This study by Rinaldi et al. presents ice nucleating particle (INP) concentrations measured in spring, summer, and autumn over three years (2018, 2019, and 2020) at the Gruvebadet observatory in Ny-Ålesund, Svalbard.

While this manuscript presents valuable data and addresses an important topic, it faces significant methodological limitations that affect the reliability of its conclusions. With very brief daily sampling periods (3-4 hours) and uneven seasonal coverage (no data from winter, June, August, or March), the data presented in this study  may not adequately capture the seasonal trends of Arctic INPs. Too many statements regarding agreements and correlations were vague and not supported by scientific quantifications, and the statistical approach lacks rigorous specification and justification. The manuscript motivations, objectives, and conclusions could also be strengthened by better summarizing findings from previous INP studies conducted in Ny-Ålesund and highlighting what new information is provided with the current study. I recommend that this manuscript should be reconsidered for final publication after major revisions.

I strongly encourage the authors to have the manuscript thoroughly revised for language to improve some unclear sentences and the overall flow of the manuscript. I have noted a few specific language issues in my detailed comments, but a more comprehensive revision would help ensure that the scientific content is communicated more clearly and effectively.

Statistical tests and correlations evaluation:

Throughout the manuscript, p-values are reported without specifying which statistical tests were applied, specifically at: Lines 194, 197, 227, 297, and 327, and in Figure 6. This omission is particularly consequential considering that datasets like INP concentrations typically exhibit non-normal distributions spanning several orders of magnitude, where inappropriate tests can lead to invalid statistical conclusions. Thus, in addition to specifying which statistical tests were used, I strongly recommend the authors include justifications for the tests selected based on an analysis of the distribution of the INP concentration data.

In addition, some agreement statements are vague and not supported by quantitative descriptions:

• Line 181: How did the author determine that the agreement was “fairly good”? Please consider using more scientific and quantitative descriptions.
• Line 192 “statistically significant differences”: did the authors conduct a statistical test? If so, which one?
• Line 291 “the variability of nINP appears mostly related to precipitation”: Did the authors do a statistical test or quantification regarding this potential relation, or is this statement purely based on visual evaluation of Figure 6? If so I would recommend a more careful phrasing.
• Line 292 “snow depth on the ground tends to be negatively associated to nINP”: Did the authors quantify this association?
• Line 300 “a clear relation”: Did the authors quantify such relation?

Introduction:

The introduction provides a good overview of previous INP studies conducted in the Arctic and their conclusions regarding the main sources of INPs in this region. However, considering the number of studies that have been conducted at the same sampling site as the results presented here, I recommend the authors add a paragraph focusing on INP  measurements from Svalbard, specifically from Ny-Ålesund, to provide the readers with a clear picture of the current knowledge from this location. Such paragraph should summarize findings from studies which were cited by the authors in the Methods and Results sections:

• Wex et al. (2019)
• Schrod et al. (2020)
• Rinaldi et al. (2021)
• Pasquier et al. (2022)
• Li et al. (2022)
• Li et al. (2023)

As well as references which are currently missing:

• Pereira Freitas et al. (2023)
• Pereira Freitas et al. (2024)
• Tobo et al. (2024)

In addition to summarizing the findings of these previous studies regarding the sources and seasonal cycle of INPs in Ny-Ålesund, the authors might want to highlight what knowledge gap their own study will cover.

Section 2.1:

The brief daily sampling periods (3-4 hours) warrant additional considerations regarding potential diurnal biases in the collected INP dataset. While I understand that short collection periods are necessary to prevent particle overload on the filters, this approach creates a significant gap in capturing the diurnal variability of INPs. The manuscript provides no information regarding the time of day when sampling occurred (e.g., morning, afternoon, or evening) nor if the sampling times varied or were consistent across campaigns. Therefore, I strongly suggest that the precise sampling time windows be specified (the authors could add a Table in the Supplement). In addition, the authors should investigate if the systematic time-of-day effects influence the observed seasonal patterns, or at least acknowledge these limitations and discuss how this might influence interpretation of seasonal trends.

Other factors limiting the interpretation of the results include:

