Zonal variability of methane trends derived from satellite data

The manuscript by Hachmeister et al. presents a dynamic linear model (DLM) applied to TROPOMI data to obtain background, seasonal, and short-term variations in the global and zonal methane growth rates. This method, they say, is computationally efficient and can rapidly accommodate the addition of new data. The paper is, on average, well written and represents a contribution to the ability to understand and potentially explain changes in atmospheric methane concentrations. However, there were several areas where I could have benefited from additional information.

1. Description of the data: I was confused by the strengths and limitations of the TROPOMI data used. Given the time spent on quantifying the errors in the growth rates due to incomplete coverage, this seems significant.
   1. I was curious about the distribution of the data. For example, how much area-normalized TROPOMI data is available in the high latitudes and tropics compared to the mid latitudes? This would help me understand the usefulness of the inhomogeneity metrics.
   2. I was also curious about the potential role of systematic biases in the TROPOMI data. The authors use the WFMDv1.8 product described by Schneising et al. (2023), but to my knowledge, this product has not been specifically validated for snow and ice covered scenes (an ongoing source of bias in other retrievals).
   3. Finally, I was curious how the authors define uncertainty for each of these datasets.
2. Validation of results: The authors compare their results to several other annual methane increases (AMIs) obtained using different data and the same method or the same data and different methods. The comparison here is largely qualitative and doesn’t attempt to explain the sources of the observed differences. It would be useful to understand what attributes of the different datasets or methods lead to the observed similarities or differences.

I was also, at times, confused or slowed by the writing style.

1. While I’m sympathetic to the need for long paragraphs at times, I found the manuscript difficult to read at times. Splitting long paragraphs into smaller components would have helped me. (For example, the introduction is a single paragraph.)
2. When equations are introduced, it would be a big help if every term in the equation was defined. This includes equations in the appendices.
3. When new terms are defined (e.g., the entropy) or methods introduced, I would have appreciated a short but intuitive explanation. I appreciated that the authors were so thorough in pointing the reader to the appropriate resource, but it would have saved a lot of time to add a brief explanation.

