General comments.

The study provides an experimental test of the influence of the deposition coefficient functions on small ice crystals in simulated cirrus conditions. Unlike previous studies at such cold temperatures (below -40 C), the experiments here are run in a large cloud chamber with many crystals growing simultaneously, and the data are compared to an advanced microphysics model of ice growth. For results, they find that supersaturation-dependent functions best fit the data, though the values are relatively large. The findings should be useful to researchers of cirrus and should be published.

The weak points of the approach, which probably should be made clearer in the text, are the apparent lack of verification that the crystals have facets (e.g., by sampling or some optical method) and the short growth times (typically about 10 min or less). Sure, the experimental conditions make these improvements difficult, though they seem like obvious steps to attempt in future studies and worthy of mention. About the facets, I would expect that small, nearly spherical crystals would have deposition coefficient functions near unity (surface roughness, higher local supersaturation) and thus not very appropriate for the theoretical model, whereas facetted crystals would have smaller deposition coefficient values that would depend on the face. So, verifying that facets exist seems important for applying the model. About the need for longer growth times, longer growth at lower supersaturations may simulate actual cirrus better and also provide a better test to the theoretical model.

Other than those issues, the approach described here looks fine, though I have some other general suggestions to help clarify the study.

1. As the experiments were done in 2013, I wondered if the data had been previously analyzed and published. If so, where and how does the present analysis differ?
2. The method of determining crystal sizes is not clear. I found the method described in the Skrotzki et al. 2013 paper, though it would help to clarify it here. Also, it seems like a rather indirect method to extract crystal size, so it may help to discuss the uncertainties.
3. How much spatial variability exists in the supersaturation and crystal sizes? Related to this issue, if crystals have a range of sizes (and shapes), how would this affect the application of the theoretical model? A related question is variability in the deposition coefficient functions even when all crystals are the same size, shape, and have the same local supersaturation—how would that affect the application of the theory? Of course, these cannot be answered exactly, though it seems worthwhile to estimate the potential influence on the results.
4. Are there any sharp images of crystals of these small sizes grown under these conditions (either from a cloud chamber or an actual cloud)? It would help to show them, or an accurate sketch, in the Introduction.
5. The growth model is also dependent on the vapor diffusion coefficient. What values were used? As the modeled rate can be more sensitive to this parameter than the deposition coefficient functions, perhaps you could make use of the sublimation phase (when it would be safe to assume a sublimation coefficient of unity) to measure the appropriate vapor diffusion constant. The values so derived would then be input into the growth model.
6. In looking at the results in Figs. 5-8, what is thought to be the main factor causing the oscillations and bumps in the ice-crystal number? Influence from the pumping, sticking to walls, sampling for IWC, new crystal nucleation, or just noise in the measurements?
7. It might help readers if there is a table defining the many acronyms.
8. The paragraph speculating about cubic ice in the conclusions could be removed. I have yet to see any convincing evidence for cubic ice in the atmosphere, though stacking faults in vapor-grown ice Ih seem to be well established.

Smaller comments and suggestions, by line number.

Line 3. May be better to always distinguish the “direct” influence of deposition coef. functions on mass uptake vs the “indirect” influence via crystal shape. In some places in the text, this is made clear, though would help here to add “direct” or some similar clarifying term.

Line 6. Can you break up the sentence to ease reading?

Line 10. Are all models declared proper nouns? I know capitalized models commonly appear in the literature, though that doesn’t automatically make it correct usage. Maybe I’m wrong here, though to some readers, quotation marks look better for the long model names.

Line 14. Maybe add that the crystal is assumed spherical, or at least, isometric?

Line 27. It looks like the authors of the 2018 paper use the term “ice crystal complexity” instead of “surface complexity”. It also seems more appropriate.

Line 37. Perhaps “constant” should be specified further to mean independent of supersaturation, temperature, and facet?

Line 42. And dependent on crystal facet.

Line 42. Here and elsewhere, the Latin abbreviations commonly are followed by a comma “e.g.,”

Line 70. It might help here to specify whether you are referring to the limiting (high-supersaturation value) of the deposition coefficient or the functional form of the deposition coefficient function.  Concerning the former, I could explain quite a few cases of the limiting (high-supersaturation) deposition-coefficient function discrepancies of not just ice, but also rare-gas crystals, as arising by heat conduction effects (J. Cryst. Gr. vol. 132 (1993) 538—550.) At the time (pre-1993), many studies of other crystals had made it clear that the limiting case, also known as the “sticking coefficient”, was always equal to unity for crystal growth (unless a chemical reaction was involved). Yet there seemed to be many values claimed for ice that were much less.   

Line 73. Here might be a place to mention prior analyses of the experiments (see the general comments). When I read the first two sentences, I thought you were re-examining the Skrotzki et al. 2013 experiments, though those must have been before 2013 and also involved only 15 experiments, much less than your 48.

Line 96. Here, and I think a few other places, you refer to a textbook or review article instead of the original authors. It seems fairer to credit the original authors of the idea. In this case, it may be Fukuta and Walter, 1970, or even earlier. Definitely not Pruppacher et al. 1998.

Line 100. It looks like Si is the vapor supersaturation ratio.

Line 121. “considered to be unity for nearly all crystals.” See 70. above.

Line 122. There were earlier molecular-beam experiments that found unity. (Sorry, I don’t recall the references, though maybe by D. Kay et al. in the early 90s or earlier.) Also, the claim that the sticking coefficient decreases with increasing temperature is a signature of heat conduction effects analyzed in 70. above.

Line 135. Gonda et al. did advanced optical microscopy much earlier, giving strong evidence for growth spirals.