• Notable imbalances in seasonal coverage (28 samples from spring, 33 samples from summer, and 52 samples from autumn) which raises concerns about the representativeness of the data, especially given the authors’ own acknowledgment that "seasonal variations in nINP are lower than the day-to-day variability observed within each campaign" (Lines 201-202). Short campaign durations (typically 2 weeks, with only the autumn 2019 campaign extending to ~2 months) provide limited capacity to capture intra-seasonal variability, which is particularly crucial during transition periods between seasons in the highly dynamic Arctic environment. Although I understand these limitations might be beyond the authors’ control, they should be explicitly acknowledged in the manuscript.
• The complete absence of winter measurements creates a significant gap in the seasonal cycle characterization. I suggest the authors explicitly qualify claims about “seasonal trends” to acknowledge the missing winter component.
• Campaigns’ timing within seasons: a close examination of the campaign dates reveals systematic timing patterns that may affect the representativeness of the seasonal characterizations: spring campaigns occurred exclusively during mid-to-late April through early May (missing March) and summer campaigns were limited to July (missing June and August). The resulting seasonal patterns presented in this study may therefore reflect specific sub-seasonal phenomena rather than capturing the full seasonal variability. As for my previous comments, I suggest the authors explicitly acknowledge the possible sub-seasonal timing biases in each nominal season and discuss how this might affect the representativeness of seasonal characterizations. In addition, I recommend the authors be more specific when discussing period sampled, for example by using “late-spring” rather than simply “spring” to avoid overgeneralizing findings.

Section 2.2:

While the authors report a measurement uncertainty of approximately ±30% for INP concentrations (Line 120), this uncertainty is not visualized in figures, and insufficiently incorporated into seasonal comparisons. This is particularly problematic when comparing modest seasonal differences that approach the magnitude of the measurement uncertainty itself. I highly recommend the authors add error bars in Figures 1, 2, 3, 4, and 5 and discuss how these uncertainties affect the robustness of the observed seasonal changes.       

Section 2.3:

Important method information is missing in this section:

• Section 2.3.1: Where was the precipitation data measured in Ny-Ålesund?
• Section 2.3.2: Could the authors provide more information regarding the black carbon measurements? What inlet was used? What flowrate? Were they any corrections applied to the data?
• Section 2.3.5: Information regarding the correlation analysis is missing (what was calculated and how).
• Please add a section describing the total particle number concentration measurements used to calculate the activated fraction.
• Please add a section regarding the time-lag analysis conducted on surface CHL data.

Section 3.2:

The approach of merging data across multiple years (2018-2020) to characterize seasonality requires stronger statistical justification and assessment of inter-annual variability. While the authors claim "very good agreement of the data distributions for the same season over different years" (Line 187), they do not provide quantitative analysis to support this assertion. This aggregation approach is particularly concerning when the authors later invoke "interannual variability of meteorological conditions and aerosol particle sources" (Line 221) to explain discrepancies with Wex et al. (2019). In addition, the authors do not discuss how representative their dataset is relative to the seasonal cycle of INPs beyond their statement Lines 188-190 which is insufficient to quantify representativeness. I would recommend the authors present a more quantitative analysis of inter-annual variability to substantiate the claim of “very good agreement”, and analyze meteorological and particle data over several seasons to determine how representative their own dataset is.

Section 3.3:

This section is titled “Summer to autumn transition” but only includes data from 4 October to 24 November 2019, which, as defined by the authors in the Methods section, correspond to autumn. Thus, I suggest that the authors modify the title of section 3.3 and rephrase any reference to a seasonal transition, including:

• Line 289: “depicts a transition between late summer conditions”
• Line 432: “contribution from late summer through autumn”

In addition to my previous comment regarding vague correlation statements which require more quantitative scientific descriptions, I would recommend the authors add a short conclusion at the end of section 3.3 summarizing the main findings and putting them in perspective with the previous studies conducted at the same location at the same time during the NASCENT project. In particular, it would be useful to highlight what new information the current study provides compared to the findings from Li et al. (2023). Finally, a wide range of aerosol measurements were conducted during the NASCENT project, including data on particle chemical composition and fluorescence. Did the authors investigate potential relations between these parameters and their measured INP concentrations?

Section 3.4.2:

Why was the time spent in contact with land limited to 5% when considering land-influenced air masses? I understand that land contribution was very low throughout the measurements (Fig. 7), but this definition of land-influence air masses is very limited (up to 95% of the time could be spent over a different ground type) and bound to bias the results. I would recommend increasing the percentage, even if it means decreasing the size of the land-influenced subset. If the authors proceed with the current definition, then please consider carefully adjusting your conclusions (as it is done adequately Lines 333-335), in particular at:

• Line 28: “both marine and terrestrial sources result important INP contributors at GVB”.
• Lines 327-328 “land-influenced subset having higher nINP” should be more carefully stated. In addition, how do the authors reconcile this with the findings from section 3.3 where higher INP concentrations were suggested to relate to air masses in contact with seawater?
• Lines 328-329 “clear contribution of land sources” should be carefully rephrased.
• Line 385 “Our analysis points out that both marine and terrestrial sources may contribute to the INP population”.
• Line 439 “terrestrial sources resulted important INP contributors at GVB” should be more carefully stated.

Abstract:

Line 10: It might be worth briefly mentioning the two inlets used since sub and super-micrometer INPs are mentioned later in the abstract.

Line 24: I suggest listing the ground type in parenthesis (seawater, sea ice, land, and snow) to clarify.

