Ice-nucleating particle concentration measurements from Ny-Ålesund during the Arctic spring–summer in 2018

Rinaldi, Matteo; Hiranuma, Naruki; Santachiara, Gianni; Mazzola, Mauro; Mansour, Karam; Paglione, Marco; Rodriguez, Cheyanne A.; Traversi, Rita; Becagli, Silvia; Cappelletti, David; Belosi, Franco

doi:https://doi.org/10.5194/acp-21-14725-2021

Articles | Volume 21, issue 19

https://doi.org/10.5194/acp-21-14725-2021

© Author(s) 2021. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/acp-21-14725-2021

© Author(s) 2021. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 21, issue 19

Research article

|

05 Oct 2021

Research article |

| 05 Oct 2021

Ice-nucleating particle concentration measurements from Ny-Ålesund during the Arctic spring–summer in 2018

Matteo Rinaldi, Naruki Hiranuma, Gianni Santachiara, Mauro Mazzola, Karam Mansour, Marco Paglione, Cheyanne A. Rodriguez, Rita Traversi, Silvia Becagli, David Cappelletti, and Franco Belosi

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AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC1: 'Referee comment to Rinaldi et al. (2020)', Anonymous Referee #1, 04 Aug 2020
- AC1: 'Reply on RC1', Matteo Rinaldi, 29 Mar 2021
RC2: 'Review of “Condensation and immersion freezing Ice Nucleating Particle measurements at Ny-Ålesund (Svalbard) during 2018: evidence of multiple source contribution” by Rinaldi et al.', Anonymous Referee #2, 21 Oct 2020
- AC2: 'Reply on RC2', Matteo Rinaldi, 29 Mar 2021

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Matteo Rinaldi on behalf of the Authors (29 Mar 2021) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (02 Apr 2021) by Allan Bertram

RR by Anonymous Referee #2 (18 Apr 2021)

Suggestions for revision or reasons for rejection

Review of “Ice-nucleating particle concentration measurements from Ny-Ålesund during the Arctic Spring-Summer in 2018” by Rinaldi et al.

General comment:
The authors incorporated several changes in the revised version taking into account most of the listed comments from my initial evaluation. The readability of the manuscript was improved, in part by the new structure and the new additions (text, figures/tables, and data, etc.). Given that several parts of the revised version are completely new, additional concerns appear to me. Although I appreciate the efforts made by the authors, I cannot recommend the publication of this manuscript until the following points are carefully addressed.

