The authors have done a strong job of revising their manuscript; I commend them on their work and apologize for my extreme tardiness in getting this assessment completed. I suggest that this should be publishable once the authors address remaining comments not addressed, or raised through the revisions.
As a general thought, I would encourage the authors to consider the sensitivity of their results to the one very clear “outlier” high absorption point in their unexplained absorption vs. ELVOC concentration plots. This point is undoubtedly having an outsized effect on the fits, especially the R2 value. This is not critical, but perhaps of interest. Additional comments follow.
The authors added mention of factors that can affect the MAC of pure BC to the intro; I suggest the authors support these contentions with references that specifically demonstrate from observations (not calculations) that the MAC is size dependent. This is certainly true if spherical particle Mie theory is used, but it is less clear this is the case for fractal particles; for example, RDG theory yields a size-independent MAC. Also, just a note that neither RDG nor Mie rely on knowledge of particle morphology; the former requires only the size of the primary spherule, but not the morphology (page 2)
L223: The authors report a positive correlation for an R=0.31, corresponding to an R2 = 0.096. This is hardly a positive correlation. I suggest that the authors perform a significance test to determine whether their correlation coefficient is significantly different from zero at some level. I am not convinced that the authors can really conclude that “the measurements suggested a positive correlation”, or that the R value reported is not strongly influenced by the two outliers at low NRPM/rBC values. The same goes for the small R2 values reported on L275/276.
It would be very useful for future reference if the authors were to report the SSA value they measured for the fullerene soot. Also, the authors cite Lack et al. (2012) for the PAX uncertainty (page 5). However, Lack et al. did not use a PAX, they used a CRD-PAS and calibrated in a totally different manner than by which the PAX is calibrated. It is not clear that the uncertainties are translatable; I think the authors need to argue that the uncertainties translate between these different instruments that were calibrated in different ways and have very different sensitivities.
L239: I suggest the authors provide more details regarding how they determined the values reported in Fig. S11 from the LEO method. LEO gives a result for every particle. They report an average value. But is the distribution normally distributed? And, for what size particle were these coatings determined? There are some important aspects to the LEO method with respect to how it is applied across the size distribution owing to differences in the smallest size particle measured by incandescence versus scattering in the SP2. Are these coating thicknesses from a particular size range?
Additionally, I have some concerns with the real discussion of the LEO method being left to the “uncertainty” analysis. We know for a fact that the NRPM/BC overestimates the coating thickness. Considering the LEO method is not just looking at “uncertainty;” it is arguably a fundamentally better estimate (despite the limitations of the method). This does not seem so much like an “uncertainty analysis” to me, as it is an alternative consideration. I strongly suggest integrating the LEO results with the NRPM/BC results throughout. It should be reasonably straightforward to show both the NRPM/BC and LEO-derived results together in the main text figures and to discuss them together. As a general point, I suggest that a better title than “Uncertainty analysis” would be “sensitivity analysis.” The vast majority of the aspects considered in this section are assessing sensitivities of the results to methodological assumptions, which is not the same as an uncertainty assessment. It is more of a robustness assessment. Regardless, this is a welcome addition to the paper.
I appreciate the authors’ addition of the R2 values as a function of wavelength for absorption vs. BC. I suggest changing “rather inconclusive” simply to “inconclusive.” I’ll note also that they report only in the supplemental but not the main text the value at the longest wavelength, for which the R2 is quite a bit lower than at higher wavelengths.
P14: I suggest that the authors in their first sentence change it to “between the measured and the reference value” rather than “theoretical value,” in line with my previous concern that it appeared the authors were comparing their observations with a calculated (“theoretical”) value. The Bond et al. value is not theoretical—it is explicitly derived from experiments.
P15: The average predicted MAC405 is likely not lower than the measured value once uncertainties are accounted for. This should be noted. The authors should provide statistical evidence that the predicted value is lower, based on e.g. a t test or some other appropriate test.
P14: I also suggest that the authors modify their discussion in relation to the Gyawali et al. (2009) study to indicate that those were theoretical values obtained via spherical particle Mie theory, which might not yield (and probably does not yield) the correct size dependence—which is what gives rise to the large variation in the AAE with size in that paper and others that have followed. For the Lui et al. study cited, the authors here should not just note that the AAE decreases with size (for more complex calculations) but that it decreases to only ~0.8 at the lower end for their realistic calculations. The authors should be more specific than saying “relatively low values of AAE should be expected.” How low is low? If 0.8 for collapsed BC is expected, than an observed value of 1 still indicates a relatively small contribution of brown carbon.
P15: I find the statement that “The association of BrC with material of lower volatility away from its sources has been reported in a number of studies focusing on biomass burning (Saleh et al., 2014; Wong et al., 2019),” unclear. The Saleh study is a laboratory study on biomass burning particles; it is by definition right by the source. But, they did consider the influence of simulated photochemical aging. The Wong et al. study is also a laboratory study, but one that did consider photo-aging of BrC. If the authors here mean that the Saleh and Wong et al. photochemically aged their laboratory samples and this means “away from it’s sources” I suggest they be more specific.
P17: There is a typo: the RI should be + 0.79i, not 0.679i.
Data Availability:
In line with current best practice and expectations for articles published in ACP, I suggest that the authors archive their data from the publicly funded study in an accessible archive prior to the publication of this work.
Presentation of Literature Results:
Upon reading again, I have a few concerns over how the previous literature is presented. Specific comments follow here:
L38: The authors should clarify that the measured Eabs accounts for the combined effects of lensing and BrC. This would help set up the discussion that follows better, especially when they report measurements of Eabs from different studies without clearly delineating the relative contributions of lensing and BrC.
L49: I suggest it would be fairer to say that studies have found a wide range of effects.
L50: The authors misstate the results of Liu. Here, the authors report the results from the TD, but Liu et al emphasize that the MAC-based method is superior. Their 405 nm value is much larger than the 781 nm value, when viewed this way. And this is largely a result of BrC absorption, with lensing making some contribution. I suggest this be revised to reflect the results of Liu et al. more accurately.
General comment on presentation of literature results: In general, I suggest the authors report the uncertainties associated with each of the specific Eabs values they mention. There can be a wide variability/range of values for a given mean value. Or, they should clarify that these are means. I also suggest that they introduce greater consistency in terms of attributing different effects to lensing versus brown carbon. For example, for the Zhang et al. 2018a study, they mention two wavelengths with no mention of attribution. But for the Lack et al. (2012) study, they mention contributions of BrC.
For the Liu et al. (2017) study, the authors might clarify that above Rbc = 3 the enhancement is not only “significant,” but that they observed a continual variation in Eabs with increasing Rbc.
For the Cappa et al. (2012) study, I believe they also report values using the MAC method, and find results similar to the TD method.
L74: Hearly should be Healy.
Rbc: The authors should clarify that different methods are used to determine Rbc. For Liu et al. (2017), for example, it is based on single particle SP2 measurements. But for most other studies mentioned, the Rbc (if measured at all) is an ensemble average.
For McMeeking et al. (2014), the absorption enhancement was negligible up to Rbc = 10. Not just below Rbc = 1.
L59: cite should be site.
Minor Comments:
L137: The distributions were almost certainly not fit with a Gaussian. They were fit with a log-normal distribution. (If they were actually fit with a Gaussian, this needs to be justified.) |
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