The paper describes size resolved measurements of major ions and total carbon at a site in the Netherlands as well as size resolved carbon isotope analyses.  Taken together, the paper addresses relevant scientific questions within the scope of ACP.

The results of the chemical analyses are not really unexpected or novel – they confirm what is known about the composition of the aerosol in the NL. Size resolved composition data, however, are not as commonly available as data for the total aerosol, so the paper adds to existing knowledge. The more interesting part, however, is the part on the carbon isotope analyses. These size-resolved analyses definitely give new data and yield insights into the sources of primary as well as aged OC (fossil, contemporary).

The title clearly reflect the contents of the paper and the abstract provides a concise and complete summary. The overall presentation is well structured and clear and the  language is fluent and precise. Proper credit is given to related work. References, however, are missing in several instances (see comments below). This occurs most often for things that are “generally known” (e.g. levoglucosan as tracer for biomass burning) or in the conclusions section when other studies are mentioned for comparison purposes without adding the reference to these other studies right where they are mentioned. This, however, is not an issue in terms of “proper credit to related work”, but an issue of final copy editing.

In summary, this measurement report definitely merits publication after important revisions (see my comments below)

Reply:

We thank the referee for the careful reading of our manuscript and for the constructive comments. We appreciate the recognition of the scientific relevance of the size-resolved carbon isotope analyses and have carefully considered all suggestions to improve the clarity and balance of the manuscript. Our point-by-point responses are given below.

Major point

One of the major results is the influence of shipping emissions on the aerosol at this coastal location. This is definitely interesting, but the main arguments for this are derived only from the ion (and TC) analysis. Sources (biogenic as well as anthropogenic) of nss-sulphate other than shipping emissions should be mentioned. No info is given why ships are sources of sulphate (of course “everyone knows” that shipping fuels have a high S content….), so this issue must be discussed (including proper references on fuel sulphur content as well as dedicated measurements in ship plumes). The relatively small modern carbon fraction (Fig. 4) in the smallest size range is attributed to traffic (cars, ships) but the link between the two sections of the MS (ions, isotopes) is not made. The issue of shipping as a major source of aerosol sulphate is discussed only regarding total sulphate and non-sea-salt sulphate with some disregard of the back trajectory analysis. There is only one “sea” sample, and even there the back trajectories show that the air mass had passed over source areas in Great Britain. Info on elemental carbon would have helped to substantiate the conclusion about the contribution of shipping emissions to the coastal aerosol at the site, but as these data obviously are not available, nothing can be done in this respect. In the absence of more samples, data on source strengths and a clearer distinction between “sea” and “land” trajectories, I would suggest weakening the categorical statements that shipping emissions _are_ _the_ main source for sulphate. They may well be, but this conclusion would need actually a lot more info and data, which would be out of scope of this study. The abstract should also be changed accordingly (Lines 13 – 15: not “the”, but “a” main source)

Reply:

We thank the referee for this important comment and agree that the role of shipping emissions was stated too categorically in the original manuscript. We agree that the original wording was too strong given the limited number of marine-influenced samples and the available source information. In the revised manuscript, we will therefore soften the wording throughout the text, including the abstract, and discuss shipping emissions as a possible major source rather than the main source. We will also acknowledge other anthropogenic and biogenic sources of non-sea-salt sulfate where appropriate.

General comments

Throughout the MS (and most often in section 3.1) mention of concentrations is qualitative instead of quantitative. Statements about a concentration as being “high” or “low” or “maximum” etc. must be quantified.

Reply:

We partly agree with the referee. Where quantitative values are important to support the interpretation, we will include them in the revised manuscript. However, we prefer not to report numerical values throughout the text, as this would considerably reduce readability. We consider the manuscript as a combination of text, figures, and the accompanying published dataset, which together provide the necessary quantitative information.

As there are only 7 samples for “land” and 1 sample for “sea” influence, some of the statements seem to be too general, and there might be some overinterpretation of the scarce data (most importantly, the “sea” sample). I suggest writing e.g. “in the spring samples” instead of “in spring”, as there are only 2 spring samples. I fully appreciate the difficulty of sampling at this site, but generalizing from a couple of samples for a whole season is risky.

Reply:

We agree with the referee that the limited number of samples does not allow broad conclusions to be drawn for entire seasons or air mass categories. We will therefore revise the wording throughout the manuscript to better reflect the scope of the dataset and avoid overgeneralization.

