the 0.03 mol/mol⁻¹ value cited here represents the typical range of their samples rather than an exclusion criterion.

Line 171: units are missing.

Line 172-177: The reasoning in this paragraph is difficult to follow. The use of “rather” and “more likely” is confusing. "Ferromanganese oxide overgrowths" and "authigenic Mn–Fe-oxide coatings" refer to the same type of contamination.

Line 174: What is meant by elevated? Please quantify.

Line 175: Please rephrase "this contamination" as not all Mn in foraminiferal calcite necessarily indicate contamination. It could also reflect (partly) natural incorporation of Mn during biomineralisation.

Line 191: This phrasing is ambiguous. Do the authors mean a 0.32 mmol/mol correction for Mg/Mn_coating within formula 1, or a constant correction for all foraminiferal Mg/Ca data?

Equation 2: How do the core-top Mg/Ca-derived temperatures compare with modern and/or pre-industrial deep-water temperatures at the study site? Please also justify the use of the Elderfield et al. (2012) calibration (originally introduced in Elderfield et al., 2010). The Elderfield et al., 2010 calibrations lower end is ~1°C. Roberts et al. (2016) specifically adjusted the Elderfield calibration for temperatures below 0 °C.

Line 225:  Is this uncertainty based on replicate measurements of the same standard material, or of multiple aliquots of the same sample?

Figure 4: Is there a reason why some interglacials and glacials are missing their labels in panel (a)? For example, MIS 13, 14, 17, and 18 are not indicated. Please clarify or add the missing MIS numbers for consistency.

Line 283: Please ensure consistent use of time units throughout the manuscript. Earlier, “Ma/ka” was used for specific ages or time periods in the past, whereas “Myr/kyr” was used for durations. Here, “1.5 Myrs” is inconsistent with that convention. The same issue appears in line 285. Please standardise the terminology.

Line 284 - 285: This statementis difficult to follow. Is the observed cooling occurring during interglacials, glacials, or consistently across both climate states? Are uncertainties associated with this trend quantified? How are these numbers calculated?

Line 313-316:The comparison is difficult to follow, as it mixes different quantities: interbasin glacial–interglacial temperature differences for 1.5–0.9 Ma with glacial-only temperatures before and after 0.9 Ma. This makes the intended conclusion unclear. Please clarify the rationale for comparing these metrics and include uncertainties.

Line 319-321: If the authors already write “We interpret the greater increase …,” this should strictly not appear in the Results section.

Figure 9: The purpose of the dashed lines in Figure 9 is unclear. In panel 9b, it appears that the upper line might represent the mean interglacial δ¹⁸Oₛ_w across all interglacials and the lower line the maximum values—but this is not explained. Were these lines calculated from the data, or were they arbitrarily chosen? Similarly, in panel 9c, it is not evident how the dashed line is intended to represent “constant deep-ocean temperatures (line 343).” It appears to be placed at ~0 °C rather than reflecting a calculated mean. If this line is meant to represent an average, please show the associated variability (e.g., 2 SD).

Line 351-353: Please add numbers for the Temperature decrease

Line 357-360: There may also be an important interbasin difference between the western and eastern North Atlantic, which challenges the assumption that Iberian Margin records can be treated as representative of the entire North Atlantic basin (e.g., Chalk et al., 2019). This aspect should be discussed, especially in relation to the statement in lines 287–290 that the carbonate ion effect cannot fully explain the temperature differences between Sites 607 and U1385. If the carbonate ion effect is not the sole driver of interbasin- and species Mg/Ca temperature offsets, the authors should explicitly consider and discuss alternative explanations, including east–west basin-scale hydrographic differences, which are currently not addressed anywhere in the manuscript.

Section 4.1: I would appreciate it if this entire section were given more structure. It is difficult to follow the connections between the different hypotheses and literature references and to identify the main message of the section. Throughout the paragraph, several mechanisms are mentioned (e.g., standing volume effect, NADW cooling, SCW salinity increase, ice sheet/shelf melting, and a stratification inversion in the North Atlantic), but they are not sufficiently integrated into a coherent narrative or overarching context in my opinion. For example, it is not clear to me whether the authors are arguing that the North Atlantic was bathed in NCW, in SCW, or favouring some other scenario.

Line 400: Please remove strong, as it is relative.

Figure 11c: Please ensure that your own data points are clearly visible. They are currently obscured by the Grimmer et al. (2025) dataset, which prevents a proper comparison between the two records.

Line 425: The period mentioned (2.75–2.15 Ma, according to the time frame defined in line 38) is not covered by the dataset. Please rephrase.

Line 427-429: Please clarify which MDOT dataset you are referring to and indicate the corresponding figure.

Line 431: See comment on line 400

Line 431-433: I would strongly recommend being more cautious with the argument that the records from Sites 607 and U1313 are complicated by multi-species measurements, since the record presented in this study (U1385) is also a derived from three different species. 

Figure 12: Please indicate uncertainties

Line 453-456: Are there any similar approaches applied to more recent, data-rich intervals? A comparison would help assess uncertainties.

Conclusion: The conclusion includes a substantial amount of important and relevant literature. I would appreciate it if these key studies were introduced in more detail in the Introduction, allowing the conclusion to focus more clearly on the study’s own findings.

Line 465-467: Most of the studies cited in this context examine glacial–interglacial changes—often limited to the last glacial cycle—and do not address variability across the MPT. It is therefore unclear how these references support the conclusions drawn here or how they relate to the long-term patterns discussed in the study.

References cited in this review that do not appear in the manuscript:

Roberts et al.: Evolution of South Atlantic density and chemical stratification across the last deglaciation, Proc. Natl. Acad. Sci. U.S.A., 113 (3) 514-519, https://doi.org/10.1073/pnas.1511252113 (2016).

B. Chalk et al.: Dynamic storage of glacial CO₂ in the Atlantic Ocean revealed by boron [CO₂^3-] and pH records, Earth Planet. Sc. Lett., 510, 1–11, https://doi.org/10.1016/j.epsl.2018.12.022, (2019).

Lamy et al.: Five million years of Antarctic Circumpolar Current strength variability. Nature, 627, 789–796, https://doi.org/10.1038/s41586-024-07143-3, (2024).

An et al.: Mid-Pleistocene climate transition triggered by Antarctic Ice Sheet growth. Science, 385, 560-565, https://doi.org/10.1126/science.abn4861, (2024).

U. Clark & D. Pollard: Origin of the middle Pleistocene transition by ice sheet erosion of regolith. Paleoceanography, 13, 1–9. https://doi.org/10.1029/97PA02660, (1998).

Willeit et al.: Mid-Pleistocene transition in glacial cycles explained by declining CO₂ and regolith removal. Sci. Adv., 5, 7337, https://doi.org/10.1126/sciadv.aav7337, (2019).

B. Qin et al.: Sustained Deep Pacific Carbon Storage After the Mid‐Pleistocene Transition Linked to Enhanced Southern Ocean Stratification, Geophys. Res. Lett., 49, (4), 1944-8007, https://doi.org/10.1029/2021GL097121, (2022).