Lines 30-31 “Such sources apparently dominate nINP in summer and early autumn outside the major terrestrial INP bursts”: to which part of the manuscript is this referring to? To my understanding, the results presented in Figures 9, S8, S9, and S10 include data from each season sampled and thus cannot provide conclusions specific to summer or autumn period.

Section 2.2:

I recommend adding more details regarding the analysis procedure with the Dynamic Filter Processing Chamber, as it was done in Rinaldi et al. (2021), including information regarding the sample preparation before analysis.

Lines 111 and 116:  The authors mention that the filter samples were stored at ambient temperature up to 6 months after sampling. This raises concerns regarding the preservation of heat-labile biological INPs, which is particularly relevant for Arctic summer samples, where marine biological contributions are hypothesized to be important. Did the authors investigate the impact of such storage protocol on the INP content of the samples? If so it would be a valuable section to add to this manuscript. If not, the authors should explicitly acknowledge the potential impact of storage conditions on INP samples and discuss how this might affect the interpretation of seasonal patterns.

Line 117: Why did the authors select a supersaturation with respect to water of 1.02?

Line 117: The limited temperature range (-15, -18, and -22 °C) examined in this study constrains the authors ability to fully characterize Arctic INPs, especially biological INPs that could be active at warmer temperatures. Although I understand this limitation is due to instrument constrains, it is particularly significant given the manuscript’s focus on marine biogenic sources of INPs which often exhibit ice nucleation activity at temperatures warmer than -15 °C. Thus, I strongly recommend the authors acknowledge the limitation of the temperature range selected and discuss (here and in the Results section) how this might affect the ability to detect and characterize the full spectrum of biological INPs, particularly those of marine origin.

Line 118: How was the INP concentration derived from the number of ice crystals visually detected?

Lines 121-122: Could the authors provide quantitative information regarding the background levels and their variability throughout the campaigns? In addition, how were the measurements corrected for the background and its variability exactly?

Section 3.1:

Lines 178-181: Did the author calculate the activate fraction using the same definition as Li et al. (2023) to confirm their statement?

Section 3.2:

This section is lengthy and could be better structured to improve the overall flow. For example, the authors could consider adding some subsections for the seasonal evolution of the 1) PM₁₀nINP (Lines 183-223), 2) AF (Lines 224-260), and 3) coarse INPs (Lines 261-276).

Lines 220-222: Was the interannual variability of meteorological conditions and aerosol particle sources investigated?

Lines 240-252: The authors hypothesize a relationship between NPF and AF but do not present direct measurements of NPF events or their contribution to the particle population during the periods studied, which could be different than those reported in Song et al. (2022). Although this link between NPF and AF is plausible, I believe that it requires stronger evidence to move beyond speculation. I recommend adding available aerosol size distributions from the periods studied, or at least acknowledging more explicitly the speculative nature of the NPF explanation where direct evidence is lacking.

Lines 255-260: This paragraph seems out of place. The first sentence regarding NPF should be moved to the previous paragraph, or deleted. The second and third sentences regarding predicted changes in the Arctic and potential impact of INPs should be moved elsewhere, perhaps in the conclusions?

Line 261: The definition of coarse INPs (size range between 1 and 10 µm) should be clearly stated somewhere in the manuscript (at the moment it is only mentioned in the caption of Figure 5). In addition, I suggest adding a short sentence to explain how the coarse INP contributions (%) shown in Figure 5 were calculated.

Section 3.3:

Lines 293-294: I recommend highlighting the three periods defined in each panel of Figure 6 using vertical shaded bands.

Line 295: In my opinion, “growing levels of accumulated precipitations” is slightly misleading, or at least it should be mentioned that the second half of the second period is characterized by the lowest precipitations recorded over the whole campaign. Similarly, Line 304 “slight increase if precipitation” is only valid for the very first half of the second period.

Lines 291-297: Have the authors considered potential relation between INP concentrations and relative humidity?

Line 303: I would suggest rephrasing “resulting in a reduction of nINP” to “corresponding to a reduction of nINP”, unless the authors have more evidence to show that it is indeed the change in air masses that caused the decrease in INP concentrations.

Line 306: Please consider replacing “probably” by “potentially” or similar, unless the authors have further evidence of this.

Section 3.4.1

Could this sub-section be renamed “Correlation analysis between black carbon and INP concentrations” to be more accurate?

Lines 312-314: The sentence starting with “Consistently” is misleading as, to my knowledge, Rinaldi et al. (2021) did not show any BC data in their study. Please consider rephrasing.

Section 3.4.3

Lines 344-350: Do I understand correctly that, other than limiting the data to PM₁ INP concentrations recorded at -15 °C in seawater-dominated samples, the entirety of the dataset was used (i.e., data from all seasons studied)? If so, what motivated the authors to do so, instead of keeping the datasets segregated by seasons (spring, summer, and autumn) which would have given more information regarding the seasonal patterns?