In addition, we will include a statement at the end of Sect. 2.1 clarifying that, due to the requirements of the different analytical techniques and the need for sufficient filter material, only samples suitable for the complete set of analyses were included. Consequently, the interpretations presented in this study should be regarded as indications rather than a comprehensive characterization of seasonal conditions or the study region.

CCN are first mentioned in the conclusions section? Of course the data are relevant for CCN issues, but if the issue of CCN should stay in the MS, more discussion is needed (including references), and CCN should be mentioned in the introduction section

Reply:

We agree with this suggestion. We will reconsider the discussion of CCN in the revised manuscript. If we retain this aspect, we will introduce it already in the Introduction and expand the discussion accordingly, including the relevant references.

Other points (roughly in order of occurrence)

Line 75: “long term sampling campaign” is not appropriate, as it suggests long term _continuous_ sampling. There are only 8 samples in total with sampling times ranging from 1.7 to 10.6 days (Table 1).

Reply:

We appreciate the referee’s comment and agree that the term long-term sampling campaign could potentially be misunderstood as implying continuous sampling. Our intention was not to indicate continuous measurements, but rather to describe the temporal extent of the study, which covered one year with dedicated sampling periods in each season. Unfortunately, not all collected samples could be included in the final analyses because sufficient filter material was required for the different measurements. To avoid any ambiguity, we will clarify the sampling strategy in the revised manuscript and rephrase long-term sampling campaign as year-long sampling campaign throughout the manuscript.

Line 105: does the customization of distance rings for the impactor stages have an influence on cut size?

Reply:

We thank the referee for raising this point. Yes, the adjustment of the distance rings has an influence on the aerodynamic cut-off diameter of the impactor stages. The aerodynamic cut-off diameter depends on the jet-to-plate distance, which is commonly described by the dimensionless ratio of the jet-to-plate distance to the nozzle diameter (S/W) (Marple and Liu, 1977). Changes in this distance modify the collection efficiency curves and therefore the particle size classification of the impactor stages (Chien et al., 2015). In our case, quartz fibre filters were used, which are considerably thicker than the aluminium foils typically used in cascade impactors. The distance rings were therefore adjusted to compensate for the increased filter thickness and the resulting influence on the collection efficiency, particularly for the smaller particle size ranges.

Line 106: info on storage conditions of pre-heated filters is missing, as is any info on field blanks (possible adsorption artefact of OC?)

End of section 2.1: describe attribution of the samples (aliquots?) for the different analyses; add where the different analyses were performed; shipping conditions; all analysis methods: LOD?

Reply:

We thank the referee for pointing out these omissions. We agree that additional methodological details will improve the reproducibility of the study. In the revised manuscript, we will expand Sect. 2.1 to include information on the storage conditions of the pre-heated filters, sample allocation for the different analyses, shipping conditions, and the laboratories where the analyses were performed. Detection limits will also be added to the respective analytical sections where applicable.

Line 128: quantify instrument blank / field blank

Reply:

We agree with the referee that the blank values should be provided. The information on instrument blanks and field blanks will be added to Sect. 2.3 of the revised manuscript.

P 8, Figure 2: these plots are impossible to interpret. Adding connecting lines might help. A table containing all the values should be given at least as supplementary material, especially as the discussion in the next three pages of text is much too qualitative.

Reply:

We thank the referee for this comment. We agree that the figure contains a large amount of information and can be challenging to interpret. However, we do not think that connecting the individual data points would improve readability. The numerical values shown in the figures are already available in the supplementary dataset (Zenodo: https://doi.org/10.5281/zenodo.19990975). For each plot, a corresponding table containing the underlying data is provided in the supplementary material. Information on data availability is also provided in the preprint (p. 19).

P 9 – 12: quantify all statements referring to “high” “low” etc. concentrations.

Reply:

We partly agree with the referee. Where quantitative values are essential for understanding the interpretation, we will add the corresponding concentrations in the revised manuscript. However, we prefer not to replace every qualitative description with numerical values, as this would make the text unnecessarily complex and reduce readability. The figures and the supplementary data tables provide the detailed quantitative information, while the text focuses on describing the main trends and their interpretation.

Lines 215 ff, discussion of non-sea-salt sulphate: rather vague, no concentrations quantified. The back trajectories for this sample also indicate that the air mass had spent some time over Great Britain, so there could also have been some anthropogenic influence (both in nss-sulfate and carbonaceous material) other than shipping.

Reply:

We thank the referee for this comment and agree that the discussion of non-sea-salt sulfate should better acknowledge other possible anthropogenic influences. The intention of this section was to provide an interpretation of the observed patterns rather than a definitive source attribution. However, we agree that the back trajectories indicate potential influence from anthropogenic source regions, including Great Britain, which could contribute to both non-sea-salt sulfate and carbonaceous material. We will revise this section accordingly and include these possible contributions.

