This paper delves into the investigation of particle number size distributions (PNSDs) and chemical composition of cloud-free, cloud interstitial and residual particles at Mount Daming in the Yangtze River Delta region of China. The research uncovers notable disparities in PNSDs across various conditions and underscores the swift transformations occurring within mere minutes during cloud processes. Innovatively, the study introduces and utilizes an automatic switched inlet system, incorporating a ground-based counterflow virtual impactor (GCVI) and a PM2.5 impactor, offering profound insights into the microphysics of cloud droplets and the influence of aerosol particles on cloud formation. While the emphasis is on PNSDs and chemical composition, a more expansive discussion on the broader ramifications of these findings for atmospheric science and environmental policy could have enriched the paper. Furthermore, a crucial point that requires meticulous attention is the uncertainty associated with the measurements. Specific comments are outlined below.

Introduction section:

(1) The paper underscores the pivotal role of aerosol-cloud interactions (ACIs) in contributing to uncertainties in radiative forcing. It emphasizes that the physical and chemical characteristics of aerosols and clouds are crucial for comprehending the aerosol-cloud interactions. However, the paper lacks clarity on the most significant characteristics that drive ACIs. I would recommend the authors to adequately explain the rationale behind focusing on PNSDs and hygroscopicity.

(2) Furthermore, hygroscopicity, a central theme of the paper, is barely mentioned, making it challenging for readers to grasp the recent advancements in this research field. Additionally, the introduction could benefit from clearer articulation of the scientific questions being addressed, which needs refinement.

Instrumentation:

• I am wondering whether the impact of drying within the ground-based counterflow virtual impactors are examined on the accuracy of PNSD measurements. Please clarify.

Results and Discussion:

(4) The authors describe the dataset in Section 3.1. I suggest relocating this description to the Method section or the Supporting Information for better organization.

(5) The authors observed that Nt was approximately 30% higher than Nmcpc. As previously mentioned, this discrepancy might partially stem from artifacts during the drying process in the GCVI. Could a comparison between PNSD data from GCVI-dried particles and fog monitor data provide any insights into this issue?

(6) The authors attributed the presence of ultrafine particles during these events, beyond the cloud process itself, to possible changes in air masses. A detailed analysis of the influence of air masses throughout the observation period is necessary to support this assertion.

(7) The scavenging efficiency of particles is calculated using Equation (1), based on changes in particle number concentration for each size bin half an hour before (CF particles) and half an hour after the onset of cloud processes (CR particles). However, cloud processes may lead to the formation of secondary species such as sulfate, nitrate, and organics, which could introduce uncertainties in the calculation. These uncertainties should be carefully evaluated. For instance, consider shortening the time periods before and after the cloud process for comparison and utilizing AMS data to assess the potential influence of secondary species formation.

(8) Fig 10: The unit for LWC should be mg m^-3.

The work by Shen et al. addresses the influence of aerosol particles on cloud microphysics, focusing on aerosol size distributions and hygroscopicity at a mountain site in the Yangtze River Delta, China. While the topic is scientifically significant, the manuscript falls short of the required standards in several critical areas. Crucially, it omits essential details about the experimental setup and analysis, such as the GCVI system's performance evaluation, operation and calibration of key instruments, and clear descriptions of data processing methods. These gaps hinder the reproducibility of the research and cast doubt on the reliability of the results, particularly those derived from GCVI measurements. The limited discussion of uncertainties further undermines the credibility of the findings, as robust conclusions require transparency in assessing potential errors.

Additionally, the manuscript requires significant revisions to improve its structure, language, and clarity. Currently, the text suffers from frequent grammatical issues and disorganized presentation, making it difficult to follow the authors’ arguments. Beyond these editorial concerns, there are substantial scientific gaps, including the insufficient contextualization of findings within existing literature and the absence of a detailed comparison of GCVI-derived results to other methods. Furthermore, the overlap in text and content with a parallel manuscript by Liu et al. (https://doi.org/10.5194/egusphere-2024-2264) raises concerns about potential self-plagiarism and the novelty of the work presented here.

