The authors present rare airborne measurements of aerosol and meteorological parameters over the Arctic ocean. Quantifying the relative role of the various sources of Arctic cloud condensation nuclei (CCN) is a challenging task, but necessary in order to improve model uncertainty. Overall, the paper is well-written and I think the results of this study are a valuable contribution to the field as they provide insight into the potential role of new particle formation over the sea ice surface as well as aloft. 

However, I believe more transparency is needed regarding the methodology of the study in order for the results to be interpreted correctly by the reader.  My suggestion is to consider this manuscript for publication after major revisions, as I believe significant changes need to be made. Most of the changes involve including analysis into the manuscript that I am pretty sure the authors have already conducted, but not shown, so the work needed is probably not extensive. I also think that there are some claims that need to be toned down, rephrased, or further contextualized, as the results of this study are not enough to support them.

General comments:

The entire analysis leans on the identification method of newly formed particles, which is nicely demonstrated and explained - in the SI. I absolutely believe that this explanation and exemplary figure are essential parts of the methods and thus belong in the actual manuscript, to convince the reader you have in fact correctly identified particles sourced by new particle formation (NPF). 

The statistics of the observations are only poorly described, leaving an important lack of context for the reader and the potential risk for miss- and overinterpretation. In section 3.1 I suggest adding how much flight time was spent in the boundary layer (BL) and  free troposphere (FT) respectively, at what frequency newly formed particles  (NFP) were identified in the BL (regardless of surface type)  and FT, and then the relative frequency of NFP over sea ice and in the vicinity of clouds. It is important to show to the reader how you identified the 3 atmospheric environments considered. Furthermore, it is stated more than once that no NFP were observed in the BL over open ocean, but this is kind of contradicted in the SI when explaining the 14% non-assigned observations. In figure 1 it is clear NFP were observed over open ocean, was this then not in the BL? More importantly, how much time was actually flown over the open ocean inside the BL? Again, Figure 1 indicates not much. Please clarify and revise, as this is stated as one of your conclusions. 

The manuscript would benefit from a bit more discussion on sources of precursors. The seasonal aspect should be considered, the observations were made in early spring, has biological productivity in the ocean (and presumed production of precursor gases) begun? Have you checked e.g satellite products? The main conclusions should also be set in this context for future reference.

Figure 2d in its current form is highly misleading. Since the measurement time is not evenly distributed across altitudes, nor concurrent in time or space, these profiles do not make sense. If you want to show vertical distributions of number concentrations, I think it should be done in a way where the reader can distinguish between flights and where the number of observations (or flighttime) is reflected. However, the figure is barely mentioned and not discussed in the text, so it could also be omitted.

Detailed comments:

Line 34: I think a correlation should rather be referred to as indirect evidence.

Line 36: See also Heslin-Rees et al, 2020 (https://doi.org/10.5194/acp-20-13671-2020 ) who showed that changes in transport patterns into the Arctic increased the marine influence on the aerosol population, rather than sea ice retreat.

Line 59: I interpret Pilz et al (2024) in the exact opposite way; free tropospheric sources of CCN were more common. Please revisit.

Lines 82-83: Please add whether the aerosol data have also been corrected for diffusion and inertial deposition or not.

Line 114: I suggest removing the word frequently. In line 121 you state it was 24% of the flight time that you identified NFP, whether that is frequent or not is not obvious but subjective.

Line 129: “Newly formed particles detected in the free troposphere account for the majority of our observations” is a misleading statement and can be used to misquote this study. 45% of all PNSD featuring newly formed particles is actually not even the majority of those cases (that would require >50%), and definitely not the majority of your observations. 

Line 130-132: The percentages presented here lack context, they do not constitute a result without knowing how much flight time was spent in each category. 

Figure 2c: How many scans do the non-hatched bars represent? Preferably add the number for each bar, or at least include a minimum and mean value.

Line 142-146: I believe this is the only reference to figure 2d. Mentioning the peaks at 1000 and 3000 m should be followed by discussion, how much observational time does this reflect? Are these peaks representative? In figure 2b it looks like the NPF- occurrence was not very long at these heights.

Line 195: Were researchers led to believe that? In recent years, a lot of effort has been put into making vertical measurements of aitken and nucleation mode particles (e.g Pohorsky et al  (preprint  at https://egusphere.copernicus.org/preprints/2026/egusphere-2026-1068/), need for vertical measurements discussed e.g in Schmale et al, 2021). Would this be the case if the research community believed it wasn’t important? Near-surface measurements are more accessible, and have therefore been conducted to a higher degree.