Lines 348-350: How do the authors reconcile the choice of using PM₁ INP data with the contribution  of coarse INPs results presented in section 3.2 and Figure 5?

Lines 363-366: I think the end of this sentence is a bit misleading and should be rephrased. The low dependence of the correlation on time lag indicates that the relation between INPs and CHL is not dictated by short-term changes of day scale, which the authors interpret as a hint that such relation is potentially related to seasonal trends of marine biological activity.

Starting from line 374: This reads like a summary/discussion and feels out of place in section 3.4.3. Could these paragraphs be included or merged with the conclusions?

Lines 374-376: In section 3.4.2, the authors stated that “in spring, sampled airmasses had the majority of contacts with sea ice or snow-covered land”. How is this interpreted as evidence that “sources of springtime INPS at GVB are likely located outside the Arctic” as written Lines 375-376? In addition, what do the authors mean by BT analysis here? If this is referring to the results presented in section 3.4.3, I do not understand how these results support the hypothesis that the sources of springtime INPs are likely located outside of the Arctic, since section 3.4.3 considers the entire period of dataset (limited to PM₁/-15 °C data and seawater-dominated samples) and thus cannot provide conclusions specific to springtime. This comment applies to lines 24-27 of the abstract as well. If the authors use “BT analysis” to refer to Figure S7, I suggest they spend more time describing Figure S7 and its findings in the main text.

Line 378-380: Where in this manuscript is it shown that summertime aerosol particles appears  more related to local sources which progressively reduce their contribution towards autumn? If this statement is based on literature, please add the necessary reference. In addition, the authors might want to indicate how this statement relates to INPs.

Conclusions

Lines 428-429: Where in this manuscript is it shown that coarse particles have a significantly higher AF compared to sub-micrometer ones? This comment applies to Lines 22-23 of the abstract as well.

Lines 433: Please consider rephrasing “can be explained by” by “could be related to” or similar, since this was not scientifically quantified.

Lines 437: Where in the manuscript is it shown that local aerosol particle sources dominate during summer and early autumn? This comment applies to Line 27 of the abstract as well (“local INP sources dominate during summer and early autumn”).

Lines 438: Could the authors specify which long-range transported aerosol particles they suggest are contributing to the INP population?

Overall: Could the authors spend some time highlighting what new information this manuscript provides, especially considering the few previous studies that were conducted at the same location over the same time periods, including their own study Rinaldi et al. (2021)?

Figure 1: The spread in the data is not clear from such plots. I strongly recommend representing the data as boxplots (same for Figure 2). In addition, the PM₁₀ and PM₁ data could be presented in the same panel (with different colors) instead of having panels a) and b). This could be done for Figure 2 as well, and then Figure 1 and Figure 2 could be combined as sub-panels.

Figure 3: I recommend adjusting the y-axis scales for each panel to focus on the concentration range covered by the data at each temperature. This also applies to Figure 4.

Figure 6: “Dark period” and “Polar night” are highlighted but never mentioned in the text. Consider removing or adding a mention in the main text. In addition, please explain how the dark period is defined exactly. In addition:

• How can the contribution of coarse INPs be zero around 26 October 2019?
• In panel f, I recommend plotting the data so that the bar width corresponds to the sampling duration of each INP sample.
• In the caption, what do the authors mean exactly by correlation coefficients with respect to time?

Figure 8b: Is there a specific reason why the datapoints are connected across temperatures?

Figure 9: Please add titles and units for each color bar.

Figure S7: Could the “Day of the Year” be replaced by the actual dates, especially in 2019, to better follow the last paragraph of section 3.3?

Figure S8, S9, and S10: The color bars (scales) are missing.

Line 24: “transport” should be “transported”?

Line 25: what do the authors mean by “low-travelling”? low-level?

Line 36: “is” should be moved after “considered” (“One of the main drivers considered is the positive […]”).

Line 49: do the authors mean “mixed-phase cloud formation” instead of “mix-phase”?

Line 58: abbreviation “T” should probably be replaced by “temperatures” here.

Line 61 and throughout the text: The second “c” in McCluskey is capitalized.

Line 68: consider replacing “by shipborne” with “using shipborne”.

Lines 69-71: I recommend moving the part of the sentence “during an Arctic research cruise on the marginal ice zone in the Chukchi Sea” to the end of the sentence to improve flow and clarity.

Line 86: What do the authors mean by “object”?

Line 103 “contextually”: do the authors mean “concurrently with”?

Line 107: “PM” should be defined.

Line 115: I would recommend rephrasing the sentence to introduce the instrument name and its abbreviation: “All the samples were analysed using the membrane filter technique Dynamic Filter Processing Chamber (DFPC) presented in Santachiara et al. (2010) […]”.

