The manuscript improved some, and as much as I would like to give the article a “go”, I still cannot do this.
The following issues cannot be left uncommented as they are wrong or inconsistent. In the end, the Editor will have to decide, to which extent the authors will have to review their manuscript once more. In any case, below are my remaining concerns, which were mentioned before and not regarded in the revised version.
Therefore I still have to say “major revisions”. Most issues can probably be revised with small additions, but with my choice of “major revisions” I want to stress that these changes are really needed and should not be swept aside.
In the following, line numbers refer to those of the following file: “acp-2020-783-author_response-version1.pdf”
1)
One of the shortcomings I still see is the way how the data were split into three different periods, referred to as “marine aerosol” (MA), “biomass burning” (BB) and “African dust” (AD). This needs to be explained and motivated somewhat better in the text. I mentioned that before, but as it was not done, I elaborate here, why that should be done, and how the current text is not sufficient:
For each period, it is assumed that INP for each day/sample are representative for the whole period, as no further discrimination is done. In the answers to my previous review, you repeatedly refer to Figs. 5 and S3. These figures show elemental composition for 3 different days for each period (one always referred to as “background”) and 3 single back-trajectories, one for each period, respectively.
However, days for which you show the chemical composition are often not those days for which INP samples were included. For example, of the 7 INP samples you use for MA, the chemical composition is given for two days which were also used for INP analysis, but not for the third. And of the two that are shown one is the background day. For BB and AD, of the three days for which chemical compositions are shown, for each period only one appears among the INP samples.
Also, for these single trajectories that are only shown for each phase (MA, BB and AD), the one single trajectory for BB and that single one for AD are given for days for which no sample is included in the INP analysis. And the trajectory you show for MA is that for the background conditions.
And what does the background condition mean, anyway? This is nowhere clearly defined (with that I aim at what “background” means with respect to the aerosol during these phases, not that these are the days with the lowest mass concentrations.)
It is, therefore, still unclear to me how representative the INP samples you chose are for the conditions during each of the three different phases. This cannot be judged based on these few data you show in Figs. 5 and S3.
So overall, there is this inconsistency that you treat all days during one period similar when it comes to interpreting INP, but on the other hand you give “background conditions” that are clearly different from other days in the same season. And nowhere is there a complete overview over the conditions for all days for which INP samples were used.
Such an overview could quite simply be done if backward trajectories would be given for all days for which INP samples are included, and that is what I recommend you to do.
Along the same line, it makes no sense to say that this one 24 hour backward trajectory suffices for the BB phase (which is what you answer to my review, but also still say in line 1386 “The 24 h back trajectories were run for the BB events as they were likely locally emitted.”); because you later claim, concerning the BB phase, in lines 1589-1591 “The lower concentrations reported in the present study can be attributed to the long distance between the burning areas (likely southern Mexico and Central America) and the sampling site.” If that latter is correct (which it may very well be, you cannot exclude this), then the 24 h back-trajectories you showed are too short. If you do the backward-trajectories for all INP samples, use the longer time period for all!
Then, depending on how these trajectories are, the text may have to be adjusted. And if not much adjustment is needed, all the better. But then at least your data put into a much stronger context.
2)
line 1073: What really irritated me is, that you write that you understood my concern about the statement “Only one in 10^5 to 10^6 of the aerosol particles can act as INP at temperatures higher than -38°C (Lohmann et al., 2016).”, but that you did not want to change it. When something is wrong in literature, it should not be promoted further (even if others have done that before). Agreeing that this statement is wrong but insisting to use it anyway is rather strange to me, particularly as it does not influence anything in your work. Why not saying it correctly? DeMott et al. (2016) more correctly say "... INPs ..., a select subgroup that may represent 1 in 10^6 or fewer of all aerosol particles". Not perfect, but better.
3)
Along a similar line as my last comment goes the following, now in lines 1649-1650, “This is the first such comprehensive study ever conducted in Mexico and also at tropical latitudes.”