Overall, the manuscript requires major revisions in both scientific content and editorial quality to meet the high standards of ACP. These revisions are essential not only to enhance clarity and rigor but also to ensure the integrity and reproducibility of the research. Extensive comments are provided below to assist the authors in addressing these issues.

Detailed comments (in order of appearance):

• Line 34: This sentence needs to be revised. Aerosols don’t “decrease and increase rainfall as a result of their radiative forcing” 
• Line 38: Reference(s) missing.
• Line 39-40: What kind of scavenging do you mean here? Nucleation of impaction scavenging? I think you need to make this distinction already clear earlier on. Also, do these values relate to fog or clouds?
• Line 44-45: Cloud particles can also capture non-soluble particles. Revise and add reference(s).
• Line 46-49: Not the precipitation evaporates but the cloud droplets/particles. The aerosol, which may also consist of soluble material, is not “reemitted into the atmosphere”. They are also there! Please revise.
• Line 50: Not so many studies have used the ground-based version of the CVI so far. I would suggest revising this sentence. A few more relevant publications could be added to this paragraph, discussing the mixing-state, hygroscopicity and coarse-mode/bioaerosols within cloud residuals using the same GCVI as used here (Adachi et al. 2022, Duplessis et al. 2024, Zieger et al. 2023, Pereira Freitas et al. 2024).
• Line 57-59: Why is the nonlinearity between cloud droplet number and aerosols (I assume concentration?) a challenge? Please refine this sentence.
• Line 59: “To enhance the estimation of aerosol-cloud interactions”. What kind of estimation? Do you mean to increase our knowledge or process-understanding? Please revise.
• Sect. 2.1: Are there any existing publications describing the aerosol and meteorological conditions at the site? If so, maybe reference them here.
• Line 96: Maybe also state the mean and STD relative humidity here.
• Line 93-95 and 101-102: This is not really relevant information. The LabView programme information and the definition of the values given for the status of the valve would ideally be moved to the data description (e.g. within a read-me file). 
• Figure 1:
  • I assume that the colored spheres within the cloud should represent the interstitial aerosol, while the blue dots are the cloud droplets. The interstitial aerosol should also be shown outside the cloud, as they will be sampled during cloud free conditions as well. Ideally they will be smaller compared to the droplets.
  • Where was the RH measured?
  • The PM2.5 inlet is not properly described. Which total flow was applied? How was it measured/ensured? What kind of cyclone/brand was used?
  • The position of the fog monitor is a bit surprising. Were cloud droplets really measured at the site or on the roof? A photo of the set-up within the SI might be useful.
  • The GCVI inlet also includes the visibility and precipitation sensor, as well as the small weather station. Please add it to the graph.
  • CCN should be CCNC.
• Line 110-111: Please properly describe what is the air speed (measured within the wind tunnel) and what are the set sampling and counter flows. What was the total instrument sampling flow?
• Line 112: Please also state the mean and standard deviation of the sampling RH.
• Line 113: The referencing regarding the GCVI is not correct here. Roth et al is a different CVI system and Shingler et al. described the CVI used within the GCVI (and not the windtunnel, etc). A proper evaluation of the GCVI system has so far only been done in Karlsson et al. (2021). 
• Line 115: The GCVI does not “tend” to yield a higher number concentration. The enrichment or enhancement factor is the result of the aerosol concentration being concentrated in the CVI inlet. The authors completely miss the evaluation of the sampling efficiency of the GCVI, which is also dependent on the ambient cloud droplet distribution. For this, it is needed to compare the cloud residual number concentrations with the parallel measured droplet size distributions of the fogmonitor (see Karlsson et al., 2021). Alternatively, the sampling efficiency can also be determined by comparing the accumulation or coarse mode number concentrations of the cloud residuals to the ambient aerosol measurements  (see Karlsson et al., 2021 and Pereira Freitas et al., 2024).
• Within the method section, the authors use exactly the same sentences as in their parallel submitted manuscript by Liu et al, currently in discussion (https://egusphere.copernicus.org/preprints/2024/egusphere-2024-2264/). This can be regarded as self-plagiarism. It is also striking that the same four days from April/May 2023 are used in both manuscripts. It almost feels that this work here could be combined with the manuscript by Lui et al. 
• Section 2.2: Basic information like sampling flows, applied corrections and performed calibrations are missing. This is important information which needs to be added for all instruments! A few important points:
  • How was the TSMPS calibrated? Was an impactor installed? Flows? How do integrated and total number concentration compare? Are the size distributions corrected for difusion/impaction losses? Details on the inversion and multiple-charge correction?
  • The MAAP usually runs with a flow of 16.6 lpm. How was it modified to sample behind the GCVI?