Line 130: “Gruvebadet” should be “GVB” to be consistent with the notations used throughout the manuscript.

Line 135: define abbreviation HYSPLIT.

Line 155: Could the authors add the references corresponding to the concentration-weighted trajectory method?

Lines 158-159: At which altitude were the trajectories simulated? Was it also 100 m above ground level?

Line 168 and throughout: Please avoid expressions such as “anyhow” and “anyway” and consider using other words such as “however” when suitable.

Lines 175-176: I recommend rephrasing this sentence to improve the flow. For example: “Recently, AF measured at T = -15 °C in the immersion freezing mode have been published by Li et al. (2023) who conducted measurements at GVB station in parallel to one of the campaigns of the present study […]”.

Line 177: I recommend rephrasing “The reported AF-15°C levels range approximately between […]” to “The AF reported at -15 °C range between approximately […]”.

Line 179: “normalized nINP on the total particle number concentration” should be normalized “by” or “with”?

Line 200 “indeed”: do the authors mean “instead”?

Line 215: Please consider moving “also” before “explain”.

Line 216: Please consider removing “also” to avoid repetition.

Line 223: “Artic” should be “Arctic”.

Line 229: The reference to Figure S5 (Line 232) could be moved to the end of this first sentence.

Line 281: Please consider replacing “by” by “with” in “never investigated by the DFPC […]”.

Line 292 “In detail”: Do the authors mean “In particular” or “More specifically”?

Line 296: Please consider replacing “Anyhow” by “However”.

Line 302: Is Fig. S3 the wrong reference here?

Line 312: Please consider adding “for” before “the spring time Arctic haze […]”

Line 323: I recommend rephrasing the beginning of the sentence: “In order to assess the contribution of land and marine sources to the INP population, two subsets were isolated from the nINP dataset […]”.

Line 327: Please specify Fig. 8a.

Line 333: Is Fig. S3 the wrong reference here?

Line 333: Please consider replace “Anyway” but “Nevertheless” or similar.

Line 340: “asses” should be replaced by “assess”.

Line 344: Please consider moving “for the analysis” to the end of the sentence.

Line 346: Please specify Fig. 8b.

Line 362: : Is Fig. S3 the wrong reference here?

Line 381: Please consider replacing “being spring” with “spring being”.

Table 1: Caption should be changed from “Tabel” to “Table”.

4.     References

Li, G., Wieder, J., Pasquier, J. T., Henneberger, J., and Kanji, Z. A.: Predicting atmospheric background number concentration of ice-nucleating particles in the Arctic, Atmospheric Chemistry and Physics, 22, 14441–14454, https://doi.org/10.5194/acp-22-14441-2022, 2022.

Li, G., Wilbourn, E. K., Cheng, Z., Wieder, J., Fagerson, A., Henneberger, J., Motos, G., Traversi, R., Brooks, S. D., Mazzola, M., China, S., Nenes, A., Lohmann, U., Hiranuma, N., and Kanji, Z. A.: Physicochemical characterization and source apportionment of Arctic ice-nucleating particles observed in Ny-Ålesund in autumn 2019, Atmospheric Chemistry and Physics, 23, 10489–10516, https://doi.org/10.5194/acp-23-10489-2023, 2023.

Pasquier, J. T., David, R. O., Freitas, G., Gierens, R., Gramlich, Y., Haslett, S., Li, G., Schäfer, B., Siegel, K., Wieder, J., Adachi, K., Belosi, F., Carlsen, T., Decesari, S., Ebell, K., Gilardoni, S., Gysel-Beer, M., Henneberger, J., Inoue, J., Kanji, Z. A., Koike, M., Kondo, Y., Krejci, R., Lohmann, U., Maturilli, M., Mazzolla, M., Modini, R., Mohr, C., Motos, G., Nenes, A., Nicosia, A., Ohata, S., Paglione, M., Park, S., Pileci, R. E., Ramelli, F., Rinaldi, M., Ritter, C., Sato, K., Storelvmo, T., Tobo, Y., Traversi, R., Viola, A., and Zieger, P.: The Ny-Ålesund Aerosol Cloud Experiment (NASCENT): Overview and First Results, https://doi.org/10.1175/BAMS-D-21-0034.1, 2022.

Pereira Freitas, G., Adachi, K., Conen, F., Heslin-Rees, D., Krejci, R., Tobo, Y., Yttri, K. E., and Zieger, P.: Regionally sourced bioaerosols drive high-temperature ice nucleating particles in the Arctic, Nat Commun, 14, 5997, https://doi.org/10.1038/s41467-023-41696-7, 2023.

