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

Guillermic, Maxence; Misra, Sambuddha; Eagle, Robert; Tripati, Aradhna

doi:https://doi.org/10.5194/cp-18-183-2022

Articles | Volume 18, issue 2

https://doi.org/10.5194/cp-18-183-2022

© Author(s) 2022. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/cp-18-183-2022

© Author(s) 2022. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 18, issue 2

Research article

|

02 Feb 2022

Research article |

| 02 Feb 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

Maxence Guillermic, Sambuddha Misra, Robert Eagle, and Aradhna Tripati

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Final revised paper (published on 02 Feb 2022)
Supplement to the final revised paper
Preprint (discussion started on 08 Feb 2021)
Supplement to the preprint

Interactive discussion

Status: closed

RC1:
'Comment on cp-2020-158', Thomas Chalk, 22 Mar 2021

Guillermic et al. present boron isotope data from the Western Equatorial Pacific (WEP) at a variety of resolutions across the Neogene. Whilst new boron isotope data from this region is welcome, their results (and interpretations) are not consistent with major findings from many other studies, a point which is not expressed well in the submitted manuscript.

I find that the paper needs some significant reworking, as the message is not clear, it is a big topic to cover and many of the appropriate references are in, but not necessarily called out at the appropriate place.

My biggest concern is with the interpretation of the record. In many places there are large offsets between the WEP data and other published data. I do not suggest that this invalidates the data themselves, but I think a more in depth explanation is often required. The reason given is commonly air-sea offsets, but this cannot be relied upon for >150ppm changes in the mid Pliocene when all the sites are supposedly ‘in equilibrium’. Many of the sites used in the previous compilation of Sosdian et al 2018 are close by (particularly ODP 872, which agrees in absolute terms with ODP 871 in the Indian Ocean). The comparison to ODP site 999 for the Plio-Pleistocene needs some more careful thought, as I do not follow the discussion on changes to air-sea equilibrium there. Diagenesis has the potential to affect these records and this is not discussed at all, nor is the reader pointed to the supplement or data comparisons to compare the raw data, calculations, and calibrations used to gather the final data.

Given the nature of this paper as a low resolution Neogene time-series, I think further validation and comparison are required.

Please note for the below:

MB15, S18, C17, D18, H09, B11, G14, DlV20 refer to the references MartinezBoti et al 2015, Sosdian et al 2018, Chalk et al 2017, Dyez et al. 2018, Hoenisch et al 2009, Bartoli et al. 2011, Greenop et al., 2014 and De la Vega et al 2020 respectively.

Some additional references I have called out to:

SubâPermil Interlaboratory Consistency for SolutionâBased Boron Isotope Analyses on Marine Carbonates - Gutjahr - 2021 - Geostandards and Geoanalytical Research - Wiley Online Library

Robust Constraints on Past CO2 Climate Forcing From the Boron Isotope Proxy - Hain - 2018 - Paleoceanography and Paleoclimatology - Wiley Online Library

Decreasing Atmospheric CO2 During the Late Miocene Cooling - Tanner - 2020 - Paleoceanography and Paleoclimatology - Wiley Online Library

Upregulation of phytoplankton carbon concentrating mechanisms during low CO2 glacial periods and implications for the phytoplankton pCO2 proxy - ScienceDirect

North Atlantic temperature and pCO2 coupling in the early-middle Miocene | Geology | GeoScienceWorld

Miocene Evolution of North Atlantic Sea Surface Temperature - Super - 2020 - Paleoceanography and Paleoclimatology - Wiley Online Library

A diatom record of CO2 decline since the late Miocene - ScienceDirect

Specific points:

Line 26: What is the evidence that these sites are in equilibrium today and for the interval studied. To my knowledge the WEP is not considered to be a stable oceanic environment over time.

Line 29: ‘reproduce the ice core record’ is very strong language for the comparison which has been carried out. There are only 16 points and no comparative data is produced (e.g. numerical data or crossplotted data).

Line 31: The Miocene data is higher than other published data, but so is the Pliocene, and arguably the latter is much more important as more data is available to facilitate the comparison.

Line 33: A 270 ppm transition during the Pliocene iNHG would be very interesting information. This is a huge change (effectively one halving of CO2). Please discuss this more in the context of the other records if you find your Pliocene data to be valid.

Line 68: There is no atmospheric CO2 data from the Pliocene available in the blue ice cores, although they did confirm the presence of ice which is of that age. Please correct this.

Line 72: Foster 2008 is not a B/Ca to CO2 paper, and most recent studies have stopped plotting the B/Ca datasets as there were found to be too many divergent controls on the incorporation.