  • What kind of corrections were performed for the AMS data? Airbeam correction? Correction for the fragmentation of CHO? Did you determine the composition dependent collection efficiency for the AMS?
  • The supersaturation schedule of the CCNC is quite short. Could you provide an example time series showing that the time was sufficient to get stable concentrations (especially when changing form 0.7% back to 0.1% SS)?
  • Did you apply any loss corrections for the FM-100? See Spiegel et al. (2012). Did you calibrate it with glass beads?
  • In your Fig.1 it seems that all instruments sample behind the GCVI during cloudy conditions (or when the GCVI is on). Could you confirm?
• Line 139: BC should be called eBC (equivalent black carbon)
• Line 171: How do you know that BC “was almost hydrophobic”? Did you measure it or do you assume it or are there previous measurements to back it up?
• Sect. 3.1 shows that there was something not working properly with the TSMPS system. It is not clear why the integrated values were significantly higher for the CF and CI cases, and why it suddenly agrees for the CR case. The total MCPC should always be similar or higher than the integrated values. The authors need to revise and present their detailed TSMPS set-up, check flows, PSL calibrations and zero-measurements (plus give details on the performed loss calculation, see comment above). Otherwise the size distributions are questionable. My suspicion is that the diameter calibration is off in the Aitken-mode particle range, since it agrees better for the CR case. The PSL and high-voltage calibration are therefore key.
• Line 195: The wording “As expected” does not make sense. Please revise.
• Line 210 and Fig.3: The number concentration values for CR will most-likely go down if you include the sampling efficiency of the GCVI (see comment above).
• Fig. 3: 
  • The measured values (solid lines) look very smooth. Did you apply any additional smoothing/averaging? 
  • For the CR cases, I would expect more variability also in the sub-100-nm range. Could you add standard deviations to your averages (or add a more detailed figure in the SI)?
  • The high values in the nucleation mode (~10nm) for the CF case are striking. Maybe this is also driven by some outliers, the authors could also try to use/show median values instead.
• Line 218: Is the value by Karlsson et al. a mean or an estimate?
• Line 239-240: What do you mean by “during these events, beyond the cloud process itself”? Are you suggesting that the cloud is leading to more interstitial aerosol during its presence? I think the confusing thing is that you call the size distribution measured behind the PM2.5 cyclone always CI (cloud interstitial) although there is no cloud present (see e.g. line 234). Suggest to revise this section and make the argumentation clearer.  
• Figure 4: Please add to the caption the inlet behind which these PNSD were measured. I assume PM2.5? Also add if these are mean or median values.
• Line 249: The authors state that Fig. 4 reveals that most significant changes in the PNSD are observed in the hour before the cloud event. However, this is not really evident from Figure 4. It is rather the opposite. The distributions change more after the event (red curves in Fig 4), while the time before the cloud started (T-0.5h) shows very similar PNSD as during the cloud.
• Line 251: How can you determine the critical activation diameter from “the evolution PNSDs throughout the cloud process”? This needs more explanation.
• Sect. 3.3. and Fig.5: The scavenging efficiency values presented here are still questionable since the authors have not determined the (time-dependent!) cloud droplet sampling efficiency of their GCVI (see comment above). This needs to be done first and then the calculations need to be repeated. Although, Figure 5 indicates that the sampling efficiency reaches ~1 on average at larger diameters, I wonder, why? Did you scale the CR PNSD data? If so, this needs to be described! If you did not scale, then it would mean that the larger droplets (which are usually poorly sampled by the GCVI) are not important. However, this would need to be determined case by case. The authors should make much more use of their measured cloud droplet spectra. As will be shown later (Fig 8b and 9b), there is indeed quite a dominance of small droplets around a few micrometers, but the variability is large. The final PNSD from the GCVI inlet (CR) should match the ambient droplet concentration (see Karlsson et al. 2021).
• Line 256-258: “…are likely removed by coagulation processes within the cloud”. How does this work? Isn’t it just measurement uncertainty and potential changes in ambient aerosol concentration (and their corresponding PNSD)?
• Line 260: The entrainment argument is very speculative. Do you have any evidence for this?
• Line 261-263: Shouldn’t it be “before and during cloud” since you used the CR (GCVI PNSD) to determine the activation diameters?
• Line 265-267: At the end of the sentence, you should better say: “changes in air mass during the cloud event”. This is one of the most crucial assumptions you are making in your approach.
• Line 269-270: It depends also on the particle number concentration and the mixing state of the respective ambient aerosol.
• Line 285-287: The authors hypothesize that the ultrafine particles take up the water since they “can be also hygroscopic” and thus inhibit larger particles to grow. This is based on the determined activation diameter (see Fig. 5), which shows quite some uncertainties.
