|Rather than review the revised manuscript in full, I have focused on an evaluation of the strength of the responses to the comments raised by myself and the other reviewer, and as to whether they adequately address the comments. While many of the changes have improved the manuscript, there still remains areas where the reviewer comments have not been addressed, as detailed below.|
Responses to Reviewer #1
Response to Line 56 comment: The changes/additions to Section 3.2 are good, but I am confused by the second-to-last statement in the response: “The rainout process is a major process to reduce the loss of aerosols in wet removal”. Is this just a typo, since the calculations show only a minor estimated contribution? I think the terms washout and rain out should be avoided, and instead use “in-cloud” and “below-cloud” scavenging to describe the different physical processes.
Response to LIne 152-154: Also a useful addition, however change “the discrepancy can be partly attributed to …” to “the discrepancy may be partly attributed to”, since it has not been established whether there is a difference in the SP2 response to BC in remote air and FS.
Response to reviewer comment on line 317-319:
The final line of text in Section 3.4 states “the changes in SO4/CO correlation were largely controlled by the rainout process and weakly influenced by aqueous-phase formation during transport.” The argument in the response to the reviewer is that the aim is to determine the impact of the cloud process on aqueous-phase formation of SO4. The difference in slopes in this case is also small, and neither the response nor the revised manuscript addresses the main point of the reviewer comment that questions the significance of the different relationships in the data. A stronger response, and argument in the revised text, would provide uncertainties in the regression coefficients and discussion of the significance of the differences in the relationships. The underlying reasons given by the authors (wet removal and in-cloud formation) are certainly plausible, but not proven based on the data shown here.
Additional minor point, but the range shown in the figure 6a is different from that stated in the revised text. The range shown in the plot includes the upper/lower limits associated with each of the Kanaya ranges...it may be better to give the same range in both (mean values?), whichever is most appropriate for the comparison.
Response to reviewer comment on line 343:
The inclusion of “absolute” size distributions does not directly address the main point of the reviewer comment, that there is little evidence of preferential loss of larger BC particles relative to the loss of smaller particles. The new Figure 7c is more helpful, showing a trend, though quite noisy, in the mode BC core diameter. A stronger response would also note that the more important parameter to examine here would be total particle diameter, not just that of the BC core. Just because the BC core is small does not mean that the total particle diameter, including a coating, is also small, and therefore may be as easily scavenged as a bare or weakly coated larger BC core.
Response to reviewer comment on line 345:
The response to the reviewer is weak. It does not address the main point of the comment, that concentrations are too low for coagulation to be an important process in removal of small BC particles. Given the manuscript focuses on changes in BC size distributions it seems such a fundamental topic should be discussed, even briefly, in the manuscript.
Response to reviewer comment to line 372:
I’m not clear which uncertainty in section 2.1 is being referred to in the response to this comment, but while I would agree that the SP2 can resolve quite small differences in rBC mass (assuming constant material properties), I think the uncertainty the reviewer is talking about here is the statistical uncertainty associated with the spread in the data, and whether there is a significant difference in fg/particle for the two conditions. Note that the comparisons of log-normal fit MMDs in Table 2 is less reliable because it includes an assumed density, which might not be constant for the two cases.
Response to reviewer comment to line 373:
The response to this comment somewhat undercuts the response to previous comments and the usefulness of Figure 7c. If size distributions change again during subsequent aging following the wet removal process, then is the apparent decrease in BC core size shown in Figure 7c meaningful or simply a random example where post-wet removal aging processes happen to give a somewhat smaller average BC core size? Could a slightly different aging process following wet removal lead to a larger average size? On this basis I think any conclusions drawn regarding size dependent loss of BC should be removed or at minimum highly qualified noting the confounding factors the authors have pointed out in several of their responses.
Responses to my comments:
First general comment (BC removal processes):
The additional discussion of BC removal processes is good, but suggest changing “Their” to “previous” in line 56 of the revised manuscript, and giving a very brief summary of the Kanaya et al. (2016) dry deposition results in section 3.2. For example, “The dry deposition in this region has already been evaluated by Kanaya et al. (2016), who found minimal decrease in BC/CO ratios for air masses unaffected by wet removal but with different transport times.” The addition of a quantitative examination of below cloud scavenging is good.
Second general comment (BC core versus shell; SP2 operating parameters):
The inclusion of SP2 operating conditions during the study is a good addition, however I do not think the response really addresses my point about the physical meaning and impacts of the BC core size versus the diameter of the mixed particle (core + shell). The BC core diameter is not the relevant diameter for CCN activation or other in-cloud scavenging processes, unless all particles are uncoated. I feel the manuscript should more clearly address this point, as well as the implications for some of the observations. For example, if most of the particles detectable by the SP2 are coated to the point where they roughly interact and/or activate in/as cloud droplets in a similar fashion then we would not expect a strong size dependence of removal. A more thorough and quantitative treatment of the interactions of BC particles mixed to varying degrees with other material with clouds would greatly strengthen the manuscript. While a full-blown microphysical modeling study would probably be beyond the scope of the investigation, some theoretical work treating particles as a simple core-shell morphology mixed with sulfate and organic aerosol and applying this to Kohler theory could be a great addition and strengthen the science presented.