Millennial variations in atmospheric CO<sub>2</sub> during the early Holocene (11.7–7.4&thinsp;ka)

Shin, Jinhwa; Ahn, Jinho; Chowdhry Beeman, Jai; Lee, Hun-Gyu; Seo, Jaemyeong Mango; Brook, Edward J.

doi:https://doi.org/10.5194/cp-18-2063-2022

Articles | Volume 18, issue 9

https://doi.org/10.5194/cp-18-2063-2022

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

https://doi.org/10.5194/cp-18-2063-2022

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

Articles | Volume 18, issue 9

Research article

|

06 Sep 2022

Research article |

| 06 Sep 2022

Millennial variations in atmospheric CO₂ during the early Holocene (11.7–7.4 ka)

Jinhwa Shin, Jinho Ahn, Jai Chowdhry Beeman, Hun-Gyu Lee, Jaemyeong Mango Seo, and Edward J. Brook

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Final revised paper (published on 06 Sep 2022)
Supplement to the final revised paper
Preprint (discussion started on 25 Aug 2021)
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Interactive discussion

Status: closed

RC1:
'Comment on cp-2021-113', Anonymous Referee #1, 14 Oct 2021

Review of

Millennial variations of atmospheric CO2 during the early Holocene (11.7-7.4 ka)

by J. Shin et al.

The authors present a new high-resolution CO2 record, measured on samples from the Siple Dome ice core, from 11.7 to 9 ka and complement an earlier data set from 9 to 7.4 ka from the same core. This results in a high-resolution CO2 record covering the beginning of the Holocene. Interpreting the combined data set they identify small millennial-scale variations of a few ppm and correlate them to various paleoclimate records. The authors speculate that solar irradiation may be responsible for the CO2 variations. The new data, although covering only 2,700 years and thus very short, are important as they close the gap of the early Holocene in the CO2 data of this ice core.

In the present version the authors do not make a sufficiently convincing case for their hypothesis of an influence of solar fluctuations in causing CO2 changes. This is due to (i) questionable data processing that results in very small sigma uncertainties, (ii) essentially correlation-based arguments, (iii) a relatively short discussion of mechanisms, (iv) a nearly inexistent critical reflection on leads and lags that are identified in the data, and (v) a missing credible causal chain from solar fluctuations to purported CO2 variations. Overall, this manuscript requires substantial revisions to reach the maturity of a CP article.

Comments:

1) The interpretation rests on the relatively small CO2 fluctuations that are visible in the filtered data presented in Fig 1. The authors report 2 sigma uncertainties based on Monte Carlo simulations. 2 sigma uncertainties typically contain more than 95% of the data points based on the assumption of normal distribution. The dashed lines in Fig 1, however, are extremely close to the running mean. How can this be? I would have expected a much wider uncertainty band based on the scatter of the data points. Such a wider band would put serious question marks on the significance and robustness of the small fluctuations (few ppm) that are reported in this paper and that are the basis for the claimed sun-CO2 relationship. The authors need to critically revisit the determination and depiction of this 2 sigma uncertainty.

2) The authors use a data processing that is not sufficiently explained. They mention a 1-yr interpolation (line 193) and a 250-yr smoothing, followed by a high-pass filtering at 1/1800 yr-1 and a resampling every 10 years. This sounds like very heavy machinery, and I wonder how robust the results are in light of these interventions. In particular, the 1-year interpolation may add some information to the time series that is simply not inferable from the limited resolution of the measurements and their individual uncertainties. I am very sceptical of this statistical treatment of the data. Furthermore, all other paleoclimate data are treated with the same method, and without showing the original data points of these records the authors do not make a convincing case for the significance of such small variations. In short, the data treatment is insufficiently described, and a robustness analysis is missing.

3) Panel B of Fig 1 shows the high-pass filtered signal. Peak-to-peak amplitudes are max 4 ppm with some fluctuations of less than 1 ppm relative to the mean. So far, such small variations in CO2 measured from ice core samples, have not been interpretable, given the typical measurement uncertainties that are known from the literature. The authors have the burden of making a convincing case that such fluctuations here can indeed be interpreted as variations in atmospheric CO2 concentrations.