Pereira Freitas, G., Kopec, B., Adachi, K., Krejci, R., Heslin-Rees, D., Yttri, K. E., Hubbard, A., Welker, J. M., and Zieger, P.: Contribution of fluorescent primary biological aerosol particles to low-level Arctic cloud residuals, Atmospheric Chemistry and Physics, 24, 5479–5494, https://doi.org/10.5194/acp-24-5479-2024, 2024.

Rinaldi, M., Hiranuma, N., Santachiara, G., Mazzola, M., Mansour, K., Paglione, M., Rodriguez, C. A., Traversi, R., Becagli, S., Cappelletti, D., and Belosi, F.: Ice-nucleating particle concentration measurements from Ny-Ålesund during the Arctic spring–summer in 2018, Atmos. Chem. Phys., 21, 14725–14748, https://doi.org/10.5194/acp-21-14725-2021, 2021.

Schrod, J., Thomson, E. S., Weber, D., Kossmann, J., Pöhlker, C., Saturno, J., Ditas, F., Artaxo, P., Clouard, V., Saurel, J.-M., Ebert, M., Curtius, J., and Bingemer, H. G.: Long-term deposition and condensation ice-nucleating particle measurements from four stations across the globe, Atmospheric Chemistry and Physics, 20, 15983–16006, https://doi.org/10.5194/acp-20-15983-2020, 2020.

Song, C., Becagli, S., Beddows, D. C. S., Brean, J., Browse, J., Dai, Q., Dall’Osto, M., Ferracci, V., Harrison, R. M., Harris, N., Li, W., Jones, A. E., Kirchgäßner, A., Kramawijaya, A. G., Kurganskiy, A., Lupi, A., Mazzola, M., Severi, M., Traversi, R., and Shi, Z.: Understanding Sources and Drivers of Size-Resolved Aerosol in the High Arctic Islands of Svalbard Using a Receptor Model Coupled with Machine Learning, Environ. Sci. Technol., 56, 11189–11198, https://doi.org/10.1021/acs.est.1c07796, 2022.

Tobo, Y., Adachi, K., Kawai, K., Matsui, H., Ohata, S., Oshima, N., Kondo, Y., Hermansen, O., Uchida, M., Inoue, J., and Koike, M.: Surface warming in Svalbard may have led to increases in highly active ice-nucleating particles, Commun Earth Environ, 5, 1–10, https://doi.org/10.1038/s43247-024-01677-0, 2024.

Wex, H., Huang, L., Zhang, W., Hung, H., Traversi, R., Becagli, S., Sheesley, R. J., Moffett, C. E., Barrett, T. E., Bossi, R., Skov, H., Hünerbein, A., Lubitz, J., Löffler, M., Linke, O., Hartmann, M., Herenz, P., and Stratmann, F.: Annual variability of ice-nucleating particle concentrations at different Arctic locations, Atmos. Chem. Phys., 19, 5293–5311, https://doi.org/10.5194/acp-19-5293-2019, 2019.

The manuscript by Rinaldi et al. presents a new dataset of ice-nucleating particle (INP) concentrations from the Gruvebadet observatory in Ny-Ålesund (Svalbard), covering spring, summer, and autumn periods during the years 2018–2020. This dataset is valuable, as aerosol–cloud interactions are of particular importance in the Arctic and are considered a potential mechanism contributing to the region's accelerated warming.

However, in my opinion, the overall quality of the study is compromised by a lack of robustness in the discussion of sample representativeness, as well as limited rigor in the application of statistical analyses and comparisons, which rely heavily on qualitative descriptions. These constitute the main methodological weaknesses of the manuscript.

The discussion of the results should be strengthened by making the connections between the presented data and the derived conclusions more explicit and well-supported. The manuscript would also benefit from a language revision and clearer articulation of its goals and main take-home message. While the development of new INP concentration datasets for the Arctic is undoubtedly valuable, it would be helpful for the authors to clarify what specific new insights their study contributes to the existing body of knowledge.

I believe the manuscript has potential, but major revisions are necessary before it can be accepted.

MAJOR COMMENTS

In this section, I provide major comments divided into two parts:

1. General Comments: These refer to overarching issues that affect the manuscript as a whole, including concerns about sampling representativeness, statistical treatment, and the clarity of data interpretation.

2. Section-Specific Comments: These address issues related to individual sections of the manuscript, including suggestions for clarification, methodological details, and improvements in presentation.

General

Sampling and representativeness of the study period

The first issue concerns the reliability of the collected filters and whether the derived data can be considered representative of the seasons in which they were collected. I am skeptical that a two-week sampling period within each season is sufficient to yield seasonally representative results. Do the authors have a justification for this choice? It may be useful to test the representativeness of such subperiods using other, longer datasets, to evaluate how well short sampling windows reflect broader seasonal patterns.

A second concern related to sampling representativeness is the limited daily sampling duration (only 3 to 4 hours per day) without discussion of expected intraday variability or justification for how representative these short time windows are of daily conditions. Additional explanation or analysis would strengthen the credibility of the dataset.