Lines 94-102: Use Hain et al. 2018 for the strongest case that δ¹¹B can be a viable CO2 proxy, regardless of other uncertainties.

Lines 103: Here you refer to various δ¹¹B studies as ‘high resolution’ and yet earlier refer to the ice cores as ‘relatively high resolution’, I would suggest being more consistent within the manuscript regarding what is ‘high resolution’ given the timescales you are talking about. The ice cores, Martinez-Boti, Dyez, Chalk, de la Vega and Greenop studies are high resolution compared with your work here, but Foster, Hoenisch, Sosdian are more similar to your new records. Consistency with this will stop some of the false equivalency made about resolution in this paragraph.

Line 126: These studies are problematic in their interpretation of CO2 data and call into question the assurance that these sites have remained in equilibrium. This point is repeated on line 152 but without an explanation to the reasoning behind. Given that this is the key assumption in this manuscript I think it deserves more attention.

Line 155: How much could disequilibrium impact these data? No reference is made to preservation or potential diagenesis changes that may impact the data to a far larger extent.

Line 160-166: The age models are not great for these cores, but I do not think that matters given the resolution of the data. It may be worth stating here that no direct comparison of ages between the cores is made.

Line 170: Missing accent on Plouzané.

Line 194: Gutjahr et al 2020 is the updated reference for this.

Line 197: This is great, where is the data though? Can you add a supplementary table?

Line 210: you have ‘less than’ and ‘<’.

Line 217: Why is the 2SD for the δ¹¹B_NEP so much larger than for the other data despite the increase in n?

Section 3.1: This needs to be much more quantitative if you are going to use it to pin all of your results on.

Line 309: These alkenone records are out of date, please refer to Tanner et al 2020 and Super et al 2018 for updated interpretations.

Line 314: The S18 study is a reinterpretation of the same data from the other two, so this sentence either needs to explain that or just use the most recent iteration.

Line 321: This section is not a fair representation of the existing data. The δ¹¹B presented here is ~13.8 ‰ and the minimum in other records e.g. S18 is ~15 ‰, in addition, the data of S18 from ODP 872 is geographically very close to ODP 806. ODP 871 from G14 appears to match the data in S18 quite well, which would imply that another reason is responsible for the difference seen here between 872 and 806 (ocean frontier, preservation or analytical). In addition, G14’s raw values (for T.trilobus) are fairly similar to the data presented here. This would then suggest the reason for the difference is in interpretation and calculation. I think plotting the available data in raw δ¹¹B and either recalculating or plotting calculated CO2 would really help with this point. There is not a huge amount of data for this period and it is worth discussing fully where it does and does fit.

Line 327: I’m not an expert on this topic but I think both of these ideas have been updated in Stoll et al 2019 and Tanner at al. 2020.

Line 328: these very warm temperatures also appear in the Atlantic TEX86 study of Super et al. 2020 which you could cite here.

Line 363: Please given the ‘marginally consistent’ value here as well, rather than just the inconsistent. Also see S18 for reconciliation between the datasets of MB15 and B11.

Line 367: de la Vega capitalisation.

Line 371-373 : please expand on the good agreement here as above. Stap et al. 2016 does not agree particularly well with the other studies.

Lines 376-384: This section reads like it should be in the introduction rather than results.

Line 385: 150 ppm is a lot of disagreement, and as stated it is down to the raw δ¹¹B values. I do not follow the vague argument about disequilibrium that has been made several times now.

As in theory, increased upwelling, increased respired carbon dissolved in surface water, reduce pH and increase CO2 estimate and vice versa.

One issue with 999 is the Panama Isthmus and potential influx of surface EEP water. Upwelling in EEP makes water more acidic therefore, if there were to be an increased influx into the Caribbean, this would reduce pH and increase CO2 estimates. For the inverse to happen, 999 would need to be a sink for CO2 so barring a huge change (e.g. reversal of AMOC), it is more likely that CO2 estimates at 999 will overestimate rather than underestimate CO2. With this in mind the difference between 806/7 and 999 would then require even more disequilibrium in the WEP.

I would favour that the Pliocene section here is more likely to have been impacted by diagenesis, or by the closure of the Indonesian through-flow, which is not discussed here.

Line 389: I am not sure you have the resolution to say this, would suggest removing.

Line 401-405: Please reference this section. I would also incite the logarithmic nature of CO2 forcing here, see multiple papers e.g. MB15, C17, DlV20.

Line 415: All of these papers DO suggest a decline over the MPT, it is the main finding of all of them.

Line 425: When is the end of the MPT, please define.

Lien 427-437: This whole paragraph is extrapolated from one point. I think just show you agree with the data of H09 and move on.

Line 466: Mejia et al 2017 would be a useful reference here.

