We thank the reviewer for taking the time to carefully read through the manuscript and the generally positive comments. The work presented here is a culmination of almost five years of effort, and it is gratifying to know that others in the community consider it a step forward. We are happy that the reviewer thinks this work is an important contribution to the field and appreciate the suggestions for improvement. Please find below the reviewer’s comments italicized, with our responses in normal font.

Line 7. Tropics – for future studies it would be interesting to include the extra-tropical monsoon regions.

We defined the “Tropics” as the region where the angle of solar declination can be 90° at least once a year. We are aware that there are several other definitions, such as the region where trade winds are primarily easterly (~±30°), or the region where the incoming solar radiation exceeds the outgoing terrestrial radiation (~±35°). Some of these definitions indeed encompass extra-Tropical monsoon regions that are of interest for the global methane budget. We will take the reviewer’s suggestion and include a larger region (~±30°) into our definition of the “Tropics” in future work.

Note that when we compare our estimates to the GCP estimates, we do evaluate our emission totals for this larger band to be comparable to the GCP definition. However, we are unable to change our definition of the Tropics throughout the current work because it would involve significant additional computation to calculate the emission uncertainties for that new definition.

Line 50. Box models. Major comment here is that Zhang et al. (2022) should be discussed and its different methodology assessed explicitly. Basu et al’s analysis is very persuasive, but the differences of methodology between Basu et al and Zhang et al. should be made clear, and the debate should be returned to in the discussion in Section 4.

We have added Zhang et al (2021) to the references here for CH₄ and δ¹³CH₄ box modeling, and have discussed results from Zhang et al (2021) in the “Conclusions and Discussion” section. We note here that none of the scenarios of Zhang et al (2021) reproduce the atmospheric δ¹³CH₄ very well (consider Figures 1B and 2A of that paper), therefore their estimate of microbial (fossil) contribution to the recent CH₄ growth is likely to be an underestimate (overestimate). In response to another reviewer, we have also added comparisons to a few other publications to the same section.

Line 60. The F parameter (presumably Flux?) is not specified. It would be good to have a small table of parameter identification to identify all the variables.

Explanation of F added.

Line 94. Maybe later in the paper (in section 4) the power of the TM5 4DVAR approach could be re-emphasised. It’s what makes this paper potent.

We are happy that the reviewer appreciates the significance of using a 3D atmospheric inverse model as opposed to a box model. We have indeed mentioned the advantages of a 3D inverse model at different places in the manuscript. However, we are unsure of how exactly to further emphasize the power of a 3D inverse model, or whether such emphasis is needed.

Line 102. Here we have fluxes termed ‘x’…see line 60.

Fair point. The difference is that in general “x” is a linear vector of all fluxes to be optimized, while F_s earlier denotes source specific fluxes that have spatiotemporal structure. Calling the vector “F” at this point would be mathematically inaccurate. To resolve this, we have added a description for “x” here, “the set of all F_s in 2.1”.

Line 136. Is Bergamaschi et al 2007 the last word on Termites? If so, maybe more work is needed. Maybe also relook at older work, such as by Zimmerman.

Zimmerman et al (1982) estimated 150 Tg CH₄/year emission from termites, which does not fit our current knowledge of the methane budget. Bergamaschi et al (2007) does not actually construct estimates of termite emissions, they use a database from Sanderson (1996) which gives a much more realistic estimate of 19.5 Tg CH₄/year. We have not found a more recent update after that. Also, we have changed the citations for termite and wild animal emissions to Sanderson (1996) and Houweling et al (1999) respectively in the text.

Lines 137 and 142. The ice core work by Petrenko’s team suggests very strongly and persuasively that natural fossil emissions are much smaller than found by Etiope et al 2019. The Petrenko team’s papers (e.g Hmiel et al https://doi.org/10.1038/s41586-020-1991-8) need to be considered explicitly here. It’s OK if Basu et al disagree with Hmiel et al, but they must explain why they refute the pre-industrial ice core results.

We cannot in fact refute the smaller geologic emission estimates from Petrenko’s group. We can only estimate the total fossil emission, and therefore have been very careful not to report anthropogenic fossil emissions. The referee is correct that if the true geologic emission in fact is ~5 Tg CH₄/year or lower (Hmiel et al., 2020), then our estimate of the anthropogenic portion of fossil emissions would be significantly higher and even further from GCP estimates. We have added a discussion of this in the section where we compare our emission estimates to the GCP budget. Note that even with a lower estimate of geologic emissions, our attribution of the recent growth of atmospheric methane still stands, because we do not expect geologic sources to change over decadal time scales.

Line 157. Presecribed sinks. OK, understand, but might be worth adding a line of discussion on the impact of this decision to prescribe sinks.

This is of course a long-standing debate in the methane community. We do not currently have a method – based solely on CH₄ and δ¹³CH₄ measurements – to disentangle the sources and sinks. Therefore, we keep the sink fixed. In a previous publication (Lan et al., 2021) we explored the possibility that the entire post-2007 methane growth was due to a trend in OH, and concluded that such a scenario did not fit the atmospheric δ¹³CH₄ data. However, we cannot currently rule out that sink variations play a relatively minor role in the renewed growth. Such a variation, however, would have to be mechanistically plausible, ruling out large trends in atmospheric OH (Anderson et al., 2021; Nicely et al., 2018). In the future we would like to explore ways to use δD of CH₄ measurements and models to disentangle the influences of sources and sinks. We have added a discussion of this in the new section “Future needs”.

