|The reviewer apologises for the delay with providing the report for the resubmitted manuscript. The very poor quality of the latter is mostly the reason for that. Conclusions very similar to those for the other study from Thanwerdas et al. discussed earlier in ACP (https://acp.copernicus.org/preprints/acp-2019-925/) can be drawn for this study as well. The authors have not learned the earlier study (which causes the same problem with spin-up/initial conditions consistency, see below major comments). The new attempt does not improve understanding of the results obtained either (even with the inconsistencies they bear), and again one cannot state that the analysis is correct. |
The manuscript uses very poor scientific language, muddled and erroneous terminology for both, atmospheric modelling and isotope composition fundamentals, which may indicate that the author(s) haven not spent enough time on carefully acquainting with good literature cited. The review process resembles very much that for the abovementioned manuscript, so I see no point in continuing saving this one with my input (although I tried well). I recommend the ACP/Copernicus editors cautiously consider future submissions from this group of authors (specifically regarding modelling of atmospheric isotopic composition), because manuscripts of such poor quality require unreasonable effort and time from editors and reviewers.
190-191 It is not clear what the statement “long enough to capture the large equilibration time associated with δ13C” means. Which equilibration time is implied, what means “to capture”, from what (non-equilibrated?) state?
supplement, Sect. 1.6 Neither 10 nor 20 years may well be not enough to equilibrate atmospheric δ13C(CH4) from a perturbed state, so without a careful analysis of how far from a realistic CH4 and δ13C(CH4) atmospheric distribution your initial conditions are, the inversion results you obtained can’t be verified for consistency. You refer to the work  that demonstrates this problem, yet you neither perform a sufficiently long spin-up nor do the analysis of the initial state for consistency. This issue is the very problem of the earlier study (https://acp.copernicus.org/preprints/acp-2019-925/) and devalues any comparison against observations in the stratosphere.
217-227 There are no reasonable grounds for choosing the same emission fluxes for all FWD-* simulations. Tested various Cl fields (and hence CH4 sink) will never correspond to emissions derived for one particular Cl field (be it or not taken from the most comprehensive study). Not only mixing but also isotope ratios will not fit here. The sensible way would be to use each INV-* simulation fluxes to gauge the effect of Cl presence. By design, you end up with inconsistent mixing ratios of simulated CH4, which further devalues results for isotope ratios. See also the comment to 315-322.
315-322 Authors misunderstand (misanalyse) the obtained results – shown biases mainly result from the various CH4+Cl sink fields that counteract the same emission term. There are no “non-linear effects associated with isotopes” – the formulation used here and presented in Text S4 is valid, however only for single well-mixed isolated reservoirs which have reached steady-state conditions (which non-linearity is implied?). Please, simulate these equations once yourself (e.g. in a spreadsheet software). You will find that at typical values (S=588 Tg/yr, k=1/10 yrs^-1, α=0.995, B(t=0)=5000 Tg, δs=−52.6‰, δa(t=0)=−47‰, ∆α=0.001), B and respective δa in each box will reach their steady-state values at about t=60 yrs. However, ∆δa will first decrease until about t=90 yrs to a value of about −9‰, after which it will reach the true steady-state at about t=170 yrs. This problem somewhat reminds the one described by . In contrast, the distributions shown in Figure 2 show merely the average difference in δ13C(CH4) over 2010-2018 resulting from different local balance between CH4+Cl sink strength and emissions, which yield spatially variable effective sink fractionation. What is the distribution of ∆ε value actually simulated, why not deriving these directly from the model? Note that troposphere is turbulent so you cannot assume a given model grid cell an isolated reservoir due to mixing and transport processes, which also renders the statement on LL321-322 absurd.
6-7 “kinetic isotope effect … of the sink kinetics”
7 “… and thus MAY strongly influence”
9 “inversionS do not prescribe”
20 how is the figure of 0.8% compares to the wetland source uncertainty itself?
37-38 precision regarding which characteristic is implied? Do you mean accuracy? Which mitigation policies are implied?
114-115 is nudging applied to the entire atmospheric domain or troposphere only?
146-147 the fact that a few studies have evaluated the KIE is the wide range of temperatures does is not the reason that large uncertainties remain; this statement contradicts the following sentence
175-176 context is not clear – is it relevant/important that some inversions did not prescribe this field?
178 what “additional information” would that be? Why using this field at all then?
180-186 Tropospheric concentrations differ by an order of magnitude between given Cl fields, yet all of them exhibit similar stratospheric concentrations and vertical gradients. How is that possible?