I commented that this is not true for tropical latitudes as Gong et al. (2020), a study you cited several times and thus should know about, also measured at tropical latitudes. Your answer was “Gong et al. (2020) was indeed performed at Tropical Latitudes; however, the authors focused on a single aerosol type (MA), instead of three different and distinct air masses as in the present study.”
So now we would need to define the word “comprehensive”, but in my understanding you are saying “Yes, our statement is not true, but we will make it anyway as this other study did not study the exact same thing as we did.”
Additionally, as you say, by now also Welti et al. (2020) is published and includes data for tropical latitudes. I would suggest you change the wording of the respective sentence at least to:
“This is the first such comprehensive study ever conducted in Mexico and among the first ones at tropical latitudes.”
4)
line 1255: Different from what you say, it has been discussed in the community already for quite some time that samples need to be stored frozen. It has even been shown that long storage times under freezing conditions may change a bacterial sample (Polen et al., 2016). It now was reported that storage at -20°C is mandatory (Beall et al., 2020). In your answer to my first review, you compare two groups of samples which were both stored at 4°C for many months (12 and 24), and their similarity might just mean that both degraded to the same degree, and that after many months of storage at this comparably high temperature of 4°C no further changes occur.
At least cite and shortly comment on the new study, as this very well could influence the outcome of your study. And consider changing your procedures in the future.
5)
line 1616: Again: Umo et al. (2015) looked at only ash particles, so any agreement has to be coincidental, as the n_s for Umo et al. (2015) relates to the surface area of ash particles, only, while your data relate to total atmospheric aerosol with many other particles and with some ash particles, and also with some soot particles in them!
This means in detail: When (at a fixed temperature) Umo et al. (2015) report a value of 1000 cm^-2, then this means that on the surface of the ash particles, there are 1000 INP per cm^2 that are active at that temperature. When your BB samples show the same n_s, it means that the BB aerosol has 1000 INP per cm^2 of the OVERALL aerosol. That is clearly something completely different.
Check and correct all of your respective comparisons respectively.
6)
Concerning the derivation of n_s, still more details are needed. If I did not overlook anything, it is nowhere to be found if you used one average surface area from the average size distribution for each of the three phases (MA, BB and AD), and if yes, from which days this average size distribution was constructed (all days for which INP measurements were included?). Or, if the measured size distribution for each separate day was used. At least this information needs to be clearly added.
Related is the sentence in line 1498, where you added “(reported by the LasAir)”. First, this inserted new information would be better given in the first sentence of the paragraph. (The sentence you inserted it to is more difficult to understand now). And second, the information you give in the review on how you derived the values shown in Fig. 6 should also be given in the manuscript, so that it becomes clear which value you show in that figure.
Minor comments:
Concerning your method, you answered that direct method comparisons have already been made, citing two papers. Knowing this helps the reader to judge the credibility of your work, and I strongly recommend that you add a short paragraph in which you cite these comparison studies and shortly summarized the respective results for your method.
line 1249: You do not want to describe your method in more details, so as suggested above cite these comparison studies, at least. But still, as readers might want to copy what you do, add at least information on how much does adding this extra plate change in distance in the impactor and as such influence the selected diameters? That may be small but should at least be mentioned, so that others who want to do similar things are aware of the fact that they should use slides as thin as possible.
line 1487 ff: Can it be excluded that these elements come from Saharan dust (during times when this source is weaker or more particles were lost on the way across the Atlantic)? Only then the karstic soil of the region should be taken into consideration. Particularly as you measured close to the ocean, a strong local influence may not be expected.
line 1555 ff: You do not want to change these comparisons, which I criticized as being a bit off, and so be it. But at least also mention that the temperatures in air and water are different for the studies done further to the North than for yours, as this may be an important parameter.
line 1577 ff: As you said above, particles can be lost, and this will likely be the main cause for lower values. This should be repeated here, too, as aging may also contribute, but would show up in a different n_s, rather than in lower concentrations. Concentrations simply HAVE TO BE lower further away from the source.
