|Review of revised version of Cohen et al. (2021), Interpol-IAGOS: a new method...|
As this is a review of the revised version of the manuscript by Reviewer #2 of the original submission, I will not include the usual introduction to the review and instead pass directly to an assessment of the modifications to the manuscript made in response to the first round of referee comments.
The author response to the comment from Anonymous Referee #1 regarding the use of Specified Dynamics (SD) simulations ( ‘... the problem with the SD-simulations could be that certain nudging methodologies may lead to introducing noise (and hence too much mixing) especially visible around the tropopause (see discussion in Orbe et al. 2020).’) misses the mark a bit. I agree that MOCAGE, being a CTM, would not suffer from problems due to nudging of dynamical variables, however the problems introduced by nudging in a SD simulation should be seen as a caveat to the results found comparing SD simulations and not as a possible application. As argued by Orbe et al (2020), the dynamical noise and resulting loss of consistency between tracers and dynamical variables is a problem with SD simulations and should be pointed out here as a possible aggravating factor. The text inserted at Page 27, Lines 9 – 10 does not adequately bring this forward. It is an important point since the use of SD simulations (or a CTM using reanalysis) is an important component of the current comparison with IAGOS observations as one would expect any significant biases in the position of the tropopause in the model would be reduced making the comparison with IAGOS-DM more straightforward.
Page 4, Lines 21 – 23: There is revised text here that reads ‘To compare the REF-C1SD simulations against IAGOS data, interpolating the simulation outputs onto the high-resolution observations would be expensive computationally, and not required because our study is not focused on processes but on climatologies.’ and was added to address the comment of Referee #1 on the original text at P4L3, that the interpolation of the model outputs on to the IAGOS observations is ‘not possible’. There is new text inserted at Page 4, Lines 16 – 18 that much better addresses the substance of the original comment by Reviewer #1. And even with the focus on climatologies (‘... our study is not focused on processes but on climatologies.’) would it not be advantageous to have high frequency model outputs that could be interpolated on to the IAGOS observations to construct a climatology that is more directly comparable with the climatology derived from IAGOS? It is difficult to argue against the view that the correct way to perform the comparison would be to have high frequency model outputs and, while computationally expensive, it is nowhere near as computationally expensive as the original model simulations. But for now we do not have high frequency model outputs from multi-model intercomparisons such as CCMI. I would suggest the authors revise the text at Page 4, Lines 21 – 23.
Page 10, Lines 6 – 12: Here the authors have added a brief description of the comparison of sampling MOCAGE daily output with the monthly sampling in response to the second half of the comment of Referee #1 to P4L3 that begins ‘In fact, it would be important to prove for a methodology paper as you have presented here that your claim of the gridded IAGOS data being representative of the monthly mean is true.’ In the response to the comment, the authors did perform a new analysis that is described in the response to Reviewer #1 using MOCAGE-M-day. There are some statistics from this comparison in the response to Reviewer #1, but the authors do not include any quantitative results from the comparison to MOCAGE-M-day in the article – as it is, the authors state ‘MOCAGE-M monthly means could be considered as representative of the month’ with no supporting information. In particular, I am not too worried about the sampling in locations with a high frequency of aircraft sampling (the North Atlantic flight corridor, for example) but some mention of the magnitude of the larger differences would be instructive.
On the reply of the authors to the comment ‘On a similar note, it would also be good to see what the benefit of the weighted gridding versus a gridding of the observations without the weighting function would be...’ To estimate the benefit I would think you would have the weighted and unweighted gridding and compare these two products to some estimate of the truth. Here, we have the original aircraft IAGOS observations, a weighted gridding of the IAGOS observations, an unweighted gridding of the IAGOS observations, and the model output. One could show differences between the weighted and unweighted gridding, but how does one show the benefits of weighted gridding? To put it another way, because the model differences are smaller for weighted or unweighted gridding, does that mean one is more correct? I suggest the authors be careful about stating they have analyzed the benefits of weighting. In particular, I am not convinced the authors have shown that ‘using a weighting function is a necessary step for a more accurate assessment’ as stated in the abstract of the revised version at Page 2, Lines 8 – 11. Given the difficulty of showing a benefit to weighting, I would suggest the authors revise the text to be clear they are showing ‘differences’ and not ‘benefits’.
Page 20, Lines 24 – 27: The text at this point was added in response to a comment from Reviewer 2 about the lack of directly addressing the effects of time averaging for the comparison with IAGOS data around the tropopause (‘It became a bit confusing when the discussion of the comparison of IAGOS-HR and IAGOS-DM zeroed in on the effect of mis-classification of points in either the UT or LS (see the comment on Page 19, Lines 4 – 6) and ignored the effect of time averaging.’). The text in this section still discusses the inability to correctly classify air masses using monthly average PV, but the problem is much more fundamental than. There is no clean separation of the stratosphere and troposphere left in the IAGOS-DM data after it is monthly averaged on constant pressure surfaces. By using monthly averages, of either the IAGOS data on a particular pressure level (IAGOS-DM) or model data, the sharp separation of tropospheric and stratospheric air around the tropopause, which would be preserved in the IAGOS-HR data, is lost. This will be a fundamental problem with analysing monthly average data in the vicinity of the tropopause and is illustrated to some extent by the differences between IAGOS-HR and IAGOS-DM. This is the point that is still missing in the text and, I think, it is an important one because it illustrates that treating the IAGOS-DM data in the way it is treated does make it more like the monthly average model data so the comparison of IAGOS-DM and the model is more valid. But because it is monthly averaged data the sharpness of the separation between tropospheric and stratospheric air masses is lost to some extent.
A couple of minor comments:
Page 6, Line 12: ‘expanding from 1980 to 2010’ should be ‘extending from 1980 to 2010’
Page 10, Lines 27 – 28: The new text ‘less measurements are needed to characterize the climatologies’ in reference to the CO observations implies that the CO climatology is somehow equally well characterized as the ozone climatology using less data. It would seem that the reason 60 CO observations are judged sufficient is that the sampling period for CO is shorter and to use the same Nthres=100 as for ozone means throwing out too much data. It is not that less measurements are needed to characterize the the CO climatology, so the wording should be modified here.