Line 230 – 232 the sentence refers to reduced concentrations of ammonium compounds related to successful reductions of sources by legal restrictions. Either add info and relevant references or delete this sentence.

Reply:

We agree with the referee. The statement was insufficiently supported, and we will add appropriate references to support the discussion of reductions in ammonium-containing aerosol related to emission control measures.

Lines 233 ff: discussions on seasonal differences: the influence of mixing height is mentioned correctly, but otherwise the discussion is focussed on absolute concentrations. The effect of mixing heights (correctly mentioned by the authors) can be removed by using ratios of individual analytes to total analytes. This might change the interpretation of seasonal differences and differences in sources

Reply:

We thank the referee for this comment and agree that normalization approaches can help distinguish changes in source composition from effects related to atmospheric dilution. However, total aerosol mass measurements are not available for this study, and therefore ratios relative to total aerosol mass cannot be calculated. We interpret the referee’s suggestion as referring to normalization relative to the sum of measured analytes. However, this approach also has limitations because not all aerosol components were quantified in our study. Therefore, we prefer to retain the discussion based on the measured concentrations while acknowledging the potential influence of atmospheric mixing conditions.

Lines 250 ff: the statement “In general, in summer more stable weather conditions cause the transport of likely cleaner air masses from the main southwest wind direction. Whereas in autumn the atmosphere over Europe experiences the passage of more low pressure systems, so that the transport of air to the station is less predictable” is unsubstantiated – either add a lot more info or delete.

Reply:

We agree with the referee that this statement is too general without further supporting information. A detailed discussion of seasonal meteorological patterns would go beyond the scope of this study. Therefore, we will remove this statement from the revised manuscript.

Lines 260 ff the discussion on chloride, sodium and calcium concentrations in general reads a bit speculative – either substantiate with literature references or modify the language (e.g. use “might be” instead of “is”…..)

line 268: Substantiate statement on reaction rate

Reply:

We agree with the referee that some statements in this section were too strongly formulated. We will revise the wording to better reflect the uncertainty of the interpretation and use more cautious formulations where appropriate. Relevant references will also be added to support the discussion.

Lines 262 – 283 (discussion on chloride, sodium and calcium to deduct the influence of seas salt): the text refers to a figure (B1) giving size distributions of these ions in mol/m³, but this figure is nowhere to be found? 

Reply:

We thank the referee for pointing this out. Figure B1 is included in the appendix of the preprint (p. 21). We will ensure that the reference to this figure is clearer in the revised manuscript.

Lines 280 – 283: add reference for particle bounce issue

Reply:

We agree with the referee and will add appropriate references regarding particle bounce effects in cascade impactor measurements.

Lines 283 ff: unclear reason for fine calcium: might be emitted from wood/biomass combustion (e.g. Khalil and Rasmussen, 2003, Atmospheric Environment) or from coal fired power plants  (e.g Meij, te Winkel, 2009, J. Aerosol Sci. – for the Netherlands…)

Reply:

We thank the referee for this helpful suggestion and for providing additional references. We will consider these possible sources of fine calcium and include this information in the revised discussion where appropriate.

Lines 284ff section on isotope analysis: Adding subsections for the two types of isotope ratios would be helpful to differentiate between the influence of fossil fuels and atmospheric processing. Another subsection heading could go after line 357

Reply:

We appreciate the referee’s suggestion. However, we prefer to keep the current structure because the interpretations of F(¹⁴C) and δ(¹³C) are closely linked throughout the discussion. In particular, the combined interpretation of both isotope ratios is needed to evaluate especially atmospheric processing, including the application of Eq. (3). Separating these discussions into independent subsections could therefore introduce repetition and reduce the coherence of the interpretation.

Lines 310 ff: the statement: “the impactor samples taken in spring show elevated F (14C, OC) compared to the other seasons” does not seem supported by Figure 4 – the green markings are “drowned” by the grey ones. As this seems to be a problem especially for the large particle range: could the high fraction of “modern” OC in spring be also influenced by pollen? Of course pollen are too large, but the aerodynamic diameter of sub-pollen particles is in this size range

Reply:

We thank the referee for this comment. We do not share the impression that the elevated F (14C, OC) values observed in the spring samples are not supported by Fig. 4. It is not entirely clear to us what is meant by the green symbols being "drowned" by the grey ones. We suspect that this may be related to the colour perception of the figure. Besides the colour coding, the individual seasons are also distinguished by different marker shapes (spring: right-pointing triangles; autumn: left-pointing triangles), which allows the datasets to be clearly separated.

