The organic component of aerosol is an important and uncertain aspect of aerosol composition, particularly in the marine atmosphere. Given the importance of aerosols in atmospheric chemistry and climate developing a better understand of this aerosol organic matter is valuable and this paper is a useful contribution to this goal.

This is a thorough and interesting study of aerosols during the spring bloom period in the Sea of Okhotsk. The chemical characterisation particularly of the aerosol is comprehensive, sophisticated. and well described. Overall I believe the paper is well worth publication but I do have some suggestions for modifications prior to final publication.

Firstly I believe it would be useful to include some further descriptions of the conditions at the time of sampling.

1. There is talk of ice algae and I’m not clear whether thee was a lot of ice at the time of sampling or not. This is potentially important because an ice cap can allow a build up of quite high concentrations of marine biogenic gases which are then released rapidly as the ice breaks up.
2. What were the wind conditions like? – this is relevant to ice break up, seawater mixing and bloom development and to seaspray emissions.
3. The apparently very low contribution of terrestrial derived atmospheric aerosol organic matter leads to a question of where the air came from during the sampling period?, so including some air-parcel back trajectories would be useful.

Throughout the discussion the authors should be clear which size of aerosol particles they are discussing. I became confused at several points. Gas phase emissions from seawater will form fine mode particles, while ejection of seawater itself will produce coarse mode particles. Some of the correlations such as in Figure 5 are not really useful given these differences.

Section 3.2 is a bit misleading. As the authors correctly note at the end of this section (line 271-2) the tracer species they use represent only a tiny fraction of the WSOM and so the origin of this material is still essentially unknown, although the correlations to MSA and 3MBTCA  are intriguing. I would suggest reorganising this section to avoid any misunderstandings over what can and cannot be said about the sources of the WSOM.

I was also a little confused by the logic of the argument in sections 3.3 and 3.4. The DOC and DON in seawater is overwhelmingly of high molecular weight and long lived. The observed relationships of DOC and DON in seawater (Fig 9) reflect the fact that they are probably actually bonded together in the same complex organic matter and the variations in concentrations in both compounds may reflect changes in production and consumption, or alternatively may reflect physical mixing of water masses. The correlations of DOC and DON in the aerosols look less convincing in Figure 9, and this correlation too could also represent mixing of air masses. Given its molecular weight, the direct emissions of seawater DOC and DON into the atmosphere  will be via bubble bursting type processes and hence associated with coarse mode aerosol, as with sodium. This process cannot therefore explain the fine mode WSOM or the relationships of WSOM to MSA and other gaseous marine biogenic emissions reported here. All the data I have seen published suggests that marine amine emissions are very small, particularly in comparison to say ammonia emissions. Hence the emission of gaseous organic compounds from seawater into the atmosphere does not seem to be able to explain aerosol DON, although it could arise from marine biogenic gas emissions of other non-nitrogenous compounds with nitrogen being subsequently incorporated during aerosol formation. So I find the authors observations valuable and interesting, I am not sure they do provide a clear explanation of the formation mechanism for the aerosol WSON as implied particularly in the abstract. I would suggest that the logic of the argument in sections 3.3 and 3.4 might therefore be clarified.

This is a review of the manuscript: “Formation of marine atmospheric aerosols associated with the spring phytoplankton bloom after sea ice retreat in the Sea of Okhotsk” by Miyazaki et al. The manuscript refers to samples collected during a field campaign in April 2021 during the bloom and post-bloom periods. The authors want to investigate the effects of marine phytoplankton emissions on the atmospheric organic aerosol composition. The results show an increase in WSON (and an associated decrease in the C:N ratio) and changes in WSOC, although bloom values are very similar to pre-bloom values from a previous study.

While the field of research is extremely interesting, I am afraid that the experimental set-up is not ideal, specifically because a pre-bloom period should have been included to better understand the effects of phytoplankton on altering the molecular composition of OA. Considering the limited number of days investigated (six) during the bloom-decay period, who can tell if the observed changes in WSON and WSOC are related to phytoplankton activity or simply internal variability (e.g., changes in air-mass sources)?

On top of that, I think that the manuscript suffers from key methodological issues: the authors used sonication to extract their organics. However, it is known that organics can degrade during sonication. Did the authors can prove that degradation of the targeted organic molecules is absent? Also, where the filter punches were located before ultrasonication? In plastic vials? How were they cleaned? This is critical as ultrasonication can release impurities from the vial walls if not properly cleaned. How many blanks were collected? How they looked like (this holds for both inorganic and organic species)? Other missing methodological details include: a) at which temperature and vacuum the rotary evaporator was operating? b) How the method for organics was validated (i.e., what is the recovery and reproducibility of the extractions)?

More general and specific comments are reported below together with some suggestions that the authors can use to improve their manuscript.

Overall, my recommendation is major revisions and reconsideration for publication when the concerns are properly addressed.

General comments:

• The authors used an HVAS and an Andersen to collect atmospheric aerosol samples. However, it is not clear in the text which filters were analyzed for what.
• Comparisons between averages were done mainly qualitatively. However, differences must be either significant or not significant with associated p-values. I suggest the authors implement the appropriate statistical tests to discuss differences between averages throughout the entire manuscript. Also, p-values must be provided for all the correlation values discussed in the text.
• From my understanding at L138-140, the authors say that they analyze oxidation products of a-pinene (3-MBTCA, pinic acid and pinonic acid) and of isoprene (2-methyltetrols). Also glucose was mentioned, but not analyzed. Why do they only discuss 3-MBTCA and 2-methyltetrols?
• There is a lot of discussion regarding WSOM, but not much regarding the WIOM. Whether I can understand the reason why WSOM increases during the bloom period (more oxidation of volatile precursors), why WIOM increases during the bloom-decay period (almost doubling)? 
• I don’t fully agree with the conclusions: “the current study highlights the importance of this atmospheric formation process of OM originating from the sea surface after ice melting in the subarctic region”. How, in the absence of data regarding the pre-bloom period? I see that isotope analyses and correlations with MSA can be supportive of this conclusion, but at the same time we do not have a clear chemical characterization of the conditions before the bloom.