• Line 287-289: The LWC values for the different cloud events are not shown. I would suggest that you include a summarizing table with all the relevant parameters (LWC, activation diameters, kappa values, chemical composition, etc.) to the revised manuscript (also including the variability of the different parameters).
• Paragraph starting in Line 293: Here the authors determine the number concentration of CCN probably using the PNSD measured behind the GCVI and compare it to the CCNC spectra (Fig. 6). First of all, it is not really clear which PNSD were used. If the GCVI data (CR) was used, then you need to include the GCVI sampling efficiency and cut-off diameter, since you only sample a sub-set of the droplet distribution! In addition, why don’t you just use the (corrected) fog monitor data? This will probably lead to different supersaturation values. In any case, you need to thoroughly also address the uncertainties in your calculations!
• Line 310: the PM1 mass concentration will change if you include the sampling efficiency and cut-off diameter of your CR data.
• Line 311: “CI particles had the highest organics mass fraction”. This is not evident from Fig. 7. CI and CR show almost the same organic mass fractions and fluctuations are within error margins. What is evident, is that the black carbon fraction is clearly higher in the CI particles (leading to a lower kappa) compared to the CR and CF cases. This you could discuss as well. A table with mean and standard deviation values for all the fog events would be more convincing here (see comment above).
• Line 329-334: If I understood correctly, you calculated the scavenging efficiencies using the observations before and during the cloud. How did the actual concentrations change/decrease after the cloud? Were the constituents really removed or just activated and then released again?
• Sect. 3.4: This is a nice case study. Ideally you can present it first, before you come to your general results.
• Line 350: In addition to the trajectories, indicating “significant air pollutants” being transported to the site, you could actually show it but presented to corresponding AMS and MAAP data in Fig. 8. Right now, it is just indicative.
• Line 357: How do you know that cloud formation occurred? It could also be that the air mass was changing and cloudy air was transported to the site. At a stationary site, clouds are probably always a moving process and an interplay between meteorology,  transport and aerosol properties. I would write here and within the entire section “cloud presence” or “residence within cloud air”
• The droplet spectra in Fig. 9b is interesting. One can not really see a distinct droplet mode (especially at the beginning of the low visibility). How do you know that these are activated cloud droplets and not hydrated aerosols (haze)? The later distributions at 19:35 and 19:40 could indicate a small droplet mode at around 25 micrometers. You could show a composite of dry and wet PNSD (from the TSMPS) and the droplet distributions (from the FM).
• In addition, as mentioned above, have you corrected the FM for losses (important especially for the larger droplets)? How was the wind speed at the event and how was the FM orientated (this info should be added to the method part). Especially the updraft velocity would be interesting to compare to your case study shown in Fig. 9.
• Sect 3.5: This section needs some thorough revisions. Right now, I am not learning much new here and in parts I am more confused after reading. Many of the statements made here can only be done if the meteorological conditions are similar, which is not easy due to the limited extent of the dataset.
  • First of all, are the scatterplots in Figure 10 just for the cloud event on the 18th of April (as mentioned in the first paragraph) or for the entire period?
  •  Second, and most importantly, some of the statements are very hand-waving and I would recommend focusing on the clear relationships. There is no relationship between the geometric diameter of the CI and CR PNSD and the cloud parameters. So maybe remove it (or move it to the SI)? Also, keep in mind that LWC and Dpe are correlated (larger or growing droplets = more LWC). I would make this point clear.
  • Line 393-395: The inverse relationship between LWC and kappa is indeed interesting. However, changes in meteorology are also a possible explanation. Can you rule out effects of temperature, updraft or air mass change?
  • Third row in Fig 10: I doubt that the N130 is also relevant for the CF, since you have particles smaller than 130 nm that have activated (see Fig. 3), so better replace it with the total number concentration and repeat the analysis (see also comments above).
  • Line 407: There is an inverse relationship between f_N130 and LWC and D_pe, but not between f_N130 and Nd (Fig 10k).
• Within  the conclusions, you need to make clear that these are only a few case studies (less than 24 hours of in cloud data over 4 days) and that the generalization of the results are difficult to make since they all depend on meteorological conditions which are not properly addressed here due to the given limitations.
• Line 443: The uncertainty of 10% is a wild guess, since you have not even performed the loss calculations for the FM and due the fact that the transition between hydrated aerosol and droplets seems to be a continuous regime (see Fig 9b and comments above).
• Line 451: How much higher was it? Could you add some numbers here? The higher CI particle number concentrations could also be due to changes in air mass. 

