Review of "Closure of In-Situ Measured Aerosol Backscattering and Extinction

Coefficients with Lidar Accounting for Relative Humidity" by Dusing et al.

This study compares lidar measured optical properties to those computed with

Mie calculations that used airborne in-situ based inputs over two different

field campaigns. In general, the manuscript is unfocused and lengthy. The

tedious amount of detail makes is difficult to completely comprehend and

judge the merits of their analysis. I strongly suggest that the authors only

include the details of the measurements that aren't described in other

publications or are essential to the analysis performed in this work. The

authors state that their study is both "unique" and "complex", which it is,

but why is it important? What science is advanced by this work? There are

only a few lines of background/motivation given that mentions radiative forcing

and cites the IPCC, but it is not clear how this work reduces uncertainty in

radiative forcing. Do the Mie-based calculations reproduce the optical

properties well enough to meaningfully reduce radiative forcing uncertainty?

The authors need give more a clear science motivation in the introduction and

then revisit their goals in the conclusions to discuss what has been learned

from this work.

As a means to reduce the scope/length of the manuscript, I would suggest that

the authors consider removing the lidar parameterization analysis. For this

analysis, it is hard to tell if the comparisons are a bit circular at times

with in-situ inputs into a Mie model being used to derive the lidar ratio

parameterization. That parameterization is then used derive the lidar

extinction. Then the lidar extinction is compare to the in-situ measured

extinction. It would make for the more straightforward comparison if the

authors just made comparisons to the lidar backscatter coefficients and

avoided the assumptions/parameterizations needed to get the extinction

altogether. This would also help shorten the manuscript. Plus, the lidar

ratio parameterization is more a necessity because of the limitation of the

Raman system to nighttime only and is less relevant to a general

audience than the closure exercise.

The overall conclusions and taken home messages of the study are completely

lost in the in the details of the comparison. The goal of the study is the

demonstrate the closure of aerosol optical property measurements, but fairly

large differences remain. The authors speculate on several different reasons

as to why the modeled and lidar-measured optical properties differ, but no

real definitive answer is provided. The study would benefit from further

analyses that are more focused on achieving closure to within a meaningful

degree of certainty and a clear motivation/definition of what is

"meaningful". Before even attempting the closure exercise, it would be useful to

discuss how good a closure one can expect given the uncertainties both the

lidar and in-situ measurements. The uncertainties appear quite large at times

which would suggest improved measurements techniques and methodologies are

need before a useful closure exercise could be performed. 

Other comments:

The abstract needs to be considerable shorter. As is, it is a detailed

summary of the entire paper and largely repetitive of the material in section

5. 

line 247: what "other studies"?

line 357: add space after "campaign"

line 523: biasing -> attenuate

line 863: remove "In Mie-theory"

Labels the panels in each figure (e.g. a,b,c) and use those labels when

referring to specific panels in the text.

Figure 6, last panel: suggest addition a scale break in the x axis. As is,

the x limits are too wide to discern any differences. 

Figures 13, 14: the large amount of overlap in data points and errors bars

make it difficult to see anything quantitative from these plots. These may be

better plotted using some type of density-based plot.

This study compares lidar optical properties to those computed with Mie calculations in function of RH. The topic is important but the work suffers of important lacks in the method section probably biasing the obtained results and related considerations. Thus a deep major revision is required based on the following major issues:

1. Lines 290-292: “Also, the residual layer containing some aerosol layer aloft the top of the planetary boundary layer (PBL) between 1250 m and 2300 m is visible indicated by greenish colors.” Given the description above and Figure 1 it is clear that ACTOS also sampled in the residual layer between ~1300 and ~2000m. I suggest to correct the sentence at line 292-293 (“The payload, therefore, was sampling in the free troposphere as well as within the planetary boundary layer and was sampling different aerosol populations”)  and ALL the related discussion and interpretation later in the results.
2. Lines 296-297: how much below 40% RH the aerosol was sampled? Consider that aerosol efflorescence (or crystallization) can occur at RH lower than 40%, even below 30% RH in function of the aerosol chemical composition (nitrate to sulfate ratio, degree of acidity, presence of ammonium chloride etc…) (Martin, S. T.: Phase Transitions of Aqueous Atmospheric Particles., Chemical reviews, 100(9), 3403–3454, 2000). Please add a deep discussion based on this point as the manuscript aims at closure in function of RH, but the aforementioned consideration poses an important issues to the capability to reach this goal.  
3. Lines 306-307, Figure 2 and Lines 316-321: The missing refractive index correction of the OPSS represents a lack of the manuscript in the way as it is actually presented. This section needs an improvement. For example, the inner “detailed geometry of the optical cell inside the instrument” should be asked to the manufacturer (or at least asking the equivalence with that reported in: Heim, M., Mullins, B. J., Umhauer, H., and Kasper, G.: Performance evaluation of three optical particle counters with an efficient “multimodal” calibration method, J. Aerosol Sci., 39, 1019–1031, doi:10.1016/j.jaerosci.2008.07.006, 2008).
4. Mie calculation should be biased using the OPSS optical equivalent diameters, thus affecting a part of section 3, discussion and all conclusions. The later (line 326) altitude-correction factor in eq. 6 does not correct the OPSS optical equivalent aerosol size-bin (i.e. the size of particles) which is, instead, the right parameter needed for proper Mie calculations . It is required to clarify this point for the reader. Moreover, the above approach generate an inconsistency with lines 359-363 (“The OPSS PNSD was corrected in terms of the complex aerosol refractive index. Here, a complex aerosol refractive index of 1.54 + i0 was used since this resulted in OPSS PNSD with a good overlap to the MPSS PNSD. The imaginary part of the complex aerosol refractive index was forced to 0 because it leads to a significant overestimation of the coarse mode in the PNSD when the imaginary part of the complex aerosol refractive index is above 0 (see Alas et al., 2019). Note, that this complex aerosol refractive index is not the refractive index used in the Mie model”) and an inconsistency with lines 368-369 (Particles larger than 800 nm have not been replaced by the PNSD measurements at ground since the refractive index correction was applied to the OPSS data”) where different methods were used. I  suggest to improve the discussion of the Mie methodology (and related approximations) from line  till line 498 to make it clearer and more consistent.
5. Lines 350-351: “truncation error of the scattering coefficient was not corrected”. Please, add also the uncertainty of scattering and not only that of extinction.
6. Lines 360-363: OPSS model 3330 of TSI only accept real part of refractive index. The use of 1.54 + i0 is mandatory, not a decision. Moreover, this can generate problems if “this complex aerosol refractive index is not the refractive index used in the Mie model” as reported. Please comment and clarify.