The paper makes use of downloaded data sets of combined CALIOP and CloudSAT observations (ice-phase retrieval products) and observations of the aerosol type (dust, smoke, clean=background sulfate, derived from CALIOP observations) in the upper troposphere over the Tibetan Plateau. Based on these downloaded products the authors discuss, mostly in a speculative way, cirrus formation processes (heterogeneous vs homogeneous ice nucleation) and what the impact of deep and strong cumulus convection to cirrus formation and properties is.

It remains unclear how they obtained the CALIOP aerosol information and how the authors combined this aerosol information with the cirrus formation (especially the ICNC data sets, ICNC= ice crystal number concentration). The authors show the final results (derived from the complex downloaded data fields) only. The reader has no chance to check the quality of the basic data, and how the authors processed the data. There are no case studies (individual scenes with vertical profiles of all downloaded and used cirrus and aerosol data ) in the manuscript that would offer the chance to check the data quality and the ways they combined the different aerosol and cirrus data sets.

In the discussion, the authors ignore the impact of dynamical conditions (gravity waves, large scale lofting, and lofting by orographic surface structures, etc.). Updrafts are needed to create the ice supersaturation conditions that are required to initiate nucleation bursts. Also, the impact of ice crystal sedimentation is mentioned only at the end of the manuscript.

The quality of the paper is very low. The discussion is filled with speculative statements. The authors must clearly indicate that they present hypothetical conclusions drawn from the observations.

In the present form, the manuscript cannot be accepted! Major revisions are need!

Point-by-point comments:

Page 5, line 15: To my opinion, one should include the ICNC solutions for particles with sizes > 25 micrometer as well. At least in some cases, >5 and >25 micrometer solutions  should be shown and compared.

Page 6, line 6: What are the criteria to identify dust in the CALIOP measurements? What are the criteria to identify wildfire smoke in the CALIOP measurements? How do you relate (link) vertical profiles of dust-filled  or smoke-filled pixels with vertical profiles of cirrus-filled pixels? Figures of individual cirrus observations are needed. One case with cirrus developing in dust, one case with cirrus evolution in smoke, one case in clean air!

You do not have aerosol and cirrus information  in a given pixel at the same time! How do you combine aerosol and cirrus information?

Page 6, line 13: What about recent smoke-cirrus papers: Mamouri et al., ACP, 2023, Ansmann  et al.,  ACP, 2025.

Page 6, line 12-16: Is smoke ice-active at temperatures around -30°C?  Is there any information about ice nucleation efficiency of smoke at a function of temperature in the papers you mention here?

Page 7, line 19: …. the number of occurrence of …. what?

Page 8, lines 20-22: Grid points identified as ‘clean’ are therefore considered to have undergone homogeneous nucleation. Again the question arise: How is ‘clean’ defined in the CALIOP data base, what are the criteria for ’clean’? During cirrus observations, you do not have aerosol profile information, and during aerosol profile observations there is probably no cirrus information in the pixels.

Page 9, line 9: Your average ICNC concentration of 187.48 L-1  is close to 150 L-1. This is  a rather low difference when keeping in mind that ICNC values can be in the range from 0.1 to 10000 L-1. What about information about the standard deviations, in addition to the average values? Should be mentioned, too! Please avoid numbers with two digits after the decimal point! Instead of 187.48  L-1 it is sufficient to write 187 L-1.

Page 9, line 14: Agreement with observations from 0.1 to 10000 L-1 (covering 5 orders of magnitude) does not indicate any level of reliability of your data.

Page 9,   lines 20-23: Numbers of 213 L-1, 253 L-1 and even 142 L-1 are so close together. I expected much larger, more contrasting differences between south and north. Why are the differences so low? Is that caused by all the DARDAR assumptions? Any comment?

Figure 1: What does it mean: The black dotted line represents a standard error of 60 L-1?  At the same time, the color plot shows ICNC values of 120 to 240 L-1? The same for the other 80 and 100 L-1 standard error lines? What do you want to say with these lines? Does that indicate the variability in the DARDAR data sets, or the errors in the colored values?  Please explain clearly what these error lines mean!

