General comments:

(1) There is a lot of really interesting material here, but it seems somewhat unfocused and in places a little confusing.  The manuscript is way too long for the average reader, I suggest tightening it up quite a bit and or consider writing two papers.

(2) SIC in the stratosphere might suggest moistening (as the authors state), but interest in that process is mostly associated with convection penetrating the tropical tropopause.  In this paper, the extra-tropical and tropical SIC are sort of lumped together.

For example, SIC moistening in the stratospheric extra-tropics is unimportant since air is moving downward there and will soon exit the stratosphere.  Whereas SIC in the tropics is very important since air is moving upward and SIC could be changing the water vapor budget. I guess my point is to wade through 34 pages of material here, the motivation could be clearer.

(3) I think the correlation with gravity waves is really part of the correlation with tropopause temperatures and isn’t a separate effect.  In Fig. 5 you see that the correlation maps (5a) and (5b) are nearly identical. As noted below, the cold temperatures are due to a number of things and gravity waves will be one of them, I am not sure how you separate them in a correlation sense, but I am pretty sure they overlap.

(4) The SIC correlation with aerosols is interesting, but aerosols are associated with fires as well as volcanoes.  The CALIPSO measurements are a direct measure, I don’t see how SO2 adds anything to this analysis.  You should also mention more clearly why you are correlating with aerosols. Basically, aerosols provide CN and thus clouds form at lower RH so cloud formation should be approximately correlated with aerosols if the environment is at saturation. Volcanic eruptions and fires contain a lot of water so there might be other things going on.  I would argue that this whole analysis might be a separate and interesting paper.  BTW, OMPS-LP also produces an excellent aerosol data set that is independent of CALIPSO.

(5) One question I was left with is: Do SIC occurrences well above the tropopause differ from those that are near the tropopause.  Your statistics in Figure 1 suggest occurrences up to about 1 km above, but are the outliers very different?  Those clouds have more of a potential of moistening the stratosphere.

Please focus Abstract on salient points, it is way too long.

Specific comments

Ln 38 net radiative heating?  You need to be careful here.  High thick cirrus will produce surface heating by blocking IR cooling to space. Do you mean in situ cooling?

Ln 43 Paragraph starting line 43, I presume you are not including Polar Stratospheric Clouds in this discussion. What does ‘high altitude’ mean? Above the tropopause?

Ln 59 Sentence starting with ‘With … ‘  makes no sense to me.

Ln 67 Awkward English. ‘Nucleation of ice crystals occurs in the presence of cold temperatures.’

Overall comment on ln 34-119.  On one hand this is a very thorough review of the literature, but its goal is occasionally illusive.  Here is what I got from 80 lines of text:

Ice clouds form in cold temperatures

Cold temperatures are due to dynamics.

Ice clouds are also injected by convection

Aerosols impact cloud formation

I suggest that the reader might benefit from a reorganization of this material along these points.

Ln 148  Spline interpolation can produce a new minimum temperature which is colder than the adjacent model levels, and the actual location of the minimum between the two model levels is unknown.  Given the reliance of this study on the exact location of the tropopause, it seems appropriate to have more extended discussion which occurs later in the paper.  Perhaps you could move that here.  More explicit discussion of the uncertainty in the tropopause height might me appropriate.

Ln 157 CALIPSO averages their backscatter data over many profiles – this averaging is the effective along track resolution of the data. You should mention this.

Ln 164 I don’t see why you are including daytime aerosols.  The S/N during the day drops significantly. If ice cloud detection is affected, aerosols will be worse since their backscatter cross section is smaller.

Ln 169 You should mention earlier that this study is not including PSCs.

Ln 180-190 I am surprised that you are using AIRS for deep convection. MODIS has the same channels (and others) and is more frequently cited for identifying cold cloud tops in the 8 and 10.6 µ channels.  Furthermore, MODIS or VIIRS has higher spatial resolution.

