|Review of revision of Bazin et al. “Phase relationships between orbital forcing and the composition of air trapped in Antarctic ice cores”|
The authors have improved the manuscript in several regards; the most important of which are the inclusion of appendix B in which they assess the accuracy of the assigned minima and maxima (as requested by both reviewers), and the use of a recently published DF-EDC volcanic synchronization. Unfortunately, in several other cases the authors did not adequately address the reviewer concerns (outlined below).
Both reviewers noted that invoking Heinrich events to explain the lag of d18Oatm behind O2/N2 is highly speculative. To my mind, justifying such a claim would require either (a) a process-level understanding of how the d18Oatm lag is linked to H-events, or (b) very strong empirical evidence that the two are linked.
Regarding (a), the authors argue that during H-events the d18O of low-latitude meteoric waters becomes enriched, which in turn increases d18Oatm. While this is indeed a plausible explanation for the observed d18Oatm trends during H-events (Severinghaus et al. 2009), it does not explain why the lag of d18Oatm behind precession should increase. I understand that superimposing d18Oatm excursions on top of the orbitally-driven d18Oatm signal can change the perceived location of the d18Oatm maxima/minima; however, it seems to me that this process is just as likely to shorten the perceived d18Oatm lag time as to lengthen it. Furthermore, the proposed mechanism does not imply a change in the response of the Dole effect to precession (as the authors suggest), but merely a shift in the perceived location of the maxima/minima due to the superposition of a second signal.
Regarding (b), the suggested synchroneity of Heinrich activity and increased d18Oatm lag time is simply not very convincing, as I argued before. The temporal mismatch is on the order of 10-20ka, so much larger than the dating uncertainty. The assigned uncertainty to the manual picks also seems too small (should be at least the 3-4ka from appendix B). Increased lag times all occur during glacial times, so the authors could just as well have invoked global temperature or ice volume as the culprit. The lag curve actually closely resembles the orbital eccentricity (old figure 4), with large lags during times of small eccentricity (and hence weak precession forcing).
In summary, I am not convinced by the evidence presented for the link between the dO2/N2-d18Oatm lag and Heinrich events. However, paleoclimate science has a long tradition of speculation (unfortunately), and undoubtedly other reviewers would be comfortable with the claims that the authors make. If the authors choose to persist in their claims, they should at the very least include the caveats mentioned here.
Both reviewers commented on the use of imprecise and incorrect language. Unfortunately the revised manuscript has not improved in this regard. The request by reviewer 1 for less ambiguity in the sentence subjects has not been implemented – even the sentence picked by reviewer 1 as an example of this problem has not been altered. I (reviewer 2) gave a list of typos and language corrections at the end of my review. The authors comment that all of these have been corrected in revision; however, on comparing to my original list to the revised manuscript I noticed that none of them have been corrected. While this was undoubtedly due to an honest mistake (e.g. mixing up different versions of the manuscript) it will need to be addressed in a future version of the MS.
1) I commented that the AICC chronology is based on orbital tuning of d18Oatm, and therefore one cannot meaningfully interpret the power spectrum of d18Oatm (Fig. 2a) because orbital frequencies are included by design. The authors concede that this is true, but make no corrections to the MS (such as e.g. remove Fig. 2a, or include this important caveat).
2) The inclusion of appendix C is an improvement, but I don’t see why the authors don’t simply plot DF tuned to AICC2012 (as in C1 upper plot) in Figure 3. That way all three cores are on the same chronology. This would avoid much confusion, and allows a meaningful comparison.
3) Line 11: the authors claim that at GISP2 the dO2/N2 behaves differently than Antarctica. This actually seems opposite to what is claimed by Suwa and Bender (2008a), who write: “The stacked GISP2 dO2/N2 record shows strong spectral power at the orbital frequencies, and dO2/N2 is in antiphase with local summer insolation. This observation is consistent with the earlier findings for the Vostok and Dome Fuji ice cores from East Antarctica. “. Please explain what you mean here.
4) On lines 275-278 the authors keep arguing for a 2ka shift in dO2/N2, which was disputed by both reviewers. Appendix C shows the uncertainty to be 3-4ka, so this is not a robust result. The 2ka shift in DF d18Oice is just due to a dating problem, and this section is needlessly confusing.
5) The attempt to correlate dO2/N2 directly to accumulation (Lines 299-307) is not meaningful, because variability in the O2/N2 signal is dominated by the local insolation signal. Kobashi et al. could study the correlation during the last 4ka, because the insolation signature is small during such a short period. The O2/N2 signal should be corrected for the insolation signal first before attempting to find correlations with accumulation – which is not an easy task to undertake.
6) Lines 346:347. I was not aware that the timing of the insolation maximum at 15 Jan differs by as much as 2 ka from that at 21Dec. This seems important to the use of O2/N2 as a dating tool. This uncertainty should be added to the 3-4ka uncertainty identified in App B for dating applications.
7) Lines 445-456. I really don’t see how this mechanism can influence the delay behind precession – wouldn’t it just shift d18Oatm in the vertical direction? This could shift the perceived location of minima/maxima both forward and backwards, depending on whether the orbital d18Oatm trend at the time is positive or negative.
8) As a general comment, it may be a good idea to discuss all the implications of your results for the future dating of ice cores in one central place. This would improve the logical structure of the work.
Some additional typos and language corrections (in addition to the previous ones that were not corrected):
Line 39: the construction of the chronology has not been confirmed, but the accuracy of the chronology.
Line 116 and 118: please avoid the “we” form when talking about published work (the author list is not the same)
Line 124: The work of Ikeda-Fukazawa seems to suggest it is diffusion through the ice crystals rather than loss through micro-cracks.
Line 186: what is meant by “this”
Line 236: what is meant by “component of the surface energy budget”
Line 284: O2/N2 age constraintS
Line 286: does not significantly improve the correlation...
Line 371: This comparison relies on...
Line 392: between 15-100ka?? Do mean you use a bandpass filter with 15-100ka period pass band?
Line 392-393: “The filter is computed using Fourier transform and convolution products”. This phrase so general that it is almost meaningless.
Line 393-394: “The delay....after cross-correlation”. How d oes this give you a continuously changing delay? Do you use a moving window to calculate the delay? Please give more details, such as the window size.
Line 412: “Matlab delay” is not defined. What is it?
Line 422: the MISA 16 lag seems to be smaller than 2ka from the figure.... (not the -3ka that is claimed)
Line 461: Heinrich events consist OF
Near Line 480: MIS 7 actually shows manual lags of 7ka or so, in the absence of H-activity....
Line 601: Marine core data