Major comments:
1. Although English is not my mother tongue, I think that it still needs to be improved. Some examples related to the Introduction only (this apply to the entire text) are provided below.
2. In the first round of comments I asked the following major point: What is different or what is novel in the present study compared to Wex et al. (2019) and Hartmann et al. (2019)? The answer was that “In this study we present parallel observations of immersion and condensation INPs, which was never achieved in the Arctic. One of our major findings is indeed related to the different behaviour of aerosol particles sampled at GVB under different ice nucleation modes”. However, the authors stated in the manuscript and in the reviewer’s response (citing a paper from one of the coauthors) that both heterogeneous ice nucleation mechanisms “might be the same process”. Therefore, they are contradicting themselves. If they authors would like to state that they are reporting the INP concentrations from two different mechanisms, a more in depth analysis is needed where the ice nucleation efficiencies of different aerosol “standards” (e.g., SNOMAX, illite, ATD, etc.) from both instruments are reported. Such experiments need to be run in parallel and using the same aerosol type and particle size. Currently, it is unclear if the observed differences are related to the used methods. Note that the size of the aerosol particles analyzed by both instruments are not the same as the pore size of the filters used by the DFPC (0.45 um) and WT-CRAFT (0.2 um) are not identical. Although it is clear that supermicron particles are likely the most efficient INPs, small particles (between 0.2 um and 0.45 um) can be soluble and change the composition of the droplets and their freezing points. Note that the used filters in both systems are neither the same. Although the authors argued in their answer that the pore size is not important, I disagree with them and I think that the combination of different filter type and different pore size can result in the capture of different aerosol particles. Also, given that the sampling time of the samples analyzed in the WT-CRAFT was much longer (4 days) than the samples analyzed in the DFPC (4 h) it is very likely that the aerosol particles analyzed in both instruments are completely different. It would have been desirable that the same filter was analyzed by both methods.
3. How can the authors confirm the absence of the liquid phase in the DFPC? Is it really possible to have ice crystal growing on individual aerosol particles? From my personal experience it is very difficult to avoid that several particles enter in contact when collected in a filter. Therefore, It would be nice if the authors can provide evidence of how the aerosol particles were distributed in their nitrocellulose filters and a picture on how an ice crystals forms on a single particle.
4. “nINP measured in condensation mode (DFPC) resulted generally higher than those measured in immersion mode (WT-CRAFT) and the deviation became even more apparent towards higher T”. The authors need to clearly discuss this. How realistic is this observation and what is the reasoning for more aerosol particles to act as INPs via the condensation freezing? Also, why at higher temperatures condensation freezing becomes a more efficient pathway to catalyze ice formation compared to immersion freezing?
5. The overall uncertainties of individual ice nucleation measurements cannot explain entirely the observed discrepancy”. How the authors reached this conclusion. What type of analysis was it performed? How the different uncertainties were calculated and combined?
6. “As we do not observe any strong indications of these influence within given uncertainties, it is at least conclusive that the size-dependant collection efficiency of aerosol particles is not a solo-dominating factor causing the difference between nINPWT-CRAFT and nINPDFPC.” This is in indirect conclusion without any clear robust evidence supporting it.
7. “the suppression of INPs due to the sample storage difference does not explain the observed general trend of nINPDFPC > nINPWT-CRAFT.” Why not? How was this evaluated and confirmed?
8. “results from higher ice activation at the conditions of DFPC analyses rather than from higher aerosol particle number concentration in DFPC samples”. I sort of agree with the authors; however, how about the chemical composition? No drastic changes in the aerosol particle concentration does not mean that the chemical composition along 4 days is constant.
9. “A detailed intercomparison of techniques is not under the scope of this study”. I disagree with this statement. Given that the authors are claiming that they report the INPs concentration via two different ice nucleation modes, they need to provide convincing evidence and not unsupported statements such as “suggest that the unexplained concentration gap might stem from other factors, and it is plausible to consider a different sensitivity of Arctic INPs to different ice nucleation modes”.
10. “we conclude that a different sensitivity of Arctic INPs to different ice nucleation modes explains the observed discrepancy.” and “it seems conclusive to address there is ice nucleation mode dependent INP propensity at GVB in 2018 at least.” I disagree with both statements.

Minor comments:

1. I am not sure how useful is to use “T” and “Ts” instead of “temperature” and “temperatures”.
2. “We hypothesized that the nINP variability at a single T can be explained by differences in freezing modes.” What does it mean?
3. It is mentioned that the Back-trajectories were “simulated for an altitude of 100 m above mean sea level (amsl) over the GVB”. Given that the long-range transport of aerosol particles was evaluated in the present study, why higher altitudes were not taken into account as the long-range transport of air masses does not take place that close to the surface?
4. “The range of nINP from Table 1 is roughly comprised between 10-2 and 103 m-3”. I would restrict this to the temperate range of the present study.
5. “suggesting that the dominant INP sources may be located at long distances (scale of the order of 100s-1000s km)” How the authors reached those numbers?
6. Last paragraph Section 4.2. I suggest to expand this a bit more including previous studies where the Arctic aerosol composition and sources are discussed including new particle formation.
7. The authors showed the clear difference in the ice nucleating abilities of submicron and supermicron particles; however, little was mentioned about their composition. I suggest to add a little discussion about this based on the available literature for the Arctic trying to link the particles composition with their size.