The referee raises an interesting point regarding a possible influence of pollen fragments. Dusek et al. (2017) suggested that pollen fragments may contribute to radiocarbon analyses of elemental carbon. However, as no information on pollen abundance or sub-pollen particles is available for the present study, we do not consider it possible to assess such a contribution. We therefore prefer not to speculate on this aspect in the manuscript.

Figure 4: please connect the data points of the individual size distributions to guide the eye

Reply:

We thank the referee for this suggestion. However, we prefer to retain the current presentation. Each data point represents an independent measurement of a discrete impactor size fraction. Connecting adjacent points would imply a continuous relationship or interpolation between neighbouring size fractions that is not supported by the available data. While such a relationship may exist, it cannot be inferred from the present measurements. In our opinion, the combination of marker colours and shapes provides sufficient visual distinction between the individual datasets.

Lines 328 ff: Please put the relevant references right where the different sources are mentioned

Reply:

We agree with this suggestion and will place the corresponding references directly at the relevant source descriptions in the revised manuscript.

Figure 5 and description in the text: add a (few) sentence(s) on why so many of the data points lie outside the regions marked in green (biomass) and grey (traffic) and on possible reasons for the large overlap between “green” and “grey”

Reply:

We thank the referee for this comment. The possible reasons for deviations of ambient aerosol samples from the literature values for primary source regions are already discussed in the manuscript. In particular, the discussion from line 375 to the end of Section 3.2 addresses the influence of aerosol aging and secondary organic aerosol formation on the observed isotope signatures. Figure 6 further supports this interpretation by illustrating the effect of atmospheric processing on the measured values.

Regarding the overlap between the biomass burning and traffic source ranges, these ranges originate from published literature values and are shown as reference intervals rather than exclusive source classifications. A detailed discussion of the variability and overlap of these literature-derived source signatures is beyond the scope of the present measurement report. Interested readers are referred to Zenker et al. (2020) and Masalaite et al. (2026), where these source signatures and their variability are discussed in detail.

Conclusion section: again, please quantify statements such as major, minor, high, low, etc

Reply:

We agree that quantitative values should be provided where they are essential for supporting a specific statement, and we will revise the manuscript accordingly where appropriate. However, we do not consider it necessary to systematically accompany every qualitative statement with numerical values. The manuscript is intended to be read together with the figures and the published dataset, which provide the detailed quantitative information. In particular, the Conclusions are intended to provide a concise summary of the main findings rather than repeat detailed numerical results, which would reduce readability.

Line 405: “a one year long sampling campaign“ would imply continuous sampling and not just a total of eight samples – please modify

Reply:

We thank the referee for this comment. We agree that the wording could be interpreted as implying continuous sampling. As clarified in our response to the related comment above, this was not the intended meaning. To avoid this ambiguity, we will rephrase the sentence in the revised manuscript as follows:

"Size-resolved aerosol filter samples in the sub-micrometer size range were collected at a site close to the Wadden Sea in the Netherlands during a year-long sampling campaign, with a sampling period of at least one month in each season."

Line 420: change “inorganic ions” to “other inorganic ions”…..

Reply:

We agree and will modify the wording accordingly.

Lines 424 ff, CCN: see general comment above

A sample of missing references: Lines 410, 431, 437, 440, 442, 443, 444, 449 - please check the whole MS for other instances

Reply:

We thank the referee for this comment. We agree that references should be included where needed to support specific statements. However, we do not consider it necessary to systematically repeat references throughout the Conclusions, as the relevant literature is already cited in the corresponding sections where the findings are introduced and discussed in detail. Repeating the same references in the Conclusions would, in our view, not provide additional information for the reader. Nevertheless, we will carefully check the manuscript for any missing references and add them where appropriate.

Technical points:

Figure 1: label bypass line

Reply:

We agree and will add the missing label for the bypass line.

Figure 5: explain the bars also in the caption

Reply:

It is not entirely clear to us whether the referee refers to the shaded grey and green areas. Assuming this is the case, we will expand the figure caption to clarify their meaning.

Figure 6: explain green / grey lines in caption

Reply:

We believe that this information is already included in the caption:

" Average δ(¹³C, OC) of the source filter are shown as lines for the different temperature steps (biomass burning - green line; traffic - gray line)."

Therefore, we do not consider further changes necessary.