4) Comments 1 to 3 also apply to Fig. 2. For the CO2 data from EDC (Monnin et al) and WAIS (Marcott et al), the curves are misleading. Inspecting the original data in these papers, I am not convinced that the fluctuations that are shown in the processed data exhibit a robust signal that would represent atmospheric variations. Here a much more careful analysis and statistical assessment (see comment 2) would have to be carried out to see whether such small CO2 fluctuations can be identified in all three ice cores. It appears on the basis of the presented information that the authors go too far in their interpretation for this relatively short record.

5) Fig 3 suggests evident leads and lags, but they are not discussed and explained in the text. If it turns out that the fluctuations are robust, then these leads and lags need to be considered and discussed in the context of mechanisms. They may be helpful in constraining the causal chain, if such does indeed exist, from solar variations to the CO2 fluctuations. The authors end their discussion at a correlation analysis among the different paleoclimatic records of Fig 3. Correlation is not causation, and thus the arguments for a solar connection to CO2 fluctuations is rather weak, if it is active at all.

6) Further to Fig 3, age scale uncertainties between the different records seem to be ignored. These would represent an additional significant uncertainty regarding leads and lags. It is evidently difficult to come up with a common age scale, but the minimum expected would be an assessment the consequences for the conclusions.

7) ENSO is offered as one of the possible mechanisms for CO2 fluctuations (lines 227ff). The discussion is rather superficial and incomplete. While Feely et al (1999) identify a decrease of CO2 during the 1991-94 El Nino, Chatterjee et al (2017) provide a more detailed, satellite-based analysis of the effects of the 2015-16 El Nino. After an initial decrease, consistent with Feely et al, they observe a stronger increase in the later stages of this El Nino, with the overall result of a CO2 increase. The two El Nino episodes are quite different with the former persisting for 3 years, while the later lasts for only one year but is stronger. Therefore, it seems not robust to assign a clear correlation between small OC2 fluctuations and ENSO.

8) Lines 256ff on a possible role of the AO are speculative and do not add substance to the paper. Either this connection should be explored more in depth or deleted.

<end of review>

Citation: https://doi.org/10.5194/cp-2021-113-RC1
- AC1: 'Reply on RC1', Jinho Ahn, 24 Jan 2022
  
  Dear reviewers,
  We thank two reviewers for their careful review of our paper, and their suggestions. We appreciate their useful comments and believe their input has improved the paper. Below, we respond to the comments in blue and the revised texts in the manuscript in green.
  All the best, on behalf of all co-authors,
  Jinhwa Shin
  
  Citation: https://doi.org/10.5194/cp-2021-113-AC1
RC2:
'Comment on cp-2021-113', Thomas Bauska, 28 Oct 2021

Review: Shin, J., Ahn, J., Chowdhry Beeman, J., Lee, H.-G., and Brook, E. J.: Millennial variations of atmospheric CO2 during the early Holocene (11.7–7.4 ka), Clim. Past Discuss.

Summary:

Shin et al., present a novel, high-quality dataset of atmospheric CO2 during the early Holocene. Using the relatively high-resolution Siple Dome ice core, they provide an atmospheric CO2 record with the best resolution possible in this underexplored time interval. They identify previously un-resolved millennial-scale variations in atmospheric CO2. Relying on statistical inferences, they suggest that solar variations may be the primary forcing of the small changes in atmospheric CO2 (2-6 ppm). Various mechanisms to link the solar variability with atmospheric CO2 level operating in the EEP, Southern Ocean and the Northern Hemisphere terrestrial biosphere are discussed.

Shin et al., provide an excellent new ice core CO2 dataset that will be of wide interest to the palaeoclimate and carbon cycle community and should certainly be published. Crucially, the record extends our knowledge about fine-scale changes in CO2 into the early Holocene. The early Holocene is an important interval to study as it gives us clues about the sensitivity and stability of the carbon cycle during past warm intervals. In the early Holocene, CO2 and global temperature have reached interglacial levels and NH temperature may have risen to peak Holocene levels (Marcott et al., 2013, albeit this is likely limited to marine margins e.g Marisiek et al., 2018; Kaufmann et al., 2020), the large ice sheets of the NH were still in retreat, and the NH terrestrial biosphere was undergoing a substantial amount of regrowth (Elsig et al., 2009).