Line 154. Very minor quibble about terms here. It is unclear whether the term “instability” is useful for the branching case on snow crystals. Perhaps the best description of branch formation on snow crystals is from F.C. Frank (Contemp. Phys., 1982), and he had no need for the term. “Instability” applies to the melt-grown ice dendrites, arising from the Mullins-Sekerka study, though vapor-growth is very different from the melt-growth case. Hollowing at low supersaturations seems unstable, judging by the various asymmetries between facets, though this hasn’t been studied in any detail. It just seems unnecessary to use the term here.  

Line 170. This sentence seems awkward. Perhaps move the “prior to nucleation” part to later in the sentence.

Line 221. This sentence is rather wordy. I think you mean “A mixing fan inside the chamber pushes the crystals up and mixes the air.” However, it seems just as much air is pushed down as up. Also possibly relevant: for the estimated crystal sizes here, it seems that settling would let crystals fall by only about a meter (~1/5^th the chamber height) over the course of the roughly 10-minute experiments. So maybe the “mixes” is useful here, not the ”pushing up”?

Table 2. It would help to define the variables in a table footnote, also give the units for CCN, the meaning of ATD, SA, SOA, as well as the meaning of the range in R. Some of these can be found in the text, but not all in the same spot.

Line 255. You use growth and evaporation here, but elsewhere deposition and sublimation.

Line 265. Perhaps clarify that the growth rate could be surface limited at any Knudsen number, though certainly when it is much greater than unity.

Line 271. It might help to define a bin here. The term comes up again in a few paragraphs.

Line 291. The “assumption” did not seem clear, and perhaps the consequence could be explained better.

Line 296. Perhaps explain that you are assuming dry adiabatic ascent to deduce the updraft to use in the model? Or, am I not understanding this? Then, on 299, I suppose by “Typical updraft” you mean this “effective vertical motion”?

Line 312. From the table, it looks like the largest size is less than 14 microns. Also, on this line, I think you mean “we assume that crystals remain isometric”. Developing a non-isometric habit takes time, so “have not yet developed” doesn’t mean all crystal faces grow at the same rate.

Figs. 5-8. It would be nice if the details in these plots were larger as everything is so small. I don’t know the best way to do this except by adding more figures. I suppose T and P plots could be combined to create a little more space, and maybe the time axis could be trimmed to 1000 s, though these would only slightly help. On the other hand, I think it would be nice to see the inferred crystal sizes as well, so this would make things more cramped, perhaps suggesting the best solution is adding more figures.

 Also, in the plots, it would help to mark certain stages with a vertical line, such as the point when sublimation begins. Finally, I think the general style of figure captions is to put all the info needed to read the plots, but none of the interpretation. For example, in Fig. 6, the legends for exp. 40 “W2001” etc. should be defined in the caption. The interpretations (e.g., Fig. 5: “…also demonstrates very efficient ice growth…”) belong in the main text.

Line 360. Unclear about “…, as there is not yet consensus…supersaturation”. Is this referring to the curve for layer nucleation rate vs supersaturation?

Line 422. “mean absolute percentage error”, or is this now a proper noun?

Line 494. Has “principal facet” been defined?

The authors re-evaluate prior cloud chamber experiments on ice growth under cirrus cloud conditions. Their focus is to compare the experiments to model calculations based either on a constant deposition coefficient or with one, which depend on surface supersaturation. For experiments preformed above a temperature of 205 K, they find that both models are able to fit experimental data whereas at temperatures lower than 205 K the data indicate larger discrepancies to both models and on whether the nucleation occurred homogeneously or is heterogeneously induced.

The paper is well written, supported by adequate figures (sometimes a bit small to read), provides an overview over the state of the science for depositional ice growth in cirrus conditions and its topic well suited for the readership of ACP. I recommend publishing it, but ask the authors to take my comments into account when preparing a revised manuscript.

Of course, it is a bit disappointing that there is no clear difference between the two model approaches when comparing with experimental data as done in Fig. 9. The authors give an explanation in the last paragraph of section 5.4. They point out that there is only a limited crystal growth observed in the experiments, which may prohibit more distinct differences between the predictions of the modelling approaches. I feel the readers would profit a lot if the authors could compare the two approaches for a hypothetical experiment in which the differences become more apparent. Following this line of thought, could the authors even recommend an “updraft” speed and time span of observation, number density of ice crystals needed in an experiment to distinguish between a constant deposition coefficient and one depending on supersaturation?

In addition, I am not satisfied with the two sentences starting on line 464: “These results also demonstrate that the seeming contradiction between the high deposition coefficients previously observed in cloud chamber experiments (Skrotzki et al., 2013) and the low deposition coefficients observed in single particle levitation diffusion chamber experiments (Magee et al., 2006) can be resolved by a non-constant parameterization for α_D. Here we have shown that both types of experiments can be consistently modeled with the same ice growth theory.” I cannot see where the authors modeled the experiment of Magee et al. (2006), who came up with a deposition coefficient of 6E-3. But I would welcome if the authors apply their supersaturation dependent deposition coefficient to the Magee et al. (2006) experimental data.

A last comment: In all figures showing the comparison of model with experimental data you take the input data for the model (temperature, pressure and ice particle concentration) as exact. A few sensitivity calculations (e.g. varying ice number density by 5 %) would be quite helpful. Or phrased differently how sensitive is the model to these constraints?

Technical comments:

Line 25: I find that “surface complexity” needs a bit more of explanation at this point in the introduction.

Section 2.1: You partly review the literature in the section. For the reader it may prove helpful if you add the temperatures of these studies, so that the reader does not need to look those up.

Line 279: I find the term “vapor tendency” very odd, but I am not a native speaker.

Line 284: again English: I suggest to delete the “however”

Figure caption Fig.9.: there is no panel “g”, it should read panel “f”.