Cloud phase estimation and macrophysical properties of low-level clouds using in-situ and radar measurements over the Southern Ocean during the SOCRATES campaign

Das, Anik; Xi, Baike; Zheng, Xiaojian; Dong, Xiquan

doi:https://doi.org/10.5194/amt-2024-124

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https://doi.org/10.5194/amt-2024-124

Preprints

05 Aug 2024

| 05 Aug 2024

Status: this preprint was under review for the journal AMT but the revision was not accepted.

Cloud phase estimation and macrophysical properties of low-level clouds using in-situ and radar measurements over the Southern Ocean during the SOCRATES campaign

Anik Das, Baike Xi, Xiaojian Zheng, and Xiquan Dong

Abstract. The Southern Ocean (SO) provides a unique natural laboratory for studying cloud formation and cloud-aerosol interactions with minimal anthropogenic influence. The Southern Ocean Clouds, Radiation, Aerosol Transport Experimental Study (SOCRATES), was an aircraft-based campaign conducted from January 15 to February 28, 2018, off the coast of Hobart, Tasmania. During SOCRATES, the NSF/NCAR GV research aircraft, equipped with in-situ probes and remote sensors, observed aerosol, cloud, and precipitation properties, and provided detailed vertical structure of clouds over the SO, particularly for the low-level clouds (below 3 km). The HIAPER Cloud Radar (HCR) and in-situ cloud and drizzle probes (CDP and 2DS) measurements were used to provide comprehensive statistical and phase-relevant macrophysical properties for the low-level clouds sampled by the 15 research flights during SOCRATES. A new method based on HCR reflectivity and spectrum width gradient was developed to estimate cloud boundaries (cloud-base and -top heights) and classify cloud types based on their top and base heights. Low-level clouds were found to be the most prevalent, with an almost 90 % occurrence frequency. A new phase determination method was also developed to identify the single-layered low-level clouds as liquid, ice, and mixed phases, with occurrence frequencies of 45.4 %, 32.5 %, and 22.2 %, respectively. Low-level clouds over the SO have significantly higher SLW concentrations, with liquid being most prevalent at higher temperatures, ice phase dominating at lower temperatures, and mixed-phase being least common due to its thermodynamic instability. Regarding their vertical distributions, the liquid phase occurs most frequently in the lower mid-cloud range (from 500 m to 1 km), the mixed phase dominates at cloud bases lower than 1 km but is well distributed along the vertical cloud layer, while the ice phase is prevalent from the middle to upper cloud levels (1–3 km). The higher occurrence of the mixed phase at the cloud base could be attributed to large drizzle-sized drops and/or ice particles.

Received: 18 Jul 2024 – Discussion started: 05 Aug 2024

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Anik Das, Baike Xi, Xiaojian Zheng, and Xiquan Dong

Status: closed

RC1:
'Comment on amt-2024-124', Anonymous Referee #1, 04 Sep 2024
General Comments
The authors use in-situ cloud probe data and remote sensing observations collected by instruments onboard the NSF NCAR GV aircraft during the SOCRATES campaign to study low level clouds over the Southern Ocean. While the topic is interesting and highly relevant, unfortunately, there are many issues with the methodology used by the authors:
The authors developed a radar-based methodology to derive cloud base. However, they themselves state that it does not agree with the standard method based on lidar observations. The lidar-based method has been proven to work well in many previous studies and since the authors do not independently validate their new method the reader concludes that the radar based method is not accurate.
The authors then develop a new cloud phase classification method based on in-situ and radar observations. The method heavily relies on spectrum width observations but fails to account for shortcomings in the spectrum width observations, which leads to inaccurate conclusions. It also relies on the liquid water path, which is derived along the aircraft track from in-situ measurements and then applied to the whole vertical column of the radar observations. In my opinion, it is not an accurate assumption to claim that LWP is constant throughout a cloud. The authors themselves state that the resulting 2D classification does not look accurate. Nonetheless, they collapse it back into a 1D classification and use both throughout the rest of the study.
The authors compare some of their results with methods from previous studies (even though for some reason they do not compare it with the phase classification that is provided in the radar/lidar dataset itself) and note that their results do not agree very well with previous studies.
I am not sure why the authors chose to develop their own method, when proven methods are readily available, and then decide to use their own method, even though they themselves have found that it does not produce good results.
Because of these issues with the methodology, the interpretation of the results, and the conclusions drawn, are also highly questionable.
Given all these shortcomings (which are listed in more detail in the Specific Comments below), I am afraid I have to recommend to reject the manuscript in its current form.
Specific Comments
Line 147: Please explain what is meant with “interpolated to fixed radar-heights at a range gate of 19.2 meters”. The range gates are already fixed. And why 19.2 m?

Section 2.2: I am very skeptical about the method that derives cloud base. How was that method validated? Using data from the GV-HSRL to determine cloud base is the state-of-the-art methodology. If the method proposed by the authors does not agree with the GV-HSRL measurements, that would generally indicate that it is not accurate. If the authors really want to claim that their method is superior, they need to find an independent validation method. Simply plotting the results on the radar observations is not sufficient.

I would also like to point out that spectrum width in regions with low signal to noise ratios, which are often observed at the cloud edges, are often noisy and not all that reliable. Using their gradient to derive cloud boundaries is therefore not recommended. You can see in Figure 1c that there is a similar gradient at the top of the cloud as at the bottom. The argument that this gradient implies drizzle or precipitation (as stated at line 177) is therefore highly questionable. The fact that the algorithm finds cloud base in the middle of a cloud layer where there is clearly no precipitation at all (Fig. 1 around 26.44) is also suspicious.

