Dear Editor, Many thanks for giving us the opportunity to revise our manuscript. We have now addressed the questions from reviewers 2 and 3. In particular, we have now revisited the questions raised by reviewer 3 in the first round of revision. Therefore, points 2-4 of reviewer 3 were moved from the first round of revision to the present one and the corresponding answers are given below. > ------------------------------------------------------------------- > Reviewer #1: The paper has been substantially improved and > the simulations have been extended to a maximum physical > time compared to rain formation. The new results are very > interesting for the community and the manuscript deserves > publication in Journal of the Atmospheric Sciences. We thank the reviewer for the encouragement. > ------------------------------------------------------------------- > Reviewer #2: The authors answered most of the questions > and concerns raised by the reviewers. ... > In the response to reviewer 1's comment: > a. The largest droplets are ~672microns. This is beyond the size > ranges of Stokes flow regime (for droplet Reynolds number of 500). > When r>100microns, drag force becomes complicated, > and Stokes flow assumption will not hold. > Processes such as drop deformation, breakup, > and even the wake flow also become non-negligible. > However, the authors did not mention or discuss the > possible impact of this assumption. "Nonlinear Stokes drag" > is not a scientific term as Stokes drag is linear drag based > on Stokes assumption. Besides, there is no formula or > supporting citation listed to describe the drag force. We have now added Eq. (8) and the text below it; see l.218-222 on page 11, "Here the term 1 +0.15 Rei (Schiller and Naumann 1933; Marchioli et al. 2008) is due to particle Reynolds numbers, Rei = 2ri |u − Vi|/ν . We adopt this term since the largest particle Reynolds number becomes large, when r exceeds values of around r = 100 μm, and the linear Stokes drag does not hold. " We have also added the discussion about the collision and coalescence efficiencies at l.478-481 in the penultimate paragraph of section 5 on page 22, "For example, the largest particle Reynolds number is in excess of 500 in some of our DNS, resulting in droplet deformation and breakup, which can be accounted for in the coalescence efficiency." > b. The argument of the collision efficiency among similar-sized > droplets in 432-438 is wrong. In Chen et al 2018, the turbulent > collision efficiency is highest among similar-sized droplets, > and this leads to enhanced condensation-induced collisions when > turbulence is present. In the response to reviewer 2's comment: Here we cited the original conclusion by Chen et al. 2018b), which is on page 10 of the present version. We have now rephrased our subsequent comments in the following way to avoid misunderstanding; see l.437-444 in the penultimate paragraph of section 4 on page 21. "First, the updraft cooling included by Chen et al. (2018b) may suppress the supersaturation fluctuation-induced broadening of the droplet size distributions, first found by Sardina et al. (2018). Updraft cooling may result in more similar-sized droplets generated by the condensation process, which leads to their enhanced collision rate. Second, they included hydrodynamic interactions between droplets. This may modify the way how turbulence affects the collisional growth dis- cussed here. ." > c. I did not understand the argument in line 372-373: "We note that > the mass loading is the same for runs with different Re_\lambda. Thus, > the shape of f(r,t) is converged for the simulation domain size and > the number of superparticles". Does the mass loading mean the mass per > volume or the total mass? How does the shape convergence relate to the > mass loading? Finally, how does this answer the reviewer's question of > whether the extending tails are due to the increased Re_\lambda or due > to the increased total number of particles? We have now dropped the sentence about mass loading since it was not related directly to the question of the reviewer. Since we keep N_s/N_grid = 0.1 for all the simulations, the collision rate of which is statistically convergent and the tail of the droplet distribution is independent of the total number of superparticles. We have now added the following at l.261-262 in section 2.c on page 13. "This also ensures that the tails of f (r,t) are statistically converged for larger values of Ns , and thus larger Reλ." and at l.390-394 in section 3 on page 19. "We noticed that there is exactly one particle per superparticles for the smallest f (r,t = 600) for all the simulations. This excludes the possibility that the wider tail of f (r,t) is due to a larger number of N s for this case with the largest Reλ . This is consistent with our statement in section 2.c that Np /N grid = 0.1 is adopted in all simulations to make sure that the tails of f (r,t) are statistically converged." in the last paragraph of section 3. > d. In line 408-409, the author mentioned the largest local epsilon in > warm clouds is "only" 10^-3 m^2/s^3. This is in fact a very