Typos:

Line 268 change rage to range

Caption Figure 4: change filter to filters

Reply:

We thank the referee for carefully identifying the typographical errors. These will be corrected in the revised manuscript.

This manuscript presents a comprehensive investigation of the size-resolved chemical composition and carbon isotope characteristics of submicron aerosol particles, based on a one-year measurement campaign conducted at a coastal site in the Netherlands. The authors combine detailed chemical analyses of inorganic ions, total carbon, radiocarbon (F14C) signatures, and temperature-resolved stable carbon isotope (δ13C) measurements of organic carbon to explore the seasonal variability, source contributions, and atmospheric processing of organic aerosol. In particular, the application of size-resolved F14C and temperature-dependent δ13C measurements provides valuable insights into the relative importance of fossil and modern carbon sources, as well as the roles of secondary organic aerosol formation and atmospheric aging processes.

Overall, this is a well-designed, rigorously executed, and clearly written manuscript. The experimental methodology is sound—particularly the integration of a Cu/Ag reduction oven to eliminate potential marine matrix interferences (halogens and NOx) in stable isotope analysis. I therefore consider the manuscript suitable for publication after addressing the following specific comments.

Reply:

We thank the referee for the careful reading of our manuscript and for the constructive and thoughtful comments. We are also grateful for the helpful suggestions, which will improve the clarity and balance of the manuscript. Our point-by-point responses are provided below.

Specific Comments

The experimental design employing a dual-impactor sampling setup to separately collect aerosol from the “land” and “sea” wind sectors is an elegant approach. However, only one marine air mass sample (SU16_S4) was ultimately obtained, with a sampling duration of merely 4.62 days (Line 221). More critically, this sample was collected exclusively in summer and therefore cannot represent the characteristics of marine air masses in other seasons. This renders the core “land vs. sea” comparison statistically very weak. In fact, the 72-hour back trajectories for this “sea” sample (Figure 3d) also traverse substantial continental areas and do not differ markedly from those of the “land” sample shown in Figure 3c. The authors are advised to explicitly acknowledge the single-sample limitation of the marine sector data in the manuscript, and to qualify the corresponding interpretations as case-study/snapshot observations, refraining from overextrapolating to general patterns along the Dutch coast.

Reply:

We thank the referee for this important comment and fully agree with the concerns raised. The limited number of samples, particularly the availability of only one marine-influenced sample, does not allow broad conclusions to be drawn regarding seasonal conditions or differences between marine and continental air masses. We also agree that the marine sample cannot be regarded as representative of purely marine conditions, as the back trajectories indicate additional anthropogenic influence from continental source regions.

In the revised manuscript, we will clarify the scope of the dataset and revise the wording throughout the manuscript to avoid overgeneralization. We will also add a statement to Sect. 2.1 explaining that, due to the material requirements of the different analytical techniques, only samples providing sufficient filter material for the complete set of analyses could be included. Consequently, the interpretations presented in this study should be regarded as indications based on the available dataset rather than a comprehensive characterization of seasonal conditions or air mass types along the Dutch coast.

Based on the observation that sulfate mass concentrations in marine air masses are comparable to or higher than those in continental air masses, the authors conclude that shipping emissions are the predominant source of sulfate at this coastal site (Abstract and Section 3.1). While this inference is directionally reasonable, the chain of evidence remains incomplete for three reasons: (i) only one summer marine air mass sample (SU16_S4) is available, with no marine air mass data from other seasons for comparison (Line 110: “Unfortunately only one sample from the ‘sea’ wind sector could be analyzed”); (ii) the contribution of long-range-transported continental sulfate to the marine air masses has not been quantitatively excluded (HYSPLIT back trajectories indicate that some marine air masses also traversed continental regions); and (iii) supporting evidence from ship emission tracers (e.g., V and Ni) is absent. It is recommended that the discussion explicitly acknowledge the limitations inherent in inferences drawn from a single sample, and adopt more cautious wording.

Reply:

We thank the referee for this valuable comment and agree that the role of shipping emissions was stated too categorically in the original manuscript. Given the limited number of marine-influenced samples and the absence of additional source-specific tracers, the available evidence is not sufficient to identify shipping emissions as the predominant sulfate source at the study site.

In the revised manuscript, we will therefore soften the wording throughout the manuscript, including the abstract, and discuss shipping emissions as one possible important source rather than the main source of sulfate. We will also explicitly acknowledge the limitations associated with the single marine sample and discuss other potential anthropogenic contributions, including long-range transported continental sulfate, as suggested by the back trajectory analysis.

