This paper presents a wide-ranging exploration of low-level Arctic cloud occurrence and associated processes based on CloudSat-CALIPSO data. The topic is quite important given the role that clouds play in the Arctic system, and the satellite perspective given here is a valuable expansion on past information available for Arctic clouds. While I believe that many of the presented results should be published, this paper is not yet close to being ready for publication. Details are given below, but here is a summary of the key problems:

• There is not enough description of some key aspects, especially regarding the MLR analysis and how some of the parameters are calculated.
• The impact of the 7-day averages is insufficiently explored and discussed. 7-days will include significant transitions in airmasses and clouds that may obscure key results. Other averaging windows should be explored.
• The effect of the blind zone (<0.5km) is not sufficiently addressed. It should be evaluated compared to other observations and understood relative to the MLR analysis. The implication of this blind zone on distinguishing MPC and USLC needs to be explored. Additionally, the language used often suggests that this paper’s results represent all low clouds, but an important sub-set of low clouds is missing. The language needs to be clear on this point throughout.
• It appears that the 0.5-3km height range is referenced to “mean sea level” instead of “above ground level,” which is a major problem for all observations over land.
• The MLR analysis is not very effective at providing robust and convincing explanations for cloud patterns. Is it not clear which results are “significant” and which are not. Some conclusions that are drawn appear to contradict prior knowledge from the literature. These require more explanation and observational evidence. Additionally, the difference between LTS and MCAO (which are very much related to each other) must be taken into account in any interpretation of stability.
• There are many process-based conclusions drawn that invoke processes that are not actually observed (i.e., entrainment, surface fluxes, cloud persistence, etc.); speculation is ok but should be labelled as such and supported by real results.

I note that this is the first time I have seen this manuscript, but that it is apparently a reworked version of a prior submission. While I do not have access to the prior reviews, based on the authors’ own description of what they have changed in the manuscript, it seems that they have only been partially successful in addressing the prior reviewers’ concerns. 

Overall, during my reading, the paper started out accessible and easy to digest but later became harder to follow, in part because of the vast amount of information and lack of coherent results from the MLR analysis. Based on all of this, the authors could consider splitting the manuscript in two parts: one that deals with the occurrence observations and more fully places them in context of other observations including a detailed assessment of the impact of the blind zone; while the second paper would provide a more clearly described MLR / coupling analysis.  Of course, this sounds to be a bit contrary to what reviewers of the prior manuscript suggested (i.e., they apparently recommended pulling information from appendices into the main text). Thus, the authors could also stick with this single paper approach, if they think it is more effective. Either way, major revisions are needed before this manuscript could be considered for publication.

Specific comments.

Line 30-33:  This sentence makes it sound like it is an “overestimation” of the liquid cloud fraction. But I think that is not true.  Perhaps it is meant that the liquid cloud fraction is “inaccurate,” but this sentence should be clarified so the intent is not left unclear based on the sentence structure.

Line 33-35:  This notion has been well established long before Raillard et al.

Line 37-39: This sentence is structurally incomplete.  You could add commas after macrophysical and microphysical, which might make it better, or revise otherwise.

Line 42-43: The studies in question are not “case studies.”  They are long-term observations at fixed observatories. One can certainly make the argument that they only represent specific locations, but not that they are case studies.

Line 45:  “between” should be “among”

Line 55:  “peculiar” should be “particular”

Line 57-58:  This comment is for space-based lidar only.  Ground-based lidar views from the other side and does not have a problem observing the ice falling out of these clouds.

Line 61-63:  This whole discussion (the whole paragraph) is based on the satellite perspective and not the ground-based perspective. It should be clarified at the top of the paragraph that this is only relevant for satellite perspectives.   Additionally, there are a number of papers that defined mixed-phase clouds from the system and process perspective, where even if there is a region of only ice below a region of liquid or mixed-phase it is classified as part of the same mixed-phase cloud system because that is where the ice formed.

Line 15-113: Overall, this introduction is an incomplete representation of the background literature on this topic. Importantly, the missing literature discusses some of the points that this paper claims need more attention.  I agree that more information is needed on Arctic low-level clouds, and thus this paper is indeed valuable, but the arguments for what this paper achieves relative to past work should be on more solid footing.

Line 129: Why is this thickness limitation put on supercooled liquid water layers?  Is there a justification for it?

Line 130-132:  Does this statement mean no lidar attenuation and/or no radar detection signal?  Or does it mean no lidar attenuation and/or yes radar detection signal?  The language is unclear.