Table 2: What is meant with “may not be single layer”? Does this mean that they could be multi-layer or deep? I don’t think it makes much sense to put both of these cloud types together in one category. The same is true for the HML category. That seems to be a deep cloud but the name of the category seems to indicate that it is a multi-layer cloud.

Line 217: What is meant with “due to the selected cloud cases”? What cases were selected? How many? And based on which criteria?

Section 2.4: I’m afraid I do not understand how LWP is calculated. Do the authors assume that the LWC is vertically constant throughout the cloud? That does not seem like valid assumption.

Figure 3: How do these results compare to similar classifications in the literature? (Mace and Protat 2018, Truong et al. 2020, Romatschke 2023)

Table 3: The LWP values have very large SDs. Are they actually meaningful?

Section 4.1: The authors develop a new methodology to derive cloud phase from radar observations. However, they do not validate the method. This leads to the following questions: a) Why was a new method developed when a phase classification is already provided in the dataset? Why do the authors think their methodology is valid if it is not verified? Why do they believe that their method is better than previous methods (that have actually been validated)? Why was it not validated?

At line 375 the authors say that they compared with previous work. What exactly does that mean? What were the results of these comparisons? Also, the classification heavily relies on LWP and spectrum width. As mentioned earlier, I am not sure how trustworthy LWP is, as it is assumed to be vertically constant (see first paragraph of Section 4.2). Again, spectrum width is noisy in low SNR regions and some, if not many, of the high values may be unreliable. (Romatschke and Vivekanandan decided not to use spectrum width in their algorithm for this reason.)

In Section 4.2., the authors state that “phase retrieval method but may be not highly depictive of the actual cloud phase”. In that case, what is the value of the 2D derived cloud phase? What is the purpose of this effort? The 2D cloud phase is then again collapsed into a 1D cloud phase product which apparently “returns reasonably accurate findings compared to other phase detection studies over the SO”. These comparisons are later shown (see below) but they are not convincing.

What is the purpose of developing this new product if other phase classifications already exist? Why start with the 1D cloud probe observations, expand them to low-quality 2D observations, and then collapse them again into 1D phase estimations? Why not use the cloud probe measurements directly and the phase classifications that were derived from them in previous studies?

Starting line 442, the 1D phase classification is compared with phase classifications from other studies. Unfortunately, the classifications from the current paper do not agree well with the classifications from previous studies. The authors speculate about the causes of these discrepancies but fail to explain why the reader should trust their results over those from previous studies.

Starting line 474 the authors suggest tuning thresholds from previous studies to match their results but I am not convinced that this is the right thing to do. Again, why do the authors think that their results are more accurate?

Section 4.3: Given all the problems pointed out earlier (unproven cloud base, unreliable phase classification), I am not sure how trustworthy and valuable this analysis is.

Section 4.3.1: For this analysis, is the 2D cloud phase or the 1D cloud phase product used?

Section 4.3.2: Given that the authors stated earlier that the 2D cloud phase product is not particularly accurate, why is it used here?

Starting line 551: I disagree with the author’s interpretation of the CFADs. In my opinion, the CFADs for the liquid (and mixed) clouds show a strong bright band signature at 0.2 km normalized height. This bright band signature contradicts the author’s claims that the clouds are predominantly liquid. This confirms that the phase classification algorithm does not produce high-quality results. Looking at Figure 7, one gets the impression that the algorithm tends to classify deep clouds with strong reflectivity as mixed, deep clouds with weak reflectivity as liquid, and thin clouds as ice. This is reflected in the CFAD categories of Figure 10. I do not see a connection with cloud phase. It is not surprising that the authors use the word “surprisingly” a lot in the description of the CFADs since the CFADs do not actually show clouds of the respective phases.

Line 586: The higher width values indicate that a significant portion of the data comes from low SNR cloud edges where width tends to be noisy.

Paragraphs starting line 599 and 609: Same as previous comment. Please do not over-interpret the high width values in low SNR regions.

Conclusions: I am not convinced by the conclusions given all the issues pointed out in the previous comments.

Technical Corrections
I would like to point out that there are many(!) grammatical issues throughout the paper which are too numerous to list. Sentences are often very long and not only the reader, but apparently also the authors get lost. Two of many examples are the sentence starting line 33 and the sentence starting line 80.

Line 25: Please define “SLW”.

Line 109 and throughout the manuscript: The instrument is called the “GV-HSRL”.

Line 128: The SOCRATES acronym has already been defined earlier.

Line 132: Type RV -> GV.

Figure 1: Please correct the values on the time axis. (As far as I know, a day has only 24 hours.)

Line 340: This sentence is a duplicate of the previous one.

Line 554: When using CFADs, please cite Yuter and Houze, 1994.

Figure 10: Altitude unit is missing.

Data availability: The authors only post a general link to the EOL Field Data Archive. It is important to list the individual datasets with their respective DOIs in this section.
Citation: https://doi.org/10.5194/amt-2024-124-RC1
- AC1: 'Reply on RC1', Anik Das, 18 Nov 2024
  
  We thank the reviewer for their valuable feedback on our manuscript. We are adding the response letter as a pdf in the supplement to this section. Our responses are mentioned in details against each comment. A reference section has also been added to the response letter.
  
