This paper uses a recent observational dataset to examine the relationships between lidar measurements (backscatter and extinction) and inlet-based in situ CCN concentrations, with the ultimate goal of evaluating model performance and HSRL-based CCN retrievals.  While the paper is well-written, I worry the conclusions are somewhat simplistic and not fully supported by the data or uncertainty analysis as presented. I would like revision to clarify the below questions before the paper is published.

Major comments:

1) While there’s nothing inherently wrong about a straightforward approach, the basic methodology as I understand it (essentially, using a linear fit to estimate CCN concentration from HSRL data) merits a more detailed description. For example, which “best fit” lines are shown in the figures? I didn't see it described.  Many standard statistics packages use ordinary least-squares, which presumes that the x-variable is a perfect measurement and all the error/uncertainty is in the y-variable, but for a regression between two observed variables, I don’t think that’s accurate. Surely HSRL-2 comes with uncertainty as well? How was this accounted for? It also seems like OLS may have been used since Figs 3 and 4 and 9 show RMSE, in units of CCN concentration, i.e. the y-variable. (Follow-up question: what’s the utility of this metric here? Is it to say that the CCN uncertainty associated with the linear regression is ~>100/cm3 in each case? Surely there’s more to it than just that? How does an estimate of uncertainty in the linear regression influence the later results, e.g. Fig 9, 8?)

1a) Specifically to the above: Line 360-361 mentions “higher uncertainties and coarser resolutions associated with the [HSRL-2] extinction coefficient”-- where is this incorporated or considered?

2) The authors also combine all three years (with different measurement times of each) into one plot, which could be fine, but in Figs 3, 4, and 6, it seems the goodness of the fit is likely strongly influenced by those cluster of high CCN, high X (X= the given HSRL-2 variable) which occur specifically in 2017. Plus the choice to force through 0-0. There are only 13 points in 2017, all >~900cm-3, which is almost an entirely different range than 2016, for example. Again, this probably could be fine, *if* the CCN/HSRL relationship(s) hold over the range of conditions as the months change. The authors consider different metrics f44, AI (if not AE) (mostly in Section 4.2), and changes in SS level, RH %, and measurement constraints for different years (Table 2), but with so few points from so few days, it’s hard to determine how consistent this relationship actually is in a multivariate sense, just from what has been presented.

2a) Further comments on Fig 6: am I reading it right that the thicker grey line is for 2018? The three diamond points I can see, do not appear to fit well to that line, since the two higher points are both below that fit and other two are right on it. Is that correct? How can that be the best fit to those four points? And are there really only two data points from 2017? Is that enough to draw conclusions from?

2b) Finally, I worry that the methodology of fitting through 0, while physically intuitive, is constraining the results in a way that’s not supported by the (somewhat limited) data which are shown. To take an extreme example, if one fits a line through (0,0) and 2 other data points which have some error associated, the fit will likely be hugely different compared to a fit through just those two data points themselves. The artificial (0,0) “data” would completely overwhelm the relationship between the actual observed datapoints, which is what the authors are trying to show. And obviously this would have a more dramatic effect for studies with fewer datapoints.  How much does this fit depend on the (0,0) constraint? It seems it may have a big effect here.

3)  I’m not clear on the purpose of Sec 4.3/Fig 8-9. First, is (or can) WRF-CAM5 be taken as a ground truth, or can HSRL-2? (I suspect neither, with the information presented). The two plots in Fig 8 are so different I’m having trouble understanding what’s the message here. The authors (Line 464) suggest that the lidar-derived method is “better” than the models. Based on what?

3a) Figure 9 has many points which suggest variability in in situ CCN which is not captured by the HSRL-2-derived product, as well as some which suggest artificial variability in HSRL-2 compared with in situ. Some cases seem to show a mismatch of an order of magnitude. What’s going on in these cases? Is this solely a function of the “expanded” dataset, i.e. those strong diversions are a result of greater mismatches in space/time? Does it have anything to do with the age/humidity/supersaturation? How does this fit into Fig 5, which at least for 2017 seems to show both young and old aerosol?  Does this matter?  As presented here it’s difficult to believe in the results of Fig 9.  

3b) If the two above points are addressed, I’d suggest flipping Figs 8 and 9; 9 should establish the validity of the HSRL-derived CCN product and then 8 could show it in the context of one model result. Perhaps that’s more what the authors are intending.

4) Figure 5, Lines 396-8: this is not correct. The main source of the BBA in this region is the south african easterly jet (AEJ-S) which is most frequently present between 5-15S, not at the equator. See: Adebiyi et al 2016 DOI:10.1002/qj.2765; Ryoo et al 2021 https://doi.org/10.5194/acp-21-16689-2021

Minor comments:

For the “amount of data within +/- X% of the linear regression line,” X=10% in the figure captions (Figs 3, 4) and 20% in the text (lines 300, 327, 330).

The authors consider both extinction and AI and draw conclusions that the latter isn’t more representative because AE has minimal variation (paragraph on Line 365), but presumably the AE used to calculate AI was also determined from HSRL-2 measurements. Did you examine the AE variability directly to support this conclusion? It seems fairly straightforward to check  (I’m considering this a “minor comment” because this is more of a curiosity rather than a major issue with the paper).

 

Line 136: a plausible and robust collocation and filtering is central and critical to the subsequent results; in other words, I’d remove the word “briefly” here.

Line 147,224: Fig 1 caption says the third deployment was only Oct 2018?

Line 170: “the exact temporal” … resolution?

Line 191: is this — here necessary? It seems a bit awkward. Maybe needs a comma?

Line 196: how do +/- 10% and 5-10 cm-3 compare to one another in absolute terms?

Line 200-1: revise, I don’t follow. Maybe missing the word “fraction”?

Figure 2b: this uses both \deltat and dt in different places (also line 231, 235)– should this be the same notation?

Figure 3a: the legend covers the 532nm datapoints; resize or shift

Review of “Use of Lidar Aerosol Extinction and Backscatter Coefficients to Estimate Cloud Condensation Nuclei (CCN) Concentrations in the Southeast Atlantic” by Lenhardt et al., submitted to Atmospheric Measurement Techniques, 2022.

Overview:

This paper presents empirical relationships between remote sensing and in situ measurements of aerosol properties that were made during the NASA ORACLES project. The goal is to inform vertically-resolved CCN concentration retrieval algorithms that are heavily based on HRSL-2 data in the southeastern Atlantic airmasses dominated by smoke. The results presented in the form of correlation coefficients indicate that there is a strong relationship between HSRL-2 observations and the in situ CCN measurements from aircraft mounted sensors.

Review:

The paper is well organized and written. The figures complement the conclusions and are laid out appropriately. I do not find the conclusions to be overwrought because the authors state that the correlations described are limited to the SEA region and BBA type that was observed during ORACLES. However, there is a general reliance on the HSRL-2 observations without adequate caution. The authors are experienced with this system, so I recommend they include a more complete description of the limitations of the instrument on the airborne platform and the how the error propagates into the relationships derived herein, especially with regards to volume averaging extinction and backscatter coefficients. After the inclusion of such a discussion, I would find the paper suitable for publication.

Minor comments:

In the second line of the Figure 9 caption, “.0.5” should be replaced with “0.5”