|The authors did address many of my comments, and I thank them for that. The paper now provides a much more complete description of what the model and the inversions do, and this facilitates the interpretation of the results. The paper also new comparisons with surface NO2 data (Fig. S7-S10). |
Still, regarding many concerns, I remain unconvinced, as explained below. The authors keep insisting in their response that "the results in the manuscript are based on the a posteriori, not the a priori" as if the large (sometimes huge) model biases were simply irrelevant. It is obvious from Fig. S11-S14 that both the prior and the posterior model fail to match the observations at most locations except the most polluted. Over many regions (e.g. Ukraine, etc.), the model-data difference for NO2 is systematic and exceeds the TROPOMI error (~1.1E15, Verhoelst et al.). This implies serious issues in the model and/or in the data (e.g. in the bias correction). Things are even much worse regarding HCHO. If we are clueless as to the causes for such discrepancies over moderately polluted regions, why should one trust the results in very polluted areas? True, the AKs provide an indication regarding where and when the inversion results are most reliable (if we accept the hypothesis that model and data are not too biased). However following that guideline, one would have to accept as very credible the NOx results for Germany in March (Figure 2 and Figure 4) indicating a strong emission increase in Northern Germany (in 2020 with respect to 2019) and an emission decrease in Southern Germany. This discrepancy between regions in the same country is an obvious artefact, as the authors implicitly admitted by removing the discussion on that region. This is a "COVID-19 paper" and the reader should be given some clues regarding patterns of emission changes which are obviously wrong. No need for cell-phone, traffic or industrial data for that. The paper does not provide any clue, probably because of the too many issues with the data (largely due to cloudiness, Fig. S16-17) and especially with the model. For example, the very wrong distribution of NO2 columns in the model over Germany (Fig S11) should have prompted the authors to try to explore its possible causes instead of relying exclusively on the power of inverse modelling. Maybe the inversion is correct, but how does it help anyone if we don't understand why?
That being said, the authors have accounted for many of my concerns and updated the text accordingly. The authors realized that the NO2 results are less reliable in March and May, which is why the ozone analysis is restricted to April, as it should. They state to their defense that "remote sensing data provide limited information for optimizing emissions [many references]" which I find contradictory since emission optimization is precisely the methodology adopted in this paper, and the paper provides in great detail relative and absolute differences (2020-2019) of top-down emissions (Figure 4 and Table 2) despite those limitations.
The new figures S7-S11 with the comparisons with surface NO2 data are interesting but I wonder about their significance. There is an overall bias reduction (31%-45%, although the precise meaning of this range is not made clear) but, despite the TROPOMI NO2 constraint, a large systematic underestimation of modelled NO2 remains with respect to the data. Why is that? Could this be due to representativity issues? Or interferences in the NO2 measurements? Note that daily averages are strongly influenced by night-time chemistry. For a proper evaluation of TROPOMI-constrained model values, it would be preferable to sample the data as well as the model in the early afternoon (say between 12 and 15 LT), since night-time chemistry is not well constrained by TROPOMI. In addition, it would be useful to summarize the comparison over the different subregions of Fig. S7-S11 in a table (including mean bias, mean absolute deviation and correlation coefficient). The authors state in their response "The absolute amount of CEDS is too low in many places" as explanation for the model underestimation. This is not a comparison of CEDS with NO2 data. There might be issues in the model (PBL mixing, chemistry) or in the data (interferences, representativity issues) which should be acknowledged first before holding the emissions as responsible.
The authors complain that they "do not understand why this reviewer is concerned about the prior emissions. This paper is not about validating CEDS (...) We could have used EDGAR emissions and reached similar results (...) [or] even used constant emission rates throughout Europe and induce the emission changes by TROPOMI". This is wrong. The striking similarity between prior and post NO2 columns (Fig S11-S14) indicates clearly that both TROPOMI and the prior determine the solution, and therefore the choice of the prior does matter a great deal. Even in areas with high AKs where the inversion is mostly driven by the observations, the changes in the patterns of the emissions induced by the inversion must be questioned: are those real or could they be related to issues in the model or in the observations? I'm not asking you to solve these issues but only to consider and discuss them in a more balanced way.
Regarding the HCHO inversion I still believe that the results of the inversion have very little value given the high differences between the model and TROPOMI. If they think that the emission differences 2020-2019 from the inversion are significant, please provide a quantitative estimation of the uncertainties on the retrieved emissions.
The authors insist that the high TROPOMI HCHO values in April in Northern and Eastern Europe are not too high, citing the negative bias over high-HCHO level sites reported by Vigouroux et al. 2020. The hypothesis that the negative bias is due to aerosol effects is what it is, a hypothesis. In April 2019 over Saint Petersburg (a megacity right in the big HCHO plume on Figure S13), TROPOMI is overestimated by about 35% based on comparisons by Vigouroux et al. Same thing over Sodankyla and Kiruna. Those direct measurements inside the HCHO hot spot are much more relevant than speculations about the possible role of biomass burning. Your manuscript should acknowledge that TROPOMI HCHO is very probably overestimated in that area, for reasons unknown. I do not dispute the fact that the direction of the emission increment in April 2019 goes in the right direction. Of course it does. But you do not need a sophisticated inversion system to infer that emissions were higher than the model prior in April 2019.
The authors did not address my comment that the bias correction might lead to different corrections being applied in 2019 and 2020, thereby creating artificial patterns in the differences between the two years.
I strongly recommend to drop that part on HCHO and the VOCs which, despite relying on a sophisticated inversion scheme, cannot do better than a simple visual inspection of model results and observations. For the NOx part, I recommend strongly to drop Table 2 and reword many parts (including discussion, abstract and conclusions) in order to convey the known limitations and uncertainties of inverse modeling (as acknowledged by the authors, see above).
- Thanks for the clarification on the AMF and the profile shapes. How does that relate to the averaging kernels (in the definition of e.g. Eskes and Boersma 2003, www.atmos-chem-phys.org/acp/3/1285/) used by other groups to derive total columns from model profiles?
- Thanks for the clarification on the observation error. Note that the TROPOMI precision estimation might actually contain non-random parts. Your inversion system does not account for model errors. Can some crude estimate be provided for those? How could their omission impact the results?
- The HCHO TROPOMI product provides random and systematic error estimates, why not using those? The 4% seems too low considering the large variability among the different sites in Vigouroux et al.
- What are the implications of neglecting diurnal variations of anthropogenic emissions?
- Table 2: please provide uncertainties if you provide numbers which you think could be used by regulatory agencies. There is ample evidence that these numbers should be taken with great caution. Or delete this table if you cannot estimate the uncertainty.
- Seasonality of top-down VOC emissions in 2019: I reiterate my comment. The retrieved patterns indicate primarily anthropogenic emissions, with hot spots in Ruhr and Rhine Valleys, Southern Holland, London, etc. Those are not biogenic emission hotspots. The inversion system is simply unable to bring useful information on the emissions, except that the total VOC emissions were much higher than the prior (and than their 2020 counterparts) in Northern Europe (which is of course very obvious from TROPOMI).