Ln 205 Gravity waves at 4µ are detected in the 30-45 km region (see Hoffmann and Alexander (2010), Fig. 3).  These waves, propagating vertically, will have much lower amplitude at their tropopause source.  For example, assume the wave is detected with a 0.5 K BT temperature (e.g. Hoffmann and Alexander Fig. 1) and using their the center of the weighting function, this wave is at ~40km, then the amplitude of the wave at 18 km will be about 0.05K by energy conservation.  There is also a spatial correction, as the wave move from the source it will decrease in amplitude.  For example, let’s say the wave is detected 1000km from the convective system and the convective system has a radius of 100km. Then the source wave will have an amplitude 3 times larger than the detected wave.  The author needs to discuss these possible or indicate why they are unimportant  corrections.

Ln 213  The difference between 7.1µ and 7.3µ bands as a method of estimating SO2 assumes you can neglect water vapor which will be important where the tropopause is below 8 km.  Volcanic SO2 is more easily detected in the UV bands – OMI on Aura is making those measurements coincident with CALIPSO and AIRS and might be a better choice.  I am still unsure why we should even use SO2 data since the aerosols come from CALIPSO and SO2 will not be evident in aerosols due to fires.

Ln 227 ‘over the tropical continents.’

Ln 228 Awkward wording… ‘The weakest signal..’

Ln 250 SIC associated with double tropopause are clearly an ‘edge of the tropics’ phenomenon – not surprising since that is where double tropopauses occur.  I am not sure why these are important.  They aren’t contributing to dehydration of the stratosphere and double tropopauses are often associated with cloudy systems so I am not sure of their impact on the radiation budget…

Ln 275 Kim et al. emphasized the cooling rate, not just the low temperature was associated with cirrus. Obviously, you need to have a saturated environment for clouds to form, cooling the air creates saturation and ice crystals form. But once they form, they fall out so if the air is just cold and not cooling you don’t see as many clouds. I think you should clarify this point.

Ln 290, Ln 304-6 What is the explanation for positive correlations? SIC’s show up where temperatures are warmer. Ln 306 appear to be guesses. You might consider that the positive correlations are associated with cooling air not cold air as suggested by Kim (see above).

Ln 335 Convection will push the tropopause upward.  So what you are doing here is finding the deep convection using AIRS and then interpolating the ERA5 tropopause height onto the point, and if the cloud observations are above the ERA5 tropopause it is a SIC.  How do you know you have correctly located the tropopause?  In fact, you don’t know if the cloud is above or below the tropopause and thus whether it is truly a SIC. You need a coincident temperature profile (perhaps GPS) to prove this.  At least give the reader some idea of the uncertainty in these estimates for the tropopause in these cases.  

BTW, radar measurements over the US coincident with soundings show that convection drives the tropopause upward, collapses and leaves behind a residual cloud.  You should quote some of these references to justify your assertions.

Ln 349-356 This discussion doesn’t add anything to the paper.

Ln 364 ‘measurements are not significantly observed in tropics’ ???

Ln 358-384 Since SICs at high latitudes are correlated with cold temperature anomalies and cold temperature anomalies are correlated with gravity waves, I am not sure I understand how these terms are independent in Fig 5. In fact, the correlation pattern in Fig. 5 are almost identical.  I suggest that you present a map of correlations between temperature anomalies and gravity waves… This might give us more insight as to the causes.  More specifically, cold temperature anomalies can be generated by mesoscale events as well as gravity waves.  It is of interest to separate the two which I think might be lumped together in your analysis.

Ln 385 I am not sure why you are even using the AIRS SO2 since CALIPSO measurement of  

aerosols is more of a direct measure of the influence of aerosols on cloud formation.

Furthermore, aerosols are also due to fires (see the anomaly at end of the period shown in Fig. 10 which is the Australian fires.) – see major comments.

Ln 427  Spearman

Ln 460 Table not Tab.

Ln 467 where did ‘Atmospheric Turbulence’ estimation come from?