The authors report that F14C(OC) values are highest in spring and attribute this to a springtime rather than summertime maximum of biogenic SOA in the agricultural region of the Netherlands—a finding that differs from observations in more forested regions and is therefore potentially novel. However, the discussion merely cites the similar finding of Dusek et al. (2017) without providing any mechanistic explanation for why an agricultural area would exhibit a spring biogenic SOA peak. Several plausible mechanisms warrant consideration: Does springtime fertilizer application lead to enhanced ammonia emissions that promote SOA formation? Do specific crops (e.g., grassland, maize) release substantial BVOC precursors during their spring growing season? Alternatively, could the elevated spring F14C(OC) reflect primary biogenic emissions (e.g., pollen fragments) rather than secondary biogenic aerosol? A more thorough mechanistic discussion of these possibilities would substantially strengthen the manuscript.

Reply:

We thank the referee for this interesting comment and agree that the elevated F(¹⁴C, OC) values observed in the spring samples raise important scientific questions regarding the underlying mechanisms. Our intention was to present an interpretation of the measurements rather than to provide a definitive explanation, as the available dataset does not allow us to distinguish between the different possible mechanisms.

We agree that enhanced secondary organic aerosol formation associated with agricultural activities, increased biogenic precursor emissions, or contributions from primary biological particles such as pollen fragments are all plausible explanations. We also considered a possible influence of pollen fragments. Dusek et al. (2017) suggested that pollen fragments may contribute to radiocarbon analyses of elemental carbon. However, no information on pollen abundance or other biological tracers is available for the present study, preventing a more conclusive assessment of a possible pollen contribution to the observed F(¹⁴C, OC) values.

We agree that expanding the discussion of these possible mechanisms will strengthen the manuscript and will revise this section accordingly. At the same time, we will emphasize that the present dataset does not allow us to distinguish between these potential explanations. We therefore regard the observed elevated F(¹⁴C, OC) values in the spring samples as an interesting finding that highlights the need for further targeted investigations into the processes controlling modern carbon contributions in this agricultural environment.

Line 60: The statement “aerosol aging is more relevant for larger particles, in the size range of the accumulation mode…” requires appropriate literature citations to support this assertion.

Reply:

We agree with the referee and will carefully review this statement in the revised manuscript. Appropriate literature references supporting the relationship between aerosol aging and particle size will be added.

Section 2.3 (Lines 128–129): Please provide the specific quantitative concentration values for both the instrument blank and the sampling blank.

Reply:

We agree with the referee and will include the quantitative values for both the instrument blank and the sampling blank in Sect. 2.3 of the revised manuscript.

Section 2.5 vs. Section 2.4: Due to inhomogeneous sample deposits on impactor filters, standard OC/EC separation was not possible. In Section 2.5, OC for 14C analysis was extracted by combustion at 375 °C in pure oxygen, whereas in Section 2.4, OC was desorbed at 200 °C, 350 °C, and 650 °C in He. These two protocols likely isolate different OC fractions. The authors should discuss the comparability of the OC extracted by these two systems, and briefly address potential OC charring during thermal processing and its possible impact on F14C(OC) measurements.

Reply:

We thank the referee for this thoughtful comment. For clarification, the statement that standard OC/EC separation was not possible due to the inhomogeneous sample deposits refers to the analysis of carbon concentrations using an OC/EC analyzer described in Sect. 2.3.

We agree that the thermal protocols applied for the F(¹⁴C, OC) and δ(¹³C, OC) analyses do not isolate exactly the same OC fractions. In general, the operational definition of organic carbon depends on the analytical protocol, including the extraction temperature and carrier gas, since there is no sharp boundary between OC and EC, but rather a gradual transition in thermal refractoriness.

The extraction protocols were optimized for their respective analytical purposes. For the F(¹⁴C) analysis, extraction at 375 °C in pure oxygen was selected to maximize OC recovery while minimizing contributions from less refractory EC. The oxidative atmosphere also minimizes the potential for OC charring during the extraction process. In contrast, thermal desorption for the δ(¹³C) analysis is performed in an inert helium atmosphere, where OC charring can occur and the resulting charred carbon is not included in the subsequent isotope analysis.

We agree that a discussion of these methodological differences would be helpful and will evaluate how this can be incorporated into the revised manuscript. However, as the underlying analytical considerations are rather complex, we will aim to keep the discussion concise and appropriate for the scope of a measurement report.

Line 225–226: Please provide a reference value for typical marine background total carbon (TC) concentrations, similar to the reference value given for remote marine non-sea-salt sulfate in Lines 223–224.