Line 472: exchange ‘many others’ for an e.g. prior to the reference list, or give a few more.

Lines 497-500: This is precisely the point of H09, C17 and D18, I do not think that the addition of one data point allows the confirmation of these claims.

DlV20 study missing from Table 2, represents the key reference for the mid-Pliocene period. The ordering of this table is also confusingly out of temporal order.

Figure 1: Watch the formatting on the scale axis for the map figure. Please add contours or change the colour scale to something more friendly for colourblindness. The x-axes are also cut off the other panels.

Figure 2: Please add a legend to the plot to define the symbols and shades. It would be helpful to colourise your data and add raw data from other studies in grey behind to facilitate easier comparison. A d11Bborate plot would also be useful to account for the different calibrations between species.

Figure 5: The updated ice core compilation of Bereiter et al. 2015 may facilitate a better comparison for the plot here, or at least including the WAIS divide data from Ahn et al. 2008. A cross plot or calculation of root mean squared error or similar would be a valuable addition.

Figure 7: S18 data is missing from this plot.

Figure 9: Much is made of the low CO2 found in MIS 30, but this figure shows lower(?) CO2 at 1-1.1 Ma which is not discussed.

Figure 10: Again S18 is missing from this figure, despite it being the most complete Neogene study to date (including this one!)

Citation: https://doi.org/10.5194/cp-2020-158-RC1
- AC1: 'Reply on RC1', Maxence Guillermic, 16 Jun 2021
 
 Dear reviewer, please find attach the detailed response. All the Best,
 
 Citation: https://doi.org/10.5194/cp-2020-158-AC1
RC2:
'Comment on cp-2020-158', Anonymous Referee #2, 10 Apr 2021
The manuscript by Guillermic et al presents new Mg/Ca and d11B measurements of planktonic foraminifera spanning the last 17 million years from the Western Pacific Warm Pool at ODP 806 and 807 with the aim of estimating past evolution of Sea Surface temperatures and atmospheric pCO2. . The most significant new contribution of this study is the addition of measurements between 5 and 17 Ma, as the majority of previous d11B measurements since the mid-Miocene are concentrated in the last 4 Ma whereas low resolution data illustrating long term trends in the 4 to 17 Ma time window are to date more limited. The estimation of pCO2 from d11B of foraminifera in this time period is sensitive to a number of uncertainties, including the assumptions of the evolution of d11B of seawater and alkalinity over time. This contribution employs the current best estimates for these parameters and illustrates the sensitivity of the pCO2 estimate to uncertainties in these parameter choices.

While the processing of the new data is clear and uses up to date alkalinity and d11B seawater estimates, the comparison with previous pCO2 estimates is not presented as clearly as it could be, and the discussion of phytoplankton (alkenone) pCO2 estimates for the Miocene is not up to date. I summarize the main content issues which I believe need to be addressed for this manuscript to provide a coherent step forward in understanding of pCO2 in this time interval. Subsequently, I have some suggestions on the organization and structure which I propose could improve transparency and clarity in the manuscript, as well as some more detailed comments.

Content and interpretation:

While the authors present for their own data an updated estimation of the CO2 considering recent proposals for d11B seawater (eg Greenop et al 2017) and alkalinity history derived from Caves 2016 or Zeebe 2005, they do not include in figures (and therefore not thoroughly consider) the published d11B-CO2 estimates which have been recalculated with these same alkalinity and Greenop et al 2017 d11B seawater parameters, namely those compiled and homogenized in Sosdian et al 2018. This is an essential update to make so that the new data from ODP 806 and 807 can be considered in context, and so that the new data contribute to an integrated better picture of the trends and absolute values. In particular, the latest Pliocene CO2 trend is quite clear in the Sosdian et al compilation. Additionally the early Pliocene and Miocene values in the Sosdian et al compilation are higher than in the original publications, and therefore are more consistent with the results as plotted here. Otherwise there is a disconnect between the figures (not homogenized parameters) and the textual mention of pCO2 values recalculated by Sosdian et al 2018. Once this is updated in figures, the discussion should also be updated and clarified.

The estimation of tropical SST over this time interval is not trivial given the uncertainty in seawater Mg/Ca, and I think this warrants further clarification and transparency. An inferred seawater Mg/Ca history is sketched in Figure 2 but the Figure caption does not specify the origin of this curve. The calculation equations are provided in supplement but the input data on seawater Mg/Ca should be illustrated along with the data forming the basis for its estimation (eg the basis from which it is derived). Figure 7 illustrates some uncertainty around the SST, but the Figure legend does not indicate what is represented by this uncertainty. To what extent does the uncertainty in calculated SST (e.g choice of Mg/Ca seawater correction, and regression) affects the estimated pCO2 due to solubility? Also, have the authors considered the influence of a pH correction to the Mg/Ca SST, as conducted in recent study (Sosdian and Lear, 2020) and shown to be significant across the MCT (Leutert et al 2020)?

