Dear Authors,

I received two reviews for your revised commentary "acp-2021-123: Comment on "Review of Experimental Studies of Secondary Ice Production" by Korolev and Leisner (2020)".

The reviews are attached below. The reviewers still do not clearly favor publication of this commentary and both indicate that major revisions are needed.

In the hope to converge to an agreeable solution, some comments when revising the manuscript:

It seems referee #2 does not question that the models by Phillips et al. can stand alone, i.e., being independent of the experiments. However, the referee states that this fact makes the commentary less substantial towards the work of Korolev and Leisner (2020). It appears the commentary deals more with the fact that indeed models can be independent of experimental results. However, the referees seem not to doubt this fact.
Referee #2 states "....while it is fair to disagree with the KL2020 characterization, all this hand waving will not be settled without more laboratory work.". One could argue that the discussion about the validity of the model is not the actual focus. Therefore, the referees question if criticizing Korolev's and Leisner's characterization is a substantial contribution as a standalone publication/commentary. As such referee #2 states "This work certainly stands on its own. I suggest the authors reconsider the title of the manuscript. Much of the manuscript stands on its own as a clarification of what was previously stated in the author’s publications."
In other words, referee #2 feels that not a commentary but resubmission as an independent research article may be the better venue for this.

Both reviewers indicated their willingness to review the revised document. We are looking forward to a revised versions of your manuscript and a point-by-point response to the referees.

With kindest regards,

Daniel Knopf


Referee #1:
Comment on “Review of Experimental Studies of Secondary Ice Production” by Korolev and
Leisner (2020), Phillips et al., acp-123

In this reviewers’ opinion, the responses to the reviewers’ comments are inadequate. How do
you move the field forward-not by writing that there’s little need to do more laboratory
experiments-especially on fragmentation, . The study makes considerable use of the Takahashi
(1995), experiments, where 2 cm ice balls were collided to generate fragmentations. How could
that be considered the final answer? I have my own experience, working with a key player in
recent identification of processes that lead to secondary ice production, and based on that have
a theory that has not been examined in-depth.

The responses by Phillips et al. are highlighted below in bold text, my thoughts on the
responses are not highlighted.

Phillips et al. (2017ab) provides details about the role of breakup in clouds. Eventually the
vast inaccuracy from omitting breakup in ice-ice collisions in current models will be widely
recognised.

Reasonable response, although I don't think they are correct in their interpretation.

As we see it there are three points we wish to convey and we have updated the text to
modify this. First, theoretical and modelling studies of SIP by breakup in ice-ice collisions are
possible even without any further laboratory experiments

I disagree with this point. It's an overconfident view

Second, our previous theoretical and modeling studies of this type of breakup are valid EVEN
IF all the previous laboratory experiments turn out to be totally erroneous. Lastly, previous
laboratory experiments about breakup in ice-ice collisions are, in fact, not as erroneous as
KL2020 tries to suggest. Any issues of representativeness or bias (e.g. sublimational
weakening with Vardiman) in both lab/field studies are possible to correct for and are not
prohibitively serious.

This is not a good response in my opinion.

In natural clouds, such hail particles (2 cm) grow by alternating episodes of dry and wet
growth, hence the layered structure of hailstone sections. There is the re-freezing of the wet
surface just like the wet surface of the frozen drop in the lab experiment.

You haven't addressed the question in my opinion.

There is the clear suggestion here from KL2020 that a grave error is introduced by applying
the lab results to estimate the breakup of graupel in natural clouds, as Takahashi et al. (1995, their
Section 4) were attempting to do. Such an estimate was the stated goal of their paper in
1995.

I agree with the reviewer and not the author.

As simulated by Phillips et al. (2015), it is perfectly possible for 1-2 cm hail particles to form
inside a cloud, and when they do so they will collide. The fact that in the lab one of the
particles was fixed is equivalent to changing the CKE by a factor of 2 relative to both being
free (as shown elsewhere here; Eq (3)) which is equivalent to a tiny error in the fragmentation
rate (as shown in Section 4 of the commentary; Fig. 4). There is no problem provided one
stratifies the data in terms of energy.

The vast majority of SIP production is in clouds where rimed particles and sometimes graupel
are involved in the SIP process. The Takahashi 1995 study is not valid for the vast majority of
situations.