Specific comments:

L17-18: I would downsize the emphasis of this sentence: “Relations between WSOC and molecular tracers suggested that the majority of WSOC of marine origin was affected […] instead of primary emissions of sea spray aerosol”. Here the authors based their interpretation on a linear correlation between WSOC and two molecules (3-MBTCA and MSA). Considering that WSOC is composed of several hundreds of different compounds, I think that this is a bit over interpretation.

L27–28: I would reformulate the sentence. Oceans are sources of volatile organic compounds, not of “secondary organic aerosols,” which indeed form in the atmosphere through reaction with atmospheric oxidants.

L65: could you also add a sea-ice map for the corresponding year, showing where the sea-ice was and at which concentration (March-April would be enough).

L68–69: I would put letters a, b, c in the panels of Figure 1 and refer to Fig. 1a etc. in the main text.

L80: Can the authors better clarify which sizes the nine-stage size-segregated aerosol samples refer to?

L70–87: It is not clear to me which aerosol fractions were analyzed for what, as in the results the authors do not refer to any specific aerosol fraction. Also, from which fractions were the organic tracers MSA, 3-MBTCA, 2-MTL, and Na+ analyzed? Based on what the authors write at L101 (“submicrometer sample”), I guess these analyses were done from the HVAS filters, but I would appreciate better clarification.

L88–L95: The authors claim that they did sampling at the surface and at 5-m depth and it seems that they report surface values for DOC and DOM and 5-m depht values for phytoplankton taxa. Why this choice?

L91: with which acid? Which concentration? For how long?

L113: “another cut of filters”, not clear which particle size is taken into account.

L115 and L140–143: Ultrasonication is usually not good for the analysis of organics as they can decompose. Can you please provide some sort of evidence that the targeted organic species are not influenced by sonication? For example, you could test pure water spiked with a known amount of targeted compounds and test it over different sonication times (5–10–20 min). It would be even better if you still have a filter and you can compare extraction just with shaking or with sonication at different times.

L129: Filter cut from HVAS? Andersen? Please specify here and elsewhere.

L139–141: As far as I can understand, the authors report that tracer compounds such as 3-MBTCA, pinic acid, and pinonic acid were analyzed. I was wondering why only 3-MBTCA is reported and not pinic acid and pinonic acid. Ratios between pinic acid and 3-MBTCA could also be particularly interesting from an atmospheric chemistry point of view to investigate how atmospheric aging proceeds.

L151: Which internal standard? At which concentration? Was an internal standard also added before rotary evaporation to assess any potential loss of the analytes or was it only used to monitor instrument performances?

L203-204: What can be the interpretation of these sulfate values? Can be a contribution from fossil sources a reason?

L206: what is the correlation coefficient between sulfate, and OC and WSOC? This information should be added to add consistency to the discussion.

L224–225: While the isotope analyses are undoubtedly interesting, I would integrate also some back-trajectory studies in order to corroborate these findings for both investigated periods (e.g., 72 hrs). This would provide additional evidence to the isotope results in clearly showing the air-mass provenance, and proving that changes in WSON are associated to changes in the marine environment and not to changes in air mass provenance.

L227–232: I would probably avoid a pie chart considering the great variability of the dataset. Discussing average values without their standard deviation doesn’t say much about whether the observed differences are actually significant.

L243 and L250 and L257: when the authors mention the word “significant” or “insignificant” they should also provide a p-value.

L249–252: It would be nice to see scatter plots of the correlations between WSOC and MSA and 3-MBTCA as well as the time series. Also, this sentence should be downsized: a simple correlation with WSOC and MSA, while suggesting a process, cannot really be generalized in the way the authors claimed (“greatly affected”). As I wrote elsewhere, organic aerosol is constituted up to several thousands of compounds.

L259–L261: I believe that this sentence should be downsized, as it is very hard to say if the lack of correlation with methyltetrols can really be associated with a lack of isoprene emissions from the ocean water. While being a tracer for isoprene emissions (I agree), it should be acknowledged that organic aerosols can consist of up to thousands of different compounds.

L262–263: “higher” and “lower” should be avoided. Were the differences in MSA and 3-MBTCA significant or not?

L264: The authors mention “increased sunlight intensity.” Can the authors provide information about radiation in the area during the investigated period (e.g., from reanalysis products) to prove this claim?

L351–352: Could a correlation between WSON and Na help in discerning between direct emissions of N-containing compounds or secondary organic aerosol formation?

L365–366: Please provide statistics in support of this claim. To me, it appears that WSOC and WIOC are influenced by great internal variability, meaning that simply comparing averages can be misleading (unless a statistical test supports the claim).

L368–370: Could you please provide the uncertainties associated with OM? Are these values significantly different?

L370–372: I would water down this sentence. Considering that OA is composed of thousands of different compounds, I think it is too generalizing to attribute sources of WSOA only based on correlations with three chemical species.

L373: “significantly lower”: how did you justify this “significantly”?

Table 1: I would also add values referring to WSON and C:N ratios.

Table 2: “terretrial” is a typo.

Figure 3d: could you consider the possibility to add above -22 something like: “marine sources”, and below -22 “terrestrial sources”.