Statistical tools and analysis

Multiple comparisons are presented in this study, using varied metrics for quantification, when provided, for example: difference in % (e.g. line 193), reduction factor (line 195), correlation (e.g. line 311), fold increase (line 226). There is no test specified establishing the statistical significance, even though in most cases, p-values are provided. The level of significance is, however, not uniform throughout the manuscript. A mix of p-values (<0.01, <0.05 and <0.1) is used depending on the specific analysis being done. Additionally, agreements and correlations are often described in a qualitative way: the use of “agreement… fairly good” (line 181), “good agreement” (line 187), “very good level of agreement” (283), or “no clear correlation” (line 311) are some examples.

Clarity of data interpretation

The overall tone of the results discussion is somewhat convoluted and overly lengthy. In several instances, the inclusion of summary tables presenting key values and statistics would help condense the information and improve readability. The main text could then focus on highlighting the general trends and key observations, rather than listing detailed numerical results. As it stands, it is difficult for the reader to retain or identify the main messages of the analysis.

Section-specific

Introduction

The authors should mention the coarse particle contribution to the INP concentration. The analysis of both PM10 and PM1 filters should be justified and contextualized from the beginning.

A clearer presentation of the data gap or the specific type of analysis targeted by the authors would help to sharpen the study’s purpose and make it more transparent to the reader.

Methods

Please review and consider the following gaps in the Methods section:

• A brief explanation of how INP concentrations are derived from the Dynamic Filter Processing Chamber measurements should be included.
• Information on particle number concentration measurements is missing and should be provided.
• The correlation analysis and statistical tools used for comparisons are not described and should be clearly outlined.
• Section 2.3.4 should be renamed to explicitly reflect the inclusion of ground-type contributions. Additionally, the methodology for assessing ground-type contributions should be clearly separated from the description of the satellite-derived ground maps and their categorization.

Results and Discussion

• The authors state that, after analyzing the seasonal distributions of their data, they observe a “good agreement” that justifies merging data from different years by season to study trends. However, this agreement is not supported by any statistical analysis, or at least none is presented in the manuscript. Furthermore, it should be noted that only in 2018 and 2019 is there a partial overlap in the sampling periods for the campaigns classified as spring and summer.
• According to the authors, “seasonal variations in nINP are lower than the day-to-day variability observed within each campaign”. How does the interquartile range influence the comparison between seasons? Is it taken into account in the values provided?.

MINOR COMMENTS

Introduction

• Line 86: The authors should mention that the new dataset corresponds to INP concentrations measured in the condensation freezing mode. Additionally, a brief comment on the relevance of this mode for cloud formation in the Arctic would strengthen the context.

Methods

Section 2.1

• Have blank filters been collected to evaluate background signal levels? How were they collected and stored?
• Line 111: The authors note that the samples were stored at ambient temperature until analysis. However, storage at ambient temperature can affect the ice-nucleating ability of the collected aerosol particles, particularly those of biological origin. Have the authors tested how their storage protocol may influence the results, for instance, by comparing it with cold-storage conditions?

Section 2.2

• Line 115: Please briefly introduce the operating principle of the Dynamic Filter Processing Chamber (DFPC).
• Line 117: Can the authors justify why the selected temperatures and supersaturations were chosen for the analysis?
• Line 120: The reported uncertainty in DFPC-based INP concentrations is 30%. How was this uncertainty accounted for in the subsequent analysis of seasonal trends, for example?
• Line 121: How was the background correction applied? Please specify the method used and provide appropriate citations.

Section 2.3

• Line 126: Please specify the location from which the rain data was obtained.
• Line 130: What is the temporal resolution of the black carbon data? How were they temporally aligned with the INP observations?

Results and discussion

Section 3.1

• Line 171: Please specify how particle number concentration was measured.
• Line 179: Could the authors calculate the activated fraction (AF), as done in Li et al. (2023), to quantitatively assess the agreement? Additionally, a quantification of the discrepancy due to the use of different lower size cutoffs would be beneficial.

Section 3.2

• The results and discussion throughout this section should be restructured and better organized to improve readability. Several different aspects are addressed (such as the seasonality of nINP, the activated fraction, and the contributions of fine and coarse particle fractions to nINP). I recommend reorganizing the section to clearly distinguish and structure the discussion around each of these key themes, including subsections if necessary.
• Line 187: Please support the statement “very good agreement” regarding the data distributions with appropriate statistical evidence.
• Line 192: Clarify that the values being compared are medians.
• Lines 192–200: Statistical significance should be assessed and reported for all the comparisons presented. In addition, please standardize the way seasonal changes are quantified—e.g., use either percentage change or increase/decrease factors consistently—or justify the use of different metrics.
• Line 200: Please indicate where in the figures or data the snow and sea-ice melt is shown. Reference the specific figure, panel, or dataset.
• Line 209: Can the authors clarify what is meant by “background of cold INPs”?
• Line 210: How do the studies cited compare quantitatively with the summertime increase reported by the authors?