  Citation: https://doi.org/10.5194/amt-2024-124-AC1
RC2:
'Comment on amt-2024-124', Anonymous Referee #2, 30 Sep 2024

1. Overview of the paper
This article proposes a new method for determining the phase and structural characteristics of low-level clouds in the Southern Ocean (SO). This study uses in situ data (in situ probes and radar) from the SOCRATES airborne measurement campaign. The main results show that low-level clouds are very strongly present during the campaign. Almost half the time, single layer low-level clouds are made up of liquid phase with a high proportion of supercooled liquid water. The distribution of phases in low-level clouds seems to depend on altitude, with a liquid phase present in the middle of the cloud and an ice phase at higher altitudes. A comparison of phase characterization methods was carried out in order to highlight the differences between the results.
This study is interesting and reasonably well presented. However, there are still a few points to be clarified in terms of methodology and validation. I would recommend some major revisions before the manuscript can be considered for publication in AMT.
2. General suggestions
The authors should specify the purpose of this study, for example to identify cloud boundaries in the absence of lidar. In order to provide more clarity on the paper's objective. I would advise authors to estimate uncertainties more accurately, simply by adding statistical parameters (standard deviation on figures), for example. For in situ probes and parameters, refer to more articles highlighting measurement uncertainties and uncertainties related to derived parameters. Above all, to show that in situ accurate and real, but is nevertheless marred by uncertainties. The authors should explain the LWP calculation a little more clearly. This is an important point in the paper, linking in situ and phase discrimination. I would advise the authors to try to validate their methods cloud boundary detection and LWP : For LWP, they should try to compare the LWP calculation with a sawtooth portion of flight in a cloud. In order to see qualitatively whether the LWP is “globally” of the same order of magnitude. For cloud boundaries, you could once again use thresholds on your contents (LWC and/or IWC) to estimate cloud top and base on sawtooth leg (as in the portion on your Fig. 1 between 26 and 27 UTC for example). The overall weather conditions for the campaign were not presented. I think it would be interesting to add a paragraph highlighting thermodynamic conditions. In particular, to link with cloud structures and the strong presence of low-level clouds.
Part 4 (Results and discussion) is interesting, with a detailed phase classification algorithm. The sub-sections are coherent, and the addition of the comparison of the different methods is an essential and clear point. However, I find the explanations of the CFADs linked to figure 10. a little complex and difficult to follow. The links between Doppler velocity, or Spectrum Width, and size distributions are sometimes complicated to make. Moreover, add definition of mixed phase; please provide ref. It is important to clary what is considered as a mixed phase cloud or layer here. (see specific comment). You can make comparison with other study, it looks like a statistical comparison and not a pixel/cloud layer by pixel comparison (which could be more relevant). It could interesting to carry out a pixel by pixel phase comparison. Phase comparison with other in situ probes such as the PHIPS which can provide an independent assessment of the cloud phase. Provide in the appendix the results of the D’Alessandro method applied to your dataset.
3. Specific comments and technical corrections
Abstract :
Line 18 : Please and microphysical to “macrophysical properties “ as the in situ measurements (CDP and 2DS) are also used to characterize the microphysical structure of the clouds
Line 24-25 : Please specify the temperature range when you mention higher temperature and lower temperatures
Introduction :
Line 33 : In the beginning of this introduction, all that’s missing is a latitude scale to define the limits of the Southern Ocean globally, not just for the campaign region.
Line 47 : The are other papers focusing on Arctic mixed-phase clouds such as Jackson et al., (2012), Järvinen et al., (2023) or Moser et al., (2023) that describe the structure of these clouds from in situ data.
Line 50-52 : Cloud you be more specific ? What do you mean by “most algorithms are tuned for specific …. climatic regions” ? Does it concern satellite retrieval algorithm where the cloud phase identification is performed priori to cloud property retrievals ?
Line 57 : For SO another recent paper Bazantay et al., (2024) and for Arctic region there is also Mioche et al., (2015) or Matus and L’Ecuyer, (2017).
Line 79 : In 1-2 sentences, the authors could propose an example of cloud-type classification based on satellite instruments. In order to get an overall idea of the different methods (in situ, spatial,…). Additionally, the authors should also state that the mixed phase identification depend on the observation scale. In the literature, different approach are used and for instance a mixed phase cloud can be composed of a combination of liquid phase pixels and ice phase clouds with no mixed phase pixels. It also depend of the instrument used to detect the cloud phase layers.
Line 82 : This sentence is really long.
Line 88 : Perhaps add instrument names for remote sensing as in line 92 for in situ probes.
Line 104 : Authors can also add “and near-surface contamination problems related to echo”.
Line 107 : However, lidar is still useful for determining cloud tops if they are made up of liquid phase (strong backscattering).
Data and methods :
Line 131 : The authors should also state that the mixed phase identification depend on the observation scale. In the literature, different approach are used and for instance a mixed phase cloud can be composed of a combination of liquid phase pixels and ice phase clouds with no mixed phase pixels. It also depend of the instrument used to detect the cloud phase layers.
Line 137 : I find this sentence not very clear, the authors could add a “small” additional explanation to explain the liquid water/ice discrimination.
Line 140 : The uncertainties arising from the in situ instruments are reflected in the PSDs, and I know that it’s complicated to estimate uncertainties in secondary parameters (such as content (IWC or LWC)). Perhaps add a sentence to effect that these primary uncertainties are reflected in the secondary parameters.
