The manuscript is based on extensive laboratory studies on the mechanism of retention/release of semi-volatile organic compounds upon freezing of raindrop-sized droplets generated from the aqueous extracts of Beijing wintertime urban aerosol. The whole set of experiment is carefully designed and executed, using state-of-the-art equipment including analytical techniques, and the statistical processing of analytical data is adequate meeting all standards of science. The objectives of the manuscript are clear, the hypotheses are valid and important, to explain a potential transport mechanism of semi-volatile organic compounds to the free troposphere. This is relevant in understanding new particle formation in the upper troposphere, which has serious implication on cloud formation and water-particle interactions in a changing climate hosting more water vapour in the atmosphere. The manuscript is comprehensive and well-written, so there is little to criticize expect typography (e.g. using ‘en dash’ characters instead of the ‘minus sign’ in all formulae.) However, the reviewer has a series of serious concerns about the relevance of the laboratory results for real-life atmosphere.

• In the study water-soluble organic compounds (WSOC) in the aqueous extract of wintertime urban aerosol serve as a proxy for real-life composition of droplets of convective clouds. However, large-scale convective cloud formation is not typical during the winter, furthermore, in winter frequent inversion and low mixing layer height prevent surface emissions to be transported to higher altitudes and participate in ice cloud formation. Whereas I agree that studying such a complex mixture may be more informative that of a few cherry-picked model species, to draw meaningful conclusions from the experiments it is important to elaborate on this issue in the manuscript.
• The laboratory experiment is designed to study the freezing of large (2 mm in diameter) raindrops. In real-life mixed phase clouds freezing of large supercooled droplets may occur via multiple mechanisms, such as riming, immersion or contact freezing. These processes are also active for much smaller cloud droplets, i.e. for those below or around the precipitation threshold. I wonder what the probability is for such a large (supercooled) raindrop to survive such effective freezing processes inside a vigorous mixed phase cloud high in the troposphere? I would guess it is very low, but it would be worth discussing anyway.
• In addition, the real-life freezing processes described above are superfast relative to the cooling process applied by the authors in their experiments, which lasts on average for 90 seconds. So again, the question arises how relevant the experimental parameters are for real-life cloud conditions in determining the gas-to-droplet partitioning of organic compounds?
• Another issue to be clarified is the application of the standing ultrasonic wave for levitating the droplets in the experimental setup. It is well-established that ultrasonic energy is an extremely effective way of mixing (see e.g. ultrasonic bath for extraction). So in terms of fluid dynamics, can we assume that in the laboratory experiments the droplets had remained thoroughly mixed until they froze up? If so, how it relates to fluid dynamics prevalent for droplets in convective clouds, in which mixing inside such large droplets may be way much less effective?
• The last issue is that in large droplets mass transfer to the atmosphere is strongly limited by the low surface area to mass ratio. Furthermore, freezing of the droplets starts from the outside because the enthalpy of fusion needs to be dissipated, then freezing forms a solid outer layer that hinders heat and prevents material transport to and from the interior of the droplet. I wonder if this mechanism is largely responsible for the nearly complete retainment of soluble species irrespective of the vast range of their physical and chemical properties?

To summarise my general comments it would be more than welcome if the authors addressed these points in their revised manuscript.

This study presents the retention of organics during the freezing of rain size droplets. The experiments were conducted on aqueous extracts of Beijing urban ambient aerosols using an acoustic levitator. The retention coefficients were determined by freezing the rain size droplets and then measured the remained substances in the frozen droplets. They showed near 1 of retention coefficients for the compounds found in the HRMS in (−)HESI mode, but more variation for the compounds found in (+)HESI mode. Correlations between the estimated chemical properties, such as henry’s low constant, and retention coefficients were discussed. The subject of this manuscript fits the scope of ACP. There are several issues need to be addressed before it can be considered for publication.

