Review of the paper „ A long-term study of cloud residuals from low-level Arctic clouds “ by L. Karlsson et al.
General comments:
With respect to the first version, the actual manuscript has substantially improved. Especially the reduced importance of small residuals with regard to all residual sizes is very good for the work.
However, there remain some critical comments, which are a summary of the main issues of the “specific remarks” below. These specific remarks are more or less only related to content, since language/wording and formal points are very good implemented.
1. Of course, the statistical treatment of the data is unique and very helpful for in-cloud CVI measurements. Nevertheless, two short case studies, one for warm one for cold clouds, where the real physical closure of cloud particle, aerosol particle and residual number concentration are presented would very much increase the confidence in the empirical approach and methodology. Moreover, at least some of the many, many open questions about small residuals in mixed-phase (cluster 1) and warm clouds (cluster 2) could be answered this way or at least some speculations could be ruled out.
2. I am still not a fan of the conclusion that say that the measured data could be an artefact or a real physical cloud process or a mixture of both like it still is in the discussion of the small residual particles. In my understanding of research one should avoid or at least quantify artefacts to be sure that they do not exist or at least do not significantly impact my measurements so that the data can then be scientifically interpreted. If this is not the case such data should not be submitted for publication. In this special case it is even more surprising and disappointing, since it is well-known that measurements with “standard”, i. e. non-phase segregating, CVI inlets are subject to large artefacts and that therefore several highly sophisticated phase segregating inlets have been developed exactly due to that reason. It is my hope that the authors further reduce their claim that the observed small residuals are related to secondary ice processes in the cloud, because their inlet system is unusable make such a statement.
3. I do not know of course what kind of measurement results the authors expected during the long operation period of the GCVI, but it is a pity that the whole set of instruments was not better selected. Beside a phase segregating CVI system, this mainly means a dedicated sensor for droplets (concentration, size distribution, LWC) and ice particles (concentration, size distribution, IWC). Especially, sensors that are able to measure LWC and IWC would have been much better to clarify the immense amount of speculations and would have been much better as a cloud detector compared to the visibility measurement.
In the conclusion, the authors promise to repeat this kind of measurements with an improved set of instruments. This is often done in conclusion chapters without any future action but I hope this time the authors take it serious due to our scientific curiosity about clouds.
4. Beside listing all the advantages of the possibility long-term ground-based residual measurements in contrast to short-term measurements with aircrafts, it would be fair to mention the disadvantage in contrast to airborne measurements as well. This means the restriction to clouds with soil contact and orographic effects (which is a general problem and not one at Mt. Zeppelin only) whereas “unbiased” clouds can be reached only by aircrafts. This should be a second point about the representativeness of the measurements together with the one in the site description concerning the representative location of Mt. Zeppelin/Ny Alesund for the Arctic.
5. It is known that the sampling efficiency of CVI systems, and particularly ground-based CVIs, changes with wind and cloud microphysical properties, i.e. it could even change within one cloud event. Therefore, it is nor clear why the authors used only one value to correct for all cloud events included in this study. In principal, each measured residual particle size distribution should be scaled/corrected with the actual CVI sampling efficiency. This is not meant as a harassment, but could indeed lead to different shapes of the averaged residual particle size distributions for the temperature or month intervals (Fig.6b, Fig.7b, and Fig.S8). Consequently, that may also change the complete cluster analysis and the respective discussion. Fig.3a and Fig.5a are not real counter arguments to that because the frequency distribution should be much broader when plotting the ratio value for each residual particle size distribution. Thus, the authors are called to address this issue.
6. Three times the authors refer to other studies to affirm similar results with their own study (L.569: Verheggen et al. (2007), L. 575-578: Seifert et al. (2003), Mertes et al. (2007)). On the other hand, these studies also show clear differences to the actual study which are not addressed at all (details about that are given in the specific remarks). This is surely not intentional, but needs to be included for a complete scientific discussion.
7. The size distribution of cluster 2 is in this revised manuscript attributed to droplet residuals. But its broad shape is very unusual for a CCN size distribution. This needs to be related to the shape of the total aerosol size distribution simultaneously present at the site. This should be examined during the text passage where cluster 2 is discussed. Moreover, the maximum possible supersaturation should be estimated in order to prove that those small particles can be indeed activated. In principal this should be related to a large updraft velocity, but this seems not to be the case according Fig.10 b.