Overall, I felt the paper makes a though-provoking observation that small, high-frequency changes in CO2 may be correlated to solar variability. However, the causal links explored in the paper are not very convincing. Because the timescales of solar variability are wide-ranging (~decades to millennia) yet highly uncertain, they can easily be misattributed other processes in the climate system (e.g. internal climate variability) or noise in a proxy system. Thus the bar should be set very high for hypotheses invoking solar forcing based purely on statistical methods.

I also had some questions about how the raw data were transformed into robust time series for analysis. Finally, although the paper is quite brief, the organization could use some improvement as I found myself having to jump around looking for key information.

I look forward to reading a revised manuscript on this exciting new dataset.

Testing the solar hypothesis

In parts of the paper, the authors compare and contrast the variability they observe in the early Holocene to that relatively well-known centennial-scale variability of the pre-Industrial late Holocene. The premise of the paper is in part setup as a test of whether Anthropogenic emissions are the main driver of high-frequency CO2 variability. But this test is never followed up on. The reader is left with some questions:

• Given the proposed link between solar and CO2 in the early Holocene, what is the predicted influence of solar variability in the late Holocene (when solar forcing and climate variability are much better constrained)?

• Do the mechanisms proposed agree with the late-Holocene CO2 data and thus support the author’s hypothesis?

• If not, does it none-the-less challenge our understanding CO2 in the late Holocene? Is there another way to test this hypothesis?

• Is there something different in the carbon cycle boundary conditions that make the comparison between the early and late Holocene difficult?

• Finally, it would worthwhile pointing out that any changes in CO2 due to solar variability are very small and, even if present, would be swamped by changes in anthropogenic emissions during the Industrial Period.

Error propagation in high-pass filtering and subsequent analysis

It was not clear to me if the analytical precision of the CO2 data was included in the high-pass filtering and also the lag correlations. This could be crucial in demonstrating the robustness of the results. For example, no uncertainty bands are provided in Figures 2 and 3. I could only a find a reference to the uncertainty in the measurements being included in caption for Figure 1. Please provide more detail in the methods section.

Also, the exact the method used to obtain the high-pass filtered time series is not mentioned. Similarly to the above, the cut-off frequency for the CO2 curve was only mentioned in the figure captions.

Comparison to other CO2 records

The WAIS Divide data in this interval lies just below the bubble clathrate transition zone. As first discussed in Lüthi et al. 2010 and shown specifically for WAIS Divide in Shackleton et al, 2019, ice core CO2 data become very noisy in this interval. Although the exact mechanism remains open for debate, this is an important caveat when discussing the agreement or lack thereof with WAIS Divide.

I agree that both records capture the YD-PB jump in CO2 very nicely. But beyond this, it is difficult to say what variability is common to both records. For example, there is essentially one major oscillation in the WAIS Divide data to compare with in the Holocene (~10.6ka) that appears seems to be heavily biased by one very high CO2 value.

On the other hand, comparison to the Dome C seems exceptionally difficult given the resolution of the data and the small amplitude. For example, Figure 2 implies that Dome C resolves variations, on the order of ~1 ppm, but the precision of the measurement at the time the data was produced is quoted as 1ppm (Monnin et al., 2001).

As a test, it would be useful to show the correlation between the Siple Dome and all the other CO2 records to quantify the levels of agreement (alternatively, the differences could be plotted). At the moment, the discussion itself tends to be well balanced, but the conclusions reached seem to me to be too positive about the apparent agreement between the datasets. For example, it is stated quite a few times (using slightly different phrasing) “In conclusion, the existing ice core records support the millennial CO2 changes in the Siple Dome record although their temporal resolutions are not sufficient.” This statement contains a contradiction. If the records are of insufficient resolution how can they be used to test the reliability of Siple Dome? My take-home from that section was the comparisons are inconclusive.

The discussion of the CO2 offsets relies heavily on the findings in Nehrbass-Ahles’s PhD thesis. As far as I know this thesis is not publically available. For me, some parts of the discussion seem to assume that the reader could easily verify various conclusions in the thesis.

Mechanistic links between solar forcing and CO2

At the transition between the results and discussion there is missing logical step that links solar variability to the climate-driven mechanisms hypothesized to be responsible for carbon cycle changes. The authors have just highlighted in the results section that the most interesting finding is the correlation with solar proxies but then immediately jump into a discussion of various climate proxies without mentioning how solar variability could plausibly force these changes. Some of these links can be gleaned from information in the introduction but I would think it would better placed at the onset of the discussion.