Reply:

We thank the referee for this helpful suggestion and agree that including a reference value for marine background TC concentrations would improve the discussion. We will add appropriate literature values in the revised manuscript.

Figure 3 & Section 2.1: Figure 3 presents aerosol mass contributions and 72-hour HYSPLIT back-trajectories for four representative samples. However, neither the figure caption nor Section 2.1 specifies the arrival height used for the HYSPLIT trajectory calculations. Please clarify the specific arrival altitude (e.g., meters above ground level) in both the methods section and the figure caption.

Reply:

We thank the referee for this comment. In the revised manuscript, we will specify the arrival height used for the HYSPLIT trajectory calculations in Sect. 2.1 and in the caption of Fig. 3.

The study by Zenker et al. reports long-term measurements at the coastal location in the Netherlands strategically located to study various sources ant their comparative impact. The study is generally well written although English of the manuscript requires improvement with several sentences of paragraphs difficult to follow. The content of the paper is strong and merrits publication after considering the following comments.

Reply:

We thank the referee for the careful evaluation of our manuscript and for the constructive comments and suggestions. We appreciate the effort invested in reviewing our work and agree that several points raised by the referee help to improve the clarity and discussion of the manuscript. Our point-by-point responses are provided below.

Line 11. Why fossil OC in particles <250nm characteristic only of traffic and not shipping?

Reply:

We thank the referee for this comment. The association of fossil OC in the smallest size range with traffic emissions refers to the interpretation of fine fossil carbon as a characteristic component of (high temperature) combustion-related aerosol, in that sense this would also include shipping “traffic”. Therefore, we agree that shipping emissions can also contribute to fossil OC in this size range. Since we single out shipping emissions later on in our discussion about sulfate concentrations, we will clarify this statement to explicitly include both vehicular and shipping emissions.

Line 61. It is important to note that accumulation mode primarily arises from cloud processing while Aitken mode particles are primary and the leftover from cloud processing. Last but not least, Aitken mode particle residence time is the longest, not of the accumulation mode.

Reply:

We thank the referee for this comment. However, following the most common definitions, Aitken mode particles (roughly 20–100 nm) mainly consist of particles emitted by combustion sources, such as traffic, as well as nucleation mode particles that have grown in size through condensation or coagulation. The Aitken mode is followed by the accumulation mode, which contains particles with diameters between approximately 100 nm and 1000 nm. Condensation and coagulation are also important mechanisms for the growth of particles in the accumulation mode. If cloud processing is relevant in shaping the size distribution, the typical accumulation mode is often sub-divided into an accumulation mode and a larger “droplet” mode. The latter consists of larger particles resulting from cloud processing. To our knowledge it is mainly over remote oceans, where particle number concentrations and condensable vapor concentrations are low, that the accumulation mode is mainly due to cloud processing.

Finally, we do not agree that Aitken mode particles have the longest atmospheric residence time. The longest residence times are generally observed for particles in the accumulation mode size range (e.g., Hobbs, 2000; Jaenicke, 1980).

Line 75. The aim of the study is not very well presented. Long-term sampling certainly helps, but what was the scientific rationale? Import section from Conclusions.

Reply:

We thank the referee for this comment and agree that the scientific objective of the study should be stated more clearly. We will add the following sentence at the end of the Introduction:

"The objective of this study was to characterize the seasonal, air mass and size dependent variation of the aerosol chemical composition and related atmospheric transformation processes at a site close to the Wadden Sea in the Netherlands."

Line 142. Is this step similar to account for charring effect? If not, is unclear.

Reply:

We thank the referee for this question. The reduction oven is not related to accounting for charring effects. The oven is positioned after the organic carbon has been desorbed from the filter samples and converted into CO₂, i.e., after the sample has already left the Sunset OC-EC analyzer.

The purpose of the oven is to remove traces of oxygen, nitrogen oxides, and halogens prior to isotope analysis, as explained in Line 143. We will clarify the position of the reduction oven in the revised manuscript by adding this information and change the sentence in line 142 in the following way:

“For the analysis of the coastal filter samples, the system described by Zenker et al. (2020) was updated to include a reduction oven, which is in line after the samples left the Sunset OC-EC analyzer.”

Line 213. Should be "low ammonia" is a limiting factor?

Reply:

We thank the referee for this comment. The interpretation depends on the perspective. Our intention was to state that ammonia availability can limit ammonium nitrate formation, meaning that high ammonia concentrations are required for substantial ammonium nitrate formation.