Line 134-143: It is good that this source of underestimation is acknowledged, however, at no point in the paper is the implication of this blind zone on the results discussed. There are many Arctic clouds that occur below 500m, as clearly shown by numerous aircraft- and ground-based observations. This seems like an important limitation that warrants further context and a detailed explanation of how it impacts the basic results/conclusions of the study. There should be an independent evaluation of these results based on, for example, ground-based observations at specific sites, to provide the reader with the anticipated underestimation of cloud occurrence due to this height limitation.      Additionally, it is noted here that the blind zone for CloudSat is dependent upon surface type, yet I believe that the 500m lower limit is used everywhere. How does this impact the results over land, where the blind zone is known to be deeper?       Lastly, this statement about 500m being “a good compromise” between two factors is problematic.  It should not really be about compromise but should instead be about ensuring that the classifications are accurate. The compromise language makes it sound like the trade off is between adding more data at lower levels while also allowing some contamination by ground clutter influences.  In my mind that is not a good compromise because it just adds bad data into the data set in order to extend it to lower altitudes. Is that the intended compromise?

Line 157:  This says 4 categories, but then the list gives 5.  The last 3 are subsets of the 2^nd. So somehow the language around this should be adjusted.

Line 162: The USLC class is emphasized in this paper as being an important new topic. First off, I do not agree that it is a new focus, as liquid-only clouds have been discussed in the literature on Arctic clouds since the 1970s. But, beyond that point there are some significant uncertainties with identifying this cloud type and distinguishing it from others. My list of comments/questions include:

• There is no indication in this manuscript of how CloudSat observations are used to determine if there is ice precipitating out of low-level, supercooled liquid-containing clouds. Given that ice production in these clouds is often very weak, how does the long range gate of CloudSat impact its ability to identify falling ice? What is the reflectivity threshold used to identify ice from other types of hydrometeors?
• The ice in statiform mixed-phase clouds is typically at the bottom, because it falls out of the liquid layers. These measurements are unable to observe the lowest heights of the atmosphere where that ice would be. Based on robust ground-based observations, there are many Arctic clouds with a top around 500-700m with ice falling out that would be in the blind zone of these measurements (and thus erroneously identified as USLC). What is the impact of these cases on the results? This would be a one-way issue where USLC is overestimated at the expense of MPC.
• For any of these clouds, it has not been clarified how liquid-phase precipitation factors into the classifications. Presumably most of the liquid phase precipitation from shallow clouds would be in the “warm clouds” category. However, there is certainly drizzle that also occurs in mildly supercooled clouds. This notion is also physically consistent: If there are indeed such a high fraction of USLC as suggested here, this must mean that there are simply not enough INPs to form ice. It is well known that there are also not many CCN in the Arctic (apart from pollution events), meaning the formation of large drops and thus drizzle formation. The challenge here is that drizzle and falling ice look similar from a radar perspective. Some comment on this issue is needed.

Line 166-169:  In one sentence it is stated that the occurrence of MPCs can be “overestimated” compared to others.  Then in the next statement it is noted that these issues lead to “uncertainties.”  An overestimate is a bias not an uncertainty.  It is important to be clear with true sources of uncertainty (i.e., could go either way) versus bias (only goes one way) as these are important for the interpretation of the results.

Line 181:  I do not see where ~3% comes from in the Supplemental material.  I do see a reference to 5% and some other numbers.  How do you arrive at this estimate of 3%?

Line 190-192: LTS, EIS, and MCAO are all similar measures, just defined at different heights. What is the meaningful difference among these for this application?

Line 195:  “… account for the type of surface underlying the cloud:…”

Line 202-209:  I assume that AOD information is only available above clouds, correct?  Given the strong stratification in the Arctic, how is it known if this aerosol interacts with the clouds?   Broadly, given the small effect found for the aerosol, the uncertainties with observing it, and the uncertainties involved with trying to relate the observed aerosol with the observed clouds, I do not see the value in including this parameter in the study. If it remains, a lot more supporting information is needed. But in my opinion, this represents unnecessary and un-useful information that detracts from the manuscript’s other messages.