I would have preferred to completely forego the presentation and discussion of the residual particle size distribution measured during mixed-phase conditions (mainly the cluster 1 discussion with 8 % of the time) and I still have some doubts about the actual existence and interpretation of cluster 2. However, this is certainly not enough to reject this manuscript presenting a unique long-term cloud particle residual data set at an important place on earth with respect to the role of clouds to arctic amplification. The authors seem to stick to these points, which is acceptable in the way it is implemented, although it does not strengthen the manuscript to my opinion. However, the issues raised in the general comments and the specific remarks in this review must be responded and where appropriate included in the manuscript for publication.
Specific remarks
L.59: beside secondary ice one should at least also mention impaction scavenging as an in-cloud process that could result in residuals that are not identical to the original CCN or INP.
L.60-64: Already here it would be fair to mention the disadvantage of ground-based or advantage of aircraft in-situ cloud measurements as already mentioned in my general comments.
Figure 2b,c; Fig.3a,b; Fig.4a; Fig5a,b: Maybe it is given overseen by me, but it is important to indicate the averaging time of the data points.
L.383-389: Here the argumentation of the authors is not correct. At this text passage clouds are discussed with a cloud particle concentration of 1 cm-3 and where the cloud particle concentration is below the cloud residual concentration. These must be more or less totally glaciated clouds, where most cloud particles (ice crystals) are rather large. This means, the very likely shattering of these ice particles in the GCVI wind tunnel would substantially increase the cloud residual but not the cloud particle concentration. This is supported by many airborne CVI measurements in ice clouds.
L.413-416: This analysis is very crude. The match of the total aerosol and cloud residual size distribution, which is more or less the exact and individual knowledge of the GCVI sampling efficiency for each cloud included in the respective data set, has to be taken into account and not only a correction factor of 2 for all clouds. This is important, because the value of the D50% is very sensitive to the correct quantitative relation of total particle to residual particle size distribution. For a first guess that can be done by normalizing the plateau between 100 and 300 nm to 1. Doing so, one would see a trend in Fig.6c, i.e. a decrease of D50% for higher updraft velocities. This would be the expected behaviour, because this means higher supersaturation with the capability to activate smaller particles. Thus, this approach leads to contrary conclusion with regard to the actual text and should be at least commented by the authors, since this is a crucial point for the description of the properties of warm arctic clouds.
L.415: All observed updraft velocities are influenced by the orography independent of the amount of the updraft. Without the orography the updraft velocity would be different for an arctic cloud. Regarding in addition the point before, one would find an orographic influence on the D50%, which is again in contrast to the conclusion in the manuscript and needs to be further considered by the authors.
L.418: Does it mean the enrichment factor is uncertain and only assumed? This should be clarified and made clear in the manuscript.
L.425-426: This is exactly what is brought up in the last two points and emphasizes that the GCVI sampling efficiency has to be determined for individual cloud events.
Fig.7: The first temperature bin from -8 to -21 °C is much too broad. In this temperature range the cloud phase could change from supercooled to totally ice including all stages of mixed-phase conditions. The reason for this broad range is most likely a statistical one. It is not known whether most included cloud events are closer to -8 or -21 °C and dominate the presentation and interpretation in and of Fig.7b and 7c. This should be presented in a more differentiated way.
L.446-452: Many of these speculations coming up by the pure statistical approach of the data, and could be checked by analysing such clouds individually, which unfortunately is totally refused in this work, although it would significantly improve the investigation.
L.552: The “some ice processes” has to be described in detail in the text and maybe “included” is a better mode of expression than “involved” here.
L. 537-542: This argumentation is straight forward and casts doubts on the conclusions drawn in section 3.2.1., like they are already expressed further up. The authors should seriously think about to change their data treatment in the mentioned section.
Fig.12: In the lower row the peaks and the decrease in the ratios to 0.5 or lower for larger diameters look very suspicious. What are the reasons for these shapes. It is still in a size region where low counting statistics does not play a role. An explanation in the manuscript is definitely needed.
L.560-562: When looking at Fig. S8 this statement seems to be not correct. Here are residual size distributions visible that are very similar to cluster 1 but measured at temperatures above – 4°C, where clouds are mostly still liquid. The authors should comment on this point.