Line 165 paragraph. Upland soil sinks especially in the moist aerated tropical woodlands – very little information on them. Might be worth a discussion here or later in paper?- e.g likely climate change response?

The referee is correct that the total magnitude of and trend in upland soil sinks are highly uncertain (Murguia-Flores et al., 2021; Ni and Groffman, 2018). While we have used a soil sink map generated by the same biogeochemical model as our wetland fluxes (so they’re at least internally consistent), we do not claim that it is perfect in any way. We have added this as an area of improvement in the newly-added section “Future needs” especially for δ¹³CH₄ analysis. We are currently setting up inversions with alternate process-based realizations of the soil sink (Oh et al., 2020).

Line 195 I tried the doi but had no answer. All I got was advice on making a cake. I quote: It “looks like there aren't many great matches for your search. Try using words that might appear on the page that you’re looking for. For example, 'cake recipes' instead of 'how to make a cake'.” 

We are unsure why the link did not work for the reviewer. Clicking on https://doi.org/10.15138/64w0-0g71 gets us to a NOAA website which asks for a password to download the dataset. The password was provided to the referees during submission, and the dataset will be made public once the paper is accepted for publication. 

Figure 3 right – shows how important it is to get isotopic measurements from Africa and S. America and South Asia. The sole site in Africa, in Namibia, samples southern ocean air. This lack of tropical observation should be stressed in the conclusions.

We agree with the reviewer and stress this in the new section “Future needs”.

Line 285 There might also be a discussion here of the difference between Basu et al’s findings and the implications of tropical wetland process models mentioned by Zhang et al..

The separation of microbial fluxes into wetland and anthropogenic by Zhang et al (2021) relied on their wetland process model and not on atmospheric data. We note this in the revised manuscript in the section where we compare results from the two works. We also note elsewhere in the revised manuscript that current biogeochemical models have several deficiencies (such as inability to correctly model tree stems and transpiration), which could prevent them from simulating a large increase in natural wetland emissions.

Line 263 C4 signature chosen seems a bit heavy – yes for pure C4 tropical grass fires but many are perhaps a bit lighter as there are lots of bushes etc in the fires also. Note also that tropical wetlands have varying C3/C4 ratios – dominantly C4 in equatorial areas (papyrus) but more C3 reeds in outer tropics. This gradation also shows in land plants – tropical ruminants are typically as much browsers as grazers.

The reviewer may have a point. From our δ¹³C-CH₄ inventory v2020 (Sherwood et al., 2021), the C4 signatures from four studies (grass fire from Brazil, Zambia and Zimbabwe) we compiled seems to be lighter, at around -17‰. However, we were concerned that they presented a very small sample size, and perhaps the material burned in those studies were not pure C4 grass. Therefore, we decided to use Cerling et al (1998), which included more than 800 plant varieties.

We would also like to emphasize here that we do not assume a grid cell to be purely C3 or C4. We calculate source signature maps for biomass burning by multiplying C3 and C4 signatures of −26.7‰ and −12.5‰ respectively (Cerling et al., 1998) with the C3/C4 fraction for each 1°×1° grid cell. This results in variation of the source signature from gridcell to gridcell depending on the C3 and C4 fractions (although, to be honest, the C3/C4 map may have unquantified errors). Bush is normally C3; so a grid cell with (say) 40% bush and 60% tropical grass will have a source signature of -26.7‰×0.4 + -12.5‰×0.6 = -18.18‰.

Line 289. Also L 348. Inundation – yes, but temperature also. It’s likely T is a key factor, with an Arrhenius relation to methane flux. But there is very little work on T impact in tropical wetlands. Lots of models simply cite Gedney Q10, based on a few much older studies.

We agree that temperature is also a key factor that controls wetland methane emissions, and Q10 is sensitive to soil and vegetation properties. In fact, the version of TEM model that we used for this paper optimized Q10 for different latitudes and wetland types separately, and we used observations from seven independent sites to optimize wetland-specific Q10 for tropical regions (please refer to Table 2 of Liu et al (2020)).

Liu et al (2020) also thoroughly investigated the sensitivity of different inundation and meteorology inputs (including different temperature datasets) in wetland emissions (Figure 4 and Table 8), and the results show that the uncertainty from different inundation extent is much larger than the uncertainty from different temperature inputs. Based on this analysis, we decided to test the impact of inundation extent on our emission estimates.

Note that a key factor may be inundation depth – if the plants are rooted or floating. If they are rooted in ooze (e.g. 4m tall papyrus) then they advect a lot of methane from the anaerobic bottom direct up the stalks. But floating plants in oxygenated shallow open waters allow water methanotrophy to eat the ebullition. So flooding increases area of inundation but may reduce emission from the deeper parts. Conversely the T in hot dry years increases emissions provided there is enough water (and wetland responses have a long, 6-12 month lag time after preciptation anomalies, but an immediate response to Temperature change.).

