This manuscript presents eddy covariance measurements of turbulent particle fluxes in the High Arctic from the the ARTofMELT campaign. This manuscript describes a technically competent measurement campaign that yields results broadly consistent with prior studies. It is reported that net deposition dominates over closed ice (median -0.02 × 10⁶ m⁻² s⁻¹), while emission events up to 0.98 × 10⁶ m⁻² s⁻¹ occur during high-wind conditions associated with blowing snow. The manuscript was interesting and nice to read and the resulting dataset is potentially valuable to further the understanding of dynamics governing particle fluxes in the Arctic.

However, in its current form, the manuscript reads primarily as a data description rather than a hypothesis-driven scientific investigation. The analysis remains superficial, and the conclusions do not offer the substantial new mechanistic or process-level insights required for publication in Atmospheric Chemistry and Physics, for which (citing the Aims & Scope of the journal):

“Articles should have important and clearly argued implications for our understanding of the state and behaviour of the atmosphere and climate or present substantial new insights into the atmosphere's role in other parts of the Earth system.”

Because the manuscript does not present significant insights or testable hypothesis, but is rather a dataset and campaign measurement description, I recommend rejection, with the suggestion that the authors consider a more specialized journal after major revision. Below I provide a non‑exhaustive list of methodological issues and suggestions to strengthen the results, should the authors choose to revise for another venue.

As a further note: Michael Tjernström and Birgit Wehner do not appear to meet the criteria for co‑authorship. I suggest removing them from the author list unless their role is clarified and justified.

Major comments:

1. The authors use an empirical wind‑speed/temperature threshold to define blowing snow. As one of the implied claims in the article is that emission events are linked to blowing snow, the authors should provide direct evidence or explicitly acknowledge this as a major caveat. Additionally, other possible causes of emission events should be explored through further data analysis.
2. The inference of emissions as measured net flux minus modelled deposition involves significant uncertainty. The manuscript should explicitly quantify the contribution of both deposition model error and measurement error to the final emission estimates.
3. Size distribution data are available but are used only to correct total particle losses and to model size‑dependent deposition. The manuscript does not explore whether emission and deposition events show distinct size signatures. This is a missed opportunity.
4. The authors exclude pollution events according to certain criteria, which effectively removes concentration peaks from the analysis. As can be seen in Fig. 4c, many peaks are excluded, but the rising and declining concentrations before and after those peaks are not. Not excluding these transitional periods may bias the fluxes. The authors should either exclude them as well (with a suitable buffer) or correct for remaining contamination. They should also consider improving the exclusion criteria; in this sense, particle size distribution could help identify ship exhaust events.
5. Because one of the main scopes appears to be the characterization of emission processes, Sections 3.2 and 3.3 could be merged. Similarly, Figures 8 and 9 could likely be combined (using kernel density estimation instead of histograms to improve visualization). Figures 10a and 10e could be made larger and represented within the same panel.
6. Section 3.5 attempts to estimate Arctic‑wide net particle fluxes and project changes to 2040 using median springtime fluxes from a single campaign. This analysis is far too simplified and should either be developed much more thoroughly or, preferably, removed entirely.

Specific line comments:

L1-4: This part of the abstract seems overly general and could be tailored better to the manuscript

L6: The terms “spatial and temporal” appear several times throughout the manuscript, but the study considers mostly surface‑dependent variability. I suggest removing these terms throughout the manuscript

L6-7: specify surface types here

L13-14: “The results … similations” indicates only one of the potentialities of the dataset, so this sentence should not be definitive

L20-31: this section is too general and should be better tailored to the manuscript scope or summarized

L52: numerical models are mentioned, but the authors should be more specific in this regard, citing the actual models they refer to

L73-74: the authors claim that this dataset is one of the longest dataset for the Arctic region. If this claim is to be made, the duration of other datasets should be explicitly stated in the introduction

L78-79: similarly to the abstract, “The results might provide…”

L86-91: A map would be much clearer than this explanation. It would also allow to represent clearly further information, such as dominating surface type, or meteorological classification (I’m referring to classification 1-6 in Fig. 4)

L157: Depending on whether and how the scope of the manuscript is redefined, the authors might consider moving Figure 2 to the supplementary material/appendix, and to summarize the corresponding methodology paragraphs

L164: The authors should specify how the high-frequency losses were corrected

L222-223: “Particle fluxes … atmospheric stability” is unnecessary

L230 (and following): units should be always reported the first time a variable appears

L247: The same roughness length is applied to all surface types, but including a z0 that varies with surface type should be a fairly low-effort improvement

L253: what does e0 depend on?

L285: The separation between meteorological periods could be made clearer by extending the dotted lines at the top all the way down through the panels

L299-302: These concentration averages might be currently overestimated. The authors should revise this part after improving the exclusion criteria for pollution periods

L339-354: Why are boxplots presented here instead of the usual plots? Why are the authors presenting binned regression analysis rather than analysis on the actual observations, which would be much simpler and more transparent?

L353-354: The authors appear to consider only linear correlation (given that they use binned quantities). Do other relationships emerge when the actual non‑binned data are considered?

L371: Why do other studies in Figure 7 report multiple values while for the current study there is just one?

L421-424: How often do negative values appear? Could the author explore attribute causes more consistently? These instances seem to constitute a non-negligible fraction of the data

L454: It could be useful to specify particle sizes here

L478-495: As mentioned above, this section appears redundant and superficial. I suggest removing it and summarizing it (if at all) as part of the conclusions or future directions

The manuscript aims to investigate the variability of turbulent particle fluxes over three surface types using five weeks of continuous eddy covariance measurements in the High Arctic obtained during the Atmospheric Rivers and the Onset of Arctic Sea Ice Melt (ARTofMELT) campaign. The main conclusion of the study is that 'while net particle deposition is observed to dominate over the packed ice, both emission and deposition are equally observed over leads and open water, underlining the importance of surface heterogeneity and turbulence intensity for the exchange of fluxes in the High Arctic'. The manuscript is mostly well written but needs some additional editing work for better readability to the general reader (mostly pointed out by the other reviewer). The dataset presented could be a valuable resource for advancing the understanding of particle flux dynamics in the Arctic.

My major concern is related to the way surface characterization has been done. Since the main conclusion of the study depends upon the classification of surface types using onboard imagery, more clarity is needed in the manuscript regarding the number of images in a flux period from each camera, image quality, area selected, internal variability in surface type, image sampling, and uncertainty in classification of the surface types using the said algorithm. Further, a solid justification to choose the so-called WAKE algorithm in place of various well-documented and validated open-source image processing algorithms for sea surface identification is needed.

Overall, I am satisfied with the scientific idea and analysis presented in the paper and recommend acceptance of the paper after the above clarification.