Line 141 : Do you use a weighted average to calculate your merged size distribution ?
Line 142 : How did you choose the threshold (40 µm) between cloud droplets and drizzle particles ?
Line 152 : Out of curiosity, did you check whether the ERA5 data matched the temperature data measured by the aircraft ?
Line 197 : The time scale is a bit strange (29 hours UTC ? ), maybe change the legend to “Since midnight (15 Jan 2018)”.
Line 230 : I’m not sure I understand the LWP calculation. In the formula, j corresponds to ? In agreement with h et al. (2018), j represents the number of points in your profile ? To have several values of LWC in the profile, means that the plane passes several times in the same column ? Or is your in situ LWC just summed over the thickness of your cloud ? This calculation and method should be described a little more, as it is essential for the study. What does n stand for ? Authors can attempt to “validate” the LWP, using the method in Mioche et al., (2017), on a sawtooth leg.
Line 250 : How is the IWC calculated ? Mass/diameter law?
Line 253 : How good is the ERA5 data in the Southern Ocean ?
Line 267 : The authors could add the grids on the figures to make it easier to see the values (even if the essential values are quoted in the text). I think a error bar should be added to figs 3.a, 4.a and b. Ilt’s always interesting to estimate the statistical error.
Line 271 : I would have preferred the definition of the LWP threshold at 10 g/m² to have been explained at the same time. This is explained in the next section (4.1).
Line 285 : Have you analyzed median values versus mean values ? Just to see if the observations follow a Gaussian curve.
Results and discussions :
Line 291 : 10 seconds at ± 100 m/s (probably more) ≈ 1 km. It is important to note that the main underlying hypothesis is that the cloud is globally homogeneous over ± 1 km.
Line 340 : Duplicate sentence
Line 352 : In the fig 6.a, the pixels representing the point counts are wider than in fig 6.d. What is the reason for this difference in definition ? Is it just that there are fewer points for these conditions (“liquid cloud droplets, drizzle and rain drops”) ?
Line 390 : I find this paragraph difficult to understand, but it’s important for understanding dimensional segmentation. The authors could perhaps be reworked.
Line 432 : It would have been interesting to have 2DS images to represent the morphological environment. But we can’t show everything…
Line 433 : The authors could add a reference to show the consistency of these remarks with other studies, also in agreement with mixed-phase clouds in the Arctic region. I also think that the PHIPS and SID-3 instruments were deployed during the SOCRATES campaign. Did you check the consistency of your cloud phase identification with asymmetry parameter derived from the PHIPS which could be a good proxy for cloud phase. SID-3 can also provide information on small ice crystals. Was this investigated ?
Line 435 : So yes, the 2DS is better to identifying images above 50 µm, but the term “easily” is a little misleading. Particle with size of 50 µm is made up of ± 5 pixels with 2DS, so it’s still difficult to characterize the phase and even more complicated if you’re trying to analyse morphology.
Line 454/503 : Authors could try to explain the difference between the comparison of the 2 methods (this study and MLR). Of course, these differences can be partly explained by the use of very different methods.
Line 480 : What could account for the difference in PLDR thresholds between Arctic and Southern Ocean ?
Line 535 : What’s not necessarily explained is that these thermodynamic parameters are dependent on the season in which the measurement campaign took place (January/February). Would partitioning phase or phase distribution be the same for identical environmental conditions in summer ?
Line 571 : I would have liked to see a reference for the influence of morphology on reflectivity unless this is a hypothesis you’re proposing ?
References :
Bazantay, C., Jourdan, O., Mioche, G., Uitz, J., Dziduch, A., Delanoë, J., Cazenave, Q., Sauzède, R., Protat, A., and Sellegri, K.: Relating Ocean Biogeochemistry and Low‐Level Cloud Properties Over the Southern Oceans, Geophys. Res. Lett., 51, e2024GL108309, https://doi.org/10.1029/2024GL108309, 2024.
Jackson, R. C., McFarquhar, G. M., Korolev, A. V., Earle, M. E., Liu, P. S. K., Lawson, R. P., Brooks, S., Wolde, M., Laskin, A., and Freer, M.: The dependence of ice microphysics on aerosol concentration in arctic mixed-phase stratus clouds during ISDAC and M-PACE: AEROSOL EFFECTS ON ARCTIC STRATUS, J. Geophys. Res. Atmospheres, 117, n/a-n/a, https://doi.org/10.1029/2012JD017668, 2012.
Järvinen, E., Nehlert, F., Xu, G., Waitz, F., Mioche, G., Dupuy, R., Jourdan, O., and Schnaiter, M.: Investigating the vertical extent and short-wave radiative effects of the ice phase in Arctic summertime low-level clouds, Atmospheric Chem. Phys., 23, 7611–7633, https://doi.org/10.5194/acp-23-7611-2023, 2023.
Matus, A. V. and L’Ecuyer, T. S.: The role of cloud phase in Earth’s radiation budget, J. Geophys. Res. Atmospheres, 122, 2559–2578, https://doi.org/10.1002/2016JD025951, 2017.
Mioche, G., Jourdan, O., Ceccaldi, M., and Delanoë, J.: Variability of mixed-phase clouds in the Arctic with a focus on the Svalbard region: a study based on spaceborne active remote sensing, Atmospheric Chem. Phys., 15, 2445–2461, https://doi.org/10.5194/acp-15-2445-2015, 2015.
Mioche, G., Jourdan, O., Delanoë, J., Gourbeyre, C., Febvre, G., Dupuy, R., Monier, M., Szczap, F., Schwarzenboeck, A., and Gayet, J.-F.: Vertical distribution of microphysical properties of Arctic springtime low-level mixed-phase clouds over the Greenland and Norwegian seas, Atmospheric Chem. Phys., 17, 12845–12869, https://doi.org/10.5194/acp-17-12845-2017, 2017.
Moser, M., Voigt, C., Jurkat-Witschas, T., Hahn, V., Mioche, G., Jourdan, O., Dupuy, R., Gourbeyre, C., Schwarzenboeck, A., Lucke, J., Boose, Y., Mech, M., Borrmann, S., Ehrlich, A., Herber, A., Lüpkes, C., and Wendisch, M.: Microphysical and thermodynamic phase analyses of Arctic low-level clouds measured above the sea ice and the open ocean in spring and summer, Atmospheric Chem. Phys., 23, 7257–7280, https://doi.org/10.5194/acp-23-7257-2023, 2023.
Wendisch, M. and Brenguier, J.-L. (Eds.): Airborne measurements for environmental research: methods and instruments, Wiley-VCH, Weinheim, 655 pp., 2013.