Major comments:

1. The manuscript presented in the current form is more like a Measurement Report, as its atmospheric implication is not fully discussed or addressed. The only three nighttime samples also limits a broader atmospheric implication. If I understood correctly, the samples were combined before the freezing and determination of retention coefficient. Why not perform the experiments for individual samples, which one can exam the variation of retention for the same compounds?
2. In the Abstract, the statement in Line 20-22 is overstated as the S- and N-containing compounds are not solely from the NOx and Sox chemistry. The statement in Line 24-26 is not supported by the results of non-sigmoidal relationship or the related discussion. The lower surface-to volume ratio of the large drop size investigated may be one of the reasons. The differences in the experimental techniques, as I understand, may be the main reason, the wind tunnel and levitation, which have totally different air dynamic environments and surrounding corresponding gas-phase organic concentrations that will affect the gas-liquid diffusion and partitioning, and thus the retention.
3. The limitation of this technique or the limited number of sample size should be discussed. For example, as the authors indicate the implication for the convective clouds, will the values measured by this levitation techniques be likely underestimated for the convection system?  
4. The correlation of retention coefficients with chemical properties. The discussion on the results of these correlations should be carefully examined. For example, Line385-392, the R square values are less than 0.1 and the F-test shows no significance, why do the statements still say that they have correlations? Then, the related conclusions are not valid anymore.

Other comments:

1. Line227-234, it is not clear what are those compound number means. How many compounds were used for and analysis? Does that include the 77 and 84 compounds which were selected for additional property calculation?
2. Line 235-237, the sentence is confusing.
3. Figure 2B, why there are such a large portion of the compounds have retention coefficients higher than 1.0?
4. Line316, why a nonnormal distribution is expected or is a true distribution?
5. Line393, in the sentence, the Figure 8 should be Figure 7?
6. Line398 and Figure 8, can you comment on why the R square is so low?
7. Line492 and 505, the authors mean “indicates” not “insulates”?
8. Line505, lower potential to retain, why is likely to reach the upper atmosphere?

This paper addresses an important phenomena potentially impacting new particle formation in the upper troposphere, retention during raindrop freezing.  The work substantially expands the breadth of compounds considered previously through the use of well-described state-of-the-art methods and sophisticated analyses. Results are interesting and provide insights into differences in retention based on compound classification and functionality.  They further suggest impacts of atmospheric chemical processing on retention.  However, the discussion of theory-based hypotheses and rational is somewhat lacking and leaves out relevant previous work, particularly regarding the expected impacts of freezing conditions on retention of low Henry’s law constant compounds.  Further, the conclusions on retention of general chemical classes and the impact of NOx chemistry are overstated based on the evidence presented and on the necessary uncertainty associated with large classes of partially identified compounds. They should be more nuanced.  The manuscript is generally easy to read and understandable but is sometimes repetitive and vague.  It also includes too many graphics that are somewhat repetitive or not informative enough for the main text.  Detailed data on the compound data informing the analysis should also be provided in a supplemental table.

Specific comments, listed by line number (more or less in sequential order):

Abstract (and conclusions): The conclusions on retention are too broadly applied to entire classes of chemicals when there is not enough data specifically for that class. The least supported is for ‘sulfides’ when only one organosulfide was identified in the dataset.  The authors acknowledge this in line 368, but still state the unsupported general conclusion in the abstract and conclusions.

20 and 476.  The fact that sulfides, lipids, aromatic hydrocarbons, and long-chain compounds were not observed in high quantities is not incidental to the conclusions of this work, as small sample size was acknowledged as likely impacting the results. 

21-22.  The statement that anthropogenically related NOx and SOx chemistry enhances retention of the resulting secondary organic aerosol’ is confusingly written. Are the authors saying that the compounds created are more polar and less volatile, increasing the formation of/partitioning to the condensed phase of the aerosol, and also retention of component species during freezing? Clarify this.

23-25.  The sentence is a run on sentence and uses a double negative, which is confusing.  

105-113. A diagram of the freezing experimental setup is needed.