Ln 481, 485 Fig. 6a

Ln 475 to 485.  This is a very interesting discussion but still does not incorporate the point that deep convection can push up the tropopause so that SIC observations that are apparently above the tropopause are actually in the troposphere.  Unless a GNSS RO measurement is made exactly at the right spot, the ERA5 reanalysis will place the tropopause at the wrong altitude.

Ln 494 It seems to me that the event frequency will over emphasize the SIC occurrence above convection. If you’re trying to connect these observations with stratospheric hydration (which is why I am interested in this) then occurrence frequency is the appropriate measure. If you are interested in the morphology of these events, then event frequency is appropriate. It might help to discuss some of these issues at the beginning of this section to motivate the reader.

Ln 511  OMPS-LP makes aerosol limb measurements and is active for most of the period you studied.

Major comments

I will start with what I think is a methodological problem. On line 489, you state that "clouds are labeled as deep convection if the cloud top brightness temperature is close to the tropopause temperature with an offset of 7K from the tropopause temperature". If I understand this, and the explanations of section 2.3, correctly, "deep convection" then means "AIRS has observed a cloud with a top temperature close to (ie as high as) the tropopause temperature". In other words, "deep convection" is not derived from a dynamical measurement, but implied by the detection of a high-altitude cloud (taking into account the detection sensitivity of AIRS). Thus your comparison of stratospheric ice clouds (from CALIOP) with "deep convection" (from AIRS) is really a comparison of stratospheric clouds (seen by CALIOP) with high tropospheric clouds (seen by AIRS), i.e. a comparison of cloud detection sensitivities of both instruments. Differences between both retrievals will be mostly attributable to instrument strengths and weaknesses considering various cloud geometries, and not to processes that might lead to formation of stratospheric cloud (like convection). I would appreciate if you could address this point and either take it into account somehow it in your comparison, or justify why you think your comparison goes beyond a comparison of instrument sensitivities. Moreover, this issue creates a problem for the definition of deep convection. AIRS detecting a high tropospheric cloud in the tropics can indeed imply "deep convection" is occurring (as deep convection is probably the mechanism that brought the observed cloud near the tropopause), but in the midlatitudes and the polar regions convection is not required to create clouds near the tropopause. Calling AIRS high tropospheric cloud detections "deep convection" outside the tropics feels wrong to me. Considering this, you might want to change the name of "deep convection" in the paper to something else ("high tropospheric clouds" ?).