Page 10, line 15: This process enhances homogeneous nucleation…. thereby increasing ICNC over the southern region. How do you know? This is just your opinion (speculation). The impact of dynamics (updraft characteristics), aerosol and INP concentration levels at given temperature, and humidity conditions  is rather complex. Simple conclusions are thus impossible! This should be stated!

Page 10, lines 17-30: The same here! ‘Easy’ and trivial solutions and conclusions cannot be obtained or drawn! The occurrence of high water vapor levels is a prerequisite for the evolution of clouds. However, without exceeding the ice-saturation-ratio threshold value for ice nucleation, nothing will happen, no ice formation will be possible.  And here updraft occurrence (amplitude, speed, duration) comes into play.

Page 11, line12: … heterogenous nucleation of INPs promotes the formation of larger crystals. How do you know? This is not a ‘law’. The size of the INP reservoir and occurring strength of the updrafts (speed, length of updraft period) strongly influence the cirrus evolution. There is no easy solution available.. That should the basic message of the discussion.

Page 11, lines 17 -19: Such safe statements are welcome!

Page 12, line 7: Growth of ice crystals  plays an important role! Ice crystals growth has also an influence on the DARDAR ICNC values. For that reason, I want see at least some comparison of ICNC solution for particle ensembles  >5 and >25 micrometer. 

Page 12,  line 14: Please repeat briefly that you assume homogeneous freezing when CALIOP does not indicate the occurrence of dust or smoke, and the aerosol type is just  ‘clean’.

Page 13, line:  …below -38°C, ….. and when there are no INPs!

Pgae 13, line 5: Do not forget the importance of updraft speed and duration (determines how many ice crystals are produced), besides temperature.

Page 13, lines 8-13: The uncertainty in the DARDAR products is large, and the found differences in the ICNC numbers are comparably small! I do not think that it is possible to draw such clear conclusions and to make clear statements when the differences are so small? Please provide a more careful discussion! Avoid speculations!

Please include the impact of gravity waves and large scale dynamics and related updraft characteristics in your discussion! Simple conclusions, as presented, are not possible. You may provide your opinion and interpretation of the observations (given in the figures). But indicate, that your argumentation is just an option, a hypothesis!

To summarize my basic opinion: Clear conclusions cannot be drawn from the different scenarios with so small ICNC differences (shown in Figures 4 and 6), in view of the large uncertainties in the DARDAR products and the large natural (atmospheric) variability in the ICNC data, linked to the complex atmospheric impact (updraft frequency, speed, period, crystal growth and sedimentation aspects, crystal collision and aggregation effects, temperature and humidity conditions.). Strong updrafts may sometimes lead to ICNC of 500-2000 L-1. Weak updrafts may often lead to ICNC from 1-10 L-1.

Figure 4: I am confused! The green line shows observations and the red line shows homogenous nucleation. But the red line is also based on observations! … for the aerosol type ‘clean’.  If I am wrong, what did I overlook? What did I miss?

Page 14, lines 8-13: This is, to my opinion, speculation. This is your opinion. My conclusion is: The differences are not significant. The updraft impact is unkown. The authors did not observe significant differences for clean aerosol conditions (hom. Freezing) compared to dusty conditions (het. ice nucleation).

Figure 5: My question is: What do you get in the case of ICNC for particles > 25 micrometer? How do the features change?

Page 15, lines 1-18: Please provide some information about typical tropopause heights! Obviously very tropical condition prevail above the Tibetan Plateau. Please avoid numbers like 103.94 L-1, better state: 104 L-1. Strong upward motions do not only transport moist air upward but also ice crystals (outflow cirrus from dissolving convective cloud towers, often denoted as liquid-origin cirrus according to the papers of Kraemer et al.). Homogeneous freezing may occur, in addition, as a further option, not as the only option. Many statements are speculative, please indicate or emphasize the hypothetic character of your statements.