Section 3.3

• This section seems more appropriate as a case study that could be incorporated under Section 3.2.
• Line 283: The authors mention a “good level of agreement” between their nINP ranges and those measured in parallel by Li et al. (2023) in immersion mode, supported by Figure S6. Please include a quantitative assessment of this agreement. How well do the two datasets align when compared as time series? Additionally, how different did the authors expect the datasets to be, given that different freezing modes were investigated?
• Line 293 and Figure 6: The three study periods should be more clearly identifiable in Figure 6. As currently presented, the lines marking the “dark period” and “polar night” distract from clearly distinguishing the discussed periods.
• Line 302: The reference to Figure S3 appears to be incorrect. Figure S3 does not depict air mass trajectories.

Section 3.4

• Line 314 and Table 2: I strongly recommend revising the code to report statistical significance using a more standard notation, such as ** (p < 0.01), * (p < 0.05), and † (p < 0.1). Note that p-values < 0.1 are sometimes interpreted as indicating “marginal significance.”
• Line 323: Can the authors clarify whether these two subsets were taken from the entire study period?
• Line 326: Are there cases where airmasses spend more than 50% of their trajectory time over seawater but are still classified as land-influenced (i.e., over land for more than 5% of the time)?
• Line 327: Please refer to Figure 8a.
• Line 333: Again, Figure S3 does not show the geographical locations of potential sources.
• Line 343: How are marine aerosol emission mechanisms taken into account?
• Line 348: Please briefly comment on why the fine size fraction of INPs correlates better with chlorophyll-ɑ levels.
• Line 362: Incorrect reference to Figure S3.
• Line 365: Can the authors provide an appropriate reference to support their interpretation regarding the lack of dependence on lag time?
• Line 378: Please specify the evidence on which the authors base their statement that the “summertime aerosol particle population appears more related to local (Arctic) sources.”
• Line 380: Please include an explicit reference to the AF mentioned (e.g., figure or table).
• Line 383: Please clearly connect the results reported by Hartmann et al. (2019) to the corresponding reference.

Conclusions

• Line 421: Please clarify what the authors mean by “higher cold INP background” and better connect this statement to the supporting evidence.
• Line 424: This conclusion is trivial since the activated fraction (AF) depends on both INP and non-INP aerosols.
• Line 438: Please elaborate on the potential sources related to the suggested long-range transport mechanism and the associated aerosol types.

Figures and tables

• In Figures 1 and 2, I recommend using semi-transparent symbols for the “all data” points to better illustrate the distribution of individual data points. Alternatively, color-coding could be used to represent the density of observations.
• In Figures S1 and S2, the symbols corresponding to T = –15 °C appear smaller than the others; please ensure consistent symbol sizing across all temperatures.
• I suggest several modifications to Figures 3, 4, and 5 to improve clarity. First, I recommend using traditional box-and-whisker plots (similar to Figure 8a) and adjusting the plot widths to reflect the time period of the measurements. I also encourage adjusting the spacing of the x-axis ticks to make it more uniform. Finally, consider merging Figures 3, 4, and 5 into a single multi-panel figure to facilitate easier comparison.
• Table 1 could include row headers indicating min-max values. “Tabel” should be Table.
• I suggest a few changes to Figure 8a to improve clarity. Temperatures could be placed on the x-axis. The number of colors can be reduced to two: one representing land-influenced and the other seawater-dominated conditions. These modifications would simplify the legend. Additionally, please clarify the meaning of the “x” inside the boxes.

TECHNICAL COMMENTS

A thorough review of technical aspects has not been conducted. However, attention should be paid to the citation list to ensure consistent formatting throughout.

References

Li, G., Wilbourn, E., Cheng, Z., Wieder, J., Fagerson, A., Henneberger, J., Motos, G., Traversi, R., Brooks, S., Mazzola, M., China, S., Nenes, A., Lohmann, U., Hiranuma, N., & Kanji, Z. (2023). Physicochemical characterization and source apportionment of Arctic ice-nucleating particles observed in Ny-Ålesund in autumn 2019. Atmospheric Chemistry and Physics, 23, 10489–10516. https://doi.org/10.5194/acp-23-10489-2023.

Hartmann, M., Blunier, T., Brugger, S. O., Schmale, J., Schwikowski, M., Vogel, A., Wex, H., & Stratmann, F. (2019). Variation of ice nucleating particles in the European Arctic over the last centuries. Geophysical Research Letters, 46, 4007–4016. https://doi.org/10.1029/2019GL082311