high eddy > dissipation rate and should not use "only". And the logic of the whole > sentence does not look clear to me either. In the revision: We have now removed "only". We have now modified this sentence as the following at l.415-416 on page 20, "...,which is much smaller than the values achieved in the laboratory and engineering applications (Shaw 2003)." > e. In 107-108 the author cited that "the turbulence enhancement on the > collision-coalescence process is sensitive to the initial width of the > DSD" which seems to contradict the finding in this study that the DSD > broadening does not depend on the initial DSD. (see fig.11) We have now added more explanation to avoid misunderstanding, " Li et al. (2018a) showed that, in the absence of condensation, turbulence enhances the collision-coalescence process" at l.107 on page 6. and "This suggests that condensation makes the combined processes almost independent of the initial size distribution, which counteracts the initial width-dependency of the collision-coalescence process (Li et al. 2018a)" at l.515-517 in the last paragraph of the appendix on page 24. > f. According to equation (3), the model does not include the > cooling due to vertical velocity fluctuation. However, it is > stated in line 148 that the updraft cooling is included. > Besides, if there is neither external forcing for T or q nor > updraft cooling term, what is the major source of supersaturation fluctuation? > Is it mainly due to the local droplet condensation? > It seems to me the PDF of Ss' is way wider than the local droplet > condensation could create (see Fig 8, the PDF ranges from -2% to +2%). To avoid misunderstanding, we have now replaced "save" by "excluding". We have now added the following at l.445-448 in the penultimate paragraph of Section 4 on page 21, "Since updraft cooling is neglected in the present study, supersaturation fluctuations are purely caused by turbulence effects through the local condensation rate Cd . This results in extreme values of supersaturation as shown by the tail of the PDF of s in Figure 8, especially for the case with the largest Reλ . This may overcompensate for the condensation/evaporation process." > g. The authors discussed the deterministic vs stochastic collisions in page 12, > however it is not true that the Lagrangian collision detection is deterministic. > First the superdroplet method is also Lagrangian, it is not clear why one is > stochastic but the other is not. Second, the main stochasticity lies in the > fact that Lagrangian method deals with individual particle and accounts for > the randomness of particle's langrangian growth history, which cannot be > captured by Smoluchowski equation. In contrary, the Smoluchowski equation > is a deterministic mean-field equation without any fluctuation. > As stated in line 245 when N_s gets closer to N_p, the superparticle > method becomes stochastic. This is because it gets closer to true > Lagrangian real particle results. We first thank the reviewer for pointing this out and for explaining the differences between these two approaches. We have now removed the statement that "Lagrangian collision detection is deterministic". Also, we have now rephrased the discussion as the following at l.228 on page 11, "The superparticle approach has been argued to be compatible with or superior over the direct Lagrangian collision-coalescence detection method" We have now also added the following at l.248-250 at the last paragraph of Section 2.b on page 12, "This suggests that the superparticle approach does indeed capture the stochasticity of the Lagrangian collision-coalescence detection method sufficiently accurately when N p /N s becomes sufficiently small." > h. The color description in fig. 5 does not match with its caption. We have now corrected it. > i. In line 369, the statement requires some clarification. > It is due to the enhanced evaporation instead of condensational > growth as the droplet decreased to smaller sizes. We have now changed the sentences to the following at l.373-374 on page 18, " The distributions of small droplets become wider with increasing Reλ , which is due to the fact that both evaporation and condensation are enhanced with increasing Reλ." > j. Line 374-378 & 458-459, The Re-dependency doesn't become weaker > as I see from Fig.7. The difference in the left tail become even larger. We have now changed "weak" to "even stronger" at l.378 on page 18. > k. Line 464, what does "parameterization-free scheme" mean? To my > understanding, a scheme is an approach to parameterize a process. We have now replaced the "parameterization-free" by "robust" at l.483 on page 23. > Minor comments: > l. Line 160-161: the time evolution of DSD is very short in any cloud, > relating it directly to cloud-climate feedback is not straight-forwarding > to me. We have now dropped "the time evolution of". > m. Line 148, should it be "same" instead of "save"? To avoid misunderstanding, we have now replaced "save" by "excluding" at l.150 on page 8. > n. Line 371, "only" is a strong word, use "mainly" instead. We have now replaced "only" by "mainly" at l.377 on