To avoid misunderstanding, we will rephrase the sentence in line 213 as follows:

“Since NOx emissions are much more constant over the year, this indicates that low ammonia availability is at least partially a limiting factor for ammonium nitrate formation.”

Line 220. 7% is due to sulphate ion fraction in sea salt composition, so it is a confirmation instead of a finding.

Reply:

We thank the referee for this comment. We agree that the presence of sulfate associated with sea salt is expected from the known ionic composition of seawater and therefore the observation itself is not a new finding. The intention of this statement was to describe the measured contribution of sea salt sulfate in the different particle size ranges.

Line 230. Last sentence of the paragraph has to be rewritten.

Reply:

We thank the referee for this comment. We agree that the statement requires further clarification. However, it is not clear whether the concern refers to the wording itself or to the scientific support of the statement. As mentioned in our response to RC1, the statement regarding reductions in ammonium-containing aerosol related to emission control measures was insufficiently supported, and we will add appropriate references to support this discussion.

Line 247. Despite smaller absolute mass, smaller particles dominate the number of particles.

Reply:

We thank the referee for this comment. However, we would like to clarify that this section discusses the mass concentrations of specific chemical components in different size ranges. Particle number concentrations were not measured in this study.

Line 257. Again low by mass and high by number.

Reply:

We thank the referee for this comment. As stated above, our discussion is based on mass concentrations of chemical components and not on particle number concentrations. Therefore, the interpretation in terms of particle numbers is beyond the scope of the present dataset. We therefore would prefer not to introduce discussions related to particle number concentrations in the manuscript.

Line 268. Quite contrary, depletion reactions take time and occurred after air masses loaded with NOx left Great Britain.

Reply:

We thank the referee for this comment. We agree that the interpretation of chloride depletion processes requires careful consideration of atmospheric processing timescales. The suggested explanation is possible, but it also requires additional information on the transport history and reaction timescales. We are not sure that we can conclusively support this with our available measurements.

We agree that our original interpretation was stated too conclusively and will revise the wording to better reflect the uncertainty of this interpretation. Relevant references will also be added to support the discussion.

Figure 4 caption. ...the geometric mean was calculated using lower cut-off diameter...and the upper cut-off diameter…

Reply:

We thank the referee for identifying this issue. We agree and will rephrase the sentence as:

"The particle size was calculated as the geometric mean of the lower and upper cut-off diameters of the corresponding impactor stage."

Line 316. ...involved in SOC formation.

Reply:

We thank the referee for this suggestion. The sentence will be rephrased as:

"F(¹⁴C) of SOA depends on the origin of the precursor gases that are involved in the formation of secondary organic carbon."

Figure 5 caption. Shaded areas not explained.

Reply:

We thank the referee for pointing this out. We agree that the shaded areas should be explained more clearly in the figure caption. This will be changed in the revised version of the manuscript.

Line 407. Objective of the study belongs to the Introduction, not Conclusions.

Reply:

We agree with the referee. The objective of the study belongs in the Introduction and will be added there as described in our response to the comment regarding Line 75.

Line 417. Does that suggest that most of anthropogenic sulphate is from shipping, because the addition of winter fossil sulphate would result in certain seasonality? Diesel emissions are also non-seasonal though, but thermal power plant emissions would be seasonal.

Reply:

We thank the referee for this comment. We would like to clarify that our study does not suggest that most anthropogenic sulfate originates from shipping emissions.

The statement referred to the absence of a clear seasonal pattern in sulfate concentrations. The sentence “In contrast, sulfate does not display any seasonal changes, because sulfuric acid and ammonium sulfate have a very low volatility” refers to the influence of volatility on seasonal behavior. In contrast to semi-volatile compounds such as nitrate, sulfate compounds have low volatility and therefore do not show a strong temperature-dependent seasonal cycle. Seasonal variability can also be caused by seasonal changes in sources; however, such a source-driven seasonal pattern was not observed for sulfate in our dataset.

The interpretation of shipping emissions as an important sulfate source was based on the observation that sulfate showed a similar mass size distribution under both land and sea wind conditions. Typically, marine air masses would be expected to contain lower concentrations of anthropogenic aerosol because they are generally cleaner (i.e. not influenced by traffic, power plants and other land sources) than continental air masses. The relatively high sulfate concentrations observed during sea-influenced conditions may therefore indicate an influence from sources over the North Sea, including shipping emissions and that these provide sulfate concentrations comparable to those from land-based sources.

However, sulfate measured during land-influenced conditions can originate from different sources, and the available data do not allow us to quantify the relative contribution of shipping compared to other anthropogenic sulfate sources.