Minor comments

1. l. 13-20: The past time makes it unclear who did the things explained. "Relations... were analyzed" -- analyzed by who?
2. l. 47: "For example, 7% of observations..." in your 2021 paper, the number given was 2.5%. Which is correct?
3. l. 148: "in previous studies..." this sentence suggests that the cited articles used ERA-Interim to derive the tropopause altitude. Please mention it explicitely. Also: it's unclear to me why a 2x resolution improvement means the threshold for tropopause can also be cut in half. Other considerations than vertical resolution influence the accuracy of the retrieved tropopause, and the distance you wish to impose on that tropopause to make sure one is in the stratosphere. Would ERA6 improve the vertical resolution 10x, you would still need to consider a larger threshold to account for other sources of uncertainty.
4. Sect. 2.2: in this section, you explain how from the CALIPSO VFM product you use cloud data, but also aerosol data. I must admit I was confused at that point since I had missed that one of the objectives of the paper was to contrast the presence of stratospheric ice clouds with the occurrence of stratospheric aerosols. As far as I can tell, the paper's objectives are only explained in the sentence l. 122-124. It might be good to expand a bit this sentence to make sure other readers will not miss it.
5. l. 163-165: I don't follow the reasoning that justifies why daytime and nighttime data are used for aerosols but only nighttime data for ice clouds. Why should "aerosols are long-lived" justify using both daytime and nighttime data? Why is increased nighttime SNR (=improved detection abilities) a good reason to use only nighttime data for ice clouds, but not for aerosols? Will not this difference in datasets influence somehow the comparisons between stratospheric clouds and stratospheric aerosols? Please clarify your reasons why keeping only the nighttime data for clouds and using both daytime and nighttime data for aerosols.
6. l. 169: PSCs often reach latitudes lower than 60°. In the north hemisphere, they were observed as far down as the Mediterranean sea : https://doi.org/10.5194/acp-7-5275-2007 I'm afraid your criteria to exclude PSCs will still lead to a large presence of PSCs in your stratospheric cloud dataset, and the presented results suggest this to be true. I suggest that PSC *are* stratospheric clouds, and the distinction you're trying to make here between PSC and other stratospheric ice clouds is not really possible -- above a given latitude, all stratospheric clouds are PSC, by definition. But not all PSCs are ice. It is unclear to me if the paper wants to include ice PSCs within the boundaries of the dataset under study, or not. Limiting the geographic scale of the study, for instance to only show latitudes below 60°, would put a limit on the importance of PSCs in the dataset considered, and in the results presented.
7. l. 171: "SICs detected at high latitudes will not be discussed in detail in this work". This is good, but all your maps still show latitudes and results above 60°. For example, the same map will mix stratospheric ice clouds along with polar stratospheric ice clouds. However, at high latitudes, only parts of the observed PSCs are shown, given the filtering described on l. 169. Thus what global maps show at high latitudes is neither representative of convection-based ice clouds, nor of polar stratospheric clouds, and I'm concerned these figures could at a glance be misinterpreted by a too-quick reader. I would appreciate if high latitudes, where the dataset under study is probably dominated by PSCs but omits an undefined amount of them, where hidden from the global maps.
8. Sect. 2.3: Many parts of this section are very similar to section 2.3 of Zou et al. 2021 (a section with more or less the same name). I've found at least one sentence that is exactly the same. Please revise this part to see if you could perhaps just reference the previous paper.
9. l. 181: could you please be more specific when you reference the 7 articles here? ie cite each paper separately when it is most relevant.
10. l. 221: "lower stratospheric ice clouds": What does "lower" mean here? I don't think low stratosphere and high stratosphere were defined so far in the paper.
11. l. 222: "Ice clouds with cloud top heights at least 250m above the first tropopause were defined as SICs" I think this has already been explained.
12. l. 248: "The occurrence of double tropopauses in general greatly impacts the SICs’ occurrences associated with double tropopauses. " I'm not sure I understand this sentence. As I read it, I think it means that when there is no double tropopause, there are no SIC associated with a double tropopause? Please clarify.
13. Figure 1. These figures show SICs are quite frequent over the Antarctic Peninsula in all seasons except DJF (Antarctic summertime). This supports the idea that the SIC dataset includes a non-negligible part of PSCs.
14. l. 258: thermal tropopauses are notably hard to retrieve over the polar regions, where the temperature gradient gets mostly flat in the stratosphere. It is not clear to me that retrievals of multiple tropopauses in those regions are neither reliable nor meaningful. What is the meaning of mutiple tropopauses when the temperature profile is flat?
15. Figure 2: In this figure, I doubt the relevance of multiple tropopauses that appear above 60°N and above 60°S. See previous comment.
16. Figure 3: This figure is very pretty, but it does not support the discussion very well. The text discusses the differences between years, and the average yearly evolution of the SIC frequencies. This discussion would be better supported by showing the average yearly evolution of SIC occurrence (ie the same Hovmoller plot as Figure 3 but for months averaged over 2007-2019), and maybe in addition a plot showing the monthly anomalies of SICs occurrence averaged over the ±20° region (I'm not sure the discussion discusses the small variations that occur outside of this latitude range).