Line 212-217. The text states that a 7-day average is “well suited to capture synoptic variability.”  By “capture,” I take this to mean “resolve” in some sense. However, I do not believe that 7-day resolution is sufficient to resolve the synoptic variability that drives Arctic clouds. Yes, these clouds can be long-lived, but there is a great deal of variation that happens on scales well less than 7 days. Thus, any given 7-day sample will contain a range of conditions that may not be narrowly representative of the state that is suggested by the average over this time period.  As an example, simply examine a timeseries of surface temperature at a given Arctic location. 7-day averages will substantially diminish the variability related to synoptic-scale variability of the clouds. Or from another perspective, it is highly likely that there will be a significant synoptic shift within most 7-day samples (i.e., a shift in airmass associated with a front) such that the 7-day value would aggregate information from two (or more) entirely different circumstances.  I understand that there is a trade-off here, and that a longer time period is needed to get statistically robust observational signals, but it is also important to be clear that averages in this way will erode the ability to clearly distinguish the relationships between environmental factors and cloud type, which vary on time scales that are not well “captured” by 7-day resolution data.  I suspect that some of the odd behavior in the MLR analysis (see below) might be due to this issue. 

Line 249-250: There is a statement here about the procedure removing the 25% least sampled grid cells.  I do not understand this concept. Does it mean that there should be 25% of the grid cells missing in Figure 5?  Perhaps this means something else. It should be clarified in the text.

Line 260:  Would be useful to note here again that Pan-Arctic means 60-82N over all surfaces.

Line 263: 48.8% of the time, not 48.8% of 50.9%.

Line 263: “evolve” should be “exist”

Line 264: “This occurrence fraction decreases….”

Line 264-265:  This is a sentence fragment; please re-write.

Figure 2: There is a major flaw in the analysis revealed by Figure 2 that appears to not be understood by the authors (at least it is not discussed). I’m surprised a paper could get this far without this issue being detected. There is significant cloudiness over Greenland as noted by multiple studies. Shupe et al. (2013) and Lacour et al. (2017) show results from Summit where clouds occur about 60+% of the time and liquid-containing clouds occur 20-30% of the time.  The results presented here suggest that there are no clouds over central Greenland. Based on the appearance of the results (diminishing cloud fraction towards the center of Greenland), I surmise that this is because this study references the height range of 0.5-3 km relative to MSL! The center of the Greenland Ice Sheet is above 3 km altitude, and thus no cloud fraction in Figure 2.  Presumably the same is true over other land areas. This issue has serious implications for the results of this study such that results over land are not comparable to observations over the ocean. This concept brings up two points for me:  1) If I am wrong about this whole notion and the 0.5-3km layer is actually defined relative to local ground level, then an explanation is needed for what is happening in Greenland. 2) If I am right about this notion, then either the whole analysis needs to be corrected so that it is defined as 0.5-3km relative to local ground level across the whole domain, or all land surfaces need to be removed from the analysis because they are not comparable to ocean regions. Additionally, the ground-clutter issue would also extend further into the 0.5-3 km MSL height level and would need to be addressed.

Section 3.1: This section is full of important results about clouds. While the definition of low-level clouds is provided (0.5-3km) the results are presented as if they represent all low-level clouds. The danger is that modelers (one of the study’s stakeholders) will take these results as metrics for their model. However, numerous papers from ground-based stations (Nomokonovo et al. at NyAlesund, Shupe et al. at Summit, Dong et al. at Alaska, Shupe et al. at Alaska and Eureka, etc.) show that clouds below 0.5 km make an important contribution to low-level cloud occurrence fraction. Thus, the results presented here are not for all low-level clouds, but for a subset. It is essential that the stakeholder community is not led to believe that the results presented here represent all low-level clouds. Thus, this point needs to be made more clearly here and elsewhere throughout the paper. Even better would be some analysis of how biased these results could be due to the near-surface blind zone.

Line 301: The annual variation of cloud occurrence is characterized as a bimodal distribution. This is not a distribution, it is a timeseries. It is more appropriate to talk about multiple seasonal maxima instead of bimodality, here and throughout the paper.

Line 327: How do you draw this conclusion about “meridional transport of heat and moisture” from the results that are presented? This point may indeed be true, but the reasoning for how one can come to this conclusion from the presented results needs more support.

Figure 4: The text in this figure is hard to see because it is so small. Additionally, it is hard to tell what the actual numbers are because the thickness of the lines is large compared to the granularity of the axis. Lastly, the axis ranges are different among the different columns making intercomparison of the cloud types difficult. This is a clever way to represent a lot of data, but it somehow needs to be made clearer.