156. Provide a brief reason why phosphorus containing species were not considered.

156 (and elsewhere).  “level 5 (L5) and higher compounds”.  Based on the context, I think ‘higher’ is referring to L1-4.  This is confusing because 1-4 are lower numbers than 5.  This is confusing; it would be better to just provide the L range being referenced.

169. “These properties” suggests more than one type of property was predicted here. However, only the effective Henry’s law constant is mentioned. Where other properties predicted here or is this a typo?

219-220.  Provide some rationale for nonuniform desorption effects being negligible.

330. “The means of the composition classes in (-) HESI vary little, generally less than 5% from each other”. This statement is vague and misleading. The range of means is 0.90 to 0.99 in Table 1.  Just state the range rather than making a statement that could misrepresent the data.

338. “CHO has lower retention …than CHNO in both ionizations”. This is not entirely supported by Table 1 for the positive ionization for which CHO had mean retention of 1.01 and CHNO had a lower mean of 0.94. The median is lower for CHO, but not the mean.  This needs a more precise and nuanced description.

345-346.  The conclusion that nitrogen chemistry of CHO enhances retention is not strongly supported by the data described here, given the above inconsistency (see comment on line 338), and the small differences between the means compared to the error (with error indicated by measured retention coefficients of a lot more than 1 for many compounds).  This really should be stated more as a hypothesis of expected differences between composition class and what might explain them, and the degree to which the evidence supports (or doesn’t support) the hypothesis.

Figures 2, 3 and 4 and Tables 2 and 3 could be provided in supplemental materials, as they are not instrumental to the main results.

Figures 5 and 6 are not both needed and could be combined into one figure (such as with an overlay, or just eliminate Figure 5)

Supplemental material should include a detailed table of compounds used in the analyses (those supporting the tables and figures shown in the main text), including their level, masses, structures, assigned composition, properties predicted, and CAS number match (when applicable and used for properties rather than a model prediction).

375. The sulphur-containing class had the highest mean/median retentions.This should be mentioned and discussed. Line 492 later concludes that SOx reactions enhance retention, but this is not discussed with the results.

385-391.  The trends with molecular weight do not seem to warrant this much discussion given they are inconsistent. Further the reasons involve the influence of vapor pressure and polarity, and require the evidence for each of those relationships. I would make more sense to put this paragraph after those discussions (and shortening it).

392-3 and 396-7.  These are repetitive as they give the same explanation. Perhaps discuss the relationship with polarity first, and then the explanation in 392-3 won’t be necessary.

Some description of the theoretical hypotheses and reasons for why retention is expected to have a relationship with these properties (through reference to previous retention or other literature) is needed.

444-459.  The discussion of the relationship with effective Henry’s law constant does not adequately address the potential influence of the conditions of freezing and freezing kinetics that are expected to have important impacts on retention coefficients for species with lower effective Henry’s constant, as discussed in previous literature.  Although the formation of an ice shell as inhibiting expulsion is mentioned at the end here, it appears to be largely an afterthought.  The data are consistent with freezing conditions that enhance trapping, increasing retention even for the lowest H* compounds (which are expected to have high variability in retention dependent on freezing conditions).  The assumption that a sigmoidal shape is expected, irrespective of freezing conditions does not do the previous literature on the retention phenomena adequate justice. (See for example Stuart and Jacobson 2003, 2004 (cited in this manuscript) and 2005, doi: 10.1007/s10874-006-0948-0).

453-455 (and 469-473). Although this is an appropriate limitation to discuss, it is too narrow. Why focus only on the potential effect of the surface to volume ratio rather than other conditions of freezing, when there are other factors that have been suggested previously as likely important based on theory and modeling?

482- 490. Solubility is expected to influence retention but was not studied here and is only discussed as a rationale for why AA don’t follow polarity and VP trends.  The expected effects of solubility on retention (and its relationship with Henry’s law constant) should be discussed more broadly, along with lack or solubility information limiting the findings.

469. ‘area’. Typo. I believe you mean surface to ‘volume’?

490 and 505. ‘insulates’.  Wrong word choice. I suggest ‘suggests’.