Such energy conservation is an absolute constraint that all collisions, whether natural or
artificial, must follow.

This is an inadequate statement that is not proven with laboratory data. This is why more
laboratory data are needed.

Referee #2:
The authors claim that 2 statements in the review article by Korolev and Leisner (hereafter KL2020) are misleading and distort the validity of their contributions.

Statement 1: The theoretical framework of collisional fragmentation developed in Yano and Phillips (2011), Yano et al. (2016), and Phillips et al. (2017[a]) was calibrated against experimental results of Vardiman (1978) and Takahashi et al. (1995).

Here what the authors said in their articles:
P.2 of Yano2011 states, “The goal of the present article is to demonstrate the important efficacy of this mechanical breakup (or fragmentation) process by a theoretical investigation. For this purpose, we take the parameters estimated by more recent laboratory data (Takahashi et al. 1995).”

P.2 of Yano2016 states, “Yano and Phillips (2011) and Yano et al. (2016, here- after YP11 for the former and YP collectively) show, under a deterministic approach, by taking the experi- mentally estimated parameters by Takahashi et al. (1995), that the ice breakup process can indeed lead to explosive ice multiplication under certain regimes.”

P12 of Phillips2017a states, “Theoretically unknown parameters are estimated from the observations, both from outdoors and laboratory experiments, by Vardiman (1974, 1978) and Takahashi et al. (1995).”

Although the word “calibrated” is not used in the text, it does characterize pretty-well what the authors state in their publications. In this manuscript, one of the main points is to lessen the stated connection between their modeling results and the Vardiman1978 and Takahashi1995 experimental results. The authors claim their modeling study results stand despite the possibility that the experimental results could be ‘totally erroneous’. I think this is correct and perhaps a better characterization of the connection is that the modeling results are consistent with these previous laboratory experiments. This idea is stated well in the manuscript. But this idea is more of a correction and corrigendum to the author’s previous statements than it is a comment on Korolev2020.
Statement 2: No parameterizations of SIP due to ice–ice collisional fragmentation can be developed at that stage based on two laboratory observations, whose results are conflicting with each other.

It is not clear how this statement applies to the author’s work since they claim their model formulation and result is not based or dependent on the experimental work. They claim their work is valid even if the experimental work is ‘totally erroneous’. The authors explain this well and this warrants publication as it emphasizes a point not well stated in their previous publications. But it would be nice of the authors also were to add some new results.

After describing the Vardiman1978 and the Takahashi1995 results, KL2020 claim it is hard to judge the consistency of the results given the differences in experimental setups and conditions. I agree but they then go on to state these results are conflicting. I agree with the authors that the word “conflicting” is likely not a proper characterization of the 2 laboratory studies. One has c within the range 1 -100 and the other has c = 50 (which may be corrected due to contact area corrections as the authors suggest, to 5-10). The authors make several good points about their model results being consistent with the experimental results. But they also concede that the laboratory experiments could be totally erroneous. So, while it is fair to disagree with the KL2020 characterization, all this hand waving will not be settled without more laboratory work.

The KL2020 review was not focused on modeling efforts. Phillips2017b cloud model-field data comparison shows good agreement with a fragmentation parameter consistent with the laboratory experimental results. This work certainly stands on its own. I suggest the authors reconsider the title of the manuscript. Much of the manuscript stands on its own as a clarification of what was previously stated in the author’s publications.

Smaller points:
Line11-16: Please break this into 2 sentences. There is also a typo here. Also be careful with the word ‘valid’ - usually this means validated by experiment. But I’m having trouble following the logic: How can the theory or model be validated by experiment when, at the same time, the authors concede the experimental results could be totally erroneous? You can’t have it both ways can you?

Line 107-108: 30 minutes is not the case for all \tilde{c}. Time is much longer for the range \tilde{c} \sim 1 to 10 as shown in Fig 3. Perhaps mention what is the lowest value of \tilde{c} consistent with the time-scale observed for the clouds in the field observations?

Line 179: The word ‘consistent’ rather than validated?

Line 265: Better to state the limit rather than ‘is minimal’.

Line 268: The 1% is only true for a certain range of values given the curve.