The references on the alkenone pCO2 reconstruction are not up to date. Lines 308-310 refer only to older publications based on a theoretical diffusive model of CO2. Recent metanalysis of culture carbon isotopic fractionation (epsilon p or ep) data suggested that due to the operation of carbon concentrating mechanisms, ep exhibits a much lower sensitivity to CO2 than originally inferred; application of the sensitivity observed in cultures to sedimentary ep measurements yields a significant pCO2 decline since the mid-Miocene (Stoll et al., 2019). This low ep sensitivity is supported by recent determinations over glaial cycles (eg Badger et al 2019) and further suggests significant pCO2 decline in the late Miocene (Tanner et al., 2020) which would be a relevant reference for comparison in section 3.4. A detailed updated discussion is provided in Rae et al, 2021.

The discussion of previously published d11B records is in many places overly superficial. For example in lines 314-316, previously published d11B records of the MCO (Sosdian et al 2018, Greenop et al 2014) are diminished in importance by suggesting " it is unclear if these values accurately reflect the atmosphere given the sites may or may not have been in equilibrium with the atmosphere.." The cited studies reflect multiple sites (ODP 926, 999, 668, 761..), all in comparably reasonable locations to be close to equilibrium with the atmosphere. Unless the authors would like to present clear new evidence that some of all of these sites are less likely to have remained in equilibrium with the atmosphere than ODP 806 or 807, the original interpretation that these sites (of preindustrial pCO2 disequilibrium <25 ppmv) remained close to equilibrium should be respected, and other potential explanations for the differences should be explored.

Site 806 and 807 are sites estimated to have fast rates of diagenetic recrystallization (Mitnik et al 2018). For example, averaged over the upper 80 m of sediment (appx 3 million years given sedimentation rates), authigenic carbonate is estimated to comprise 19% of total carbonate at 806 and 36% at 807; in comparison other sites like ODP 999, the authigenic carbonate is <1% of total carbonate in the same depth and time interval. It might be helpful for the authors to acknowledge this and comment on evidence for how this may or may not affect the 11B and Mg/Ca results of the planktic foraminifera.

The coherency of the d11B-pCO2 estimates with ice core pCO2 is always a useful comparison, but its effectiveness relies on the precision of the age model used for this portion of the sediment core (as well as the precision of the ice core age model, which cannot be investigated here). Particularly relevant to the last 800 ka, section 2.2. should detail on what the age models are based not just the publication source. From the reference cited for the last 1.35 Ma, it appears the age model is based on d18O of planktic G. ruber - is it still tuned to SPECMAP chronology as in Lea et al 2000, or is it retuned to LR05? In Figure 5, I think it would be better to show the site 806 d18O G. ruber in the upper panel, eg the metric from the same site and age model as the d11B estimates, rather than the LR05. Then, I would suggest in addition to the time series, a scatterplot of the d18Oplanktic vs d11B-based pCO2 from 806 (assuming that d18O is available for the same core intervals - this gives an estimation of the coherency of pCO2 and glacial cycles in the same core without age uncertainties; were any d18O made on 807?), and also importantly a scatterplot of the d11B-based pCO2 vs ice core pCO2 .

Suggestions on organization:

I recognize the challenge of illustrating the effects of possible assumptions of d11B and alkalinity on the final CO2 calculation, but I am not convinced the current organization is the most effective and it leads to an unusual ordering of figures. The Methods heading "2.7 " effectively starts presenting results and sensitivity analysis.

The authors might consider if a more direct presentation of results and discussion could:

a) begin with section 3.1, and start with the current Figure 5 - the last 800 ka uses modern d11B sw and alkalinity so is not subject to the uncertainties/sensitivity analysis on both parameters .

b) continue with a section on the measured indices and summarizes the findings in of the current Figure 2 which presents the measured results

c) comment on the inferred trends in SST and uncertainties in their calculations , and comparison with other SST histories both from Mg/Ca (Sosdian and Lear 2020) as well as TEX86 (Zhang et al. 2014, ) Lines 286-288 needs to clarify if the measured Mg/Ca is consistent with the other published Mg/Ca, or if the calculated temperatures are consistent with the published Mg/Ca calculated temperatures; and in the latter case, have the temperatures for all these studies been recalculated using the same assumptions of Mg/Ca seawater and temperature regression as used for the new data here?

