|The authors have explained their observations more carefully and have added considerable discussion regarding the drop fracturing/spicule formation secondary ice process demonstrated in Leisner’s lab and suspected from in situ evidence presented in Lawson’s recent JAS paper. It would appear that the manuscript is now including the drop fracturing/spicule formation secondary ice process as an alternative possibility. This reviewer was not lobbying for this, but instead, I am attempting to point out that there is insufficient evidence to show that any secondary ice process, and especially the H-M process, can “clearly” and totally explain the observations. Perhaps I did the manuscript an injustice by pointing out that a recent paper suggested another possibility for rapid glaciation in tropical clouds. |
The main points I want to make, and the aspects of the manuscript that need to be modified, are found in several places in the manuscript that state that a secondary ice process is clearly active. The manuscript bases this on measurements of primary nucleation. However, what the manuscript only alludes to, and does not actually lead the reader to consider, is that mixing of ice from previous cloud turrets could potentially account for much, if not all of the observed high ice concentrations. Now to be clear, this reviewer is not stating that recirculation of ice is accounting for the high ice concentrations, only that the measurements are not sufficient to conclude that any particular ice production or “contamination” mechanism is responsible. The manuscript mentions recirculation and the work of Blyth and Latham (1997) - others have also published this possibility – but the manuscript only casually addressed this possibility, and not as a mechanism that could account for the high ice. The main point here is that the clouds the manuscript describes appear to have very complex dynamics with downdrafts mixing with updrafts and multiple turrets (bubbles) rising up through regions with old ice. There is mention of a region in the repeated penetrations of a “newly developing cloud”, which is actually more than one turret, where an updraft penetrated the downwind region and showed the highest droplet concentration of the cloud pass. Figure 7 shows that the original cloud penetration (10.3), which was 1 km wide, is almost 5 km wide with four distinct regions of updraft > 7 m s-1 and two distinct downdraft regions 23 min later in penetration #13. Furthermore, there is a 14.5 min gap between penetrations 11.1 and 11.3. It appears to this reviewer that the cloud penetration #10.3 may be the only cloud that was not exposed to possible contamination from recirculation. The manuscript casually states (line 913) that cloud penetrations were “spaced a few minutes apart”, but this is not the case in the midst of the only cloud that was considered to be “isolated”. The remainder of the dataset is collected ad hoc while flying down a line of cu. It is virtually, if not literally impossible to draw definitive conclusions about the ice processes developing in a single turret (bubble) based on these measurements in a dynamically complex cloud system.
To be fair, the authors have done an excellent job of describing the measurements. However, the manuscripts leaps to conclusions stating that there is clearly a secondary ice process active, when contamination from recirculating bubbles could be playing a significant role. Has Dr. Blyth weighed in on this? Perhaps one way to clean up the manuscript would be to consider this contamination to be another secondary ice process, but that is a bit misleading.
There are also places in the manuscript where it states that, for example line 894: “Much of the ice measured in the mature, stratiform regions showed columnar features, suggesting H-M is likely to have been the dominant ice formation process at the end of ice formation.” However, one can only conclude that the columns grew within the temperature region (-3 to -7 C) where H-M is active, not that the H-M process was responsible for their production. It is statements like these that are misleading and need to be clarified.
This reviewer is admittedly too lazy to go through the manuscript and correct all of the locations that need to be deleted or re-worded. The manuscript should be limited to describing the observations, which provides the scientific community with considerable value, with perhaps some suggestions as to possible ice production or contamination mechanisms. It should not, however, lead the reader to conclusions, and conclusive statements need to be evidenced by actual data, not speculations about data.
That said, I will go through and point out a few places that I have highlighted where some of the changes need to be made.
Line 8: Change ‘indicating’ to ‘suggesting’ and add a clause to the effect: …’or due to contamination from recirculating ice particles.’
Line 16: Change ‘initial secondary’ to ‘first observable’.
Line 25: Change ‘it is clear’ to ‘it is possible’. (Eliminate or at least avoid using the term ‘clear’ in the manuscript, as very few observations in this dataset appear to be ‘clear’.)
Line 80: Change ‘showed’ to ‘suggest’
Line 472: What was the nature of the instrument error?
Line 488: Quoted from the manuscript: “Compared to Run 11.4, the downwind side was more turbulent, and was predominantly updraft, whereas a similar region in Run 11.4 was predominantly downdraft. … but the highest droplet concentration was measured in the downwind side, where a small section of cloud contained NCDP of 420 cm-3 in a
10 m s-1 updraft.” This is evidence strongly suggesting that ice contamination from recirculation was a likely possibility in this cloud system.
Line 515: If larger particles can be mixed in, so can smaller ice particles. Here you point out that recirculation is likely occurring. Go ahead and explain that this can increase observed ice concentrations, albeit, by an unknown amount.
Line 567: The manuscript points out that recirculated ice can “accelerate [cloud] development”, but what is meant by cloud development? Isn’t it really ice enhancement?
Line 615: Good observation, but I suggest that you say “strongly suggesting that ice was recirculated…” instead of “have been recirculated”. We don’t know for sure.
Line 622: There is not sufficient evidence to make this statement. All you can state based on the observations is that the observed ice concentration is higher than expected via primary nucleation reported in the literature.
Line 625: This contradicts several previous statements and cannot be conclusively supported by the observations.
Line 691: The high ice concentrations are not observed in developing that are definitely uncontaminated. Strike developing.
Line 715: It is not ‘clear’ and this statement needs to be eliminated, modified or at least qualified.
The remainder of the manuscript waxes on about secondary ice and makes grandiose conclusions. I have already addressed how these sections need to be reframed, so I will only point out a few examples in these sections. Many more can be found.
Line 765: changed ‘acknowledged’ to ‘studied’.
Line 823: Lawson et al. (2015) do not use the term “chimney clouds”, which can be found in Heymsfield and Willis (2014), and Lawson et al. did not analyze data from ICE-T “chimney clouds”. Change to ‘updraft cores with vertical velocities on the order of 10 m s-1.
Lines 840 – 850: The secondary ice processes described are not the only possibilities. Recirculation needs to be addressed. Use of the word ‘clear’ is not justified. Observations of ice in H-M temperature regime is not sufficient evidence to attribute their origin to H-M mechanism.
Several more examples within these themes follow in the manuscript. I will leave it to the authors to modify the manuscript appropriately.