This manuscript analyzed the spatial distribution of IN and ON over the Greater Bay Area and found differences in ON composition between urban and marine aerosols. The results are important to estimate nitrogen deposition and its impacts on ecosystems in coastal areas. However, the following comments need to be addressed before publication:

Lines 107-108: This study collected the data of biogeochemical oceanographic measurements. For the discussion on ecosystem implications, I may suggest the authors to combine seawater Chl-a and analyze the potential impacts of aerosol ON input to marine ecosystems. 

Lines 147-151: The ship-exhaust influenced samples exhibited higher TC concentrations than clean marine samples. How about the EC concentrations in the PM2.5 samples with and without ship-exhaust influence? Did you observe any other difference in aerosol components between clean samples vs ship-exhaust influenced samples? 

Lines 252-253: Please describe how to calculate the offshore distance? Some sampling locations are very close to the shore and surrounded by the continent on three sides? 

Lines 266-269: I may suggest adding the back trajectories of air masses to address the influence of anthropogenic pollutants on the sampling location.

Lines 271-274: The spatial distribution of sulfate is confusing. Please describe the distribution of sulfate aerosols using the observed data or add a figure to describe it.  Why is sulfate shaped more by regional background transport and the marine boundary layer? The authors need to elaborate the reasons more clearly.

Lines 279-281: The ratios did not vary a lot. In my view, the difference (34.6% vs. 32% vs. 27%) may not be significant. Is the ON contribution significantly different between the three regions? How about the significance level of their difference?

Lines 344-357: The variation of ON and IN during the typhoon period is interesting, but more explanations are needed. Why only NH4-N increased, but there were not obvious variations for the concentrations of NO3-N or ON?  

The authors attributed the higher NH4-N during the typhoon period to the transport of continental/inland air masses. However, some air masses on 26 July were from the ocean. Why did the continental air masses not lead to higher ON or nitrate during the typhoon period? 

Why continental air masses lead to enhanced particulate NHx through gas-to-particle partitioning? More evidence is needed. Are there any other possibilities?

In addition, back trajectories of air masses on 24 July (in yellow) in Figure 4 are difficult to read. Please change the color.

The authors emphasized “Ecosystem Implications” in the title and calculated aerosol nitrogen deposition in Section 3.4. To what extent would these aerosol nitrogen depositions impact the marine ecosystem of the Greater Bay Area? 

And how about the levels of nitrogen nutrients in coastal seawater of the Greater Bay Area? If the waters are eutrophic, aerosol nitrogen deposition may not have an obvious influence on the marine ecosystem in this area.

The manuscript presents a genuinely valuable and rare dataset, pairing shipboard PM2.5 nitrogen speciation over the GBA coastal ocean with concurrent urban sampling at Tsuen Wan. The authors employed a multi-method approach, and utilizing molecular AMS fragments to investigate ON oxidation states is a sensible strategy to add mechanistic depth. However, the primary concerns holding the paper back are methodological rather than presentational, specifically regarding comparability and quantitation. The core marine-urban contrasts are confounded because the authors compare irregularly spaced, sub-daily marine filters against 24-hour urban integrals, and they evaluate filter-IC data, which is subject to known artifacts, against artifact-free MARGA data. Furthermore, the AMS oxidized/reduced ON diagnostics are biased by co-extracted inorganic nitrate, the offshore gradient statistics fail to account for spatial-temporal autocorrelation, and the authors build headline conclusions on insufficient evidence—such as determining ship-influenced ON chemistry based on only four samples, or annualizing deposition fluxes from a three-week summer window. In summary, while the dataset is suitable for publication in this journal, the manuscript requires a major revision to address analytical artifacts, reanalyze the data, and temper the interpretive claims to align with what the measurements can robustly support.