We agree that inundation and plant root depths, and lags in wetland emissions are all very important but missing parameters/processes in current biogeochemical models. Also, current biogeochemical models do not accurately simulate the methane emissions from aquatic sources (Rosentreter et al., 2021), tree stems (Barba et al., 2018), and transpiration (Helfter et al., 2022) properly. These missing processes/parameters cause major uncertainties in biogeochemical models, which probably explains why current process-based wetland models cannot explain the large increase in emissions from natural wetlands (Zhang et al., 2021).

Line 344 – estimate of pyrogenic emissions not changing? That’s a bit surprising?

Yes, it is a bit surprising. Our GFED 4.1s prior does have a small downward trend in pyrogenic emissions, but that is taken out when we assimilate δ¹³CH₄ data. In the revised manuscript, we have compared our results with a few others in recent literature that have also used δ¹³CH₄ data (McNorton et al., 2018; Thompson et al., 2018; Zhang et al., 2021). They all infer a downward trend in pyrogenic emissions, which then requires an upward adjustment in fossil (since that is the only other enriched source) to balance the ¹³C budget. However, we think it likely that in those studies the pyrogenic trend was forced by the prior and not the data. McNorton et al (2018) did a test where they took all trends out of their prior fluxes, and their resultant estimate did not have a pyrogenic trend in the posterior. This is in line with our finding of a negligible trend in pyrogenic emissions.

Line 395. It would be interesting to model what I’d call the monsoonal tropics, rather than limit by geometric latitudes – i.e the region within the sweep of the Inter-tropical convergence zone.

Agreed. As mentioned in an earlier response, we would like to do this in future work, potentially aided by addition δ¹³CH₄ samples from the Tropics.

Line 508. Maybe there should be a mention here of Feng et al. (2022)Tropical methane emissions explain large fraction of recent changes in global atmospheric methane growth rate."

Feng et al (2022) pin ~80% of the recent growth of atmospheric methane on Tropical emissions. This is actually a larger fraction than suggested by our Figure 11.

Line 525 The paragraphs where Basu et al. paper discuss ‘GCP’ findings need to be rewritten and the important work of Zhang et al needs to be addressed. There might also be a discussion of the conflict between Basu et al’s findings and the implications of tropical wetland process models (compare Zhang et al., who accept the modelling). Note that many process models share a major weakness in their dependence on a Q10 assumption that is based on very little observational evidence.

We have added a section specifically comparing our results with Zhang et al (2021).

Line 560 More generally, perhaps in the discussion section, maybe the paper could discuss the wide range of needs: more tropical isotopic measurements, better information on isotopic signatures (but I note Line 503), better knowledge of tropical soil uptake, better assessment of Cl and OH sink fractionation, and the potential usefulness of D/H isotopic monitoring. It might also help to add here a table 6 of the methane budget findings by source.

We have added a “Future needs” section under Discussions to address these issues.

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Cerling, T. E., Ehleringer, J. R., and Harris, J. M.: Carbon dioxide starvation, the development of C4 ecosystems, and mammalian evolution, Philos. Trans. R. Soc. Lond. B. Biol. Sci., 353, 159–171, https://doi.org/10.1098/rstb.1998.0198, 1998.

Feng, L., Palmer, P. I., Zhu, S., Parker, R. J., and Liu, Y.: Tropical methane emissions explain large fraction of recent changes in global atmospheric methane growth rate, Nat. Commun., 13, 1378, https://doi.org/10.1038/s41467-022-28989-z, 2022.

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Houweling, S., Kaminski, T., Dentener, F., Lelieveld, J., and Heimann, M.: Inverse modeling of methane sources and sinks using the adjoint of a global transport model, J. Geophys. Res., 104, 26137–26160, https://doi.org/10.1029/1999JD900428, 1999.

Lan, X., Basu, S., Schwietzke, S., Bruhwiler, L. M. P., Dlugokencky, E. J., Michel, S. E., Sherwood, O. A., Tans, P. P., Thoning, K., Etiope, G., Zhuang, Q., Liu, L., Oh, Y., Miller, J. B., Pétron, G., Vaughn, B. H., and Crippa, M.: Improved Constraints on Global Methane Emissions and Sinks Using δ¹³C-CH₄, Glob. Biogeochem. Cycles, 35, e2021GB007000, https://doi.org/10.1029/2021GB007000, 2021.

Liu, L., Zhuang, Q., Oh, Y., Shurpali, N. J., Kim, S., and Poulter, B.: Uncertainty quantification of global net methane emissions from terrestrial ecosystems using a mechanistically based biogeochemistry model, J. Geophys. Res. Biogeosciences, 125, e2019JG005428, https://doi.org/10.1029/2019JG005428, 2020.

McNorton, J., Wilson, C., Gloor, M., Parker, R. J., Boesch, H., Feng, W., Hossaini, R., and Chipperfield, M. P.: Attribution of recent increases in atmospheric methane through 3-D inverse modelling, Atmospheric Chem. Phys., 18, 18149–18168, https://doi.org/10.5194/acp-18-18149-2018, 2018.

