Effects of atmospheric dynamics and aerosols on the  fraction of supercooled water clouds

Li, Jiming; Lv, Qiaoyi; Zhang, Min; Wang, Tianhe; Kawamoto, Kazuaki; Chen, Siyu; Zhang, Beidou

doi:https://doi.org/10.5194/acp-17-1847-2017

Volume 17, issue 3

Atmos. Chem. Phys., 17, 1847–1863, 2017
https://doi.org/10.5194/acp-17-1847-2017
© Author(s) 2017. This work is distributed under
the Creative Commons Attribution 3.0 License.

Volume 17, issue 3

Research article 08 Feb 2017

Research article | 08 Feb 2017

Effects of atmospheric dynamics and aerosols on the fraction of supercooled water clouds

Jiming Li et al.

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Final revised paper (published on 08 Feb 2017)
Preprint (discussion started on 25 Feb 2016)

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AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC1: 'Review of the paper "Effects of atmospheric dynamics and aerosols on the thermodynamic phase of cold clouds" by Jiming Li et al.', Anonymous Referee #1, 22 Mar 2016
- AC1: 'Response to Reviewer#1', Jiming Li, 03 Jun 2016
RC2: 'Review for "Effects of atmospheric dynamics and aerosols on the thermodynamic phase of cold clouds"', Anonymous Referee #2, 23 Mar 2016
- AC2: 'Response to Reviewer#2', Jiming Li, 03 Jun 2016

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Jiming Li on behalf of the Authors (06 Jun 2016) Author's response Manuscript

ED: Referee Nomination & Report Request started (06 Jun 2016) by Johannes Quaas

RR by Anonymous Referee #2 (15 Jul 2016)

Suggestions for revision or reasons for rejection

\documentclass{article}

\begin{document}

\section{General comments}

The authors have made substantial changes to the original manuscript that have eliminated much of the questionable material pertaining to the evaluation of cloud thermodynamic phase temperature ramp schemes in models. They have also expanded the latter part of the manuscript pertaining to the statistical relationships between meteorological parameters and cloud thermodynamic phase, focusing on particular regions of interest. The results are intriguing, however, my main concern is that the physical interpretations of the many correlations in the manuscript are lacking. Moreover, many parts of the analysis appear to be speculative rather than rigorously verified. I also question the robustness of some of the results, which need additional clarification. Finally, many statements in the manuscript read as though correlation implies causation and care must be taken to avoid such statements, as there could clearly be other confounding factors involved. My recommendation is: publish with major revisions. Specific comments follow.

\section{Major Comments}
\begin{enumerate}
\item \textbf{Results, Section 3.1, Lines 354-356:} The authors write that the negative correlations between skin temperature and SCF in the mid- and high latitudes ``mean" that high skin temperature promotes the glaciation of supercooled droplets, and that it the positive correlations ``mean" that high skin temperature inhibits glaciation in the tropics. Firstly, correlation does not imply causation. These correlations may be caused by many different confounding factors that lead to mechanisms that are completely unrelated to skin temperature. What is the physical mechanism for why high skin temperature promotes glaciation in the mid- and high latitudes? This was never mentioned in the manuscript. The authors explain that high skin temperature in the tropics inhibits glaciation because it triggers deep convection, which lofts the liquid droplets to the colder isotherms, but what is the mechanism for the mid- and high latitudes? Secondly, the area of the tropics that the authors are referring to appears to be only a small part of the entire tropics (how many gridboxes/what is the percentage of the area of the tropics that is positively correlated?). Thirdly, if high skin temperature is indeed inhibiting glaciation due to a triggering of deep convection in the tropics, then shouldn't the coldest isotherm, i.e.\ $-$30$^{\circ}$C also show positive correlations in the tropics as well? The correlations between relative humidity and SCF and vertical velocity and SCF appear to support your argument in the tropics, but please clarify the effect of skin temperature.

Next, there is an apparent contradiction between the authors' explanation of the correlations found in the tropics and Figures 1, 2 and 3. The authors explain that vigorous convective activity, high relative humidity as well as high vertical velocities in this region cause supercooled liquid to loft to higher altitudes too quickly to allow for glaciation of supercooled liquid, which would suggest that SCFs should be higher in this region for the aforementioned reasons. Yet, Figs. 1, 2 and 3 all show that the tropics contain mixed-phase clouds with some of the lowest SCFs in the world. Please clarify.