Key questions

1. Are the marine–urban contrasts partly analytical rather than atmospheric? The authors adopted MARGA for the urban site precisely because it avoids artifacts like NH4NO3 volatilization and HNO3 adsorption (lines 185–193). However, the authors compare this artifact-free data against marine filter-IC data, which suffers from exactly these biases. How much of the central N–NH4+/N–NO3- contrast (marine ≈ 1.8 vs urban ≈ 5.4) survives once these known marine filter artifacts are bounded?
2. How much of the NO+/NO2+ contrast is driven by inorganic nitrate, and can AMS actually support the ON claims? The marine samples retain appreciable inorganic nitrate (lines 329–336), which directly contributes to NO+/NO2+ (lines 237–238). The lower marine ratio is likely just a different mixing ratio of inorganic/organic nitrate, not proof of a less oxidized organic pool. More importantly, the capability of AMS to quantitatively measure organic nitrogen is inherently very limited. Coupled with the small sample size, the current data simply cannot bear the weight of the mechanistic conclusions drawn in Section 3.3.1. The authors must quantify the inorganic bias.
3. Is the “unique ON chemistry” conclusion supportable at n = 4? The authors build two full paragraphs of complex mechanism (imidazole-like heterocycles, secondary amides) in Section 3.3.2 based on exactly four offline AMS ship-influenced samples (line 205). What is the sample-to-sample variability here? Does this sweeping claim survive it?
4. Is the offshore ON gradient robust to the confounding of distance, region, and time? The cruise progressed through regions A→C over three weeks, meaning offshore distance is heavily entangled with west–east position and sampling date. The trend test (lines 289–298) treats these distance bins as independent. How did the authors handle the strong temporal and spatial autocorrelation? Does the gradient survive a test that actually accounts for it?
5. What are the bulk ON measurement uncertainties, and do they support annualized deposition fluxes? The reported ON values (0.07–0.12 µg m-3, Table 1) are extremely close to the detection limits of thermal-evolution methods, yet no LOD or uncertainty metrics are provided. Furthermore, the deposition fluxes (Table 2) are annualized from a brief 23-day summer window. Summer marine air does not represent the annual cycle. This extrapolation is unwarranted.

Major comments

1. Marine filters ran 1.2–17.1 h (mean 3.8 ± 2.8 h; lines 138–139), meaning the marine record is effectively sub-daily and irregularly spaced, whereas the urban filters are 24-h integrals (line 153) and the urban nitrate/ammonium are hourly MARGA. Short filters capture transient peaks that 24-h integration smooths out, which inflates apparent marine variability and shifts marine concentration statistics relative to the urban site. This directly undermines the statement regarding “broadly comparable concentrations and temporal variability” (lines 321–324) and the distributional comparisons in Fig. 3. The authors must state the averaging times side by side, and either aggregate the marine data to a comparable time base or demonstrate that the mismatch does not drive the observed contrasts.

1. The authors adopt MARGA for the urban site specifically because filter sampling suffers semi-volatile NH4NO3 loss (lines 189–193). However, they then compare those artifact-free urban values against marine nitrate and ammonium measured by filter-IC, which is subject to exactly that loss and additionally to positive HNO3 adsorption on quartz filters. The marine N-NH4+/N-NO3- ratio (≈ 1.8) versus the urban ratio (≈ 5.4) (lines 325–328) is one of the headline contrasts of the manuscript, and it is heavily confounded by this inconsistency. Note also that in mass terms, the marine samples show NO3- (0.38–0.58 µg m-3) exceeding NH4+ (0.19–0.25 µg m-3) across all regions (Table 1), so the “NH4+-dominant” framing depends entirely on the nitrogen-mass conversion and on the assumption that filter nitrate is unbiased. The authors must bound the filter artifacts (e.g., using denuder or backup-filter data, or literature values for this specific sampler and duration) and propagate that uncertainty into the marine–urban ratio comparison.

1. First, the offline AMS analyzes water-extracted, nebulized material, reporting water-soluble ON only, while the thermal-evolution IN/ON is from filter punches (bulk). The authors use “ON” for both without reconciling the two operational definitions; the manuscript needs to clarify which quantity is which throughout, and whether the bulk ON and AMS-derived ON fractions are actually consistent. Second, and more importantly, the NO+/NO2+ ratio and the CHN-vs-CHON split are highly sensitive to the inorganic nitrate present in the extract. Because the marine samples retain appreciable nitrate (as argued by the authors regarding sea-salt processing, lines 329–336), a lower marine NO+/NO2+ partly reflects a larger inorganic-nitrate contribution to those fragments rather than a genuinely less oxidized organic pool. The interpretation in Section 3.3.1 and the conclusion (lines 522–527) require this bias to be quantified or explicitly bounded; otherwise, the oxidized/reduced dichotomy remains unsupported.