Specific comments

• Line 80: I didn’t understand what “model data” meant.
• Line 98: I was confused by the reference to satellite data. Which instruments are used?
• Lines 97 – 100: I was a bit confused by this data description. You refer to the “time series of monthly values of the column-averaged mole fraction of atmospheric methane,” which seems to be at an almost-global spatial resolution between 60°S and 60°N. Is that correct? Later in the paper (Line 367) you refer to total-column data from UB-C3S-CAMS and seem to apply the DLM to this data. If indeed you use this raw data, it would be helpful to provide more details (on coverage, potential biases, etc., as described above for TROPOMI).
• Line 106: It would be helpful to provide a brief summary of the approach used by Buchwitz et al. (2017).
• Line 116: How is uncertainty defined? Have the uncertainties been evaluated? For example, I know that the SRON-provided TROPOMI uncertainty is biased low because it only considers instrument errors, and excludes retrieval errors. I would be curious, for example, if the uncertainties used here are larger over snow- and ice-covered scenes, or at low albedos, as I would expect.
• Lines 119-120: Please briefly define (intuitively) the asymmetry and entropy of the data. What metric do you use for asymmetry? Skewness?
• Lines 123 - 126: Please briefly distinguish between the temporal inhomogeneity and spatial inhomogeneity.
• Lines 123 – 129: Did you confirm that the inhomogeneity metric removes data over timesteps or regions with sparse data? I wasn’t sure if your statements that H_T “tends to be higher in cells with sparse data coverage” and that the H_S filtering process “removes days with highly inhomogeneous coverage” provided this confirmation.
• Lines 124 – 125, Figure 1: I was surprised that there isn’t higher temporal inhomogeneity at high latitudes, where I would expect there to be significant seasonal inhomogeneity due to the variation in the amount of sun over the course of the year. Am I misunderstanding something about your metric?
• Lines 138: I was confused to which time series you add the Gaussian noise, the CAMS/INV data or the WFMDv1.8 time series?
• Line 171: I was confused about what you solve for using your Kalman Filter. Is it the variances of the Gaussian random walks?
• Lines 174 – 176: Can you provide more information about the parameters you used in your MLE? For example, how do you define the errors on the observations?
• Line 187: I was confused by what you meant by “variance in the level and seasonality,” which you use later for model evaluation. In particular, I’m confused how seeking low variance in the level wouldn’t incentivize low growth rates. I’m probably misunderstanding something!
• Line 193: I didn’t understand what you meant by “the average MSE across all five folds per DLM provides the AMSE.” I’m assuming this is standard k-fold cross validation, but I’d appreciate additional clarity!
• Lines 209 – 210: Please define all terms even if they seem obvious (as requested above). I was also a bit confused by the indexing. i seems to index across the models in equation (4) but across the time steps in equation (5). As a result, I also didn’t understand how equation (5) quantifies the model uncertainty without indexing over the models.
• Lines 224 – 226: I didn’t understand why the WFMDv1.8 mask wouldn’t include the effect of polar nights. Or are these meant to separate out the effect of polar nights from the total effect of TROPOMI sampling, including polar night effects?
• Lines 228 – 220: Are you referring here to the S5P masks from the WFMDv1.8 data? Does it or does it not include the additional masking to simulate polar nights?
• Line 232: What does “remaining bias due to sampling” refer to? What was the original bias?
• Lines 241 – 244: It would be helpful to specify that this is for each zonal band individually (perhaps “we calculate a zonal error” in Line 241).
• Line 245: I didn’t understand what the word “visualizes” intends to convey here.
• Lines 250 – 251: Perhaps I’m not familiar with the convention in the field, but I would have found units of ppb/yr to make it clearer that you’re comparing slopes. (Even though you are expressing the increase for a specific year.) I think this is also what you do later in the manuscript (e.g., Line 312).
• Lines 253 – 254: Per my point (2) above, could you provide a brief description of the methods used for each of these comparison data sets?
• Table 2: Why aren’t σ_DLM and σ_{sampling (SZA)} given here? I assume I’m missing something about why these quantities aren’t provided for the zonal results—it would be good to clarify somewhere in the text.
• Lines 260 – 261: Do you mean “…agree well with the DLM-based AMIs for the UB-C3S-CAMS and NOAA-GML datasets”? Or do you mean that you compare your DLM-based AMIs for each dataset to values derived with other methods for each dataset? Please clarify. Can you also provide more details on what it means to “agree well”? Do your results agree within error bars? More generally, to my point (2) above, I would be interested in how much of the variance between the results is due to different datasets vs. different methods.
• Figure 6: It would be helpful to, in the caption, note that you use the format @ in your naming convention. Also, is there a method to the color scheme? If so, can you explain this in the caption? If not, it might be useful to group together datasets with the same symbol and methods with the same color.
• Line 283: What do you mean by the “identification of zonal bands with anomalous methane increases using zonal AMIs”?
• Lines 284 – 289: I agree that it’s preferable to look at zonal information on monthly time scales, before it’s well mixed, but would mixing completely prevent us from getting zonal information on annual or seasonal time scales? Wouldn’t column data give information about the surface (i.e., newer, less mixed methane), providing zonal information even on annual or seasonal time scales? If so, it’d be useful to be less absolute in your statements about the timescales on which zonal information can be obtained.
• Figure 7: In general, I’d use either -90° (no directional suffix) or 90°S. I was confused by the reference to -90°N. For consistency with the text, I’d use 90°S.
• Line 312: “For 2020 growth rates increase strongly from roughly 0 ppb/y to 20 ppb/y.” Are these global growth rates or southern hemisphere growth rates? If the latter, are you averaging across all southern hemisphere bands?
• Lines 315 – 316: The CAMS/INV-SRF results seem to show growth rates in the southern hemisphere remaining relatively constant for this year, compared to the decrease you see. Do you have thoughts on why this may be?
• Line 324: Do you have evidence from your work to support this claim or are you relying on consistency with past studies? If the latter, it may be clearer to write that the increase is “consistent with increased southern hemisphere wetland emissions” might be better. (I agree! You find good support for this claim. But seeing an increase in southern hemisphere emissions alone does not necessarily imply increased wetland emissions.)
• Lines 327 – 329: As above, do you have evidence from your own work to support this claim? In order to make the argument that it’s attributable to “the return to pre-pandemic methane emissions from the energy sector,” you would need to show that the northern hemisphere methane emissions decreased during the pandemic despite the increase in oil and gas emissions. This is beyond the scope of this work, though you could certainly cite other studies that show this and argue that your results are consistent with those results.
• Lines 335 – 336: You write, “Comparison of our global AMIs with global AMIs from other sources indicate, [sic] that the effect of transport related sampling biases seems to be limited.” This is interesting—can you justify it a bit more? Isn’t it possible that there are consistent biases across the data sets or methods?
• Lines 338 – 340: I was a bit confused by this statement because the area where you find the largest differences between WFMD and CAMS/INV is also where your inhomogeneity metric is the largest (the southern tropics). Can you rule out artifacts from sampling related biases?
• Line 355: Instead of “other fluxes,” it might be clearer to write “non-wetland fluxes.” This is a personal preference, though.
• Lines 356 – 357: This again feels a bit beyond what you are able to show in this work. Might it be better to say “suggests” instead of “indicates”?
• Line 365: Is this true? From visual inspection of Figure 6, it seems that there are a number of studies for which the error bars don’t overlap (e.g., NOAA-GML (v2023-05)@NOAA MBLR for 2019 and 2022).
• Line 373: Is it true that “no significant sampling biases exist for zonal bands”? See my previous comments (on Lines 338 – 340) about potential bias in the southern tropics.
• Lines 384 – 385: You made a different argument in Section 6 as to why transport changes aren’t causing the observed growth rates. I find this one less convincing: an inverse system could easily alias transport errors into fluxes—this is a significant source of error in inverse modeling.
• Lines 387: As above, I’m not sure your study allows you to draw firm conclusions on the causes of the changes in the growth rates.
• Lines 390 - 391: The low computational cost, support for low-latency updates, and lack of reliance on a prior are neat features of this method! It might be worth mentioning sooner!
• Line 396: You write, “This indicates….” What is “this”?