17. Section 2.3: I find this section quite confusing. It does not include the easiest way to look for a correlation: a scatterplot. Why not plot first the frequencies of SIC in 5x10° cells against the average tropopause temperature in the same cells? This would let you first conclude on the existence of a correlation between both quantities. Then figure 5 would let you identify regions where the correlation is positive and where it is negative, and finally figure 6 would let you identify possible variations of these correlation signs in time.
18. l. 289: I understand that a positive correlation means that SIC are more frequent when the tropopause is warm, and less frequent when the tropopause is cold. If that is your understanding too, could you propose some kind of explanation or process responsible for positive correlation? This result is clearly at odds with the findings of the articles you cite, and cannot go by unadressed.
19. figure 5: When first reading section 3.4, only figure 5a is discussed. The other three figures are discussed further down. This is unusual and should be adressed somehow in the text or the legend.
20. l. 296-300: providing pseudocode is not required for such a simple operation. The explanation lines 294-295 is enough.
21. figure 6: like with figure 3, I'm not sure the plot supports the discussion in an optimal way. The anomalies in SIC frequency shown in Figure 6A are very weak almost everywhere except in the ±20° band -- most of the plot is not useful. In my view it would be much more readable to provide simpler line plots that describe the average anomaly in different latitude bands -- for example one line for ±20°, one for > 20°N and one for < 20°S. The same quantity of information would be offered, and the correlation/anticorrelation with the temperature anomalies would be much easier to see.
22. l. 307-308: "tropopause temperatures are negatively correlated with the occurrence of SIC... especially over tropical continents" you already concluded that from figure 5. Compared to figure 5, figure 6 adds the time periods and latitude bands where the correlation was positive and where it was negative. This is what should be discussed when focusing on this figure.
23. l. 314: In my understanding, deep convection is triggered by strong sunlight over water vapor-saturated areas, and occurs primarily in the tropics, especially in the warm pool and over the ITCZ -- see for instance https://doi.org/10.1016/j.atmosres.2020.105244 that provides an example of such a definition. "Deep convection" then means convection that is triggered near the surface and generates vertical motion all the way up to the tropopause (hence the "deep"). In your plots (figure 7), the warm pool appears as a minor hotspot of deep convection, and the ITCZ is not really visible. Moreover, your plots suggest that deep convection is very frequent over, for example, the northern Atlantic (30°N-70°N) -- all during the cold, sun-deprived wintertime (DJF). I find all this very puzzling, and would appreciate if you could clarify the meaning of "deep convection" that you support in this article. Could you perhaps cite articles that support this definition? (note that my first major comment somewhat fixes that confusion, by clarifying that "deep convection" in the text really means "a cloud observed above the tropopause by AIRS")
24. section 3.4: Figure 9 clearly shows that the gravity waves considered in the present article (and derived from AIRS) are mostly related to the presence of the polar vortex -- polar gravity waves above 60N in DJF and above 60S in JJA dominate the figures. There is some limited GW activity visible in the tropics, for instance in DJF, but it is clearly minor compared to the polar regions. Gravity waves have been known to trigger PSC formation above mountains for quite some time, especially ice PSCs (see for instance https://doi.org/10.5194/acp-4-1149-2004). Trying to relate this GW activity with SICs will naturally lead to results dominated by PSCs. Again, it is a major problem to me that your paper does not address the confusion between stratospheric ice clouds in the Tropics (that can be generated by deep convection) and stratospheric ice clouds in the polar regions. PSCs are related to the polar vortex and are only partially represented in your dataset, both intentionally (as you filtered out some of them on purpose) and unintentionally (PSCs are optically thin and require specific detection and identification techniques). Given the object of study of your paper, I think it is necessary to make stronger efforts to exclude PSCs from the input dataset but also from the presentation of the results.
25. l. 385: Figure 10 is in my opinion way too busy to provide the basis for a reliable visual identification of correlations between stratospheric aerosols related to eruptions and SIC. It is too easy in my opinion to visually miss important features. Like with figures 3 and 6, the use of an Hovmoller plot is overkill and your interpretation would be much better served by zonal average plots.
26. l. 413: Reverdy et al. 2012 do not use the CALIOP level 2 product that is used in the present article. Please clarify what misclassifications you imply, supported by more relevant references.
27. l. 428: "three regions..." how or why were these three regions selected? What makes them special a priori? Why aren't the other regions worthy of their own correlation plots? Besides, it is unclear to me what the three full-page figures 13, 14 and 15 bring to our understanding of what drives the evolution of SIC. The figures-to-text ratio (3 pages of figures for less than one page of text) is off here. The text l.431-459 discusses when SIC occurrence is most correlated with a given metric and when it is correlated with another metric. Maybe only the metrics with an average correlation coefficient above a given threshold could be shown, or figures 13 to 15 could be moved to an appendix.
28. l. 473 "solidly": Do you mean here that your analysis was good?
29. l.473 "250m is a reasonable tropopause threshold..." again, I do not find this argument convincing.
30. Section 4.2: see my first major point.
31. l. 494-499: I think this has already been explained in lines 194-199.
32. Figure 16: same remark as before on the limited usefulness of Hovmoller plots