Page 16, lines 3-11: What about a possible quick depletion of the dust INP reservoir? Do you have CALIOP data that indicate that the INP reservoir is (always) very large so that a strong decrease of INP concentration is unlikely? Huang et al. (2021) is published in Plateau Meteorlogy. Please provide further references in well known journals.

Figure 7b: How are the profiles in Fig. 7b computed? Is that the average of all profiles used in Fig. 7a?

Page 16 lines 12-27: Now potential sedimentation contributions to ICNC at different height levels come into play, for the first time in this manuscript. The paragraph is full of hypotheses and opinion-like  statements. Please clearly indicate the hypothetic character of your statements. The atmospheric conditions, processes, and impacts are too complex to allow simple and straight forward conclusions and to provide the impression: We tell you the truth!  I leave out here to repeat my ‘warnings’ already stated above…. We need an open discussion, hypotheses are welcome, but we need to avoid the impression that we found clear results (answers) showing in detail and very clear how ice crystals  formed, either  via homogeneous or heterogeneous ice nucleation path ways, and what the role of aerosols, temperatures and water vapor is in these ice formation processes.

Page 17, line 5 to page 18, line 6: The paragraphs are again full of speculative statements. Again, we need an improved scientific discussion with clear indication that hypotheses are given. Speculations need to be indicated as such! Avoid speculation as much as possible!

Some remaining questions: How is smoke identified by using CALIOP backscatter and depolarization ratio information? As I know, smoke particles may be non-spherical when transported quickly into the upper troposphere but in the lower and middle free troposphere they are spherical and do not cause depolarization. In contrast, dust always shows high depolarization ratios! How can we unambiguously distinguish smoke from dust?

Figure 7b: What do you  mean with ‘non-dust’? Do you assume ‘clean’ conditions (homogeneous freezing conditions) or ‘clean plus smoke’ conditions?

Figure 8b: The same here! What do you mean with ‘non-smoke’? Do you assume ‘clean’ conditions (homogeneous freezing conditions) or ‘clean plus dust’ conditions?

At the end, the abstract and the conclusion sections need to be carefully updated when the revision of the main parts of the manuscript is completed.

Without significant improvement of the manuscript with my comment statement as a guide, I will not recommend to publish this study.

This manuscript presents a climatological analysis of cirrus cloud properties over the Tibetan Plateau, with a particular focus on ice crystal number concentration and its relationship to aerosols and different ice nucleation processes. The topic is scientifically relevant and clearly within the scope of ACP, and the overall methodological approach is interesting and merits further investigation. However, in its current form, the manuscript has several important limitations. In particular, some of the conclusions appear stronger than what can be robustly supported by the analyses presented.

I therefore do not recommend acceptance of the manuscript in its present state and suggest major revisions. The authors would need to strengthen and better document their analyses, clarify aspects of the methodology, and refine or more carefully justify several of their interpretations in order to support their conclusions. The general and specific comments below focus on the most significant issues identified in the manuscript.

General comments:

