|The manuscript presents an interesting new set of discrete CH4 measurements from the Siple Dome ice core, allowing the authors to mostly discuss the early Holocene trend of atmospheric methane and to elaborate on the possible mechanisms involved to explain the trend and variability.|
The analytical work is substantial and I commend the authors for this. However, like the two previous reviewers, I am puzzled by the claimed analytical error of about 2 ppb, when compared with the variability observed when performing blank tests of the system (5 to 15 ppb). The community usually attributes the blank of CH4 analytical systems to degassing of the glass walls of the containers, itself depending on the variable ambiant CH4 concentration in the laboratory and cold room, and on the thermal history of the container. This can introduce a lot of variability, intra-day and inter-day. It is quite surprising that a small variability can be claimed by the authors at the intra-day level. I understand that the authors argue – for a good reason - on the reproducibility of duplicate measurements conducted many days apart on the Siple Dome samples, to claim that their evaluation of the different sources of erros is correct. But it remains quite puzzling from an experimental point of view… I’d suggest for the future evolution of the analytical procedure – and if not done yet – to consider performing again these blank tests while the containers are kept closed in the cold room, under zero air (or nitrogen) filling, before introduction of the ice sample. I’d suspect that this would considerably reduce the inter-day variability of the blanks.
A correction for solubility is applied on each data point. Am I wrong or the blank tests are conducted by adding a standard gas to the blank ice ? If this is the case, then the solubility effect should be accounted for - at least partly - through the blank measurements as part of the standard gas gets into diffusive equilibrium with the blank water during the melting phase, and no (or a small) additional correction should apply.
Figure 1 shows at ~9.6 kyr BP a CH4 spike which may not represent a true atmospheric feature when taking into account the smoothing of atmospheric variations related with gas enclosure conditions at Siple Dome. So there seems to be other sources of errors that the claimed 2 ppb analytical error do not fully cover. Or a good explanation should be brought on why such a narrow spike is observed in the Siple Dome record.
The gas enclosure brings me to another concern : the authors make a big case on the interpolar gradient. This is a tricky signal to obtain and to interpret. Notably, gas trapping conditions are key. An ideal case is to combine northern and southern records affected by similar gas trapping conditions. When combining Greenland records with the Siple Dome one, this is clearly not the case. At least the authors should consider convolving the Siple Dome signal with a log-normal distribution reflecting the gas trapping conditions at Siple Dome, before comparing with Greenland records and calculating an IPD. Or they should restrict on only using the WAIS Divide record, despite the fact that it was previously published and not resulting from the authors’ work…
Aside from the gas enclosure aspect, I wonder indeed if it makes sense in the end to calculate CH4 source strengths changes with a 3-box model while the source evolution is partly attributed to a shift of the ITCZ. The latter necessarily affects the inter-box exchange time as well as the pertinence of the exact latitudinal « boundaries » used between boxes. Isn’t there a circular argument here ?
I’m not sure that any reference to variable OH in polar regions really make sense. By far most of atmospheric CH4 is oxidized in the inter-tropical band and at relatively high altitude. The polar component does not really matter here.
Apart from the points raised above, I find that the authors correctly addressed all remarks made by the two reviewers as well as the editor.