The authors present a compilation of Antarctic paleoatmospheric CO measurements from 7 firn air campaigns and three ice cores measured at high resolution using continuous flow analysis. To the best of my ability to tell, none of these data (with the exception of Berkner Island firn air) have previously been published. These new records span the time range from -835 CE to the 2000s and link with modern atmospheric observations in Antarctica. Two firn air models are used to reconstruct the CO history for the part of the record covered by firn air.

Main comments

The records appear to be of very high quality, with careful attention given to calibration and corrections for analytical effects. The robustness of the reconstructions is confirmed by good agreement among the records, as well as by agreement between firn air measurements and direct atmospheric observations for overlapping time intervals. The Antarctic ice core records also appear to be free of significant amounts of in situ – produced CO that has previously been seen in Greenland ice cores.

In my opinion this study represents a large advance in our understanding of atmospheric CO history. CO is a key player in global atmospheric chemistry, and a reliable CO history is required for a full understanding of natural variations in atmospheric chemistry as well as impacts of the industrial transition. This study provides this much-needed history.

The interpretation included in the paper is qualitative only, but I think this is OK as the reconstruction itself is a very significant contribution that merits publication in CP.

One of the most significant findings of the study is that prior Antarctic ice core CO measurements (presented in Wang et al., 2010) appear to have been biased high by 0 – 20 ppb (depending on ice core and time interval). I would trust the results of this new work over the older measurements due to improved measurement techniques, careful attention to procedural effects, agreement among multiple records as well as the fact that the continuous flow technique used here has been verified against at least one discrete-sample technique (Fain et al., 2022). I think this new paper should go somewhat further in their discussion of the prior Wang et al results in the sense of alerting the readers that the isotopic measurements in Wang et al should now be interpreted with more caution – extra 10 – 20 ppb represents an additional 25 – 50% of CO, and this extraneous CO could certainly have a large impact on CO isotopic values. I still think that the Wang et al conclusion that the LIA CO minimum was mainly driven by reduced biomass burning is likely correct however.

Figure 5: Instead of just showing charcoal index, I think it would be more useful here to have a multi-panel figure showing the full new CO record together with acetylene and ethane (Nicewonger et al papers cited in this paper) in addition to charcoal.

Minor comments:

Line 103: Because Greenland ice core [CO] is so strongly affected by in situ production, absolute NH paleoatmospheric values are difficult to estimate. I think it would be more accurate to say that the Greenland ice core records allow for the reconstruction of “atmospheric trends” rather than “atmospheric history”

Table 1: should be “-44” for T at ABN

Line 161: air stored in electropolished stainless steel tanks is affected by slow [CO] growth in my experience. If measurements from these tanks are used for [CO] reconstructions, it would be useful to see results of tests of [CO] stability in the tanks that were used.

Line 200: The Wang et al 2012 and Petrenko et al., 2013 references cited here are missing in the references list at the end of the manuscript

Line 340: correct this sentence for grammar

Figure 1: middle panels (c and d) are too busy in my opinion – too many lines to be useful for the reader. I would recommend showing the GFs for just 2 – 3 depths per site – perhaps just the deepest sampled depth and another depth close to the lock-in depth.

Line 434: “filtered to remove lab air infiltrations”

Vasilii Petrenko

The manuscript titled “Southern Hemisphere atmospheric history of carbon monoxide over the late Holocene reconstructed from multiple Antarctic ice archives” presents new firn air and ice core measurements of CO from multiple Antarctic sites. Measurements from all sites are evaluated collectively to reconstruct a CO atmospheric history that covers the last three thousand years. All sampling and measurement methods, including the firn air modeling required to retrieve atmospheric gas records from firn air data, are sound and explained in sufficient detail here as well as in preceding publications. Both the firn air and ice core CO data and the retrieved atmospheric history are original and of interest to ice core community and atmospheric scientists.

I have to say I am not as enthusiastic about the interpretations offered in the manuscript as I am about the measurements. First off, the interpretations are overly qualitative. Given the heavy emphasis on the measurements, I am accepting of the fact that there is no atmospheric modeling, hence no real attempt to interpret the record quantitatively. However, it is strange that there is not even a quantitative overview of the present day CO budget. Section 3.5 and its subsections would benefit from a comprehensive reimagining.       