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Zhang, Z., Poulter, B., Knox, S., Stavert, A., McNicol, G., Fluet-Chouinard, E., Feinberg, A., Zhao, Y., Bousquet, P., Canadell, J. G., Ganesan, A., Hugelius, G., Hurtt, G., Jackson, R. B., Patra, P. K., Saunois, M., Höglund-Isaksson, L., Huang, C., Chatterjee, A., and Li, X.: Anthropogenic emission is the main contributor to the rise of atmospheric methane during 1993–2017, Natl. Sci. Rev., 9, https://doi.org/10.1093/nsr/nwab200, 2021.

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In response to the reviewer's curiosity about the monsoonal Tropics, we have added numbers for three additional latitude bands, 90°S-30°S, 30°S-30°N and 30°N-90°N, to Table 4. We have also added the change from 30°S-30°N (monsoonal Tropics) as an additional panel to Figure 11. We hope this will make comparison easier to other methane studies which uses this definition of the Tropics.

We thank Dr. Manning for taking the time to carefully read through the manuscript and the generally positive comments. The work presented here is a culmination of almost five years of effort, and it is gratifying to know that Dr. Manning considers it a step forward. We appreciate the suggestions for improvement. Please find below Dr. Manning’s comments italicized, with our responses in normal font.

The relationship between this paper and Lan et al, 2021, is important and as they are in different journals it can help to repeat a bit more of what is in Lan et al here. E.g. the range of scenario options that had been considered in Lan et al before this paper adopts C_WL+ as the base for inversion analysis.

Sections 2.3, 2.4 and 2.5 contain detailed description of the setup of Lan et al (2021), which we have repeated here in order to save the reader from having to (re)read Lan et al (2021). Many of the sensitivity tests described in detail in section 2.6 are precisely scenarios that were explored in the forward runs of Lan et al (2021). If Dr. Manning could suggest additional details from Lan et al (2021) that would bear repeating here, we would be happy to add them.

In section 3, I see no mention of how stratospheric removal is treated in the TM5 model. As this leads to return of air with some isotopically enriched CH4 back into the troposphere, and that enrichment varying with latitude, it can effect the δ13C analysis.

In the submitted manuscript, lines 158 onward read “Monthly climatological CH₄ loss rates in the stratosphere due to OH, Cl and O(¹D) were constructed from a run of the ECHAM5/MESSy1 chemistry transport model (Steil et al., 2003; Jöckel et al., 2006).” TM5 is a full atmosphere model, so isotopically enriched CH₄ from the stratosphere is recirculated back into the troposphere by TM5’s stratosphere-troposphere exchange, which is typical among offline transport models (Krol et al., 2017).

Section 4.1 “Comparison with Thanwerdas et al 2021” seems to have been added after the rest of the paper had been written. I think it would read better if this section was merged into section 3.6 “Comparison to the GCP budget”.

This is a good point, that section was indeed added at the last minute because Thanwerdas et al (2021) came out at the very tail end of our writing. We agree that all comparisons to other work and estimates should be together. We have therefore moved all such comparisons to the “Conclusions and discussion” section, which now contains comparisons to (a) the GCP budget, (b) Zhang et al (2021) following a recommendation from another reviewer, (c) Thanwerdas et al (2021), and (d) comparisons to a few other top-down studies, as recommended by another reviewer.

The rest of section 4 starts with a summary of what has been covered in the paper and then moves on to consider options for future development. After comparing this with some other papers in ACP, I would suggest that it would be better to have section 4 just focused on how the results can be developed with future work, and to move the initial summary, currently at the beginning of section 4, to a section 5 on “Concluding remarks” that summarised some of the key points made in the paper.

This is also a good point. We have taken Dr. Manning’s suggestion and reorganized the manuscript as follows. Section 3 now contains just the results from our runs. Section 4 is now called “Conclusions and discussion”, which contains, in sub-sections, an enumeration of the important conclusions from our work, comparisons to other published estimates and work, improvements planned to our framework in the future, and areas that need progress to better use atmospheric δ¹³CH₄ data for disentangling the methane budget.

The Courtier et al 1998 reference given here would be better as the peer reviewed version published in Quarterly Journal of the Royal Meteorological Society, 124:1783-1807, 1998. https://rmets.onlinelibrary.wiley.com/doi/abs/10.1002/qj.49712455002

Good catch! We have changed the reference to Courtier et al (1998).

References

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Jöckel, P., Tost, H., Pozzer, A., Brühl, C., Buchholz, J., Ganzeveld, L., Hoor, P., Kerkweg, A., Lawrence, M. G., Sander, R., Steil, B., Stiller, G., Tanarhte, M., Taraborrelli, D., van Aardenne, J., and Lelieveld, J.: The atmospheric chemistry general circulation model ECHAM5/MESSy1: consistent simulation of ozone from the surface to the mesosphere, Atmospheric Chem. Phys., 6, 5067–5104, https://doi.org/10.5194/acp-6-5067-2006, 2006.

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Lan, X., Basu, S., Schwietzke, S., Bruhwiler, L. M. P., Dlugokencky, E. J., Michel, S. E., Sherwood, O. A., Tans, P. P., Thoning, K., Etiope, G., Zhuang, Q., Liu, L., Oh, Y., Miller, J. B., Pétron, G., Vaughn, B. H., and Crippa, M.: Improved Constraints on Global Methane Emissions and Sinks Using δ¹³C-CH₄, Glob. Biogeochem. Cycles, 35, e2021GB007000, https://doi.org/10.1029/2021GB007000, 2021.