d) discuss sensitivity of Neogene pCO2 estimations to assumptions of d11B seawater and alkalinity, which could introduce the current Figures 3 and 4 as the sensitivity of the results to d11Bseawater and alkalinity (and is there sensitivity to SST) and incorporate the introduction to this currently in the methods section

-continue with the discussion of temporal trends in calculated pCO2

As the manuscript begins to go through the main pCO2 results, I am not fully convinced that the current organization of the discussion is the most straightforward and concise. In the current organization the authors new data seems like it gets buried within the discussion. If the current time interval based structure is used, I believe it would be useful if in each heading of the results/discussion section, the authors presented first the summary of their own new results, and followed it with comparison to other proxy pCO2 results and finally to climate. Also, if organization based on time periods is used then clearer section headings are needed For example 3.3 is "Miocene" but 3.4 is "Late Miocene" which is a period nominally included included within the Miocene heading. I am not sure if division of the Pliocene into the warmth then glacial intensification then Pleistocene (3 sections) is really needed to discuss the author's new data, as these are time periods with substantial previously published data and interpretations and the authors new data are largely consistent with and reproduce these earlier results. Overall, I believe the discussion section can be streamlined and made more concise. Some sections such as 3.9 seem very extraneous, as there is really limited new SST data and it is not coherently presented to evaluate east west gradients; I suggest this section be eliminated from the discussion. Section 3.8 is not really clear in advancing a mechanism for the CO2 variation, and I suggest the key points might be effectively commented within the context of the Miocene and Pliocene sections of the text.

-------------------

Detailed comments:

ALL of the figures should more accurately show the true data density, including Figures 3 and 4 - continuous fill patterns and no symbols is not a clear way to represent the data. At minimum, symbols are bars are needed to show where there are datapoints (alternatively rather than complete shading, points with error bars could be illustrated to show the sensitivity).

And in FIgures 6-8 and 10, the broken shading at least alerts to the data gap, but I think it would be ideal to show no shading over the long intervals without datapoints.

Please clarify the basis of the age model (eg benthic d18O, biostratigraphy, etc), Section 2.2 is not sufficiently clear.

Could a more direct heading for Methods section 2.6 be developed?

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References cited (not cited in the manuscript):

Mitnick, Elizabeth H., Laura N. Lammers, Shuo Zhang, Yan Zaretskiy, and Donald J. DePaolo. "Authigenic carbonate formation rates in marine sediments and implications for the marine δ13C record." Earth and Planetary Science Letters 495 (2018): 135-145.

Rae, James WB, Yi Ge Zhang, Xiaoqing Liu, Gavin L. Foster, Heather M. Stoll, and Ross DM Whiteford. "Atmospheric CO2 over the Past 66 Million Years from Marine Archives." Annual Review of Earth and Planetary Sciences 49 (2021).

Sosdian, S. M., and C. H. Lear. "Initiation of the Western Pacific Warm Pool at the Middle Miocene Climate Transition?." Paleoceanography and Paleoclimatology 35, no. 12 (2020): e2020PA003920.

Stoll, Heather M., Jose Guitian, Ivan Hernandez-Almeida, Luz Maria Mejia, Samuel Phelps, Pratigya Polissar, Yair Rosenthal, Hongrui Zhang, and Patrizia Ziveri. "Upregulation of phytoplankton carbon concentrating mechanisms during low CO2 glacial periods and implications for the phytoplankton pCO2 proxy." Quaternary Science Reviews 208 (2019): 1-20.

Tanner, Thomas, Iván HernándezâAlmeida, Anna Joy Drury, José Guitián, and Heather Stoll. "Decreasing atmospheric CO2 during the late Miocene Cooling." Paleoceanography and Paleoclimatology (2020): e2020PA003925.
Citation: https://doi.org/10.5194/cp-2020-158-RC2
- AC2: 'Reply on RC2', Maxence Guillermic, 16 Jun 2021
 
 Dear reviewer, please find attach the detailed response. All the Best,
 
 Citation: https://doi.org/10.5194/cp-2020-158-AC2

Peer review completion

AR: Author's response | RR: Referee report | ED: Editor decision

ED: Reconsider after major revisions (21 Jun 2021) by Hubertus Fischer

AR by Maxence Guillermic on behalf of the Authors (22 Jun 2021) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (22 Jun 2021) by Hubertus Fischer

RR by Anonymous Referee #2 (25 Jul 2021)

Suggestions for revision or reasons for rejection

Overall I would like to praise the authors for the careful revision of the figures which has really clarified the presentation of the new data and its comparison with previously published records. The text now reads more clearly in many sections as well. There are a few final issues I would propose the authors clarify, and some proofing issues that I identify.