This manuscript presents a thorough evaluation of the global occurrence of stratospheric ice clouds (SICs) and their relationships with tropopause temperature, recent deep convection, gravity waves, and stratospheric aerosols. Potential relationships with modes of climate variability (QBO and ENSO) were also examined, but did not reveal strong association. The identification of SICs is based on the CALIPSO lidar observations, which are arguably the best available resource for global analysis, complemented by additional high-quality, satellite-based identification of the remaining parameters related to SICs. It was demonstrated well throughout that tropopause temperature and convection/gravity waves are strong controls for the occurrence of SICs, as expected. The analysis presented is thorough and the methods used are appropriate. It will be a meaningful contribution to the literature. I have one general comment related to an important element of the discussion that I believe is missing, but otherwise only a collection of suggested minor edits.

General comment: an important limitation resulting from the use of CALIPSO data is bias introduced by the lack of sampling the diurnal cycle (critical for evaluating deep convection and, one would assume, much of the related SICs). I do not know how large the bias would be and am not aware of studies that allow one to quantify/estimate it well since it will be dependent not only on the frequency of sources, but also on the timescale of sublimation (which implies microphysics may be important, etc.). However, I do expect it is significant (especially over land masses). For example, overshooting convection in North America has a pronounced diurnal cycle with a frequency maximum that falls almost entirely between the CALIPSO sample times (e.g., see 10.1175/JAMC-D-15-0190.1, 10.1002/2017JD027718, & 10.1029/2021JD034808). Other regions with frequent land-based overshooting storms have similar diurnal cycles. This suggests that much of the SICs that occur may not even be sampled, especially over land. Thus, the discussion throughout the manuscript requires an acknowledgement of this bias and how interpretations of the results might change.

Minor suggested edits: 

Line 17 - "and western" should be "and the western"

Line 37 – “hydrate stratosphere” should be “hydrate the stratosphere”

Line 40 – “, intensity” should be “, and the intensity”

Line 49 – “Six encounters…” the opening of this sentence is poorly phrased. Please revise.

Line 72 – “ice clouds” should be “ice cloud”

Line 78 – “are” should be “is”

Section 2.1 – I recommend defining the first and second lapse-rate tropopauses as LRT1 and LRT2, respectively. LRT is commonly used in the literature and helps to clearly communicate the definition used throughout. I would also recommend not bothering to define a cold-point tropopause acronym, since it is only used here.

Line 262 – recommend revising “motion of the Sun” to “location of peak insolation”. The sun isn’t moving…

Figure 2 – is this analysis relative to all observations or DT events only? Please add note to clarify.

Line 400 – “we” should be “were”

Figure 12 and related analysis – the overlap of several regions seems undesirable. It would be good to test sensitivity to having them be defined more exclusively.

Line 427 – “Spear-man” should be “Spearman”

Line 448 – “Two” should be “The two”

Line 480 – “in average” should be “on average”

Line 486 – “, lowering” should be “, and lowering”

Line 527 – “In the MIPAS” should be “In MIPAS”

Line 588 – “tropauses” should be “tropopauses”

Line 599 – “its” should be “their”