In your answer (line 810) you say: ”We are not comparing the ice nucleating abilities of the three air masses based on the onset freezing values, we did it based on the n_s values.”
But actually, the amount of comparison you do for n_s values in Section 3.5 is very limited. There are conclusions given on that in the conclusions section which are not given in Section 3.5, which might merit to be included and discussed there.
Technical issues:
line 1345: Delte the “s” in “INP_s(T)” in equation 3.
line 1458: Add “"in the BB season" after “background conditions”, as this is not the case during MA.
line 1461: Use GoM (instead of Gulf of Mexico), as you’ve done throughout the text.
line 1470ff: “… corroborating that the sampled air masses during this season contained a comparatively high mass fraction of particles emitted from BB.” At the end of this sentence, it should be added “when PM2.5 was high”, as you show yourself that potassium was not always high during this phase (Fig. 5 and Fig. S2a).
Literature:
Beall, C. M., D. Lucero, T. C. Hill, P. J. DeMott, M. D. Stokes, and K. A. Prather (2020), Best practices for precipitation sample storage for offline studies of ice nucleation in marine and coastal environments, Atmos. Meas. Tech., 13, 6473-6486, doi:10.5194/amt-13-6473-2020.
DeMott, P. J., T. C. J. Hill, C. S. McCluskey, K. A. Prather, D. B. Collins, R. C. Sullivan, M. J. Ruppel, R. H. Mason, V. E. Irish, T. Lee, C. Y. Hwang, T. S. Rhee, J. R. Snider, G. R. McMeeking, S. Dhaniyala, E. R. Lewis, J. J. B. Wentzell, J. Abbatt, C. Lee, C. M. Sultana, A. P. Ault, J. L. Axson, M. Diaz Martinez, I. Venero, G. Santos-Figueroa, M. D. Stokes, G. B. Deane, O. L. Mayol-Bracero, V. H. Grassian, T. H. Bertram, A. K. Bertram, B. F. Moffett, and G. D. Franc (2016), Sea spray aerosol as a unique source of ice nucleating particles, Proc. Natl. Acad. Sci. USA, 113(21), 5797-5803, doi:10.1073/pnas.1514034112.
Gong, X., H. Wex, M. van Pinxteren, N. Triesch, K. W. Fomba, J. Lubitz, C. Stolle, B. Robinson, T. Müller, H. Herrmann, and F. Stratmann (2020), Characterization of aerosol particles at Cape Verde close to sea and cloud level heights - Part 2: ice nucleating particles in air, cloud and seawater, Atmos. Chem. Phys., 20, 1451-1468, doi:10.5194/acp-20-1451-2020.
Polen, M., E. Lawlis, and R. C. Sullivan (2016), The unstable ice nucleation properties of Snomax (R) bacterial particles, J. Geophys. Res.-Atmos., 121(19), 11666-11678, doi:10.1002/2016jd025251.
Umo, N. S., B. J. Murray, T. M. Baeza-Romero, J. M. Jones, A. R. Lea-Langton, T. L. Malkin, D. O'Sullivan, L. Neve, J. M. C. Plane, and A. Williams (2015), Ice nucleation by combustion ash particles at conditions relevant to mixed-phase clouds, Atmos. Chem. Phys., 15, 5195–5210, doi:10.5194/acp-15-5195-2015.
Welti, A., Bigg, E. K., DeMott, P. J., Gong, X., Hartmann, M., Harvey, M., Henning, S., Herenz, P., Hill, T. C. J., Hornblow, B., Leck, C., Löffler, M., McCluskey, C. S., Rauker, A. M., Schmale, J., Tatzelt, C., van Pinxteren, M., and Stratmann, F.: Ship-based measurements of ice nuclei concentrations over the Arctic, Atlantic, Pacific and Southern Ocean, Atmos. Chem. Phys., https://doi.org/10.5194/acp-2020-466, in press, 2020. |
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