Line 359: The negative correlation with OCwarm is minimal or even the opposite for most seasons and is only really observed in summer in some regions. 

Line 362-364: These results imply that specific humidity at 700 hPa is anti-correlated with IWV. This is a remarkable result (that I have a hard time believing).  Is there further evidence for this or could it somehow be a result of the 7-day windows used for the analysis?

Line 370 (and elsewhere): This section presents some perplexing results that seem to defy fundamental physical process understanding. For example, here it says that ice clouds are related to less stable atmospheric conditions, and below it is noted that USLC are associated with more stable conditions. There is a lot of literature on this topic. Optically, ice and liquid clouds are vastly different, with the former typically being optically thin and the latter being optically thick. Thus, over land and sea ice surfaces for much of the year, the surface will cool much more under ice clouds compared to liquid clouds where the surface can actually warm. (The same is true over the ocean in winter, although the ocean temperature is less responsive.) At the same time, the liquid clouds themselves will more readily cool (cloud top radiative cooling) and vertically mix the atmosphere making it less stratified. These processes push the liquid clouds towards radiative equilibrium with the surface (i.e., the classic LWN approaching 0 W/m2), while the ice clouds would not be (i.e., a big deficit of LWN at surface). Thus, from this first-order set of processes, the ice clouds should be associated with a more stable boundary layer, and the liquid clouds with a less stable boundary layer. However, one of the strongest and most consistent signals in the MLR analysis is the inverse relationship between ice clouds and LTS, and the direct relationship between USLC and LTS. Assuming there is not an error in the analysis, to me this suggests that the LTS parameter does not typically represent the stability of the cloud layer itself (which would behave as outlined above) but instead it represents the difference between the ABL (i.e., cloudy, near-surface environment) and the free troposphere above the cloud layer. This would be a remarkable result, but I’m not clear how it happens. If this is indeed true, it would be great for the paper to describe exactly how it is true, i.e., what is the mechanism?

Building on this previous point, it is fascinating to see the difference in the MLR between LTS and MCAO.  LTS is the difference in potential temperature between 700 hPa and 1000 hPa, while negative MCAO is the difference in potential temperature between 800 hPa and the surface. The surface and 1000 hPa are fairly close to each other, so the main difference here is the difference between 700 hPa and 800 hPa, and the sign.  For ice clouds, the MCAO signal is indeed weakly of the opposite sign compared to LTS, but is pretty close to 0!  The relative relationships are less clear for the other cloud types and sometimes both LTS and MCAO are the same sign in the MLR. This implies that there is some funky behavior happening between 700 and 800 hPa, or that the MLR has some issues (whichever it is should be explained). The relative behavior of LTS and MCAO is central to any discussion about the cloud states. MCAO is arguably more representative of the cloud itself, as the clouds themselves more often encompass 800 hPa than they do 700 hPa.  On the other hand, 700 hPa is more often above the cloud in the free troposphere. Thus, to make the claims in the text about the relation of cloud types to stability requires invoking both of these parameters. 

Line 372: “the presence of moisture at higher altitudes”:  What does this mean?  I thought the analysis was for clouds between 0.5-3 km.  What are the “higher altitudes” and the “upper cloud layers” mentioned here?

Line 375: With Figure 4 as presented, I cannot tell what the actual numbers are, but the values for AOD appear to be inconsequentially small.  Are these significantly different from 0?

Line 387: “lack of representativeness of linear regression models”.    So are these models not representative?  The whole analysis is based on the notion that they are, but if it is now stated that they may not be, what is the implication for this whole line of analysis?  This statement really supports the need for a clearer discussion of what this MLR analysis really means and how reliable / representative it actually is.

MLR Analysis in general:  This MLR analysis brought more questions than answers. First, it is hard to see the real numbers in the figure, and it is not clear which values are significantly different from 0. Perhaps there is some symbol that could delineate the signals that are significantly different from 0.  Also, as outlined above, there are some results that seem to defy the basic physical understanding of these clouds, and those results have largely gone without supporting analysis to describe why.   Additionally, there are some apparent differences between USLC and MPC that need to be better described. At a basic level those two cloud types are not that different from each other; the primary component of each is the supercooled liquid water.  Both have similar radiative cooling that should drive cloud-scale buoyant motions to sustain the clouds. The primary difference is that in MPC there is weak ice formation while in USLC there apparently is not (although above I outline some questions about the ability to always identify the difference). To ensure that the MLR analysis has meaning, there needs to be significant additional analysis of these results and clear description of the mechanisms involved.