Technical Comments:

Line 41: Add a reference after “quantify”.
Line 57: Change “condensation nucleus” by “INP”.
Line 57: Change “a nucleus” by “INP”.
Line 58: Add “at temperatures above 0C” after “water droplet”.
Line 58: Change “in” by “via”.
Line 58: Add “when T is decreased” after “immersion freezing”.
Line 58: What do the authors mean with “extramural”?
Line 65: Remove “according to Fig. 13”.
Line 66: “an exception of K-feldspar”. Do the authors mean that K-feldspar it not a mineral?
Line 67: “biogenic INPs”. It was called biotic above.
Line 67: “to support”. To favor?
Line 75: Delete “next”.
Line 76: “The Ocean was considered to be a prevalent source of INPs”. What do the authors mean?
Lines 76-77: “based on the high negative correlation between nINP and the time since the sampled air masses have been over the open ocean”. Unclear.
Line 79: “probable submicron fragments”. Unclear.
Lines 82-83: “oceanic air tripled after about one day of passage over land”. Unclear.
Line 94: Remove “six samples” and “seven samples” as I found it useless.
Line 96: Should “Santl-Temkiv et al., 2019; Wex et al., 2019” be “Tobo et al. (2019)”?
Line 99: “to fill the present gap of INP observations in the Arctic environment”. The lack of measurements?
Lines 100-101: “by two INP quantification techniques”. This is very awkward.
Lines 102-104: Delete “Recent modeling simulation and remote sensing studies suggest immersion freezing is the most relevant heterogeneous ice nucleation mechanism in mixed-phase clouds, which are prevalent in the Arctic (Hande and Hoose, 2017; Westbrook and Illingworth, 2011).”
Line 175: Delete “Next, we briefly explain our experimental procedure”.
Lines 214-215: “The number concentration in the resulting overlapping range was taken from the SMPS data as SMPS provides more size bins”. Unclear.
Line 228: “operating flow rate of 2.3 m3 h-1” for how long?
Lines 325-235: Delete.
Line 510: “bio INP”. It was not defined before.

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RR by Anonymous Referee #1 (19 Apr 2021)

ED: Reconsider after major revisions (19 Apr 2021) by Allan Bertram

AR by Matteo Rinaldi on behalf of the Authors (28 Jul 2021) Author's response Author's tracked changes Manuscript

ED: Publish subject to minor revisions (review by editor) (08 Aug 2021) by Allan Bertram

Dear authors,

Thank you for carefully considering the referee’s comments and significantly improving their manuscript based on the referee’s comments! I think all the modifications and responses are adequate, except for the response to the first main comment raised by Referee 2. Below I restate the referee’s comment and suggest changes to further address the referee’s comment.

Main comment:
“… It needs to be highlighted in the abstract and conclusion that results are preliminary because of the small sample size. Findings in the abstract and conclusion should be limited to the strong signals that are expected to be reproducable in future investigations. For less clear results it should be stressed that more observations are needed. The limitations of the applied analysis due to the size of the available dataset should be stated clearly in each section. …

In response to the main comment above, I think the authors have done a reasonable job of discussing the limitation of the applied analysis in Section 3 (Results) and Section 4 (Discussion). However, the limitations of the applied analysis are not acknowledged well in the Abstract or Conclusions, especially when discussing the sources of the INPs. Please edit the Abstract and Conclusion so that the limitations of the analysis for source identification are included in the Abstract and Conclusions and/or weaken the statements in the Abstract and Conclusions regarding the source of the INPs so that the Abstract and Conclusions are more consistent with Section 3 and 4. If you can make these changes, I think you will have adequately addressed all the referee's comments.

Sincerely,

Allan

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AR by Matteo Rinaldi on behalf of the Authors (02 Sep 2021) Author's response Author's tracked changes Manuscript

ED: Publish as is (06 Sep 2021) by Allan Bertram

AR by Matteo Rinaldi on behalf of the Authors (14 Sep 2021) Manuscript

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Short summary

This study aims to add to the still scant ice-nucleating particle (INP) observations in the Arctic environment, investigating INP concentrations and potential sources, during spring and summertime, at the ground-level site of GVB. The lack of a clear concentration seasonal trend, in contrast with previous works, shows an important interannual variability of Arctic INP sources, which may be both terrestrial and marine, outside the Arctic haze period.