Steil, B., Brühl, C., Manzini, E., Crutzen, P. J., Lelieveld, J., Rasch, P. J., Roeckner, E., and Krüger, K.: A new interactive chemistry-climate model: 1. Present-day climatology and interannual variability of the middle atmosphere using the model and 9 years of HALOE/UARS data, J. Geophys. Res. Atmospheres, 108, https://doi.org/10.1029/2002JD002971, 2003.

Thanwerdas, J., Saunois, M., Berchet, A., Pison, I., Vaughn, B. H., Michel, S. E., and Bousquet, P.: Variational inverse modelling within the Community Inversion Framework to assimilate δ¹³C(CH₄) and CH₄: a case study with model LMDz-SACS, Geosci. Model Dev. Discuss., 2021, 1–29, https://doi.org/10.5194/gmd-2021-106, 2021.

Zhang, Z., Poulter, B., Knox, S., Stavert, A., McNicol, G., Fluet-Chouinard, E., Feinberg, A., Zhao, Y., Bousquet, P., Canadell, J. G., Ganesan, A., Hugelius, G., Hurtt, G., Jackson, R. B., Patra, P. K., Saunois, M., Höglund-Isaksson, L., Huang, C., Chatterjee, A., and Li, X.: Anthropogenic emission is the main contributor to the rise of atmospheric methane during 1993–2017, Natl. Sci. Rev., 9, https://doi.org/10.1093/nsr/nwab200, 2021.

We thank the reviewer for taking the time to carefully read through the manuscript and appreciate the suggestions for improvement. Please find below the reviewer’s comments italicized, with our responses in normal font. 

As explained in the introduction section, this study is motivated by the large uncertainties in the global methane budget. More specifically, a mismatch of 160 Tg/yr between top down and bottom up in the GCP budgets is mentioned. The procedure for specifying prior uncertainties, however, adds up globally to 7% (40 Tg/yr) which doesn’t quite reflect this uncertainty. The difference may be more than a factor 4, as the prior budget uncertainty probably reflects only a single year. The setup of prior fluxes mentions a rescaling to make sure that the prior budget is consistent with the observed trend. In sensitivity tests also alternative rescaling is applied to restore the source-sink balance in the a priori budget. It is unclear why this is needed, given that the measurements used in the inversion contain this information (strictly speaking measurement information is double counted in the setup that is used). My guess is that the division of the full time series into blocks and the initialization of these blocks requires the rescaling. If the prior is over constrained for methodological reasons this raises the question how the choice of rescaling might have steered the solution in the direction of the main outcomes and how suitable the proposed time splitting methodology is.

The first step in performing any inversion is a good forward model, which includes a realistic prior flux. Since most bottom-up estimates for long-lived greenhouse gas fluxes do not reflect the atmospheric growth rate, it is standard practice, especially for long model runs, to adjust these fluxes to get the correct decadal atmospheric growth for CO₂, CH₄ or SF₆. See, e.g., Houweling et al (2017) for an overview for CH₄, Chevallier et al (2010) and Weir et al (2021) for implementation for CO₂, and Patra et al (2011) for implementation for SF₆. Our approach of starting with priors that match the global growth rate is entirely in line with this philosophy. In fact, we would go even further and argue that starting with a prior that has a known bias in something as basic as the decadal growth rate violates one of the basic premises of Bayesian estimation, which is that the prior is unbiased. For short inversions this may result in posterior biases that are negligible. However, for long inversions, starting with a biased prior will usually result in a biased posterior (e.g., Bruhwiler et al (2014)) and an atmospheric tracer field that moves farther away from the truth with time. This is clearly not desirable for an atmospheric inversion.

Regarding the referee’s observation that our 1σ prior error of 40 Tg/year is four times smaller than the gap of 160 Tg/year between top-down and bottom-up GCP estimates, this is correct but not entirely relevant to the setup of an atmospheric inversion. The 160 Tg/year gap is a bias (there is no reason to believe that the GCP bottom-up estimates are normally distributed around the truth), and the prior error covariance is not supposed to be a measure of the bias in the prior, nor the spread between a set of bottom-up fluxes. The prior error covariance is supposed to be the covariance of (prior – truth). Since we have scaled the prior to match the decadal growth rate (i.e., mitigated the prior bias), we only need to provide enough “slack” in the prior to encompass the range of flux estimates that may arise from reasonable bottom-up models. We note that with a 1σ error of 40 Tg/year, 95% of the bottom-up flux estimates are supposed to lie within a range of ±2σ or 160 Tg/year.

Finally, regarding the referee’s concern that we are using the same data twice in creating a balanced prior, while theoretically true, is a red herring that makes little difference in practice. Figure 1 shows the annual growth rate of CH₄ derived from NOAA’s marine boundary layer (MBL) sites and from daytime flask samples at Mauna Loa (not included in MBL). The differences are very small at the annual scale and ~1 ppb or less for five-year averages. In this work, we used MBL-derived growth rates (blue circles) to adjust our prior and did not assimilate Mauna Loa flask CH₄ data. Figure 1 suggests that if, instead, we had just used (non-assimilated) Mauna Loa flask data (red squares) to calculate the growth rate and adjust our prior, it would have made very little difference to the prior and consequently even less difference to the posterior. Technically, this is because we are using up exactly one degree of freedom from the data to adjust the prior – the annual growth rate – leaving many, many more for the inversion to interpret.

