|After reading the revised manuscript and stages of peer-review, I agree with many points by reviewer M. Tesche – the work is useful but some more needs to be done, largely along the lines suggested by that reviewer, to demonstrate that the conclusions are robust. I therefore recommend further revisions, after which I think this can be a valuable contribution to ACP.|
There is one area where I wonder if Tesche has misunderstood, and the authors could reword to make sure others don’t have the same issue, which is the Cattrall et al. (2005) reference. On first reading, I also thought this was wrong. The authors reference Cattrall et al. (2005) in the context of direct measurements of lidar ratio, while the study is not direct measurements but models based on AERONET inversions. However Cattrall et al. (2005) do also include a table of results from field campaigns which were (I think) direct measurements. I think that table is what the authors mean by ‘direct measurements’, not the Cattrall analysis itself. So the authors should be careful how they reference this study, to make sure people don’t get the wrong impression.
I also feel it’s important to point out the limitations of the AERONET estimates of lidar ratio; it is a calculated value based on an inversion (i.e. a retrieval result). It is sensitive to both coarse mode size but also fine/coarse partition, so there are several effects to disentangle. This links into points Tesche raises about error and the conclusions of the analysis. I have some more suggestions about this below. But, as Tesche notes, I think it’s important to be more explicit about the limitations of these indirect measurements, as others may not be aware of them.
For the SODA data, based on the HSRL comparison, the authors state that for AOD > 0.05 the lidar ratio uncertainty should be <50%. What fraction of the data used for the main study are for AOD < 0.05? From Figure 3 it is hard to tell because these are scatter plots not scatter density plots, but it looks like there are a lot of points there, especially at lower wind speeds. And from Figure 6 I think saying ‘Additionally, Fig. 6b illustrates that the relative uncertainty in the SODA retrieved Sp is less than 50% for AODs > 0.05’ is misleading because it could be understood as an upper bound; it might be better to say a ‘typical uncertainty of order 50%’ because there are a whole bunch of points with errors approaching 100% for AOD in the range 0.05-0.1.
I partially agree with Tesche’s comments on the scatter plot of SODA AOD vs. HSRL. The authors should color-code points in some way to indicate where they were taken, and/or the aerosol type. I would imagine that the type-dependence of SODA AOD validation is weak but we don’t know unless we can see the data. Also, as well as R2, the RMS error and also any bias would more useful (as they will alias into scatter and bias in the lidar ratios too).
In their response the authors point out only 13 coincidences with the Maritime Aerosol Network and say this is not enough to validate the SODA method. I think this data would still be valuable to include, even if only 13 points, as another point of comparison. In fact the small data volume might be an advantage in some ways because if there is some point which matches very well or very poorly it is easy to identify and dig into the data to figure out why. This would be a good backup to the current evaluation against HSRL.
As the reviewers and authors note, there are some spurious regions in Figures 1 and 2 (e.g. Asian coastlines, but also off the west coast of South America, which might be sulfate from mines, and Australia, in some seasons) where the AOD and lidar ratio are elevated, which are probably not marine aerosol cases. I suspect this will affect some things like the PDFs of lidar ratio in Figure 4, and the whole analysis based on wind speed. I therefore suggest that the authors make some further data cut to be more confident that they are looking at marine aerosols, and redo the relevant later analyses based on that. Perhaps take some large boxes over parts of the open oceans, and exclude the data in these coastal regions. That would make the results more convincing, and if these coastal cases were spurious non-marine data, I expect it would bring out any marine signal in the remainder more clearly.
Figure 3: This should be redrawn as a scatter density plot for clarity. Also, the least-squares results should be removed because this technique is not mathematically appropriate for finding regression relationships for this type of data (even though people do it a lot). This is because errors are not Gaussian (in low-AOD conditions the error distribution is truncated because AOD cannot be negative), because both datasets have non-negligible error (least squares regression assumes the x-axis data are ‘correct’), and because the error is AOD-dependent (so treating all points equally is not appropriate). Just plotting a 1:1 line over a scatter density histogram would be clearer to see the main point of the figure, and less statistically problematic.
Figure S2: This should really be in the paper, not in the supplement. People often don’t read supplements, and it is a plot on which a lot of discussion rests. I expect it may look a bit different if the coastal regions are excluded, but really it highlights some of the issues Tesche and I have. For example, the wind speed distribution has very few low or high values (see also Table 2) and yet these are the wind bins which will have the strongest influence on the linear fit because they are the extrema. And, especially for wind speeds < 5 m/s, many of the bin medians and means lie quite far from the 95% confidence interval of the linear fit. This is clear evidence that the linear model or error estimate on it are not appropriate (perhaps the true model is not linear, the data are not independent of each other, error characteristics of the data are different between low-wind and high-wind conditions, etc). One way to (partially) deal with this would be to chop the data into e.g. 10 equally-populated bins, and do the regression along that wind speed range.
Further, one can draw a roughly flat line through this shaded confidence interval from 0 m/s to about 10 m/s, or about 5 m/s to 15 m/s; either way this is saying that any real change in lidar ratio with wind speed over this data range cannot be distinguished from zero with 95% confidence. So the authors should be careful not to overstate their finding. Perhaps excluding the coastal outliers will help with this.
I am also curious, if the authors attempt a direct correlation between raw (i.e. unbinned) lidar ratio and wind speed, what is the value of R^2? If it is very low then perhaps it would be better to look at one or two parameters which are explaining a higher proportion of the variance in the lidar ratio instead (this kind of echoes Tesche’s statement about the utility of this part of the analysis). Or at least make an estimate of the variance in the lidar ratio caused by their retrieval uncertainty, if possible how much is random vs. systematic, and how this compares to the wind-induced variability. I am not yet convinced that the results are not entirely spurious here. For example higher wind means higher AOD (on average), and so lower uncertainty on lidar ratio. This may in part be the cause of the wide distribution in lidar ratio in Figures 4 and S2 in low-wind conditions. So if a lot of the error in low-wind conditions is systematic and not random, it is possible all we are seeing in this wind analysis is the difference between some positive bias in low-wind conditions, and smaller errors in high-wind conditions. Or it could be that coastal regions with lower wind speed also have contamination from non-marine (continental) aerosol sources which have higher lidar ratios. Or it could be a combination of these factors. It seems like a bit of a waste if the authors do not dig into this more deeply.