Line 197-207: The information given here is highly relevant, but I question the conclusion of this section. The cited Weber study observed one NPF events during one in 38 flights, at 4200m. Why do you say that your results (in contrast?) indicate that NPF occurs frequently in the Arctic FT, based on the 11 flights of which two above 3200m if I understand correctly? If you had not encountered NFP during these flights, would you have concluded that NPF may not occur at that height at all? I don’t think so. Similarly, you can also not claim that it happens all the time because you observed it. Overall, I think that a discussion on where NPF “primarily occurs” in the Arctic can not be settled based on this limited set of measurements. 

Line 244: See also Khadir et al, 2023 (https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2023GL104325) for the link between NPF and precipitation found at Zeppelin Observatory. To me, it looks like something happens specifically around 24-30 hours back for the NFP trajectories, particularly in panel 5b,d,e,f,g and i. I think this could be investigated or at least discussed further.

LIne 346: In the ABL case study, figure 7c, The number concentration varied a factor of 2 within 30 minutes, a few times during the flight period. In figure 10c, the number concentration at cloud top is clearly actually the same as at cloud base at first, and goes up after a couple of scans. How can you be sure that the difference you see is actually because you are at cloud base or top, respectively, and not spatial/temporal variability?

Figure 12: Why not show the no NFP cases like in Figure 5?

Line 390: Context missing, how much flight time over ocean and what would you expect during this season? 

Line 398: Where are the clear indications? I believe you have 2 arguments for this, one measurement of higher concentrations of small particles at cloud top (though not consistent throughout the measurement period) and a reference that cloud tops provide favourable conditions for NPF. I disagree that they constitute clear indications.

Lines 404-405: I think the measurements you present, and the analysis of the 3 scenarios are unique and highly valuable to this research field. However, I think this statement is not really grounded in your data. There is no reason to believe that NPF in the Arctic FT is not geographically widespread, but these measurements also don’t prove that they are. Also, what is geographically widespread? Be more precise, or less strong.

The figures 5, 2d, 8, 11 and 12 are difficult to read when printed out because of the grid. Perhaps it can be made softer or sparser.

Summary

This study presents novel measurements of vertically-resolved aerosol size distributions in the Arctic, collected during a flight campaign that was carried out in the vicinity of Svalbard and Greenland in spring 2024. The measurements are further contextualised and investigated with the aid of Lagrangian back trajectories. The study focuses on the occurrence of newly-formed particles in the Arctic boundary layer and free troposphere, and as such constitutes a valuable contribution to a key research question regarding the role of the surface vs. the free troposphere in the sources and sinks of Arctic aerosol. I recommend that the study should be published after some minor revisions, detailed below.

Main comments

Research gap and previous literature: the introduction and other parts of the manuscript rightly raise the question of boundary layer vs. free troposphere new particle formation as a key research gap in our understanding of Arctic aerosol, and highlight that vertically-resolved measurements of aerosol size distributions in the Arctic are currently lacking and are therefore of great value to the community. However, in my opinion there are certain lines in the manuscript that are either too strong or misrepresentative in their view of the conclusions of previous studies. For example, see lines 2-3 in the abstract (“Prior studies have predominantly investigated NPF in the Arctic atmospheric boundary layer (ABL), concluding that this phenomenon primarily takes place close to the surface.”); line 49 (“These latter airborne studies predominantly suggested that NPF close to the surface inside the atmospheric boundary layer (ABL) prevails, and that free tropospheric NPF is less common.”); or lines 190-196 (“The presence of newly formed particles in the Arctic free troposphere distinguishes our observations from previous airborne studies utilizing aircraft and helicopter measurements… these results led researchers to assume that NPF in the Arctic primarily occurs close to the surface”).

It is true that many previous studies regarding observations of new particle formation/newly-formed particles in the Arctic have focused on surface measurements, but in my opinion, this is a result of the relative sparsity of vertically-resolved measurements, and not due to a particular consensus within the community that only the boundary layer is important, as is implied in these sections of the manuscript. I recommend revising these sections of the text to make this distinction clear.

I also note on this subject the Community Comment posted on 29 May 2026 relating to another previous study that presented measurements of newly-formed particles in the Arctic free troposphere. The authors should consider how that study relates to the discussion within this manuscript and include as needed.

Classification of NFP periods: it is not overall clear how the three NFP regimes (free troposphere, ABL above sea ice, vicinity of clouds) were selected. Are these simply individual case studies that were selected by the authors? The fraction of “unclassified” NFP observations is fairly high (figure 2a), almost as high as ABL over sea ice. Figure 2b puts them mostly in the ABL. What kind of conditions do they correspond to?