Before the comments about section 3.5, I will list a few about the rest of the manuscript. The paper convinced me that the previous ice core CO record by Wang et al. (2010) includes spurious features, most notably the large biomass burning peak during the late 19^th century probably never was. You speculate that analytical bias during discrete analysis could be the cause of the discrepancy. First, the Wang et al. (2010) data do not look biased because there is a period in the middle when the two data sets agree. Second, Wang et al. (2010) also presented stable isotope data, with the higher CO mixing ratios corresponding to heavier isotopic ratios. This was interpreted as a combustion signal. Is there any information in the isotopic ratios that could be helpful in determining the source of spuriously high CO? It is also worth commenting on the uncertainty in the ice core chronologies for D47 and SP.

It is not clear how the mean and the uncertainty band for the firn histories presented in Fig. 1e,f are computed and then translated to Figs. S7 and S11?

The degree of smoothing in the IGE-GIPSA model is clearly higher than the CSIRO model. Are there differences in model physics in the lock-in zone, or are we mainly looking at the effects of different tuning approaches? You can address this by including firn model parameters in the SI, perhaps. The IGE-GIPSA model inversion displays a clear peak in the late 1980s followed by a minimum in early 2000s. I’m thinking this is primarily due to minor offsets in the data sets, si this correct? In the CSIRO inversions and the instrumental record (including Fig. S10) these features are not all that apparent.        

What are the relative contributions of different sources of error to the uncertainty bands reported for the ice core data sets in Fig. 2 and what approach did you use in translating them to the uncertainty bands shown in Fig. 3 and Fig. 4? What is the

Table 1 should include analysis dates.

Comments on section 3.5     

It is not clear why you chose the two regional charcoal indices as the only benchmarks for comparison to the CO record in section 3.5.2. When calculating how much of the CO over Antarctica is from fires, the emission magnitudes from different regions cannot be ignored. Therefore, you need more than just sensitivity arguments to discard Africa and most of South America from consideration. It is worth thinking about what inference can be drawn from a comparison with the charcoal records presented in Fig. 5 within this context. CO lifetime is short but not short enough to just ignore the low attitude SH, or even all tropical fires. This is what model sensitivity studies show (e.g. Nicewonger et al., JGR, 2020). The most straight forward interpretation of the fact that neither one of the charcoal indices looks like the CO record during the LIA is that CO variability over Antarctica is driven by integrated fire variability occurring over a much larger geography. Most (80-90%, see GFED inventories) of the global fire emissions today occur at tropical latitudes (30degN – 30degS). I do not see any reason to think the situation should have been much different in the past because that is where most of the biomass is. For the same reasons, one can argue that those charcoal indices do not correlate with CO during the LIA because fires in those regions do not correlate with variability in bulk of the fire emissions in the SH. This is not very surprising given that the charcoal indices do not correlate with each other either.         

In contrast, the paper concludes the two charcoal indices may represent local fires instead of a regional signal (section 3.5.3, lns 669-673). I do not think that you can reach this conclusion using CO data alone for reasons that I stated above; however, let’s assume for a moment this is true. What does this mean for the period prior to LIA? Can we draw any conclusions from the similarity between these charcoal records and the ice core fire proxies like CO, ethane, acetylene, and BC? I should note, I do not even agree that the charcoal indices do not show variability prior to the LIA. Most obviously, the Oceania index displays a long term rise that starts around 1000 CE and continues for about 1000 years.  

I agree with Vas Petrenko that comparing your CO record to the other ice core fire proxies that are in agreement with CO would have put you on a better path to establishing, at the very least, that the Antarctic CO record prior to industrialization is indeed largely a record of gas emissions from fires. This is actually a pretty strong confirmation of the arguments you lay out in the beginning of this section about OH, methane oxidation, and BVOCs not factoring in to CO variability in the PI atmosphere. In its current state, the manuscript is not very convincing in this respect. It is especially the comparison with ethane that would be of interest given that both gases have very similar lifetimes. Depending on what you see in those comparisons, I can see the discussion evolving in different directions, including some simple quantitative comparisons.  

Finally, you mention in the abstract that both the growth from 1940 to 1985 and the following decline are observed globally (lns. 47-48), which is interesting except you do not offer any interpretation for the period after 1900 CE until the very last paragraph of the manuscript under summary and conclusions where this discussion seems misplaced. It would be better if there is a separate subsection about this period, discussing in a little more detail what you are referring to in the abstract.