I am sceptical that solar forcing could explain all this variability or, moreover, disentangled from all the forms of internal climate variability. I would welcome a clearer presentation of the chain of events/mechanisms that could link solar to CO2 (e.g. a schematic).

In a future revision, I recommend using the TSI reconstructions. See Roth and Joos, 2013 and references therein for an overview of what I believe is state-of-the-art. Although the reconstructions come with their own host caveats and uncertainties it would be useful to consider if the variability in TSI is plausibly large enough to impact the climate and carbon cycle as the authors suggest.

Line by line comments:

Line 93: “We use a similar method to calculate the significance of this correlation against a random red-noise process. At each of the 1,000 steps, we use an AR(1) model (lag-1 auto regression) to fit the series.”

What does “the series” refer to here?

“Then, we calculate the percentage of correlations between the randomized synthetic series that are lower than the correlation coefficients of the real series to assess the significance of the correlation.”

Can you relate this to the more traditionally reported p-value? Alternatively, at what values is a test significant?

Section “3.1 The new high-resolution CO2 record during the early Holocene”. Would this section read better if it followed immediately on the from the analytical methods section? The flow of the paper is a bit interrupted by the inclusions of the time series methods before the actual data description.

Line 134 “In-situ production of CO2 cannot be ruled out but the effect should not greatly impact the offset between records from the different ice cores.” This conclusion seems a bit premature, as you have not discussed organic production. Also, the remaining section seems to suggest that in-situ production is indeed the likely culprit for the offsets among cores.

Lines 143-153. This section was a little hard to follow as it mostly refers to a figure or set of figures in Nehrbass-Ahles that the reader cannot see. For example, the paper refers to a very large offset between EDC and Law Dome data in this interval which, to my knowledge, has never been published. While it is probably a good idea to reference this thesis as it seems has influenced the discussion, I would suggest keeping the references to specific data and conclusions therein to a minimum.

Line 163 “The nssCa can be produced in ice by the carbonate-acid reaction or transported as a dissolved form.” This discussion could use some nuance about what we’ve actually measured in the ice when we report nssC. Elevated nssCa is not a sure sign you’ve had production by reaction with carbonate minerals, most the time it’s increased dust delivery. What you’d really want to see is some sort of anomalous change in the ratio of soluble Ca (increase) to preserved carbonate minerals (decrease) - which at the moment we can’t easily measure. One reasons being is that when we melt the cores, some of these Ca-rich minerals dissolve. The best resources to think through these issues are the original CFA papers by Anklin et al. 1995.

Line 165 “we pay attention to the observation” please consider a different phrasing.

Line “In summary, CO2 data sets from different ice cores share similar trends in CO2 change despite offsets in longer term means of a few ppm. These offsets between the Siple dome CO2 record and others do not impact our conclusions.”

If “trends” refers to the gradual decline in CO2, I feel you have made a convincing case. However, if “trends” refers to millennial-scale changes that this needs more support.

Line 181 “The rapid CO2 increase at 11.7-11.3 ka might be associated with abrupt warming at the end of the last glacial termination (Marcott et al., 2014; Monnin et al., 2001)”. I would argue that this is clear now but please note that the “abrupt warming” is restricted to Greenland and parts of the NH.

Lines ~200. All r-values need supporting significance values (preferably p-value style)

Line 215. The comparison with the ATS seems like tangent as once I looked into the SI it seems the comparison focus on the CO2 jump at the onset of the Holocene. If ATS is central to the discussion I would suggest showing it in Figure 3.

Line 220. On the topic of the solubility pump, note that ~5 ppm changes in CO2 would require ~0.5 deg C changes in mean ocean temperature. Is this plausible given the regional changes in SST you show?

Figure 4. It would be helpful to have an arrow indicating which direction shows the proxy leading CO2 and which directions shows the proxy lagging CO2.