1. This manuscript makes strong claims regarding the impact of aerosols on cirrus clouds and the competition between homogeneous and heterogeneous ice nucleation. While I agree in principle that such effects can, and should, be observable to some extent, I do not find that the present study sufficiently supports these claims. First, the ICIC metric is somewhat unclear and would benefit from a clearer justification (see below). More importantly, comparisons between regions with differing aerosol concentrations may also implicitly involve comparisons between different meteorological regimes, which could explain at least in part the observed differences in Ni. This issue may be particularly relevant over the Tibetan Plateau, given the strong geographical and dynamical contrasts within the region. This point is partly acknowledged in Section 3.2.3, where the presence of dust and smoke is associated with weak vertical winds conditions. The manuscript would benefit from a more convincing effort to disentangle meteorological influences from aerosol effects, and at a minimum from explicitly acknowledging that the observed differences in the satellite data may not be attributable to aerosol presence alone.
2. I find the discussion of homogeneous nucleation to lack precision and, at times, to be misleading. On several occasions (see below), the manuscript refers to the “homogeneous nucleation of water vapour,” which is not physically possible in the atmosphere and therefore requires clarification. More generally, it is unclear throughout the manuscript whether the authors are referring to the homogeneous freezing of supercooled water droplets (particularly relevant in deep convective regions) or to the in-situ homogeneous freezing of aqueous aerosols under sufficiently high supersaturation (also relevant in this region). The manuscript would benefit from a more specific and physically grounded discussion of the ice formation processes being considered. In addition, clarity would be in my opinion substantially improved by explicitly distinguishing between in-situ formed ice and liquid-origin ice in the discussions.
3. Several datasets are used simultaneously in the analysis. While each of them appears reasonable and of good quality, they have different sensitivities and retrieval characteristics (e.g., Ni from combined lidar-radar retrievals, IWC from radar-only retrievals, and aerosol classification from lidar-only observations). These differences could substantially influence the results and their interpretation, and the associated limitations should be discussed in more detail.
4. Specifically, the aerosol product is not sufficiently described. It would be helpful to specify the exact CALIPSO aerosol product used (product name, version, and horizontal/vertical resolution), and to clarify whether the aerosol information was temporally and vertically colocated with the cirrus observations, or instead whether any aerosol detected within the full column and/or within a given grid cell was considered. In addition, it would be useful to clarify whether aerosols are expected to be reliably detectable in the vicinity of deep convective events with the chosen approach, and to discuss the implications and potential limitations of the method used.
5. The ICIC (IWC confined INPs concentration) variable is also unclear. It is described as “the logarithm of the ratio between the number of smoke (dust) particle occurrences and the IWC in each grid cell”, with no further justification. Is there a reference for this technique, or at least provide a justification as to what

Specific comments :

1. Page 3 lines 22-24: This statement is misleading. Homogeneous nucleation of water vapour does not occur in the atmosphere. The wording should be revised accordingly.
2. Page 5 line 4: Please specify more precisely which months are included in the definition of “summer.” In addition, please clarify whether both daytime and nighttime measurements are used. If so, it would be important to discuss whether the absence of nighttime CALIPSO retrievals after 2012 has an impact on the analysis and results.
3. Page 8 lines 6-8: As noted above, homogeneous freezing near -38°C applies to supercooled water droplets and aqueous aerosols, not to water vapour itself. This sentence should be corrected accordingly to avoid confusion about the underlying physical process.
4. Page 8 lines 9-12: “However, due to the continuous dynamic growth of ice particles through condensation, accurate simulation remains challenging. Moreover, purely homogeneous nucleation events are extremely rare in the natural atmosphere.” - This statement would benefit from further clarification and appropriate references. In particular, the claim that purely homogeneous nucleation events are extremely rare is not self-evident in the context of this study, given that the manuscript aims to identify signatures of homogeneous freezing from CALIPSO observations. Additional justification and supporting literature should be provided.
5. Page 10 lines 26-27: “For example, high Ni in one grid cell could be due to abundant water vapor rather than the effect of INPs” - Please clarify what is meant by this statement. Specifically, does “abundant water vapor” refer to higher supersaturation leading to enhanced in-situ ice formation, or to the freezing of water droplets within deep convective updrafts (i.e. liquid-origin ice)? Clarifying this point would help to better interpret the role attributed to INPs.
6. Section 3.2.1 and Figure 4: It would be helpful to explain more clearly how “observations” and “homogeneous nucleation” are distinguished using the satellite dataset, as the basis for this separation is currently difficult to follow. In addition, the interpretation that lower Ni reflects heterogeneous nucleation suppressing homogeneous nucleation would benefit from further justification, since alternative explanations also seem plausible. For instance, lower Ni could reflect weaker or less frequent updrafts (and therefore lower supersaturation), or differences in cloud origin (e.g., predominantly in-situ cirrus with limited contribution from liquid-origin ice detrained from deep convective updrafts).
7. The inferred influence of aerosols on cirrus clouds in Figure 5 currently appears rather speculative. It would be helpful to further analyse and quantify the relationships shown in the figure to better support the proposed interpretation, potentially by combining the cirrus properties with the aerosol information (e.g., aerosol occurrence/classification) in a more explicit way.