Citation: https://doi.org/10.5194/amt-2024-124-RC2
- AC2:
  'Reply on RC2', Anik Das, 18 Nov 2024
  
  We thank the reviewer for their valuable feedback on our manuscript. We are adding the response letter as a pdf in the supplement to this section. Our responses are mentioned in details against each comment. A reference section has also been added to the response letter.
  
  Citation: https://doi.org/10.5194/amt-2024-124-AC2
  - AC3: 'Reply on AC2', Anik Das, 20 Nov 2024
    
    For response to comment 40. We forgot to add a line. this is the revised response to that particular comment.
    40. Line 535 :What’s not necessarily explained is that these thermodynamic parameters are dependent on the season in which the measurement campaign took place (January/February). Would partitioning phase or phase distribution be the same for identical environmental conditions in summer?
    Response: We have added a sentence highlighting the exclusivity of these thermodynamic parameters to Jan/Feb (during SOCRATES). The results should be similar for the entire climatological winter months NDJFM (Dong, 2024), but further scrutiny is needed to evaluate how they change for the summer months. Note that these months (Nov-Feb) are the climatological summer season for the Southern Hemisphere.
    
    Citation: https://doi.org/10.5194/amt-2024-124-AC3

Status: closed

RC1:
'Comment on amt-2024-124', Anonymous Referee #1, 04 Sep 2024
General Comments
The authors use in-situ cloud probe data and remote sensing observations collected by instruments onboard the NSF NCAR GV aircraft during the SOCRATES campaign to study low level clouds over the Southern Ocean. While the topic is interesting and highly relevant, unfortunately, there are many issues with the methodology used by the authors:
The authors developed a radar-based methodology to derive cloud base. However, they themselves state that it does not agree with the standard method based on lidar observations. The lidar-based method has been proven to work well in many previous studies and since the authors do not independently validate their new method the reader concludes that the radar based method is not accurate.
The authors then develop a new cloud phase classification method based on in-situ and radar observations. The method heavily relies on spectrum width observations but fails to account for shortcomings in the spectrum width observations, which leads to inaccurate conclusions. It also relies on the liquid water path, which is derived along the aircraft track from in-situ measurements and then applied to the whole vertical column of the radar observations. In my opinion, it is not an accurate assumption to claim that LWP is constant throughout a cloud. The authors themselves state that the resulting 2D classification does not look accurate. Nonetheless, they collapse it back into a 1D classification and use both throughout the rest of the study.
The authors compare some of their results with methods from previous studies (even though for some reason they do not compare it with the phase classification that is provided in the radar/lidar dataset itself) and note that their results do not agree very well with previous studies.
I am not sure why the authors chose to develop their own method, when proven methods are readily available, and then decide to use their own method, even though they themselves have found that it does not produce good results.
Because of these issues with the methodology, the interpretation of the results, and the conclusions drawn, are also highly questionable.
Given all these shortcomings (which are listed in more detail in the Specific Comments below), I am afraid I have to recommend to reject the manuscript in its current form.
Specific Comments
Line 147: Please explain what is meant with “interpolated to fixed radar-heights at a range gate of 19.2 meters”. The range gates are already fixed. And why 19.2 m?

Section 2.2: I am very skeptical about the method that derives cloud base. How was that method validated? Using data from the GV-HSRL to determine cloud base is the state-of-the-art methodology. If the method proposed by the authors does not agree with the GV-HSRL measurements, that would generally indicate that it is not accurate. If the authors really want to claim that their method is superior, they need to find an independent validation method. Simply plotting the results on the radar observations is not sufficient.

I would also like to point out that spectrum width in regions with low signal to noise ratios, which are often observed at the cloud edges, are often noisy and not all that reliable. Using their gradient to derive cloud boundaries is therefore not recommended. You can see in Figure 1c that there is a similar gradient at the top of the cloud as at the bottom. The argument that this gradient implies drizzle or precipitation (as stated at line 177) is therefore highly questionable. The fact that the algorithm finds cloud base in the middle of a cloud layer where there is clearly no precipitation at all (Fig. 1 around 26.44) is also suspicious.

Table 2: What is meant with “may not be single layer”? Does this mean that they could be multi-layer or deep? I don’t think it makes much sense to put both of these cloud types together in one category. The same is true for the HML category. That seems to be a deep cloud but the name of the category seems to indicate that it is a multi-layer cloud.

Line 217: What is meant with “due to the selected cloud cases”? What cases were selected? How many? And based on which criteria?

Section 2.4: I’m afraid I do not understand how LWP is calculated. Do the authors assume that the LWC is vertically constant throughout the cloud? That does not seem like valid assumption.

Figure 3: How do these results compare to similar classifications in the literature? (Mace and Protat 2018, Truong et al. 2020, Romatschke 2023)

Table 3: The LWP values have very large SDs. Are they actually meaningful?

Section 4.1: The authors develop a new methodology to derive cloud phase from radar observations. However, they do not validate the method. This leads to the following questions: a) Why was a new method developed when a phase classification is already provided in the dataset? Why do the authors think their methodology is valid if it is not verified? Why do they believe that their method is better than previous methods (that have actually been validated)? Why was it not validated?

At line 375 the authors say that they compared with previous work. What exactly does that mean? What were the results of these comparisons? Also, the classification heavily relies on LWP and spectrum width. As mentioned earlier, I am not sure how trustworthy LWP is, as it is assumed to be vertically constant (see first paragraph of Section 4.2). Again, spectrum width is noisy in low SNR regions and some, if not many, of the high values may be unreliable. (Romatschke and Vivekanandan decided not to use spectrum width in their algorithm for this reason.)

In Section 4.2., the authors state that “phase retrieval method but may be not highly depictive of the actual cloud phase”. In that case, what is the value of the 2D derived cloud phase? What is the purpose of this effort? The 2D cloud phase is then again collapsed into a 1D cloud phase product which apparently “returns reasonably accurate findings compared to other phase detection studies over the SO”. These comparisons are later shown (see below) but they are not convincing.