The section on future work mentions some of the limitations of the current setup that will need to be improved on. The question is how these limitations may affect the conclusions from this work on the relative importance of changes in microbial and fossil emissions. Here, attention is raised for uncertainties in OH, rightly so I would say. A study of Zhao et al (ACP, 2020) concludes that sink uncertainties are about as important as emission uncertainties. As Lan et al (2021) and others have shown, changes in the sink are unlikely to explain the post 2007 increase. However, this doesn’t mean that the sink should have remained constant. There is little consensus on the longer-term OH trend, particularly between the atmospheric chemistry community and those who study methyl-chloroform. Worden et al (2017) tried to quantify the impact of hypothetic OH trends on the microbial / fossil emission trend partitioning. The question is how sensitive the conclusion on microbial versus fossil emission increases is to the possibility of a non-zero OH trend that is within the uncertainty of methyl chloroform. I realize that this is a difficult question to answer, but to draw conclusions on emission scenarios postponing the discussion on OH to future work is too easy in my opinion.

The reviewer makes a valid point. While a purely OH-driven explanation for the recent growth in CH₄ has been ruled out by Lan et al (2021), smaller variations in the CH₄ budget are entirely possible due to variations in OH. Before getting into the possibilities for OH changes, we would like to make two comments. First, while the global methane emissions depend strongly on the total sink, the split between microbial, fossil and pyrogenic sources based on δ¹³CH₄ has a very weak dependence on the total sink (no dependence at steady state). This is because the total sink strength does not factor into the relationship between the emission-weighted source signature and the atmospheric δ¹³CH₄ at steady state (Miller, 2004). Second, OH is not the only sink of atmospheric methane. It is the largest sink but has the smallest discrimination between ¹²C and ¹³C. Therefore, a downward trend in OH makes atmospheric CH₄ heavier because the other sinks become (relatively) more important. Most studies that try to attribute the recent growth of methane to sink changes (e.g., Rigby et al (2017), Turner et al (2017)) miss this fact because they assume OH is the only sink of methane. In the presence of other sinks (chlorine, oxygen, soil sink), if even part of the upward CH₄ trend were to be explained by a downward trend in OH, it would require even more microbial contribution than what has been reported in our work to match the δ¹³CH₄ time series.

There are two kinds of possible variations in OH, trend and interannual variability with no long-term trend. Not only would a decreasing OH trend be insufficient to explain the recent trends in CH₄ and δ¹³CH₄ for reasons detailed above, neither is there any mechanistic explanation for why such a trend should exist for the past fifteen years (Nicely et al., 2018; Anderson et al., 2021). In fact, oxidation of CH₄ by OH may have increased in recent times due to the reduction in CO emissions (Gaubert et al., 2017). On the other hand, interannual variability in OH is a very real possibility that is simulated by most atmospheric chemistry models. We have hesitated to use OH directly from an atmospheric chemistry model because their simulation of the decay of methyl chloroform or the north-south gradient do not match constraints from observations (Montzka et al., 2011; Patra et al., 2014). However, in the near future we plan to impose OH variations calculated by several different atmospheric chemistry models to see what difference that makes on our methane emission estimates.

Besides comparisons to the GCP inversions there must be some specific comparison with other methane modelling studies that have used isotopic measurements. Some of those also used 3D models (e.g. Thompson et al, 2018 and McNorton et al, 2018). In the case of McNorton et al (2018), the largest contribution to the emission increase was attributed to the energy sector. Apparently, within the uncertainty of different models and setups it is possible to arrive at different conclusions regarding the contribution of microbial and fossil sources to the CH4 increase. It is important to understand what explains this, which may be difficult, but to compare and acknowledge the different outcomes is easy and should be done.   

Thompson et al (2018) use a 2D model without zonal structure, and not a 3D model. However, we take the reviewer’s point about comparison with other top-down studies that use CH₄ and δ¹³CH₄ data. In the revised manuscript, we have added sections to compare our results to Thompson et al (2018), McNorton et al (2018) and Zhang et al (2021). The most significant difference we find between our work and these three previous studies is that unlike us, all three studies estimate a significant downward trend in pyrogenic emissions. Since pyrogenic emissions are the heaviest of the three categories, their reduction necessitates a larger increase in fossil emissions to reproduce the δ¹³CH₄ trend. We note that our prior pyrogenic emissions from GFED 4.1s do have a negative trend (van der Werf et al., 2017), and therefore our smaller posterior trend must be driven by atmospheric data. It is possible that the larger negative trend in pyrogenic emissions seen by these three studies were driven more by their assumed prior emissions than atmospheric data. This is supported by the “INV_FIXED” sensitivity test of McNorton et al (2018), where they do not impose a prior trend on pyrogenic emissions and consequently see no trend in the posterior.

Line 69: Another number should be used for r_std. Footnote 1 is well taken, but the use of the outdated R_PDB=0.0112372 causes confusion in the literature that is better avoided.