Line 423: “Spring” should be “spring”

Line 430-432: Here it is stated that “entrainment” and “heat and humidity fluxes” drive the distribution of phase partitioning. However, the analysis has not examined entrainment or surface fluxes. Thus, unless there is more analysis that actually shows the role of these processes, this can only be considered speculation and should be labelled as such.

Section 3.3.3:  It has not been explained how coupling was calculated.  Presumably this is related to the cloud-level potential temperature versus the surface potential temperature.  Is this determined for each individual observation and then averaged over 7 days for all observations in a given grid cell? Or is there somehow an average potential temperature profile that is then analyzed?  The details here matter.  Moreover, just like all other parameters, cloud-surface coupling state can vary quite a bit on sub-7 day time scales (see the results from ASCOS), such that it is not clear what this coupling analyses even means. 

Line 444:  This statement suggests that the coupling state is dependent on whether or not cloud level turbulence is related to surface fluxes. While this may be true over ocean, it is not necessarily true over other Arctic surfaces. Indeed, cloud generated turbulence is also an important factor and the proximity of the cloud-driven mixed-layer to the surface can lead to a coupled situation (i.e., no intervening potential temperature gradient), independent of surface fluxes.

Line 465-466:  This process should be described in more detail.  How do increases in air temperature lead to instability?  Warm air over a colder surface would instead lead to stability near the surface. Since this text is talking about a maximum in surface coupling, it is this atmosphere-surface interaction that is important.  Please explain.

Line 472:  “these results are only representative of low-level clouds as a whole.”  Actually, the results are representative of clouds between 0.5-3 km.  This is different than low-level clouds as a whole. 

Line 483:  “surface” instead of “surfaces”

Line 501: This result has not been shown.  I did not see any information about surface turbulent heat fluxes impacting phase partitioning.  Some information that may be relevant for such processes might be implied from some of the data, but clear analysis of that data and clear conclusions regarding interpretation of that data must be presented before drawing such a conclusion.

Figure 7:  These results are seemingly inconsistent with those from Griesche et al. (2021), who observe that coupled clouds have more ice than decoupled clouds. Griesche et al. have recently submitted a new paper further supporting their conclusion. While these papers are for shorter periods of time at singular sites in the sea ice, they use sensors that are much better suited to examine this problem.

Line 532-533:  While I appreciate the attempt to compare to surface observations, this comparison is not very functional as presented.  One value is a multiyear, pan-Arctic value while the other is a value from 6 weeks of observations at one location.  It would be much better to isolate the satellite observations at the time of year and location of the ground-observations (even including multiple years would be fine) in order to attempt to compare processes in a more appropriate way.  A better attempt at comparisons of this nature would improve the manuscript substantially.  For example, during the process of reviewing this paper, I have done multiple comparisons where I visually extracted data at specific points to compare to ground observations from different papers. A more thorough analysis of this type would be quite useful to confirm or contextualize some of the main findings. 

Line 540:  “breakup” itself has little relevance.  Better to say “… the minimum extend of the pack ice…”

Line 555:  I believe here you mean “ice clouds” not “clouds”

Line 557-558: This conclusion is a stretch. There is literature indicating that moisture entrainment aloft can help sustain mixed-phase clouds, but, to my knowledge, this has not been shown for ice clouds.  Also, ice clouds do not have the radiative cooling that liquid clouds do, and thus there is little turbulence to drive entrainment. This statement should be removed or supported by more evidence. 

Line 574-575: Based on the information I can extract from Figure 2, Nomokonova et al. show more liquid-containing clouds than identified here.

Line 583-585: Here is again more speculation that is not labeled as such and is not supported by observations or analysis presented in this paper.  No information has been presented on entrainment or INPs, and little has been provided on aerosols at all. 

Line 595-597: This is opposite of the result suggested by Griesche et al. (2021, and newly submitted).

 Line 609: remove “or breakup” as nothing has been shown about this process.

Section 5: This is now the second time some of these results have been summarized.  The partitioning of information between Section 4 and 5 should be re-assessed to ensure a clear delineation and to minimize redundancy.