What is the purpose of developing this new product if other phase classifications already exist? Why start with the 1D cloud probe observations, expand them to low-quality 2D observations, and then collapse them again into 1D phase estimations? Why not use the cloud probe measurements directly and the phase classifications that were derived from them in previous studies?

Starting line 442, the 1D phase classification is compared with phase classifications from other studies. Unfortunately, the classifications from the current paper do not agree well with the classifications from previous studies. The authors speculate about the causes of these discrepancies but fail to explain why the reader should trust their results over those from previous studies.

Starting line 474 the authors suggest tuning thresholds from previous studies to match their results but I am not convinced that this is the right thing to do. Again, why do the authors think that their results are more accurate?

Section 4.3: Given all the problems pointed out earlier (unproven cloud base, unreliable phase classification), I am not sure how trustworthy and valuable this analysis is.

Section 4.3.1: For this analysis, is the 2D cloud phase or the 1D cloud phase product used?

Section 4.3.2: Given that the authors stated earlier that the 2D cloud phase product is not particularly accurate, why is it used here?

Starting line 551: I disagree with the author’s interpretation of the CFADs. In my opinion, the CFADs for the liquid (and mixed) clouds show a strong bright band signature at 0.2 km normalized height. This bright band signature contradicts the author’s claims that the clouds are predominantly liquid. This confirms that the phase classification algorithm does not produce high-quality results. Looking at Figure 7, one gets the impression that the algorithm tends to classify deep clouds with strong reflectivity as mixed, deep clouds with weak reflectivity as liquid, and thin clouds as ice. This is reflected in the CFAD categories of Figure 10. I do not see a connection with cloud phase. It is not surprising that the authors use the word “surprisingly” a lot in the description of the CFADs since the CFADs do not actually show clouds of the respective phases.

Line 586: The higher width values indicate that a significant portion of the data comes from low SNR cloud edges where width tends to be noisy.

Paragraphs starting line 599 and 609: Same as previous comment. Please do not over-interpret the high width values in low SNR regions.

Conclusions: I am not convinced by the conclusions given all the issues pointed out in the previous comments.

Technical Corrections
I would like to point out that there are many(!) grammatical issues throughout the paper which are too numerous to list. Sentences are often very long and not only the reader, but apparently also the authors get lost. Two of many examples are the sentence starting line 33 and the sentence starting line 80.

Line 25: Please define “SLW”.

Line 109 and throughout the manuscript: The instrument is called the “GV-HSRL”.

Line 128: The SOCRATES acronym has already been defined earlier.

Line 132: Type RV -> GV.

Figure 1: Please correct the values on the time axis. (As far as I know, a day has only 24 hours.)

Line 340: This sentence is a duplicate of the previous one.

Line 554: When using CFADs, please cite Yuter and Houze, 1994.

Figure 10: Altitude unit is missing.

Data availability: The authors only post a general link to the EOL Field Data Archive. It is important to list the individual datasets with their respective DOIs in this section.
Citation: https://doi.org/10.5194/amt-2024-124-RC1
- AC1: 'Reply on RC1', Anik Das, 18 Nov 2024
  
  We thank the reviewer for their valuable feedback on our manuscript. We are adding the response letter as a pdf in the supplement to this section. Our responses are mentioned in details against each comment. A reference section has also been added to the response letter.
  
  Citation: https://doi.org/10.5194/amt-2024-124-AC1
RC2:
'Comment on amt-2024-124', Anonymous Referee #2, 30 Sep 2024