Sincerely,

Thomas Bauska

References:

Martin Anklin, Jean-Marc Barnola, Jakob Schwander, Bernhard Stauffer & Dominique Raynaud(1995) Processes affecting the CO2 concentrations measured in Greenland ice, Tellus B: Chemical and Physical Meteorology, 47:4, 461-470

Elsig, J., Schmitt, J., Leuenberger, D. et al. Stable isotope constraints on Holocene carbon cycle changes from an Antarctic ice core. Nature 461, 507–510 (2009). https://doi.org/10.1038/nature08393

Kaufman, D., McKay, N., Routson, C. et al. Holocene global mean surface temperature, a multi-method reconstruction approach. Sci Data 7, 201 (2020). https://doi.org/10.1038/s41597-020-0530-7

Lüthi, D., Bereiter, B., Stauffer, B., Winkler, R., Schwander, J., Kindler, P., Leuenberger, M., Kipfstuhl, S., Capron, E., Landais, A., Fischer, H., & Stocker, T. F. (2010). CO2 and O2/N2 variations in and just below the bubble-clathrate transformation zone of Antarctic ice cores. Earth and Planetary Science Letters, 297(1–2), 226–233.

Marsicek, J., Shuman, B. N., Bartlein, P. J., Shafer, S. L. & Brewer, S. Reconciling divergent trends and millennial variations in Holocene temperatures. Nature 554, 92 (2018).

Roth, R. and Joos, F.: A reconstruction of radiocarbon production and total solar irradiance from the Holocene 14C and CO2 records: implications of data and model uncertainties, Clim. Past, 9, 1879–1909, https://doi.org/10.5194/cp-9-1879-2013, 2013.

Shackleton, S., Bereiter, B., Baggenstos, D., Bauska, T. K., Brook, E. J., Marcott, S. A., & Severinghaus, J. P. (2019) Is the noble gas based rate of ocean warming during the Younger Dryas overestimated? Geophysical Research Letters, 46, 5928-5936. https://doi.org/10.1029/2019GL082971

Citation: https://doi.org/10.5194/cp-2021-113-RC2
- AC2: 'Reply on RC2', Jinho Ahn, 24 Jan 2022
  
  Dear reviewers,
  We thank two reviewers for their careful review of our paper, and their suggestions. We appreciate their useful comments and believe their input has improved the paper. Below, we respond to the comments in blue and the revised texts in the manuscript in green.
  All the best, on behalf of all co-authors,
  Jinhwa Shin
  
  Citation: https://doi.org/10.5194/cp-2021-113-AC2
EC1: 'Comment on cp-2021-113', Eric Wolff, 29 Oct 2021

Two reviewers have commented on your paper. While both of them would like to see the data published, they make quite substantial comments requiring substantial responses and, if you choose to submit a revised manuscript, major revisions of the existing version. Please respond to all their comments. Please pay particular attention to the concerns of both reviewers about the statistcs that led to very scattered data becoming a very narrow error envelope, and the huge scepticism (which I share) about your assertion of a solar link. When you have submitted your author responses I will be able to recommend whether you should produce a revised version. If that is the case, i would expect to send it for further review.

Citation: https://doi.org/10.5194/cp-2021-113-EC1

Peer review completion

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

ED: Reconsider after major revisions (01 Feb 2022) by Eric Wolff

Thank you for your responses to the reviewers. Both reviewers want to see the data published but both were very sceptical about your data processing and the robustness of your conclusions. I was not very convinced by your responses in some cases.

In particular, it is crucial to know whether the dataset after smoothing is robust, ie are the 2 ppm variations real. Your responses assert that they are but I suspect they will not convince the reviewers. Given how scattered your data are, I wonder what happens when individual data points are removed. Indeed, at about 11 ka you had an anomalous low point in the paper (Fig 1), which has been removed in your response to rev 1 (Fig 1). And as a result an entire excursion (the largest in the dataset at 11-11.2 ka) in the smoothed data has disappeared. Why was this point removed and what would happen if other outliers were removed? In other words I think you need a statistical test that examines the effect on the smoothed record of randomly removing a proportion of the data - do the smoothed variations persist? If you do not address this then it is likely that your paper will be rejected on its next iteration.

In addition large claims require strong evidence. the assertion about solar activity being the control still seems without mechanism and should not therefore be the centrepiece of the paper. Again, unless you can bolster this section (or play down the solar connection) the paper may be rejected.

I am happy for you to produce a new version, but i emphasise that both reviewers expected major revisions, and unless you address the two points above satisfctorily I am not convinced that either they or I will be willing to accept the paper.