1. Section 3.1 argues that ON is dominated by continental sources and is rapidly attenuated during marine transport (lines 298–305), yet Section 3.3.1 attributes the marine reduced-N enrichment to marine biogenic origins (alkyl amines, amino acids, bubble-burst DOM; lines 385–391). These claims pull in opposite directions: if ON is continental and declines offshore, the marine-biogenic reduced-N pool is merely a minor, diminishing contributor. Thus, “enrichment in reduced-N fragments” is a relative statement about composition, not evidence of biogenic dominance. The manuscript offers no independent marine-biogenic tracer. The authors should test the biogenic attribution directly (e.g., using MSA if measured, examining the offshore trend of the CHN fraction itself, or correlating with wind speed/ocean-color productivity). As currently written, the biogenic-source language overreaches the available evidence.

1. The 75 marine samples are binned into six distance classes and tested with Mann–Kendall and Sen's slope (lines 289–298). However, offshore distance is heavily confounded with region (A→C, west→east) and sampling date, as the cruise progressed in space and time simultaneously. Furthermore, samples are spatially and temporally autocorrelated within persistent monsoon air masses, meaning the effective degrees of freedom are far below n = 75. The central contrast (that ON shows a significant offshore trend while IN does not) rests on p-values from a test that falsely assumes independence. The authors must (a) account for autocorrelation (e.g., blocking/clustering by air-mass episode, or reporting effective sample size), and (b) demonstrate that the ON gradient is not merely an artifact of the west–east regional gradient or temporal drift over the campaign. Similarly, Fig. 5 reports multiple Mann–Whitney comparisons with no stated correction for multiple testing.

1. The contamination criterion relies on a single threshold (NOx > 100 ppb for ≥10 min; lines 148–150), which is high enough that diluted or aged ship plumes below 100 ppb would pass into the retained “marine” set—the exact set upon which the reduced-N/marine narrative depends. Concurrently, the authors build Section 3.3.2 (“Unique ON chemistry...”) entirely on only four AMS ship-influenced samples (line 205). The authors need to (a) justify the 100 ppb/10 min threshold or test sensitivity to it, (b) report the residual ship influence expected in the retained marine samples, and (c) substantially soften Section 3.3.2 and the corresponding conclusion, given the n = 4 limitation, unless more samples can be added.

1. While the dry-deposition arithmetic is internally consistent (yielding ≈0.14 kg N ha-1 yr-1 from Ca ≈ 0.4 µg N m-3 and Vd = 0.11 cm s-1), the core issue is representativeness. Annual fluxes are extrapolated from a brief three-week summer window under southwest-monsoon marine air, which drastically underrepresents winter continental outflow and its characteristically higher IN. Consequently, reporting values in “kg N ha-1 yr-1” overstates what a summer campaign can legitimately constrain; the authors must label these as summer-representative or campaign-scaled fluxes, not annual, unless robust support for the extrapolation is provided. Additionally, the marine–urban Vd difference (0.11 vs 0.13 cm s-1) falls well within the uncertainty of a first-order size-segregated scheme. Calling them the “same order” (lines 477–478) carries little actual information. The authors should state the Vd uncertainty range and temper the deposition comparison accordingly. Furthermore, they should note whether hygroscopic growth of sea-salt-influenced particles at high marine RH was considered, as this raises effective size and Vd.

1. Using the region-mean ions in Table 1, the measured cations fall significantly short of the anions on a charge basis (cation/anion ≈ 0.64–0.66 in region C), and NH4+ (≈13–15 neq m-3) is far below what is needed to neutralize sulfate alone (≈40–42 neq m-3). This implies either the aerosol is strongly acidic with a large unmeasured H+ pool, or there is a massive cation deficit in the IC data. For a submission to a high-tier venue relying on IC as a core method, providing an ion balance and a neutralization/acidity check is mandatory. The outcome directly affects the “NH4+-dominant” framing. The authors must add an ion-balance figure or table and adequately discuss this cation deficit.