Minor comments:

• Line 62: “physic-chemical” -> “physico-chemical”
• Fig. 3 caption: Better say “shown for the entire measurement period.” And state that the fits are log-normal fits.
• Within the manuscript, the authors often use the term “cloud processes” but just mean that they are measured during the presence of clouds.  
• Line 346: incoming -> changing (air has hopefully been always around)
• Line 348: are -> were
• Line 391: It should be Fig 10.
• Line 453: Check typos (mechanisms, remains)

References:

Adachi K, Tobo Y, Koike M, Freitas G, Zieger P, Krejci R. Composition and mixing state of Arctic aerosol and cloud residual particles from long-term single-particle observations at Zeppelin Observatory, Svalbard. Atmospheric Chemistry and Physics. 2022 Nov 10;22(21):14421-39.

Duplessis P, Karlsson L, Baccarini A, Wheeler M, Leaitch WR, Svenningsson B, Leck C, Schmale J, Zieger P, Chang RW. Highly Hygroscopic Aerosols Facilitate Summer and Early‐Autumn Cloud Formation at Extremely Low Concentrations Over the Central Arctic Ocean. Journal of Geophysical Research: Atmospheres. 2024 Jan 28;129(2):e2023JD039159 

Karlsson L, Krejci R, Koike M, Ebell K, Zieger P. A long-term study of cloud residuals from low-level Arctic clouds. Atmospheric Chemistry and Physics. 2021 Jun 14;21(11):8933-59.

Pereira Freitas G, Kopec B, Adachi K, Krejci R, Heslin-Rees D, Yttri KE, Hubbard A, Welker JM, Zieger P. Contribution of fluorescent primary biological aerosol particles to low-level Arctic cloud residuals. Atmospheric Chemistry and Physics. 2024 May 13;24(9):5479-94.

Spiegel JK, Zieger P, Bukowiecki N, Hammer E, Weingartner E, Eugster W. Evaluating the capabilities and uncertainties of droplet measurements for the fog droplet spectrometer (FM-100). Atmospheric Measurement Techniques. 2012 Sep 20;5(9):2237-60.

Zieger P, Heslin-Rees D, Karlsson L, Koike M, Modini R, Krejci R. Black carbon scavenging by low-level Arctic clouds. Nature communications. 2023 Sep 7;14(1):5488.