As we note in that footnote (and the reviewer seems to agree), the exact value of r_std affects neither our formulation nor our conclusions. However, since we have used the long-standing value 0.0112372 from literature (Craig, 1957), it would be incorrect of us to modify the text and simply substitute that value with another value (which one?) from more recent literature. Furthermore, even though the meat of our conclusions would not change, since there are several places where conversion between δ’s and tracer fluxes are performed, some of the exact numbers in our figures and tables might. Adopting a new value of r_std consistently would entail reprocessing our observations and prior fluxes and redoing every single one of our model runs. We think that this is too much of an ask at this stage, and therefore respectfully decline the reviewer’s recommendation.

Equation 8 and 9: What is the advantage of modelling CH4 and CH4 delta' over modelling CH4 and 13CH4? Both choices provide all the information that is needed to compute model analogues of CH4 and d13C measurements given sources, sinks and atmospheric signatures, right?

The most straight-forward set up of an atmospheric inversion has the form d(conc)/dt = fluxes – loss. This lets us assimilate measurements of ‘conc’ and estimate ‘fluxes’. If we set up the problem where ‘conc’ is either CH₄ or ¹³CH₄, then the second mass balance equation would lead us to estimate fluxes of ¹³CH₄. This is one step removed from what we want, which are fluxes of CH₄. It is true that at each iteration, we could calculate the adjoint emissions of ¹³CH₄, then transform them into adjoint emissions of CH₄ through partial derivates and assumed surface maps of the isotope signatures. However, that is one additional transformation we would have to build into the variational loop. Formulating our mass-balance the way we have (equations 8 and 9) lets δ¹³CH₄ measurements directly influence and optimize CH₄ surface fluxes without that additional transformation.

Line 108: What time step is used in B?

The time resolution at which fluxes are optimized, i.e., monthly.

Table 1: Does "microbial" make a distinction between natural and anthropogenic microbial emissions? Emissions from the main contributors ruminants and natural wetlands would have rather different uncertainties.

It does not. We are aware that this is a limitation of our current work, and we have mentioned this at several places in the text. In principle, CH₄ emissions from agriculture, waste and wetlands can have small differences in their δ¹³C signatures that vary geographically. In practice, neither our source signature maps nor our δ¹³CH₄ measurements are extensive or detailed enough to reflect or utilize such differences.

Figure 2b: What motivates the use of this scheme over a single long sequential inversion? (memory / max. run time of a job?) 

The limitation is indeed the maximum allowed run time of a job on the clusters we had access to. In a 1997—2017 inversion performed as a single run, we would need to perform 21-year TM5 forward and adjoint runs, either of which would exceed the 8 hours allowed per job on our cluster.

Line 183: This assumes that the scale conversion error can be represented by a random uncertainty, changing from sample to sample with zero mean. Whereas, in reality this scaling error would be systematic. Then how appropriate is the treatment of this uncertainy?

The reviewer is right that a different scale means a systematic difference in measurements. However, we use the scale conversion factor to correct for that, and what is left, i.e., the “uncorrected” error, is assumed to be mostly random. We have accounted for the uncertainty in the scale conversion factor in the total measurement uncertainty. Random uncertainty also exists during scale propagation for labs on the same scale (the absolute scale uncertainty is typically larger, but if all measurements are on the same scale, the absolute scale uncertainty is not a problem). We estimate this uncertainty using the reproducibility of standards, i.e., changes in measurements of the same standards over a long period of time. The scale propagation uncertainty is also included in the total measurement uncertainty.

Line 194: How about model representation errors, particularly in measurements from tower sites?

We do include a model representation error, calculated for each measurement, based on modeled tracer gradients. This is mentioned on line 107 of the original manuscript with Meirink et al (2008) as the reference. Note that this model representation error, being specific to TM5, is not included in the released dataset.

Line 230: A table would be useful that summarizes the adjustments that are made in the sensitivity tests. 

We agree that there are quite a lot of sensitivity tests. However, since the tests are exploring very different axes (e.g., source signatures, initial fields, atmospheric chemistry, wetland inundation, to name some), we could not come up with way to summarize them in a table efficiently. We have therefore taken the current approach of grouping them by motivation and listing them as separate subsections.

Line 240: This assumes that the relative importance of Cl for the oxidation CH4 and MCF is the same, which is not the case.

Not really. For each instance of tropospheric chlorine, we came up with an OH scale by repeatedly running TM5 forward with that tropospheric chlorine and different scalings of OH, until (iteratively) we arrived at a scale that gave the same CH₄ lifetime in our model. No equivalence between CH₄ and MCF was assumed.

Line 259: Why would systematic errors in fractionation factors be non-gaussian?

We are not sure if the reviewer has put down the appropriate line number for this comment. In the original manuscript, line 259 is under §2.6.3, which discusses systematic errors due to source signatures, while errors in fractionation factors are covered in §2.6.2. Since the term “non-Gaussian” occurs in the original manuscript in §2.6.3, we will assume that they are talking about source signatures and not fractionation factors.

In a Gaussian distribution, values that are equidistant from the mean on either side are equally likely. However, if the assumed source signature of a region in our inversion is (say) –45‰, and a second source signature map reports –50‰ for that region, we cannot simulate that with a Gaussian perturbation on the first map. Any Gaussian perturbation around a mean of –45‰ will yield –50‰ and –40‰ with equal likelihood. That is, we cannot design a covariance matrix that, under random Gaussian perturbations around –45‰, will yield –50‰ more often than –40‰. This is what we mean by “non-Gaussian”, and this why we have not explored source signature errors in our Monte Carlo ensembles.