Line 625-627:  This statement attempts to “segregate” USLC and MPCs because of their differences.  However, it is not clear that they are so different physically. From a basic physical standpoint, they both have populations of supercooled liquid water droplets. One has appreciable ice observed by CloudSat, the other does not. However, it is not clear the extent to which the cloud ice is actually present but just not observed (issues outlined above). Moreover, it is unclear if there is drizzle in these USLC clouds that would serve a similar mass loss role to ice. From a radiative standpoint, the ice plays little role, so the overall differences would have to come down to detailed properties of the cloud liquid (that are not shown here). There could be some differences in lifetime, but there are many aspects that would have to be considered to unravel that possible difference (and those aspects have not been mentioned or addressed here). The MLR analysis shown here does reveal some differences, but it is not clear how much those are driven by spatial differences in where these sub-sets of clouds occur versus actual process differences (i.e., is it clear from the data that at the same location and time of year MPC and USLCs behave differently at a statistically significant level?).  Based on my long experience with these clouds, I speculate that it is quite possible that the main difference could simply be that some airmasses consume all their available INPs before the clouds lose all their moisture.  To some degree this has to be true because, according to most ice nucleation theory, if there are appropriate INPs available they will nucleate ice. Overall, I think the conclusions should stick to what can be concluded from the data that has been presented. Speculation on the meaning of results is fine, but it should be labelled as such and based on some evidence.     

Line 637: The paper has not shown any diagnostics of orographic lifting. Indeed, it appears that the analysis may have a significant bias for observations over land, and especially over orographic features (see above). Thus, I would not trust any of the results related to orography.   This also raises an important question related to my earlier comment about the height reference relative to the land surface:  If MSL is used instead of AGL, how are some of the parameters calculated? i.e., 1000 hPa is below the surface of most mountains. Indeed even 700 hPa is below the surface over central Greenland. 

Line 660:  The “longevity” of USCLs has not been examined here. Rather, a collection of snapshots are analyzed jointly.  These observations do not say much about longevity.

Line 661-662: This statement has not been shown.

Figure S1: Top box should be “unknown”

Figure S2c:  I assume this table is for total and MPCs that are low clouds (0.3-5km). That should be included in the caption.

Figure S3, S5, S7:  I assume these figures are for total low clouds (0.3-5km). That should be included in the captions.

The paper analyses an eight-year time series of active satellite measurements of low cloud frequency of occurrence over the Arctic, thus extending previous work to longer time series. An existing method is used to distinguish four different types of low clouds, present their spatio-temporal distribution, and analyze the main drivers responsible for the distribution. In general, the data record and the topic of the study are very interesting, as our knowledge on Arctic clouds is still limited.

The manuscript builds on a study previously submitted to AMT, which I have reviewed. In general, I find the manuscript (especially its first half) much improved with respect to reorganisation and readability. The manuscript now also includes an investigation of the coupling of clouds to the surface, which I had suggested in my initial review. Unfortunately, the exact method by which the authors derive the concept of “coupling” is not described in detail. Here, the main question is whether this has been done on the individual cloud profile scale or whether the 7-day averaging has been applied. For the latter, I believe no sensible statement can be made.   Such analysis may help explain why the authors find that ice clouds are more frequently coupled to the surface than liquid clouds. I have strong difficulties identifying a physical mechanism which could lead to this finding. Here, and also in other cases, I miss a clearer, physically oriented analysis that digs into the data to identify specific conditions/regions/times when such a process takes place. Ideally, typical cases could be extracted that can then subsequently be presented in detail for a solid interpretation. Indeed, moving the paper from a more measurement-focused (AMT) to a more physics-oriented journal (ACP), I would have expected a stronger focus on the physical mechanisms leading to the observed cloud distributions.

In addition, several of my other points of criticism, e.g. blind-zone, orographic effects, are not addressed in the newly submitted version. Furthermore, I suggested the inclusion of further parameters into the MLR analysis to relate more to physical processes, e.g. subsidence, in-cloud temperature, airmass characteristics. Furthermore, I was very skeptical about the seven-day averaging performed before calculating the correlations. This could be the cause of artificial correlation and requires further sensitivity studies. Furthermore, I recommend the use of machine learning techniques instead of the linear approach.  

As already mentioned above the second part of the manuscript is rather difficult to read with many repetitions in sections 4 (Summary and Discussion) and 5 (Conclusions). Especially, section 4 includes several comparisons with the results of other studies. However, here, often rather different regions and time frames are compared which would need to be considered. While of course of interest, it might be better to focus only on speculating on the physical mechanisms of a few key findings with more in-depth analysis rather than the presented rather long list.

I do not provide a more detailed review as it is clear that still substantial revisions are needed before the paper can be published.