Hide

AR by Jinho Ahn on behalf of the Authors (15 Mar 2022) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (18 Mar 2022) by Eric Wolff

RR by Anonymous Referee #1 (10 Apr 2022)

Suggestions for revision or reasons for rejection

Re-Review of

Millennial variations of atmospheric CO2 during the early Holocene (11.7-7.4 ka)
by J. Shin et al.

The authors present revisions to the original manuscript and address comments by two reviewers. I appreciate the detailed response to the comments. Again, the new high-resolution data of the Siple Dome record is a very valuable data set for the period 7.4 to 11.7 kyrBP. This data set should eventually be available to the scientific community. However, the revised version still suffers from the two major issues: (i) statistical treatment of the data to isolate millennial-scale variability, (ii) interpretation of the purported cyclic variations found based on (i).

Many minor points were addressed by the authors in the revised version, but the two major issues are still of concern and are not convincingly addressed. This prevents me from recommending publication.

Major Comments:

1) The uncertainty band of the CO2 data remains unrealistically narrow as Figure 1 evidences. a 2*sigma uncertainty of only 0.87 ppm may result from a statistical analysis but does not withstand common-sense analysis of the original data as depicted in Fig. 1. A 2*sigma uncertainty band should contain about 95% of the values, when assuming Gaussian distribution of the uncertainty. The number of data points outside the grey band in Fig. 1 is clearly exceeding 5% of the total number of data points.

2) The authors quote 0.87 ppm as “the uncertainty of a measured value”. This cannot be true as many of the data points in Fig. 1 indicate an individual uncertainty of 3 ppm, a much more realistic value of the current analytical approaches to measure CO2 on ice samples. This point is a fundamental one for it determines to which extent variations in the time series can be identified.

3) The successive filtering – 250-year running mean, then 1/(1800 year high-pass filtering – with a 1-year interpolation in between these steps is still applied. The authors essentially employ a band-pass filter to isolate variability on time scales from 250 to 1800 years. This treatment will necessarily result in some millennial variability even if applied to a white noise time series. I am therefore not convinced that this statistical analysis provides an unbiased view of the CO2 data. Therefore, I remain very skeptical of the treatment of the data.

4) The absence of a mechanistic model, or at least causal chain, to relate solar variability to CO2 changes makes the statements very speculative. Unless a stronger case is built I am seriously doubting the conclusions of this paper as formulated in the last sentence of the abstract.

<end of review>

Hide

RR by Thomas Bauska (28 Jun 2022)

Suggestions for revision or reasons for rejection

Re-Review Shin et al.., Millennial variations of atmospheric CO2 during the early Holocene (11.7–7.4 ka)

First and foremost, I profusely apologize for being so late with this review. In hindsight, a part time work schedule meant that I should have managed my time differently with this paper.

Overall, the authors have addressed many the technical concerns of both reviewers regarding the data quality and processing. They have improved the description of the signal smoothing techniques and the question of offsets between CO2 records is now treated more thoroughly. To the question of how accurate the reconstruction is presented by the authors, I am now of the opinion that the only true test of the data quality and data processing techniques will be done through replication studies using more precise methods and perhaps better-quality ice cores. It remains my opinion that the data set itself will be of wide interest to the paleoclimate community and is thus highly deserving of publication.

Regarding the mechanisms proposed in the study, both reviewers questioned the links to solar variability in the initial round. Ultimately, little has changed in the terms of the conclusions of the paper (note the abstract and conclusions remained relatively untouched). This is of course the prerogative of the authors, but I would have appreciated seeing a more in-depth rebuttal in the authors’ responses. I personally would have thought the link to TSI would have featured less prominently in lieu of an expanded discussion on the direct carbon cycle mechanisms (terrestrial biosphere, Southern Ocean controls).