Technical corrections

• Line 335: “indicate,” -> “indicates” (no comma)
• Lines 346 - 347: “(Peng et al., 2022)” -> “Peng et al. (2022)” for all three references in this sentence
• Lines 396 – 397: “(a) The” and “(b) No” -> “(a) the” and “(b) no” (lowercase)
• Line 401: “future satellite mission” -> “future satellite missions”

The manuscript by Hachmeister et al. derived the global and zonal methane growth rates from 2019 to 2022 using an ensemble of DLMs. They found a strong increase in SH in 2020 and a slowdown in methane increase in NH in 2022. The results are compared to previous studies on methane changes and show generally good consistency. Methane growth is an important topic and fits the ACP readership. However, I have a few concerns about the methods and presentation, and the readers can benefit from more clear presentation of this manuscript.   

The authors apply DLM to a few datasets, some are concentrations and others are emissions. It is not clear to me how these datasets are treated differently in the analyses. For instance, the increase in concentration should be affected by both emissions and methane losses, whereas CAMS/INV data should only reflect changes in emissions. This should be clearly stated in the result discussion and comparison.

Section 3.2 has a mixture of literature review and method. It is not clear what exactly has been applied in the DLM fit in this work based on the descriptions. For instance, the authors mentioned the Kalman Filter in line 172. Has it been applied to this work? If so, what are the detailed setups? If not, this information should be removed to avoid confusion. The rest of this section has similar issues.

In addition, the analyses of the cause of methane increase are very vague. Figure 10 and Figure 11 separately show emission changes from wetlands and other sources, but how are they separated? Why is it only presented for this dataset? In lines 354-355, it is not clear how the authors did the source attribution, or these are just hypotheses. In most other places, the authors only cite previous work to explain the sources of methane changes. This gives me the impression that this work does not add much new to explain the methane increase signals.