The text at the end of methods (lines 242-243) summarizes the processing of Mg/Ca to SST, noting that it is corrected for influences of pH and salinity. However, additionally, the SST has been corrected for inferred changes in the Mg/Ca of seawater (detailed in the supplement). This point also needs to be mentioned in lines 242-244 of the main text, so the reader is aware of it, and is directed to the supplement for further details.

The figures include detailed dashed lines to show correspondance to specific events such as MMCT defined from the benthic d18O stack of Zachos 2008 (and in younger part Lisieki-Raymo). I would suggest also including the low resolution benthic 18O from Lear et al 2015 from 806, to help document the comparison with these events within the same site, because the benthic 18O at 806 and the d11B-based CO2 and SST can therefore be compared within 806 without the complication of uncertainty in age models due to the normal limitations of precision in biostrat.

line 406 makes a rather broad statement about the shift in d13C and d18O over the MMCT supporting drawdown of CO2 by organic carbon burial, with no reference. As these benthic data were previously published and interpreted, and this coincidence and organic burial hypothesis advanced long ago, I would suggest referencing a number of papers which have produced the benthic 13C and 18O results and originally provided this interpretation, to support your link of organic carbon burial with CO2 drawdown. The recent discussion paper in Climate of the Past by Raitzsch et al. provides detail over this interval and may be worth citing as well.

The section 3.6 makes a few general statements that could be better balanced with context and caveats. The linking of the MCO pCO2 increase with the Columbia River is interesting but I think it is better balanced to comment that this is superimposed on temporal variation of the large volcanic CO2 flux from seafloor production, which has been estimated by recent tectonic models with increasing precision (eg Muller et al 2016). Likewise the estimated volume and CO2 flux from the Columbia River Basalts is very modest compared to other LIP in compilations (Courtillot et al 2003), suggesting that if it is contributing to high CO2 at the MCO, a better understanding of eruptive volume and volatile emissions is needed.
Likewise a bit of clarification about the d7Li is required - eg. note that the authors favored alkalinity model is Caves et al, but Caves is discussing specifically why d7Li is not necessarily a proxy for silicate weathering flux. I agree that it is interesting to note the coincidence of inflections in the d7Li curve and features of the pCO2 record, but I find the current lines 508-524 have gone too far in oversimplifying the d7Li and a few sentences to provide better context to the interpretation of d7Li and debates would make this final section much more useful.

Detail: Lear 2015 is missing in the reference list (it is cited in text line 179).
Detail: Supplemental Information (there is no "s" needed at the end of "Information")
Detail: the citation of Tanner et al 2020 in line 360 does not make sense as that sentence refers to MMCT and Tanner et al cover only the Late Miocene after 8 Ma. The citation in line 414 is appropriate although the proposed reason for differences is unclear attributing it to " the oceanographic setting of 1088" without indicating what process about the oceanographic setting is proposed to explain the difference.
Detail - line 436 either "during" or "from" - one of these words needs deleting
Detail - line 483-484, use consistent formatting for the +/- values of CO2.

Raitzsch, Markus, Jelle Bijma, Torsten Bickert, Michael Schulz, Ann Holbourn, and Michal Kučera. "Atmospheric carbon dioxide variations across the middle Miocene climate transition." Climate of the Past 17, no. 2 (2021): 703-719.

Müller, R. Dietmar, Maria Seton, Sabin Zahirovic, Simon E. Williams, Kara J. Matthews, Nicky M. Wright, Grace E. Shephard et al. "Ocean basin evolution and global-scale plate reorganization events since Pangea breakup." Annual Review of Earth and Planetary Sciences 44 (2016): 107-138.

Courtillot, Vincent E., and Paul R. Renne. "On the ages of flood basalt events." Comptes Rendus Geoscience 335, no. 1 (2003): 113-140.

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RR by Thomas Chalk (09 Aug 2021)

ED: Reconsider after major revisions (10 Aug 2021) by Hubertus Fischer

Dear authors

the revised version of your manuscript has now been seen by the two referees that also assessed the initial version. Both referees acknowledge the significant changes that you did in the revision, which over most parts meet the points of criticism initially raised by both the reviewers. Reviewer #2 has added a few more constructive suggestions for improvement in the second review, in particular on the long-term volcanic and weathering carbon imbalance, which I would ask you to include in your re-revisions. Both referees also make a few comments on language/textual improvements etc. (see also my editorial comments below). I would regard these points raised by the referees as minor revisions as they imply mainly textual changes and can be implemented in a straightforward manner.