page 18. > ------------------------------------------------------------------- > Reviewer #3: > This is a resubmission of a previous paper. > I examined the authors' responses to my previous comments. > Unfortunately, most of my comments and criticisms were not > addressed directly. The authors' responses were typically > very short. My main concerns (points 2, 3, 4) were basically > avoided in their response. I am therefore unable to recommend > the paper for publication in this revised form. We have reviewed our changes in response to comments 2, 3, and 4 of the reviewer. We have now made further modifications. In the following we reproduce the original comments of the previous report and discuss our corresponding changes. > 2. Given the work was intended to study the combined growth, I find the > assumption of unity collision efficiency being problematic. One may > argue this assumption augments the effects of condensational growth on > collision-coalescence, as the real collision efficiency for the size > range where the condensational growth is effective is typically small. In the first version of the paper, we discussed the assumption of the unit collision and coalescence efficiency. We have now enriched our discussions about them as the following at l.477-483 in the penultimate paragraph of section 5 on page 22, where we now write: "In the present study, the collision and coalescence efficiency were assumed to be unity, which may substantially overestimate the collisional growth. For example, the largest particle Reynolds number is in excess of 500 in some of our DNS, resulting in droplet deformation and breakup, which can be accounted for in the coalescence efficiency. This suggests the existence of an upper bound for the enhancement of turbulence on collisional growth. Since the turbulence-induced collision efficiency is a very challenging problem (Grabowski and Wang 2013), it may be useful to incorporate a robust scheme of collision efficiency in the superparticle approach." We did already discuss this and compared our results with those of Chen et al, 2018, where the collision efficiency was included. We have now enhanced our discussion at l.431-444 of section 4 on page 20 and 21. Our old paragraph with the new improvements reads: "Chen et al. (2018b) compared droplet size distributions for different ε̄ when both condensation and collision were included. They attributed the condensation-induced collision to the fact that “condensational growth narrows the droplet size distribution (DSD) and provides a great number of similar-sized droplets” (Chen et al. 2018b), which is inconsistent with our finding that condensational growth produces wider distributions with increasing Reλ and therefore facilitates the collisional growth. However, we emphasize that there are two crucial differences compared to our present model. First, the updraft cooling included by Chen et al. (2018b) may suppress the supersaturation fluctuation-induced broadening of the droplet size distributions, first found by Sardina et al. (2018). Updraft cooling may result in more similar-sized droplets generated by the condensation process, which leads to their enhanced collision rate. Second, they included hydrodynamic interactions between droplets. This may modify the way how turbulence affects the collisional growth discussed here." > Furthermore, as shown in other DNS studies, dissipation rate also affects > the collision efficiency. Therefore, their observation of weak effect > of flow dissipation rate may be largely a result of the assumptions made > and the approach taken. We addressed the above question in the first round of revision. To facilitate the review, we first recall our response from that time: "We have now run all the simulations until 600 s = 10 minutes, where we also observe the dependency of f(r,t) on \bar{\epsilon} as shown in Fig.6, 7, 9, and 10." Also, in the abstract of the first round of revisions, we said, "We find that the droplet size distribution broadens with increasing Reynolds number and/or mean energy dissipation rate." Also, at l.470-471 in the first paragraph of conclusion on page 22, we said, "Therefore, the combined condensational and collisional growth is influenced by both the Reynolds number and the mean energy dissipation rate." > 3. It is also troublesome that no quantitative comparison is made between > the authors' results and other DNS results on collision-coalescence > rates and condensational growth. They only use their own data > as reference. In the first revision we responded "We explained this from l.463-471." There we said "Since the turbulence-induced collision efficiency is a very challenging problem (Grabowski and Wang 2013), it may be useful to incorporate a parameterization-free scheme of collision efficiency in the superparticle approach. Entrainment is also omitted, which is supposed to cause strong supersaturation fluctuations. Aerosol activation is not included in the present study. Invoking all the cloud microphysical processes is computationally extremely demanding – even on modern supercomputers. We strive to achieve this in future