1. Overview of the paper
This article proposes a new method for determining the phase and structural characteristics of low-level clouds in the Southern Ocean (SO). This study uses in situ data (in situ probes and radar) from the SOCRATES airborne measurement campaign. The main results show that low-level clouds are very strongly present during the campaign. Almost half the time, single layer low-level clouds are made up of liquid phase with a high proportion of supercooled liquid water. The distribution of phases in low-level clouds seems to depend on altitude, with a liquid phase present in the middle of the cloud and an ice phase at higher altitudes. A comparison of phase characterization methods was carried out in order to highlight the differences between the results.
This study is interesting and reasonably well presented. However, there are still a few points to be clarified in terms of methodology and validation. I would recommend some major revisions before the manuscript can be considered for publication in AMT.
2. General suggestions
The authors should specify the purpose of this study, for example to identify cloud boundaries in the absence of lidar. In order to provide more clarity on the paper's objective. I would advise authors to estimate uncertainties more accurately, simply by adding statistical parameters (standard deviation on figures), for example. For in situ probes and parameters, refer to more articles highlighting measurement uncertainties and uncertainties related to derived parameters. Above all, to show that in situ accurate and real, but is nevertheless marred by uncertainties. The authors should explain the LWP calculation a little more clearly. This is an important point in the paper, linking in situ and phase discrimination. I would advise the authors to try to validate their methods cloud boundary detection and LWP : For LWP, they should try to compare the LWP calculation with a sawtooth portion of flight in a cloud. In order to see qualitatively whether the LWP is “globally” of the same order of magnitude. For cloud boundaries, you could once again use thresholds on your contents (LWC and/or IWC) to estimate cloud top and base on sawtooth leg (as in the portion on your Fig. 1 between 26 and 27 UTC for example). The overall weather conditions for the campaign were not presented. I think it would be interesting to add a paragraph highlighting thermodynamic conditions. In particular, to link with cloud structures and the strong presence of low-level clouds.
Part 4 (Results and discussion) is interesting, with a detailed phase classification algorithm. The sub-sections are coherent, and the addition of the comparison of the different methods is an essential and clear point. However, I find the explanations of the CFADs linked to figure 10. a little complex and difficult to follow. The links between Doppler velocity, or Spectrum Width, and size distributions are sometimes complicated to make. Moreover, add definition of mixed phase; please provide ref. It is important to clary what is considered as a mixed phase cloud or layer here. (see specific comment). You can make comparison with other study, it looks like a statistical comparison and not a pixel/cloud layer by pixel comparison (which could be more relevant). It could interesting to carry out a pixel by pixel phase comparison. Phase comparison with other in situ probes such as the PHIPS which can provide an independent assessment of the cloud phase. Provide in the appendix the results of the D’Alessandro method applied to your dataset.
3. Specific comments and technical corrections
Abstract :
Line 18 : Please and microphysical to “macrophysical properties “ as the in situ measurements (CDP and 2DS) are also used to characterize the microphysical structure of the clouds
Line 24-25 : Please specify the temperature range when you mention higher temperature and lower temperatures
Introduction :
Line 33 : In the beginning of this introduction, all that’s missing is a latitude scale to define the limits of the Southern Ocean globally, not just for the campaign region.
Line 47 : The are other papers focusing on Arctic mixed-phase clouds such as Jackson et al., (2012), Järvinen et al., (2023) or Moser et al., (2023) that describe the structure of these clouds from in situ data.
Line 50-52 : Cloud you be more specific ? What do you mean by “most algorithms are tuned for specific …. climatic regions” ? Does it concern satellite retrieval algorithm where the cloud phase identification is performed priori to cloud property retrievals ?
Line 57 : For SO another recent paper Bazantay et al., (2024) and for Arctic region there is also Mioche et al., (2015) or Matus and L’Ecuyer, (2017).
Line 79 : In 1-2 sentences, the authors could propose an example of cloud-type classification based on satellite instruments. In order to get an overall idea of the different methods (in situ, spatial,…). Additionally, the authors should also state that the mixed phase identification depend on the observation scale. In the literature, different approach are used and for instance a mixed phase cloud can be composed of a combination of liquid phase pixels and ice phase clouds with no mixed phase pixels. It also depend of the instrument used to detect the cloud phase layers.
Line 82 : This sentence is really long.
Line 88 : Perhaps add instrument names for remote sensing as in line 92 for in situ probes.
Line 104 : Authors can also add “and near-surface contamination problems related to echo”.
Line 107 : However, lidar is still useful for determining cloud tops if they are made up of liquid phase (strong backscattering).
Data and methods :
Line 131 : The authors should also state that the mixed phase identification depend on the observation scale. In the literature, different approach are used and for instance a mixed phase cloud can be composed of a combination of liquid phase pixels and ice phase clouds with no mixed phase pixels. It also depend of the instrument used to detect the cloud phase layers.
Line 137 : I find this sentence not very clear, the authors could add a “small” additional explanation to explain the liquid water/ice discrimination.
Line 140 : The uncertainties arising from the in situ instruments are reflected in the PSDs, and I know that it’s complicated to estimate uncertainties in secondary parameters (such as content (IWC or LWC)). Perhaps add a sentence to effect that these primary uncertainties are reflected in the secondary parameters.
Line 141 : Do you use a weighted average to calculate your merged size distribution ?
Line 142 : How did you choose the threshold (40 µm) between cloud droplets and drizzle particles ?
Line 152 : Out of curiosity, did you check whether the ERA5 data matched the temperature data measured by the aircraft ?
Line 197 : The time scale is a bit strange (29 hours UTC ? ), maybe change the legend to “Since midnight (15 Jan 2018)”.
Line 230 : I’m not sure I understand the LWP calculation. In the formula, j corresponds to ? In agreement with h et al. (2018), j represents the number of points in your profile ? To have several values of LWC in the profile, means that the plane passes several times in the same column ? Or is your in situ LWC just summed over the thickness of your cloud ? This calculation and method should be described a little more, as it is essential for the study. What does n stand for ? Authors can attempt to “validate” the LWP, using the method in Mioche et al., (2017), on a sawtooth leg.
Line 250 : How is the IWC calculated ? Mass/diameter law?
Line 253 : How good is the ERA5 data in the Southern Ocean ?
Line 267 : The authors could add the grids on the figures to make it easier to see the values (even if the essential values are quoted in the text). I think a error bar should be added to figs 3.a, 4.a and b. Ilt’s always interesting to estimate the statistical error.
Line 271 : I would have preferred the definition of the LWP threshold at 10 g/m² to have been explained at the same time. This is explained in the next section (4.1).
Line 285 : Have you analyzed median values versus mean values ? Just to see if the observations follow a Gaussian curve.
Results and discussions :
Line 291 : 10 seconds at ± 100 m/s (probably more) ≈ 1 km. It is important to note that the main underlying hypothesis is that the cloud is globally homogeneous over ± 1 km.
Line 340 : Duplicate sentence
Line 352 : In the fig 6.a, the pixels representing the point counts are wider than in fig 6.d. What is the reason for this difference in definition ? Is it just that there are fewer points for these conditions (“liquid cloud droplets, drizzle and rain drops”) ?
Line 390 : I find this paragraph difficult to understand, but it’s important for understanding dimensional segmentation. The authors could perhaps be reworked.
Line 432 : It would have been interesting to have 2DS images to represent the morphological environment. But we can’t show everything…
Line 433 : The authors could add a reference to show the consistency of these remarks with other studies, also in agreement with mixed-phase clouds in the Arctic region. I also think that the PHIPS and SID-3 instruments were deployed during the SOCRATES campaign. Did you check the consistency of your cloud phase identification with asymmetry parameter derived from the PHIPS which could be a good proxy for cloud phase. SID-3 can also provide information on small ice crystals. Was this investigated ?
Line 435 : So yes, the 2DS is better to identifying images above 50 µm, but the term “easily” is a little misleading. Particle with size of 50 µm is made up of ± 5 pixels with 2DS, so it’s still difficult to characterize the phase and even more complicated if you’re trying to analyse morphology.
Line 454/503 : Authors could try to explain the difference between the comparison of the 2 methods (this study and MLR). Of course, these differences can be partly explained by the use of very different methods.
Line 480 : What could account for the difference in PLDR thresholds between Arctic and Southern Ocean ?
Line 535 : What’s not necessarily explained is that these thermodynamic parameters are dependent on the season in which the measurement campaign took place (January/February). Would partitioning phase or phase distribution be the same for identical environmental conditions in summer ?
Line 571 : I would have liked to see a reference for the influence of morphology on reflectivity unless this is a hypothesis you’re proposing ?
References :
Bazantay, C., Jourdan, O., Mioche, G., Uitz, J., Dziduch, A., Delanoë, J., Cazenave, Q., Sauzède, R., Protat, A., and Sellegri, K.: Relating Ocean Biogeochemistry and Low‐Level Cloud Properties Over the Southern Oceans, Geophys. Res. Lett., 51, e2024GL108309, https://doi.org/10.1029/2024GL108309, 2024.
Jackson, R. C., McFarquhar, G. M., Korolev, A. V., Earle, M. E., Liu, P. S. K., Lawson, R. P., Brooks, S., Wolde, M., Laskin, A., and Freer, M.: The dependence of ice microphysics on aerosol concentration in arctic mixed-phase stratus clouds during ISDAC and M-PACE: AEROSOL EFFECTS ON ARCTIC STRATUS, J. Geophys. Res. Atmospheres, 117, n/a-n/a, https://doi.org/10.1029/2012JD017668, 2012.
Järvinen, E., Nehlert, F., Xu, G., Waitz, F., Mioche, G., Dupuy, R., Jourdan, O., and Schnaiter, M.: Investigating the vertical extent and short-wave radiative effects of the ice phase in Arctic summertime low-level clouds, Atmospheric Chem. Phys., 23, 7611–7633, https://doi.org/10.5194/acp-23-7611-2023, 2023.
Matus, A. V. and L’Ecuyer, T. S.: The role of cloud phase in Earth’s radiation budget, J. Geophys. Res. Atmospheres, 122, 2559–2578, https://doi.org/10.1002/2016JD025951, 2017.
Mioche, G., Jourdan, O., Ceccaldi, M., and Delanoë, J.: Variability of mixed-phase clouds in the Arctic with a focus on the Svalbard region: a study based on spaceborne active remote sensing, Atmospheric Chem. Phys., 15, 2445–2461, https://doi.org/10.5194/acp-15-2445-2015, 2015.
Mioche, G., Jourdan, O., Delanoë, J., Gourbeyre, C., Febvre, G., Dupuy, R., Monier, M., Szczap, F., Schwarzenboeck, A., and Gayet, J.-F.: Vertical distribution of microphysical properties of Arctic springtime low-level mixed-phase clouds over the Greenland and Norwegian seas, Atmospheric Chem. Phys., 17, 12845–12869, https://doi.org/10.5194/acp-17-12845-2017, 2017.
Moser, M., Voigt, C., Jurkat-Witschas, T., Hahn, V., Mioche, G., Jourdan, O., Dupuy, R., Gourbeyre, C., Schwarzenboeck, A., Lucke, J., Boose, Y., Mech, M., Borrmann, S., Ehrlich, A., Herber, A., Lüpkes, C., and Wendisch, M.: Microphysical and thermodynamic phase analyses of Arctic low-level clouds measured above the sea ice and the open ocean in spring and summer, Atmospheric Chem. Phys., 23, 7257–7280, https://doi.org/10.5194/acp-23-7257-2023, 2023.
Wendisch, M. and Brenguier, J.-L. (Eds.): Airborne measurements for environmental research: methods and instruments, Wiley-VCH, Weinheim, 655 pp., 2013.