\item \textbf{Abstract, Lines 57-59:} This is another example of a sentence that reads as if correlations between SCF and U imply that U is the cause for high SCFs in the mid- and high latitudes.

\item \textbf{Results, Section 3.1, Lines 384-385:} Again, another sentence insinuating that correlation implies causation.

\item \textbf{Results, Section 3.2, Lines 396-398 and 405-408:} These are yet more statements that read as though correlation implies causation. One cannot conclude from these correlations that the meteorological parameters examined in the study impact the SCF, but only that these results provide further evidence to support previous studies that have established a causal effect. Too many of such statements occur in the manuscript to list. Please revise the manuscript bearing in mind that correlation does not imply causation and eliminate all statements that imply a causal effect strictly from only a correlation analysis.

\item \textbf{Dataset and methods, Section 2.1:} Please provide more details on the GOCCP-CALIPSO product. How exactly is this product more consistent with the CALIPSO simulator within COSP (line 172: ``fully-consistent" is too general)? Technical details starting with how the Level 1 CALIPSO data is processed is recommended. How are horizontally-oriented ice particles treated in the product? Were daytime or nighttime data used? Were there quality checks to minimize misclassification of thin cloud layers with aerosols?

\item \textbf{Results, Section 3.2, Lines 396-406:} The mechanism of how horizontally-oriented crystals are eliminated by strong horizontal winds is not clearly explained. Please clarify. Next, as mentioned in the previous comment, does your data include horizontally-oriented particles in the first place? And if so, did you look into whether the frequency of occurrence of these particles actually decreased before making this conclusion? Please clarify.

\item \textbf{Results, Section 3.2, Lines 362-370:} Please provide a clear physical explanation for why positive (negative) correlations exist between LTSS and SCF over land (ocean) in the mid- and high latitudes.

\item \textbf{Dataset and Methods, Section 2.3:} Why wasn't the Level 3 product used? The Level 3 product was further processed and screened to remove some misclassifications between thin clouds and aerosols. The screening affected mostly cirrus clouds, but it may be worth repeating the analysis with this product to check whether the results are consistent.

\item \textbf{Results, Section 3.3, Fig. 11:} Have the authors tried grouping the high, medium and low RAFs into bins with different thresholds? Would the results be robust to having bins with different thresholds? I recommend the authors to redo the analysis using different threshold values for their high, medium and low RAF bins to check how robust their results are to the choice of RAF bins.

The extratropics of both the northern and southern hemispheres are grouped into a single category even though the aerosol loadings are very different for these two regions. I suggest that the authors separate their analysis of the extratropics into the northern and southern hemispheres and/or over ocean and land. This may help clarify the contributions from the various regions and enable more generalizations of the statistical patterns seen. For example, this could help to better interpret the ``U"-shaped pattern seen in Fig. 11d.
\end{enumerate}

\section{Minor Comments}

\begin{enumerate}
\item \textbf{Abstract, Line 40:} Please specify the months of the year. There were some changes to CALIPSO prior to November 2007.
\item \textbf{Abstract, Line 55:} Insert ``more" after ``relatively".
\item \textbf{Abstract, Line 60:} There is a word missing in between ``regional" and ``of". Perhaps ``influence"?
\item \textbf{Introduction, lines 72-74:} It is misleading to discuss cirrus clouds in this context. The authors are referring to a layer of mixed-phase clouds at the same isotherm, not two different layers of clouds at two different altitudes and temperatures. The difference in the optical thickness of the mixed-phase clouds due to the liquid and ice partitioning is what is important, and not the greenhouse effect. The authors may also mention the difference in the lifetime effect depending on the liquid and ice partitioning. There should also be a reference here.
\item \textbf{Introduction, lines 84-85:} It would be clearer if the term ``mixed-phase cloud" was mentioned here. The terminology is used later, but never defined upfront. Here would be a good place to introduce it.
\item \textbf{Dataset and methods, line 185:} Mlmenstadt $\rightarrow$ Mulmenstadt
\item \textbf{Dataset and methods, line 201-202:} Please provide a reference here.
\item \textbf{Results, Section 3.1, line 312:} 30 $\rightarrow$ $-$30
\item \textbf{Results, Section 3.2, Lines 419-421:} Have the authors checked that the high RAFs here are indeed due to dust and polluted dust? It may seem intuitive to make such an assumption, but the RAFs also include smoke and it is not clear that it does not dominate the RAFs rather than dust and polluted dust without verification.
\end{enumerate}
\end{document}