Similarly at line 388, (“Specifically, these particles were detected in the free troposphere, inside the atmospheric boundary layer (ABL) over sea ice, and in the vicinity of clouds. No clear indications for newly formed particles inside the ABL over open ocean were found.”) it is implied that these three regimes describe an exhaustive framework for all conditions under which NFPs were observed. I would recommend a more in-depth discussion of the unclassified events and how the three regimes were selected to support this conclusion more strongly, or otherwise to amend this text.

Conclusions about process-level drivers and broader relevance of case studies: in my opinion, some of the conclusions made for each of the three regimes are put too strongly compared to what the data shows. Although many of the hypotheses that the authors put forward can certainly be argued to be consistent with what is presented, I do not agree in every case that the data here is enough to rule out other possibilities definitively. Specifically:

• Line 273: “The spatial variability of the number concentration of nucleation mode particles suggests geographically heterogeneous processes and points toward newly formed particles as the result of regional formation rather than long-range transport, as the latter would likely lead to rather constant concentrations of newly formed particles along the flight track.” And 280: “This temporal variability points toward a regional source as well, since it suggests that we observed an NPF event that becomes weaker throughout the day” I struggle to understand this argument that spatial/temporal heterogeneity in number concentration rules out long-range transport. What are the mechanisms that would remove such variability in the nucleation mode if it was formed in an air mass that has been transported? I would be grateful if the authors could explain this argument further.
• Line 394: “With respect to the newly formed particles detected inside the ABL over sea ice, we conclude that these particles are presumably the result of regional NPF events induced by precursor gases (conceivably iodine components) originating from the sea ice, leads, or snow present in the measurement region.” Related to the point above, I believe the measurements presented under section 3.3 could indeed be consistent with a source related to precursors from the sea ice, leads, or snow, but I do not feel that the results in section 3.3 prove this robustly.
• Line 397: “Concerning newly formed particles observed at both cloud tops and cloud bases, we found clear indications that these particles are very likely formed at the cloud tops and subsequently mixed down to the cloud bases, with the cloud tops providing a favorable environment for NPF to occur.” If I understood correctly, in section 3.4 it is argued that because the number concentrations of the nucleation and Aitken modes are higher at cloud top than at cloud base, this indicates that formation occurs at cloud top followed by growth within cloud that causes fewer particles to be observed in these sizes at cloud base. While this interpretation is believable, I think that the words “clear indication” and “very likely” are too strong here without further evidence that this is what takes place (e.g. dedicated large-eddy simulations of the event).
• Line 206: “Our data support these latter observational results and indicate that NPF might occur frequently in the Arctic free troposphere over large geographical areas.” The words “frequently” and “large geographical areas” here are somewhat subjective, I recommend to be more precise. While the measurements in this study are indeed novel and valuable, the frequency or geographical extent of the processes discussed here cannot be assumed outside of this field campaign.
• Line 403: “In particular, for the first time, our study presents observational results which indicate that NPF in the Arctic free troposphere could be a geographically widespread phenomenon, and that free tropospheric NPF is connected to warm-air intrusions.” Here I raise the same point as above about the use of “geographically widespread”. Also, though the discussion about warm air intrusions based on the results in figure 5 is very interesting and certainly warrants further attention, I would recommend to soften the phrase “free troposphere NPF is connected to warm-air intrusions”. The data presented here does not rule out, for example, that free tropospheric NPF could also take place outside of warm air intrusion conditions.

Minor comments

Figure 3b (also to lesser extent figure 6b and 9b): I find it somewhat difficult to distinguish non-NFP trajectories from NFP trajectories. Please consider separating into two subplots or adjusting the transparency of the NFP trajectories.

Figure 5 vs figure 8: Could the two sets of trajectories in figure 8 be combined into one average NFP trajectory for consistency with figures 5 and 12? From what I understand of the text in section 3.3, the only key difference between the results of the two trajectories is that there was more contact with clouds in the trajectories arriving on 15^th April than for those on 13^th April. This could perhaps be summarised in the text and/or with a supplementary figure rather than including both sets of trajectories separately in the main figure and describing them in the main text.

Figures 5, 8 and 12 (also see comment above): although figure 5 aids the comparison of NFP vs. non-NFP conditions for the first case of free troposphere conditions, the equivalent two figures for the other two cases do not provide this direct comparison, presumably because the non-NFP periods are not available in the other two cases. As such, perhaps it would be more informative to combine figures 5, 8 and 12 so that the NFP trajectories of each case can be directly compared. The non-NFP trajectories of the free troposphere case could also be included.