|After a detailed reading of the authors’ comments and of the updated version of the manuscript, I am still concerned about the approach adopted by the authors. I must acknowledge that the authors extended the presented data analysis to support their conclusions. Nevertheless, I regret to note there are still not fully transparent aspects and not obvious choices in the data analysis which does not allow the presented analysis to be complete and to improve the accuracy of results.|
My concerns can be summarized in the two following major points.
The authors state that they initially “did not provide quantitative thresholds about how we separated ice and liquid clouds because of the challenges in their estimation. As a consequence their preferred to use manpower to manually analyze the data set and decide where ice is or not.“ Nevertheless, In their response, the authors also provides an approach fundamentally based on the definition of a threshold on lidar volume depolarization ratio for the detection of ice-containing clouds.The comparison between the “manual” data selection and those based on the automatic data classification, independently on the difficulties intrinsic to the definition of credible thresholds for the automatic algorithm, opens the way to the following thought: considering that with the automatic selection the difference in the percentage of surface-coupled and decoupled clouds is lower compared to the manual analysis (i.e a factor of about 1.5-4 vs a factor of 2-6 on average in between 0°C and -10°C) can we consider this difference as the results of the level of subjectivity of the analysis? Or is this an indication that the analysis is largely affected by the irreducible uncertainties due to the assumptions done in the retrieval of lidar products? Assuming the error bars in Fig.5 are a good estimation of statistical uncertainty according to Seifert et al. (2010), the variability between the “manual” and “automatic” data processing may be representative of a bias which may affect your manual approach. Although the results demonstrates that majority of clouds in the height corresponding to the interval 0°C and -10°C are surface-coupled, the quantification of their fraction must be as accurate as possible and potential systematic effects, such as those due to a manual data analysis, should be discussed in the manuscript.
2. The authors removed from the manuscript the analysis on the estimation of INP concentration and added a new analysis to demonstrate the hypothesis that the aerosol source acting as INPs in Arctic are the similar to those of a continental site, i.e. Leipzig, which is used as a comparison term in the data analysis.
First of all it is not clear to me why, using a multi-wavelength Raman lidar, aerosol extinction profiles in clear sky, presented in the updated manuscript version, and consequently, lidar ratio profiles are not retrieved from Raman channels. The capability of a multi-wavelength Raman lidar are fully neglected with consequent increase of the uncertainties in the retrieved products. Assuming a constant value of the lidar ratio may be considered acceptable only for ice cloud, although also I that case the variability of lidar ratio could affect at smaller extent the selected thresholds. The retrieval of the aerosol lidar ratio from Raman lidar measurements from could definitely, coupled with the particle depolarization ratio and air mass back-trajectories, clarify the role of different aerosol types involved the ice clouds formation (several example from literature can be provided, but I am sure the authors knows all of them very well). This could also avoid to include the comparison with Leipzig in support of the authors interpretation of a major role for the continental aerosol in the ice cloud formation in the Arctic and increasing the credibility of the presented analysis, which appears still too speculative.
I want also to add that aerosol backscatter profiles in Fig. 7 must be shown over a longer vertical range to ensure the reader can have a clear idea of the calibration accuracy of lidar profiles.
About the presented investigation of the aerosol sources using FLEXPART model, if it is true that marine fraction decrease with height, above 2 km, it remains the major source at all levels, while the other aerosol types slightly increases with the height, except for "grass cropland" aerosol which has a bit larger increase. I do not see any reference to support the authors’ statement of similarity with the aerosol composition typical for the Leipzig site, which is not a marine site. For this part, the analysis looks carried in out in hurry and must be deeper.
At this point, although the statistics presented in the manuscript on the surface-coupled and decoupled ice-containing clouds are interesting, I am not sure if the content of the manuscript is sufficient for publication on ACP. Major revisions are still required and if points above cannot be fulfilled in a short time by the authors, I’d suggest to re-submit the manuscript once data are more consolidated.