studies. Due to the aforementioned limitations, we have not attempted to compare droplet-size distributions obtained from the current work with observational data. Such a step would make sense once we have a more realistic representations of the large scales, where the flow is dominated by convective driving instead of volume stirring, as in the present work." which we thought that we had addressed the suggestion to perform a quantitative comparison with other DNS on collision-coalescence rates and condensational growth. We have now addressed the question as discussed in the following and have modified the text substantially. We have now compared our f(r,t) with the one from Chen et al. (2018b) at l.442-444 on page 21, "these two differences result in an overestimation of the combined collisional and condensational growth in the present study. When comparing the tail of f (r, 400) in Figure 7 with Fig.1 in Chen et al. (2018b), our value is about 20% larger than the one in Chen et al. (2018b)." The collision-coalescence was examined in details in "https://journals.ametsoc.org/doi/full/10.1175/JAS-D-18-0081.1", where the \epsilon-dependency of the collision rate was observed and compared against the theories of the collision rate. We also discussed that the \epsilon-dependency of the collision rate is consistent with the work of others. The pure condensation process was investigated in our earlier paper (2019, JAS 19, 639) "https://www.atmos-chem-phys.net/19/639/2019/", where a detailed comparison with the stochastic model developed in other groups are presented. In the present manuscript, we investigate how the combined condensation and collision-coalescence depends on \epsilon and Re, which is based on the previous works of the cloud microphysics community instead of just ours. We have now also added more corresponding references in section 4. > Line 109-113, they indicated that their results on > collision-coalescence are different from other DNS results based on > deterministic collision-coalescence detection. To me, this indicates > that their stochastic Monte-Carlo approach and the use of very small > number of superdroplets could be sources of the problem. In the first round of revision, we corrected our old statement where we addressed the collision-coalescence result of Li et al. (2018a) which we said is consistent with previous DNS studies. "Using a Lagrangian collision-detection method, Chen et al. (2018a) found that turbulence strongly affects the broadening of the size distribution. Li et al. (2018a) showed that, in the absence of condensation, turbulence enhances the collision-coalescence process. They also found that this enhancement effect is sensitive to the initial width of the droplet-size distribution.", which is now at l.105-109 on page 6. This correction is kept in the current revision. > 4. In addition, if we trust their conclusion regarding the importance > of large-scales of turbulence, then the forcing scheme used in their DNS > needs to be critically examined. DNS of box-turbulence with large-scale > forcing scheme could not provide a physically realistic description of > large-scale turbulence. We agree with the referee, and we have searched through the literature whether other groups have discussed the shortcomings of such a forcing scheme. However, this does not seem to be the case, and this is also understandable, because it would ultimately require a comparison with a sufficiently big simulation where buoyancy can be correctly represented. In the previous iteration, we responded "We have now added such a comment at the end of the conclusions, where we say that 'Such a step would make sense once we have a more realistic representations of the large scales, where the flow is dominated by convective driving instead of volume stirring, as in the present work." This was in connection with the interest in comparing with observational data. We have now also discussed further why the volume stirring forcing is adopted in the present study at l.448-452 in the penultimate paragraph of section 4 on page 21, "As discussed in section 2.a, stochastic forcing is adopted in the present study, which cannot sufficiently capture large scales of turbulence. This is limited by the state-of-the-art supercomputer power. This is why all the DNS studies of the turbulence and cloud microphysics communities (e.g. Saito and Gotoh 2018; Chen et al. 2018b) have employed volume-stirring." We hope that our detailed response to the previous report, and our new changes in response to those have convinced the reviewer that we have tried our best to address the main concerns and that we have not avoided them. We also would like to emphasize that we have gone to the state-of-the-art limit of the cloud microphysics and turbulence communities to tackle these problems. The application of the superparticle in cloud microphysics has been endorsed by the cloud micro-physics/macro-physics community. We refer to the workshop “Eulerian vs. Lagrangian methods for cloud microphysics,” held in Krakow in April 2019 and the paper " Modeling of cloud microphysics: Can we do better?" for details.