Citation: https://doi.org/10.5194/amt-2024-124-RC2
- AC2:
  'Reply on RC2', Anik Das, 18 Nov 2024
  
  We thank the reviewer for their valuable feedback on our manuscript. We are adding the response letter as a pdf in the supplement to this section. Our responses are mentioned in details against each comment. A reference section has also been added to the response letter.
  
  Citation: https://doi.org/10.5194/amt-2024-124-AC2
  - AC3: 'Reply on AC2', Anik Das, 20 Nov 2024
    
    For response to comment 40. We forgot to add a line. this is the revised response to that particular comment.
    40. Line 535 :What’s not necessarily explained is that these thermodynamic parameters are dependent on the season in which the measurement campaign took place (January/February). Would partitioning phase or phase distribution be the same for identical environmental conditions in summer?
    Response: We have added a sentence highlighting the exclusivity of these thermodynamic parameters to Jan/Feb (during SOCRATES). The results should be similar for the entire climatological winter months NDJFM (Dong, 2024), but further scrutiny is needed to evaluate how they change for the summer months. Note that these months (Nov-Feb) are the climatological summer season for the Southern Hemisphere.
    
    Citation: https://doi.org/10.5194/amt-2024-124-AC3

Anik Das, Baike Xi, Xiaojian Zheng, and Xiquan Dong

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Short summary

Understanding the cloud phase and macrophysical properties of Southern Ocean clouds is crucial to enhancing our understanding of the region. The cloud radar and in-situ probes during the SOCRATES aircraft campaign are used to develop a new method to determine cloud boundaries and dominant phase. Low clouds (<3km) are found to be the most dominant cloud type (~90%), with liquid being the most dominant phase type, followed by ice and mixed with a greater incidence of drizzle around the cloud base.


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