Referee Report: PDF

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RR by Anonymous Referee #1 (18 Jul 2016)

Suggestions for revision or reasons for rejection

The authors have produced a substantial amount of work to answer reviewers’ concerns and they deeply changed the structure of their paper. Although I appreciate they took into account my comments, there are still several major flaws in the study that make me think the paper need a major revision before being ready for publication. You’ll find hereafter some of my main concerns:

1) I noticed several plagiarisms in the introduction. It seems that the authors picked part of different introduction in other papers (yet referenced), and sometimes, they didn’t even bother change the full sentence. Here are 3 examples I noticed (there are probably many more):
Line 100: observations have verified that supercooled drops may coexist with ice crystals in mixed-phase clouds at temperatures as low as -40ºC (Borovikov et al., 963; Sassen 1992) typically for a few hours (Korolev et al., 2003) or even longer times (Boer et al., 2009).
Cesana et al 2015: liquid and ice particles can coexist in mixed-phase clouds typically for a few hours [Korolev et al., 2003], but sometimes longer, for instance in Arctic [e.g., de Boer et al., 2009].

Line 109: Changing the phase description in a general circulation models (GCMs) could lead to biases not only on the radiative flux (Yun and Penner, 2012) but also in the zonal cloud fraction, the heating rate, the humidity, and the cloud water content (Cheng et al., 2012)
Cesana et al., 2016: Recent studies have shown that changing the phase description in a GCM could lead to biases not only on the radiative flux [Yun and Penner, 2012] but also in the zonal cloud fraction, the heating rate, the humidity, and the cloud water content [Cheng et al., 2012].

Line 112: A recent GCM intercomparison study indicated that the difference in albedo feedback among different models is primarily a result of the differences in the poleward redistribution of cloud liquid water due to differences in mixed-phase cloud algorithms (Tsushima at al., 2006): the models that produce more supercooled water clouds have a higher sensitivity.
Cheng et al., 2012: A recent GCM intercomparison study indicates that the difference in cloud albedo feedback among different GCMs is primarily a result of the differences in the poleward redistribution of cloud liquid water due to differences in cloud thermodynamic phase parameterizations [Tsushima et al., 2006]. The models that produce more supercooled water clouds have higher climate sensitivities.

2) The method the authors used to derive the SCFs is not clear. They need to better explain how they did it. For example, there is no such -10 isotherm in the CALIPSO-GOCCP product. Did they choose one 3deg-temperature bin only for each -10 -20 -30 isotherm? I personally couldn’t reproduce their figure 1 2 and 3 using CALIPSO-GOCCP data. Anyhow, I found particularly difficult to believe there are almost no SLF over shallow cumulus region around –10degC, which is why I doubt the results presented here.
Even if the calculations were correct, the result section is far too descriptive and there are no discussions behind the description. The authors should revisit their results sections to make it shorter more clear and delete all descriptions irrelevant to the discussion.

3) I don’t understand the first paragraph of section 3. The authors seem to pick randomly parameters and try to find a correlation between them. It is very confusing and need to be fully re-written. Again, the authors have to pay attention to the explanations and clearly state why they chose one parameter over another and why did they change with respect to the bands of latitude.

4) In general the method to compute the figures is unclear and blurry. For example, how did they get this 10x10 grid from the 2x2 in the correlation figures. What about the results in Fig. 11.

5) Finally, I’m not a native speaker but I can tell that an English editing seems to be necessary as the manuscript contains a lot of spelling and grammar mistakes.

Some specific comments I started to write down:

Line 69 This sentence is wrong. The IPCC statement is as follow: "Cloud feedbacks remain the largest source of uncertainty in climate models" ipcc 2007/2013

71 important is not appropriate

84 – 86 This is not formulated in a correct English

97-103 The second part (However...) is confusing, please reformulate by adding something like may coexist "for a certain time" as opposed to "in equilibrium" found in the first part.

109 – 121 Why do you talk about models suddenly?

129 – 132 What's the point of these sentences? I guess you want to demonstrate that CALIPSO can be used to distinguish cloud phase, then link these sentences to the previous one such as: For example, using combined …

164 – 168 Please reformulate too long and confusing

168: single goal. It is not the single goal of the CALIPSO-GOCCP but rather the main goal among others.