Dear Authors,

After reviewing your responses to the reviewers and conferring with referee #2, I am generally inclined to accept your commentary for publication. However, there are still a couple of points that you would like considering rephrasing. This may be in part because different communities, here experimentalists and modelers, have different connotations of the applied phrasing.

In the revised version of the manuscript, you make clear that the underlying theory of breakup in ice-ice collisions stands alone. I think there is no doubt about this valid contribution to this research area. However, as it is written, I agree with referee #2, that how you use Vardiman 1978 and Takahashi et al. 1995, is best described as calibration. You derive that for c > 1, you have explosive breakups. With no experimental data at hand, which c value would you chose? For example, for a c =1, you may discard the entire effect (if I am not mistaken). c=300 is likely too much, etc. To give you an example what I mean: a speedometer by itself is fundamentally valid, i.e., a linear response to a rotating wheel. However, it is only as good as the calibration is. As the measurement of speed gets better, the accuracy of the speedometer also increases (assuming its theory of operation is correct). Again, this has nothing to do with the foundations of the speedometer/theory. My feeling is that no one doubts fundamentally the theory you developed and applied. However, there are many theoretical studies in our field that need further laboratory data to yield higher accuracy. This is a typical process.

I also feel that the wording in the review article of both studies being conflicting may not be the ideal choice of words. Likely they are not consistent with each other since they were operated a different conditions. However, in my opinion, this is not such an important point. Only more studies will help to achieve convergence and this process usually takes time.

Regarding the point of failing to include the rotational energy from oblique collisions. I appreciate your discussion on this matter. Your reasoning makes sense. However, and I believe both referees struggled with this, you describe a highly idealized case of spheres. In the atmosphere, we are likely not dealing with spheres but with irregular shaped ice crystals. I can follow your argument in the manuscript, but would it stay around 10% for rotating ellipsoids colliding or other shapes? Of course, you argue for the case of the experiment where spheres were present, but the results of your theory are applied to the “real” world where you likely have not perfect spheres. I do not think that this issue needs to be further discussed in detail here but maybe acknowledging caveats, when data is lacking, may be appropriate. In other words, your discussion may imply that this effect is “always” negligible although we have never “observed in situ” two colliding particles followed by breakup. Someone operating in the atmosphere (not lab or model) may misunderstand your points and will just disagree instead of seeing the broader application of your theory. Hence, providing caveats may be beneficial, also to motivate more research.

Referee #2 and I feel this is valuable addition. I hope these thoughts help to perform the last minor revisions before publication of your manuscript.

With kindest regards,

Daniel Knopf

Dear Authors,

I am happy to accept your manuscript for publication in Atmospheric Chemistry and Physics. Below I have a couple of suggestions for technical corrections you may or may not follow. Those suggestions come about because of the fact that we are a scientific community working together advancing science. I would like to believe that potential misunderstandings are truly misunderstandings and not more. As such, I would change some of the wording/tone in the manuscript. Your point of view in this commentary is very clear and further emphasis besides giving the facts is not much needed. However, I will leave this to you to decide.

With kindest regards,

Daniel Knopf

Technical corrections:
Line 54: “Before the correction…”. Is this statement needed? KL2020 promptly admitted to these mistakes and corrected those in the corrigendum. Points that are fixed by the corrigendum do not need to be mentioned again.

Line 321: Superfluous “2” in “KL20202”.

Line 383: “This contentious claim…”. I suggest removing “contentious” since it is not quantifiable. It is a claim and some readers will agree or disagree with your reasoning.

Line 415: “In short, KL2020…”. This reads/feels a bit personal/emotional. I may be wrong with this. I suggest “In short, KL2020 provide a misleading picture of our work, despite the Corrigendum.”

Line 422: Again, I suggest changing the tone of the sentence. “Since sentence B (above quote) is such a strong claim, it is valid to ask what other criticisms could be made to support it beyond those expressed by KL2020.”

Line 520: “The review of SIP by KL2020 (their Section 4) continues to depict our work…..”. I suggest: “The review of SIP by KL2020 (their Section 4) depicts our work…..”.

Line 534: “Given….”. I would suggest to omit this entire statement. This is a fact of the past and does not help the current discussion much.