I suggested a test using the TSI and the late Holocene data that might allow the authors to test their solar link, which was partially completed. I was hoping that a nuanced discussion of how TSI can be highly variably in the last millennium, but CO2 varies more slowly (possibly related to anthropogenic land-use changes) might temper the conclusions about solar forcing of CO2. In the current manuscript, it seems that the test agreed with their hypothesis in one instance (Maunder) and not in the other considering all the cores and much more muted response in WAIS Divide (Sporer). Other oscillations in TSI were ignored (minima at ~1300 CE and ~1050CE) and there was no discussion of the lead/lag timing. For example, it seems strange of me that the sharpest drop in CO2 of the last millennium (~1600 CE) coincides with a maximum in TSI and not a minimum. With only two tests and a 50% success rate, the results are most likely down to random chance. In my opinion, the paper doesn’t really follow through on these results into the discussion and conclusions and they are simply presented as a result. Again, in my opinion, there is a conclusion to be arrived from this, which is that whilst solar forcing might be important in some instances, it is clearly not the major driver of all sub-millennial CO2 variability. If the author’s feel the test is inconclusive than it might be a better choice not to include it at all rather than include it but not tie it to any firm conclusions.

My recommendation is that paper can now be published in its current form with the understanding that further refinement of the underlying ice core records is needed with more data and that a discussion of the solar links will be borne out in the subsequent literature.

Sincerely,
Thomas Bauska

Hide

ED: Publish subject to minor revisions (review by editor) (29 Jun 2022) by Eric Wolff

Thank you for your revised paper, which I sent to two experts for re-review. Firstly I add my apologies that the process took so long: I was keen to get the opinion of both original reviewers but this took a lot longer than anticipated.

The result of the re-review is rather unsatisfying. Both reviewers want to see your data published as an important addition to the overall CO2 dataset from ice cores. However both of them felt you had not really addressed their primary concerns (1) about how robust the variations you discuss are and (2) about whether you have made a convincing case for a solar forcing of the variations.

I have therefore decided that I will in principle consider a further revision with a view to publishing the data. I have classed it as minor revision because I do not intend to ask for further review: I know what the reviewers are worried about and I will be able to judge whether you have dealt with the issues to an acceptable level. I thus want to make it clear that while this is technically classed as minor revision, I am expecting substantial changes (as outlined below), and the paper could still be rejected after the next revision if I don’t see them.

Please consider all the comments made by the reviewers. I will now explain what I see as the main issues that still need to be addressed. This includes some minor issues I have noted myself. Please answer each of my comments as well as those of the reviewers.

1. Data quality. In their para 2, rev 1 makes the point that many of the individual data points show a much larger error bar than the cited analytical uncertainty. Please address this point, as it is clearly not the case that the value at a particular depth is known to within 0.87 ppm.

2. I think the issue about the very narrow error envelope shown in Fig 1 and FigS6 is about presentation. This is the envelope of 250-year averages. But because it is shown continuously it gives the impression that even centennial scale wiggles in the data are real, which is not defendible. Please deal with this at minimum by the following:
(a) On Fig 1, the caption please add “2 sigma uncertainties of the 250-year mean value, and cannot be used to interpret variations on shorter timescales” .
(b) I am very concerned that the minima and maxima you later interpret might be strongly influenced by single outliers, eg at 10.8 ka and 11.1 ka. By using 250 year means you are implicitly assuming that the true concentration is rather smooth, and that the existence of data points far from the smooth line is the result of deviations caused by the enclosure process and that these are Gaussian. The existence of these outliers questions that. Please carry out (maybe in supplement) a kind of bootstrap analysis. What I mean is that you should remove outliers (e.g. any data point more than a standard 2 sigma from the line) and show what the smoothed line then looks like. If this removes any of the major deviations you subsequently interpret than this should be stated in the text and should make your interpretation more cautious.
(c) A small technical point. In the text it says you did 10000 MonteCarlo runs, in the caption to fig 1 it says 1000. Please correct.

3. A second issue with data quality concerns the comparison with EDC and WAIS. There are some technical issues with this, as well as some opportunities missed.
(a) the text in lines 114-117 says “the CO2 offset between Dome C record and Siple Dome record is quite random (Figure 2B) because of scattering in the WAIS Divide”. I assume you mean the offset between WAIS Divide and Siple Dome, please correct.
(b) It makes no sense to calculate correlations that include the major rise out of the YD. Of course all records will show correlations if they include a giant step. Please redo your correlations using only the period to 11.5 ka (the period you use in your filtered record in Fig 1).
(c) before interpreting very small variations in CO2 it is important to show they are robust, ie observed at different sites. As rev 2 says this will really only be tested when we have other data, but you can do more with what you have. You already dismissthe WAIS Divide data but you don’t actually let the reader see the crucial comparison even for EDC-SD. Thus the reader cannot judge whether your statement “We observe that CO2 data sets from Siple Dome and Dome C share similar trends in CO2 variations” is correct. So please add a figure (I would propose in the main text (not supplement), maybe as another panel to Fig 2) in which you produce the filtered record (as in Fig 1B) for all 3 sites. When you have done this please discuss seriously how robust your findings are, and exercise an appropriate caution in the rest of the paper depending on the result.
(d) Line 164 and line 15 “The Siple Dome CO2 record shows millennial variability of ~2–6 ppm”. Looking at Fig 1B, the maximum variation is clearly only 4 ppm, please correct.