181-183 From the previous statement and Fig. 1 one cannot state that “latitudinal distributions of tropospheric concentrations are similar”. Do you mean zonal/altitudinal relative changes? How you define/estimate spatial variability around the mean value? Is it gridcell-based, zonal average-based, how altitudes are considered etc.?
supplement, 109 what does “last state of the atmosphere” imply?
216 explain what “simple forward simulation” means
245-248 why only δ13C (without mixing ratio) profiles are being compared?
250-260 the message of the whole paragraph is incomprehensible – what the “4 months” period is referring to, simulated period or CPU wall time? If the latter, on which system?
254,273 it is not clear in what sense the methods are “more robust” and “less robust”, please explain
265 same as for 250-260 – what does (~1 minute) refer to?
285-288 differences of 20% and 10%, respectively, are not “slight” in this case; since you have all model output data at hand, it is straightforward to find the reason for this discrepancy instead of conjecturing
287 “tropopause” and “tropopause level” have different meanings and definitions
289-294 same as for 285-288: differences of 30% and more can’t be considered “slight”
Table 4 how are concentrations (here and throughout the manuscript) weighted (volume/mass/CH4 MR)?
301-302 the mentioned spatial distributions do not exhibit similar patterns
312-313 comparing δ13C(CH4) biases is meaningless here because they are derived on top of inconsistent mixing ratio biases (see also comment to 217-227 and 315-322)
S115 ambiguous 3% uncertainty for δ13C
S135, S138, S205 use of CH4 isotopologues masses is improper, abundances (e.g. moles) should be used, thus it is not clear whether the calculus presented in the Supplement is correct
22 remove “albeit this influence is small below this altitude”, redundant
23 “CH4 vertical” −> “CH4 mixing ratio vertical”
41 “13C:12C atmospheric isotope composition of CH4” −> “12C/13C isotope ratio in atmospheric CH4”, remove “denoted by d13C(CH4)”
51 poor formulation, “distributions … are very large with overlapping values”. How large? What are “overlapping values”?
54-55 KIE and isotopic fractionation are not the same phenomena/entity. Read some basic literature on isotopes, e.g. 
77 extraneous semicolon
92 “total CH4” −> “CH4 mixing ratio”
96 vague “with the atmospheric isotope composition”, remove
127 “Cl + CH4” −> “Cl”
151 remove “generously”
153 “version 10” mentioned twice
199 what “our system” implies?
231 full stop missing
232 poor language (“observations measured”)
238,240 “The analysis”, “35 others” −> “35 profiles are provided”
242,246 extraneous commas
257-259 poor English, rewrite
271-272 “… biaS increaseS over time but stabilizes after…”, “would apply”−> “would have to apply”
279-280 “Cl sink” −> “estimate(s)”
Table 4 headings are misleading, “oxidation” −> “fraction of total”, “Conc.” −> “Cl concentration”; use of “oxidation” and “sink” implies these are not the same terms
Figure 2 “average” −> “averaging”, use “left/right column”
supplement bullets in units are replaced by dots
S23 what “its global concentration” refers to? It can’t be parity discussed in the previous sentence
S52 do you refer to the supplement Sect. 1.6?
S68-S78 use “grid cells” or similar instead of “pixels”; latter refer only to raster images
1. Tans, P.P., A note on isotopic ratios and the global atmospheric methane budget. Global Biogeochemical Cycles, 1997. 11(1): p. 77−81.
2. Criss, R.E., Principles of Stable Isotope Distribution. 1999, New York: Oxford University Press. 264.
This paper investigates the role of pre-scribed Cl-fields on simulated CH4 and the 13C(CH4). The current inversion system does not yet include a tropospheric Cl sink, and since the group is currently extending their system to include 13C(CH4) observations, this paper is a logical first step. The necessity of this paper apparently appeared when the authors performed their first inversion (presented in the Supplement). As a result, the paper is a bit unbalanced and thin in content. The title promises “atmospheric inversions”, but the main paper only presents forward simulations as a series of sensitivity simulations to map out the impact of various choices for the Cl field. I therefore suggest to remove “through atmospheric inversions from the title”.
For the rest, the paper is well written, and I will attach an annotated pdf with minor comments. The box model inversions are an elegant way to estimate the global impact of the Cl sink on emissions and their required signature. However, the comparison to the vertical profiles are only performed for CH4 mixing ratios. The results indicate that the model does not perform very well, but that this likely a transport issue rather than an issue with the Cl sink. However, it remains totally unclear how well the model performs in the stratosphere concerning 13C(CH4), while the action of Cl is critical here. I therefore suggest to include an analysis of the modeled 13C(CH4) profiles and compare to the available observations (https://acp.copernicus.org/articles/11/13287/2011/acp-11-13287-2011.pdf)