Line 305: As shown in Houweling et al (2017) what matters more for the initialization than the gradient are the initial atmospheric burdens of CH4 and 13CH4 – which take longer to equilibrate. It is unclear how the burdens differ between the scenarios that are tested.

This is true, and was pointed out earlier by Tans (1997). For each of the scenarios that would result in different atmospheric CH₄ and ¹³CH₄ burdens, we did a long forward run from 1984 to equilibrate the atmospheric burdens by 2000.

Figure 5: It is obvious that the CH4-only inversion will not get the isotopic source/sink balance right (it would be a coincidence if it did). But if you would account for mean offsets in this balance (e.g. by a different choice of fractionation factors), then I wonder how well it might reproduce the observed d13C time variation (towards the end of the time record it seems to be getting some of the observed variability right).

This is possible in principle. The thing to note here is that even in the CH₄-only inversion, the initial field and prior fluxes are constructed to match the atmospheric CH₄ and δ¹³CH₄ trends, yet in the absence of δ¹³CH₄ data they progressively stray away from observed δ¹³CH₄. We agree with the reviewer that if they did not, that would be a coincidence.

Figure 6: It is obvious that the CH4 only inversion is performing worse than the CH4 + d13C inversion. But it is not obvious that the CH4 + d13C inversion is doing better than the prior. Some further quantification of this would be useful to evaluate the performance of the isotope inversion. 

The reviewer is correct that the prior seems to do as well as the joint inversion in Figure 6, while the CH₄-only inversion always does worse. In fact, if we calculate the mean mismatch in δ¹³CH₄, only for the HIPPO comparisons does the joint inversion do significantly better than the prior. The table below shows the mean difference between modeled and observed δ¹³CH₄ values from the three campaigns. As in Figure 6, the main point is that the CH₄-only inversion does significantly worse and is therefore likely to yield incorrect emissions.

We think the prior is doing well in this comparison because the prior fluxes, scenario “C_WL+” of Lan et al (2021), were constructed to match the background CH₄ and δ¹³CH₄ fields quite well. They did not match the observed high-latitude seasonality in δ¹³CH₄, but the aircraft data shown in Figure 6 do not have the samples to pick that up.

Figure 8: The perfect separation between the two sensitivity tests in several of the panels puzzled me initially. The way I understand it now is that the shaded region is the difference between the reference inversion and the sensitivity test. The puzzling plots show impacts of two tests that point systematically in opposite direction of the reference. It would help to add a clarifying sentence in the text.

A stronger OH fractionation makes the atmosphere heavier, requiring a larger (smaller) fraction of microbial (fossil) to match the same observations. Since chlorine has the strongest discrimination among all sinks, a smaller chlorine sink makes the atmosphere lighter, requiring a smaller (larger) fraction of microbial (fossil) to match the same observations. Therefore, a stronger OH fractionation and a smaller chlorine sink affect the fossil/microbial partitioning in opposite ways, resulting in the structure seen in Figure 8. This is now explained in the figure caption.

Line 400: Why "this suggests"? You have all the numbers needed to quantify the contribution of the Tropics to the total, right?

Correct. We were just being cautious, as in “suggests” instead of “proves”, because our inversion is not the last word on the methane budget. We have changed the phrasing to “Therefore, the largest contribution to the global increase in microbial emissions between the two periods comes from the Tropics.”

Line 401: The trouble is that the Tropical continents have almost no measurement coverage, especially for d13C. Could this outcome just be explained by larger a priori uncertainties in the Tropics making the flux adjustments the least costly?

We would of course love more δ¹³CH₄ measurements (also more CH₄ measurements) in the Tropics. However, the point here is that we only get this majority attribution to the Tropics if we use δ¹³CH₄ data. If it were just a function of the prior flux uncertainty, we would also see this attribution in a CH₄-only inversion.

Section 4, discussion: To end the paper with this section title suggests that the paper has no conclusions, whereas this section actually contains a numbered list of conclusions. Due to this, the conclusions appear to be somewhat hidden for a reason that is unclear to me. I would suggest to avoid any confusion, particularly among those readers who quickly want to jump to the conclusions, by changing the title into ‘Discussion and conclusions’.

This suggestion is well taken. We have completely reworked this section, calling it “Conclusions and discussion”, with a subsection called “Enumerated conclusions”. Comparisons with other published papers and future directions are other subsections of this section now.

Line 65, This suggest that L refers to a lifetime, whereas instead probably something like “Loss” was meant. The use of “lifetime” is confusing because that would be 1/L. I realize that the sentence can be read differently, but it is better to avoid possible confusion.

We called it “inverse lifetime”. However, we agree that this can be confusing, so in the revision we say “can be denoted as a loss rate or inverse lifetime”.

Line 116, “eq. (12)” i.o. “(12)”

Corrected.

line 212: 'errors' i.o. 'variations'? 'Variations' is ambiguous in this context in the sense that it could refer to real variations as opposed to errors.

Fair point. Changed “variations” to “errors”.

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