4. The comparison with other records is OK to make (Fig 3) as long as you have caveated about how robust the variations you see are (as per my previous comments). However again please be honest and cautious. While you get reasonable correlations with 14C and 10be, it is nonetheless the case that only 2 of your 3 serious dips have an expression in your solar proxies. At 9.1k, the solar proxies are antiphased with CO2. You should mention this. Taken together with the discussion of later solar variations (around line 250 and discussed by rev 2), these should cause you to caution that the link with solar is very speculative.

5. Please redraft section 4 and the abstract to be very cautious based on all the above. In particular the sentence “These relationships suggest that weak solar forcing changes might have impacted CO2 by changing CO2 outgassing from the Southern Ocean and the East Equatorial Pacific and terrestrial carbon storage in the Northern Hemisphere over the early Holocene” suggests you have established a mechanism which is not the case. I am OK with you making the case that there is a tentative correlation with solar forcing but in the abstract you should not go further.

Comments to the Author: PDF

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AR by Jinho Ahn on behalf of the Authors (31 Jul 2022) Author's response Author's tracked changes Manuscript

ED: Publish subject to minor revisions (review by editor) (01 Aug 2022) by Eric Wolff

Thank you for your comments on the reviews and for your revisions to the manuscript. Although I share the feeling of the reviewers that you are overstating the robustness of the millennial variations you discuss, i think there are now enough caveats that the data can safely be published and readers can draw their own conclusions. There are two issues where further edits are needed. I refer to line numbers in the clean, final pdf:

1. Line 256-7. "However it is the case that large variations of solar forcing at ~11.1, 10.1 and 8.3 ka. The 14C production rate and 10Be flux are correlated with CO2 at ~9.1 ka on submillennial time scales." This doesn't make sense - the first sentence doesn't finish and the second sentence refers to a correlation at a single time point. Please check and edit this paragraph.

2. I understand that you restricted correlations between CO2 and other climate records to 11.45-7.45 ka. Did you also do this for the correlations (lines 115 and 128) between ice core records? In any case, what is relevant for assessing whether the millennial variations you see are robust or not is the correlation of the filtered/detrended records (as shown in Fig 2B). I would be very surprised if these are as high as you cite. Please cite the correlation coefficients of the filtered records. Please also reconsider the phrase (line 126) "We observe that CO2 data sets from Siple Dome and Dome C share similar trends in CO2 variations despite the CO2 offset in longer term means of 3–8 ppm". To me the blue line (SD) and the red line (EDC) do not share the same millennial peaks, rather they are offset, and you should acknowledge that.

Please address these two points and I should be able to accept the paper.

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AR by Jinho Ahn on behalf of the Authors (07 Aug 2022) Author's response Author's tracked changes Manuscript

ED: Publish as is (09 Aug 2022) by Eric Wolff

Short summary

We present a new and highly resolved atmospheric CO₂ record from the Siple Dome ice core, Antarctica, over the early Holocene (11.7–7.4 ka). Atmospheric CO₂ decreased by ~10 ppm from 10.9 to 7.3 ka, but the decrease was punctuated by local minima at 11.1, 10.1, 9.1, and 8.3 ka. We found millennial CO₂ variability of 2–6 ppm, and the millennial CO₂ variations correlate with proxies for solar forcing and local climate in the Southern Ocean, North Atlantic, and eastern equatorial Pacific.

Millennial variations in atmospheric CO2 during the early Holocene (11.7–7.4 ka)

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Millennial variations in atmospheric CO₂ during the early Holocene (11.7–7.4 ka)