Line 184 It is possible that GOCCP slightly underestimates the ice clouds in the lowest layers in the Arctic but not in the mid-lat cases as demonstrated in Cesana et al ., 2016 (Cesana G., H. Chepfer, D. Winker, X. Cai, B. Getzewich, H. Okamoto, Y. Hagihara, O. Jourdan, G. Mioche, V. Noel and M. Reverdy, 2016: Using in-situ airborne measurements to evaluate three cloud phase products derived from CALIPSO, J. Geophys. Res. Atmos., 121, doi:10.1002/2015JD024334)

Line 185 – 187 What’s the point of this sentence?

Line 188: which version? Day / night / day+night?

Line 202 Does that mean you use the bin -9 to -12 for -10degC? Please clarify

Line 234 – 244 How does this relate to the rest of the discussion

Line 271: 10x10 seems very large. Did you try a sensitivity test at 5x5 that should be enough to gather statistically representative samples over 8 years.

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ED: Reconsider after major revisions (24 Jul 2016) by Johannes Quaas

AR by Jiming Li on behalf of the Authors (06 Sep 2016) Author's response Manuscript

ED: Referee Nomination & Report Request started (07 Sep 2016) by Johannes Quaas

RR by Anonymous Referee #2 (06 Oct 2016)

Suggestions for revision or reasons for rejection

The overall quality of the manuscript has improved and I appreciate the efforts of the authors in taking all of my suggestions into account. I still have a few more suggestions. Please see the comments below.

• Please have a native speaker proofread the manuscript. There are too many grammatically incorrect sentences present in the current version.
• Lines 70-73: There needs to be a reference after this statement, e.g.
1) Tan, I., T. Storelvmo, and M. D. Zelinka. "Observational constraints on mixed-phase clouds imply higher climate sensitivity." Science 352.6282 (2016): 224-227.
2) McCoy, D. T., Hartmann, D. L., Zelinka, M. D., Ceppi, P., and Grosvenor, D. P. (2015). Mixed‐phase cloud physics and Southern Ocean cloud feedback in climate models. Journal of Geophysical Research: Atmospheres, 120(18), 9539-9554.
3) Tsushima, Yoko, S. Emori, T. Ogura, M. Kimoto, M. J. Webb, K. D. Williams, M. A. Ringer, B. J. Soden, B. Li, and N. Andronova. "Importance of the mixed-phase cloud distribution in the control climate for assessing the response of clouds to carbon dioxide increase: a multi-model study." Climate Dynamics 27, no. 2-3 (2006): 113-126.
• Lines 116-118: I know what the authors are saying here, but this needs to be more thoroughly explained to a reader who is not familiar with this study.
• Section 3.2: I appreciate the explanations provided by the authors, but this section is not well-organized and needs to be re-written for the sake of the reader.
• Figure 11 and lines 547-556: Coming back to this, the original results combining the two hemispheres shown in the second round of revisions (originally d to f) should be shown here instead of the results separating the southern hemisphere (new figures g to i), the reason being that the southern hemisphere has far fewer aerosols compared to the northern hemisphere. Thus, just as how the correlations weaken or even vanish at colder temperatures as the authors have shown, the correlations between SCFs and aerosol frequencies are less likely to be statistically significant in the southern hemisphere, as the authors have already pointed out on lines 552-553 (the confidence level was reduced). It would therefore be more appropriate to show the more statistically robust results shown in the original Figure 11 instead of the less statistically robust results presented in the current version of the manuscript. Moreover, the fact that the aerosol product used in this study was the Level 2 product, which does not have the additional level of screening that the Level 3 product that Tan et al. (2014) used, adds to the level of uncertainty.
• Lines 560- 564: This statement implies a causal relationship based on statistical correlations, which is incorrect. One cannot be “certain” from the analysis that the meteorological parameters examined in the study impact the variation of SCFs. The authors need to be much more careful in their language and avoid making causal statements.

Referee Report: PDF

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RR by Anonymous Referee #1 (17 Oct 2016)

ED: Reconsider after major revisions (28 Oct 2016) by Johannes Quaas

AR by Lorena Grabowski on behalf of the Authors (28 Dec 2016) Author's response

ED: Referee Nomination & Report Request started (03 Jan 2017) by Johannes Quaas

RR by Anonymous Referee #1 (17 Jan 2017)

ED: Publish subject to technical corrections (19 Jan 2017) by Johannes Quaas

AR by Jiming Li on behalf of the Authors (20 Jan 2017) Author's response Manuscript

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Effects of atmospheric dynamics and aerosols on the fraction of supercooled water clouds

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