However, referee #1 also raises a point on the overall accuracy/validity of your pCO2 reconstruction based on the validation against the ice core data and I have to admit this gives me some headache as well. According to the figure caption of Figure 3E your r^2 is only 0.09, i.e. this would imply that only 10% of the variance in your d11B-derived pCO2 could be explained by atmospheric CO2 as contained in ice cores. Is this correct or is the r^2 of 0.09 only a typo? Looking at this figure, I visually can see a clear correlation although with a regression slope larger than 1. In the main text you also refer to some p values, but these numbers do not agree with the ones in the caption and I am unable to attribute the numbers to the respective subplots. Please double check all the numbers and change the text to make things crystalclear. Moreover, it is unclear to me what the uncertainties in the x and y component of the scatter plot 3E refer to. In fact, some of the ice core CO2 data (x-axis) have a larger uncertainty than the d11B-derived data points (y axis) which appears virtually impossible as long as this does not include dating uncertainties. Please also mention in the caption which evaluation/corrections scenario you used for the d11B-derived pCO2 in Figure 3E. Finally, your linear regression is suggesting a slope smaller than 1 although the range in the d11B-derived pCO2 is larger than the range in ice core CO2!!!??? This is likely due to you using a one-sided regression, which in case of considerably uncertainties in x and y underestimates the slope. In fact, you should use a 2-sided regression (York et al., American Journal of Physics, 2004) for this scatter plot. It is also puzzling that 50% of the data points do not fall within the prediction envelope, what is the error this envelope refers to? In any case, for the validation period of the last 800 kyr your data seem to be clearly related to atm. CO2 but seem to overestimate somewhat the true atmospheric CO2 concentration range either due to methodological, correction/evaluation, diagenesis or CO2 surface water saturation issues. Although this systematic overestimation must not hold back in time, it is important to openly communicate that the absolute levels of your pCO2 reconstruction may be biased. However, the relative changes on time scales of 1 Myr, where alkalinity changes do not play such a great role may be more reliable. The issue of uncertain absolute CO2 levels in the past is also nicely illustrated in your evaluation scenarios, which show that the overall Miocene CO2 levels strongly depend on the assumptions made during the evaluation/correction of the data in particular on alkalinity. This is clearly an issue the d11B community will have to work on in the future.

In summary, I think the low correlation/weak validation of your data for the ice core period does not justify rejection of the manuscript as the paper, nevertheless, adds substantial information on pH and CO2 changes over the last 20 Myr. However, I strongly feel that the discussion should be more open to the limitations of the reconstruction and the large uncertainties in the overall reconstructed CO2 levels. This is in my eyes overly optimistic in the current version. A more critical assessment of the overall levels especially in the conclusions and the abstract, would likely also satisfy the criticism of referee #1.

I therefore would urge you to include such a more differentiated discussion in the re-revised version. Please add a point-to-point reply to the points raised by the referees and me in this second round of reviews and a track change version of any re-revised manuscript relative to the current revised version. Your replies will decide whether another independent review of the paper is needed. Please find below a few more technical editorial comments that I would ask you to include as well:

- at several instances in the paper you refer to the ice core data as "Vostok data". This is incorrect as only the data younger than 420 kyr are from Vostok, the older data is from the EPICA Dome C ice core. Please change this throughout the manuscript by just referring to "ice core data" and providing the relevant references (Petit et al., 1999, Lüthi et al., 2008, Bereiter et al., 2015). In the main text a reference such as "as compiled by Bereiter et al., 2015" may be sufficient in many cases but at least in the figure captions the original data references should be provided. A similar point was raised by referee #1 for the d11B compilation by Rae et al. Again, provide the full original references at least in the figure captions. Note also that in several figures you refer to the ice core data as Bereiter et al, but this data set only covers the last 800 kyr. Earlier ice core data comes from blue ice samples. Please correct accordingly and provide the correct references (see also comments on Figures below)

- in line 118 you refer to an air sea flux of xx ppm, this is not a flux but an air sea difference

- line 172: there is something wrong with this sentence

- throughout the manuscript add a space between numbers and units

- line 411. Here you refer to a pCO2 peak at 9 Myr in Sosdian. I couldn't find this point, maybe refer to the age more precisely?

- line 517: there is something wrong with this sentence

Figure 2: There are brown triangles in figure 2B and a cross in figure 2C but not in the legend

Figure 3: see comments on Figure 3 above and in review #1. Please delete the subscript Rae et al in the legend and cite the data and compilation papers in the caption

Figure 4: there are orange circles in this figure but not in the legend

Figure 5: Please delete the subscript to individual papers in the legend and cite the data and compilation papers in the caption

Figure 6: Please delete the subscript to individual papers in the legend and cite the data and compilation papers in the caption. There are bold and thin triangles/squares in the figure but not in the legend.

