|This is my second review of the manuscript and there are still a|
few minor points I would like to see addressed before publication.
The authors have considerably revised the presentation of their
results since the first submission, especially they have followed
the suggestions made by Reviewer 1 in restructuring the discussion
of the main results (old sections 3.2 and 3.3). The new
presentation is more concise and better structured than before.
Concerning my major concerns from the previous review the authors
have included two additional figures and discussion to address the
question of independent surface measurements for validation (new
Fig 5) and posterior covariance (new Fig 11). The latter point is
satisfactorily answered by the new figure and corresponding
discussion, whereas for the first point some minor questions remain
However, my most major concern (the definition of the emission
regions) still requires some additional justification and
discussion. The authors mention in the reply and added to the
manuscript that the region definition follows 'existing Transcom
basic functions' and they cite DeFries et al. (1994). However,
DeFries et al. (1994) presents a satellite based global vegetation
classification, which may be relevant for defining CO2
emission/upkate regions, but has very little to do with CH4
emissions. Maybe the definition of Transcom regions was based on
DeFries, but I still don't see the relevance for CH4. My major
concern of considerably different economic developments in the
large Eurasian region is not considered in any detail. Next to the
(in my view insufficient) motivation of the region definition the
authors have added a note of caution in the conclusions. However,
the authors seem to suggest that the kind of aggregation errors
they are dealing with will level out when looking at a region total
(somewhere too high, somewhere too low). That this does not have to
be the case and that it is related to where observations are
available was nicely demonstrated by Kaminiski et al. (2001).
Although their findings are based on much coarser transport
simulations their regions are similarly coarse as in the current
study. In conclusion, I would like to ask the authors for a more
meaningful motivation of the region definition (beside the DeFries)
reference and change the comment in the conclusion towards the
possibility of the aggregation error causing significant biases in
the posterior fluxes.
Other comments (page and line numbers referring to the
track-changes version of the manuscript:
Page 3, Line 30: Abbreviation for 'kinetic fractionation' is not
very commonly used and only twice more in the paper, at which point
one does not remember the definition. Please remove the
abbreviation and replace by complete term.
Equation 3 (and elsewhere): I don't think the dots are the correct
notation for a matrix multiplication here. Also follow the ACP
guide on which font type to use for matrices and vectors.
P7, L1f: What is the rational for choosing these sites? Especially
the high-altitude site seems to cause more discussions than it can
convince that the simulations worked well. Why not use other
continuous CH4 surface observations even though no d13CH4
observations are available at such sites? In the end, GOSAT and
TCCON don't provide isotopic information either.
Figure 5: Why is there a jump in the prior at the end of 2013? This
is visible at both locations but not for any of the other sites
displayed in Figure 1. It is indeed strange that d13CH4 is
decreased so much at HAGCOC. Is there a problem with comparing the
simulations with high-altitude data? How was the difference in
topography between model and reality considered?
Figure 11: This is an interesting and helpful figure. There is just
one clarification I would like to ask for. Since values in the
figure are between -1 and 1, I assume this is not the posterior
covariance matrix but some normalised version of it. Please
indicate how it was normalised. Furthermore, it is very difficult
to interpret the by-sector part of the matrix because no x axis
labels are included. I suggest to include a numbering in the
existing y axis labels and use the same numbers on the x axis as
well. This would allow for a quick identification of which
sectors/regions actually showed considerable posterior covariance
Kaminski, T., P. J. Rayner, M. Heimann, and I. G. Enting (2001), On
aggregation errors in atmospheric transport inversions, J. Geophys.
Res., 106(D5), 4703–4715, doi: 10.1029/2000JD900581.