L.562-565: The manner how the Cloudnet information is used here is a little bit misleading. Cloudnet only indicates the frequency of ice, mixed-phase and liquid clouds, but not the ratio of crystals to droplets in a mixed-phase cloud, which is mostly dominated by droplets in terms of number. Moreover, only clouds at temperatures higher than -21°C were studied. At this temperature clouds are very rarely pure ice clouds. Thus, this text passage is not very convincing.
L.569: The citation of Verheggen et al. (2007) is appropriate to document the WBF process but is inappropriate to explain cluster 1 at this place. Fig.3 in Verheggen et al. (2007) shows the same ratio as a function of particle diameter and those graphs steadily increase with diameter and show no maximum at 20 nm in contrast to Fig.12a. Thus, this reference must not be used in a wrong sense to justify the existence of cluster 1 size distributions in cold clouds found in another publication.
L.572-573: The authors need to specify the “cold temperatures” exactly. According to the presented data, the temperatures are in a range that it is very unlikely to have pure ice clouds. Moreover, the cloud particle concentrations are in the several cm-3 range according to Fig.S8, which is very high for a pure ice cloud. Again, an appropriate sensor to support this speculation is missing, so that this sentence and statement should be reworded or left out.
L. 575-578: Again, only half of the truth is told here. Namely, the similar shape of the residual particle size distribution to presented ones in two other publications. But it is not taken into account that the Seifert et al. (2003) study is definitely carried out in pure ice clouds and that Mertes et al. (2007) used indeed a phase separating CVI inlet, which in addition was especially designed to avoid droplet and ice particles shattering, which is not the case in this study. What is additionally concealed is the fact, that the simultaneously measured background aerosol looks completely different to the one in this study. Consequently the “ratio” looks totally different compared to the ones in this study which make up cluster 1 (Fig.7c). The interpretation of the residual size distribution should always include the ambient background particle size distribution, which proofs in Mertes et al. (2007) and e.g. also in Kupizewski et al. (2016) [JGR] that small particles does not play a role in mixed-phase cloud formation. These facts need to be included here, in order to prevent that the reader gets a wrong impression by the stated “similarity” of the present study to the former ones.
L. 595-597: I do not understand the first sentence and therefore in addition not the message about decreased influence from snow. With the second sentence the authors left the reader alone with the decision to refer the observation to a measurement artefact or to a real cloud process, which is a not goal oriented approach to my mind. So here it would be desirable to make the statements more clearer and more determined.
L.615: What is meant by the nuclei here? An INP and/or CCN or something else? It is hard to believe that an INP will be fragmented by an ice particle shattering during ice-ice collisions. Are there any indications that INPs undergo fragmentation?
It is much more likely that small residuals stem from CCN matter build in the ice lattice. Since ice particles in mixed-phase clouds are mainly formed by droplet freezing (immersion and contact freezing), the CCN matter should be still in the ice particles and condense to small particles during the ice sublimation in the CVI in the absence of the INP. However, I would not call it “fragments of CCN”, since it is not a mechanical fragmentation.
L.618-619: So, the absence of small cloud particles is a clear indication for an artefact sampling. But here it is presented as a marginal contribution with respect to the observation of secondary ice. This is a wrong formulation, since the existence of secondary ice is not proven and thus also not the connection to the observation of small residual particles. Therefore, the original statement here needs to be rebutted by rewording this sentence.
L. 628-629: It is not clear, why small cloud particles must be ice fragments from secondary ice processes only. The authors themselves refer to the Wegeron-Bergeron-Findeisen process, where droplets lose water for the growth of ice particles and therefore getting smaller. So small particles in mixed-phase clouds could also be evaporating droplets. The authors should also take this possibility into account.
QL. 641-643: To support the interpretation of the cluster 2 size distribution, it would be good to estimate the maximal supersaturation in the cases this cluster was observed. This should be possible with the available measurements of temperature, cloud base height and vertical wind speed and would reveal if particles with a diameter of 30 nm (mode diameter of cluster 2) can be activated and how soluble they have to be. This is done in the cited reference Schwarzenboeck et al. (2000) as well as in the accompanying model study by Gérémy et al. (2000) [Tellus, 52B, 959-979] to evaluate the observation of small residuals in warm clouds and would be a profit here as well.
L. 672: I may have overlooked, that the term “cloud nuclei” was defined, but I would prefer still name it CCN and INP.
L. 676: To activate 20 nm particles is even more difficult as 30 nm particles. With this statement, a calculation of the max. super-saturation is indeed needed to see if this possible at all and if yes, for which type of aerosol particles. |
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