Figure 7: Please delete the subscript to individual papers in the legend and cite the data and compilation papers in the caption. There is no legend for the SST and d11B-pH subplots

Figure 8: Please delete the subscript to individual papers in the legend and cite the data and compilation papers in the caption. There is no legend for the SST subplot

Figure 9: Please delete the subscript to individual papers in the legend and cite the data and compilation papers in the caption. There is no legend for the SST subplot

Figure 10: Please delete the subscript to individual papers in the legend and cite the data and compilation papers in the caption. There is no legend for the SST subplot

Figure 11: Please delete the subscript to individual papers in the legend and cite the data and compilation papers in the caption.

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AR by Maxence Guillermic on behalf of the Authors (27 Oct 2021) Author's response Author's tracked changes Manuscript

ED: Publish subject to technical corrections (12 Nov 2021) by Hubertus Fischer

Dear authors

thanks for all the changes. I think this has greatly improved the paper and made the discussion much more differentiated. I had another read of the paper and found a list of language issues that I would ask you to fix (see list below). Please also check the quality/resolution of your figures. At least Figure 5 is very bad resolution in my pdf.

Please send a short list with the changes you did together with the revised version.

All the best Hubertus

Language edits (please note that the line numbers below refer to your new "Authors tracked changes" version)
line 36: "from the Miocene to the late Quaternary"
line 59: I would suggest to delete: "from regions...atmosphere."
line 64: "into older atmospheric"
line 65: "of CO2 prior to"
line 82-85: there is something wrong with this sentence, please fix
line 107: "Moreover, although"
line 118: "open ocean region"
line 133: "support stable air-sea (dis-)equilibrium conditions"
line 135: "on prior low-resolution recosntructions"
line 143: "correcting for"
line 146: "recent times"
line 182: "A comparison of"
line 233: "on 11B"
line 259: "using d11Bborate"
line 262: "are provided in"
line 269: "1 Myr"
line 289: "are met despite large scatter"
line 291-92: unclear, clarify this sentence especially on bootstrapping
line 295-96: I do not agree or misunderstand: The age scales for the marine records may be consistent with each other but they are independent of the ice core age scale. Please clarify sentence.
line 319: "were reconstructed"
line 324: ", respectively"
line 326: "small (ca. 1°C) change into"
line 339: "used in our calculations"
line 340: "are provided in"
line 382: the part "in concert with ocean circulation " is unclear, clarify
line 399: "suggest that the"
line 413: "pCO2 data increase"
line 420: "are found during"
line 431: "of pH of"
line 461: " "Raitzsch"
line 485/86: "regions from 3.3. to 2.7 Ma"
line 518: it is debated whether eccentricity directly plays a role. May be write "high amplitude, lower frequency (app. 100 kyr) cycles"
line 556: "to MCA is generally in parallel to increasing volcanic"
line 563: explain K-Pg boundary
line 573-74: fix/clarify sentence "will determine the nature... seawater d7Li"
line 582: "by a change"
line 585: "increasing seawater"
line 587: "MCO is synchronous"
line 619-20: fix sentence: "and the MCO values...higher pCO2"
line 621: replace "likely" by "potentially" ???
line 626: "for the time interval app. 3.3-3.0 Ma"
line 627: " for the Pliocene"
line 1072: "corrected for"
line 1075: "to recent times"
line 1078: "squares represent data"
line 1094: "pCO2" SUBSCRIPT "ice core"
line 1096: "bootstrapping"
line 1097-98: fix/clarify sentence
line 1102: "temperatures were"
line 1133: "from the compilation by Rae"
line 1135: "using the constant"
line 1152: "color is indicating"
line 1156: "temperatures"
line 1159: "are compilation data from Rae"
line 1163: "pCO2 values"
line 1164: "pCO2 values"
line 1168: "color is indicating"
line 1172: "temperatures"
line 1177: " pCO2 values"
line 1190: "color is indicating"
line 1194: "temperatures"
line 1198: "represent the CO2 compilation"
line 1199: "from the compilation by Rae"
line 1209: "color is indicating"
line 1213: " temperatures based on literature"
line 1217: "from the compilation by Rae"
line 1228: "are indications when"
line 1230: "color is indicating"
line 1236: "shown is the timing of"
line 1237: "the eruption of"

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AR by Maxence Guillermic on behalf of the Authors (25 Nov 2021) Author's response Manuscript

Short summary

Here we reconstruct atmospheric CO₂ values across major climate transitions over the past 16 million years (Myr) from two sites in the West Pacific Warm Pool using a pH proxy on surface-dwelling foraminifera. We are able to reproduce pCO₂ data from ice cores; therefore we apply the same framework to older samples to create a long-term pH and pCO₂ reconstruction. We give quantitative constraints on pH and pCO₂ changes over the main climate transitions of the last 16 Myr.