General comment:

This manuscript presents simultaneous measurements of gaseous and particulate water-soluble organic nitrogen (WSON) in urban Chengdu during winter, investigating the gas-particle partitioning coefficients (F_p), their diurnal variations, and the dominant role of aerosol liquid water content (ALWC) driven by NH₄NO₃. While the topic aligns with the scope of the journal Atmospheric Chemistry and Physics (ACP) and the data acquisition appears rigorous, the current version lacks the mechanistic depth expected for a process-oriented study. I recommend publication after a Major Revision​ addressing the conceptual and methodological concerns outlined below.

• My major concern is regarding about the overlap with the authors’ prior work. The analytical framework employed here is highly consistent with the authors' previous studies on gas-particle partitioning in different regions. The conclusion that ALWC dominates WSON partitioning while pH and temperature are relatively weak largely replicates the findings of the aforementioned studies. Chengdu is not merely as another high-humidity site comparable to other areas. So I strongly recommend the authors to refocus the discussion on how the unique meteorological and topographic constraints of Chengdu modulate WSON partitioning behaviors differently than those reported in coastal or northern China cities.
• My second concern is the amine partitioning. While the manuscript notes the enhanced partitioning of methylamine (MA) and dimethylamine (DMA) into the particle phase during polluted periods, it does not explore the underlying mechanisms beyond physical partitioning. It remains unclear whether the observed MA/DMA partitioning reflects purely physical dissolution or if it is linked to chemical consumption via reactions in the aqueous phase. Distinguishing between physical partitioning and chemical-enhanced partitioning would significantly elevate the mechanistic insight of the paper. Furthermore, the discussion should address how changes in aerosol pH (resulting from NH₃ mitigation) might non-linearly affect amine partitioning and secondary formation via aqueous chemistry in this specific high-humidity environment. This would bridge thermodynamic partitioning with chemical transformation.
• Another concern is the partitioning coefficient (F_p) dynamics. While the manuscript’s most notable contribution is the provision of field-derived F_p(WSON) data, I am concerned that the subsequent analysis with drivers of the partitioning coefficient itself. Throughout the Results and Discussion, the authors attribute variations in particulate WSON (C_p) and gaseous WSON (C_g) to factors influencing F_p. However, by using C_p (or C_g) as the primary dependent variable in correlation analyses and S-curve fittings, the manuscript conflates concentration dynamics with partitioning thermodynamics. To rigorously isolate F_p drivers, the authors should redefine the dependent variable as F_p. Without this distinction, the claim that ALWC "drives" F_p remains circumstantial.

Specific Comments:

• Lines 75-77: The authors state here that the gas-particle partitioning of amines is governed by multiple factors, including aerosol pH, relative humidity, and the composition of the condensed phase. This statement is of interest and warrants further discussion / interpretation. Since the gas- and particle-phase amines have been measured in this manuscript, I would recommend the authors providing an in-depth discussion on their partitioning mechanism in the text.
• Introduction: On the whole, I believe that this section could be greatly improved. It could be more focused to better serve the specific aims of this study. And the recent findings on the WSON or WSOC gas-to-particle partitioning observation, particularly the authors’ own work should also be summarized.
• Materials and methods: The manuscript currently describes the sampling site only in terms of its urban location, coordinates, and surrounding land use, and lacks meteorological context relevant to partitioning. Given the central variable of this study (i.e., F_p(WSON)) is highly sensitive to relative humidity, temperature, boundary layer height and ALWC and chemical composition of aerosol, all of which are strongly shaped by the topographic confinement of the Sichuan Basin. So I suggest the authors add details on basin meteorology and the unique emission characteristics of Chengdu to justify the site's selection.
• Lines 110-134: While the OC-to-OM conversion factor (k=1.6) is mentioned in Table 1, the Methods section contains no explicit statement​ on how OM was derived from measured OC. F_p definition should also appear in this section, not only in Results/Figure captions
• Lines 197-241: The inference that "more NOCs are formed during the accumulation of OM" from an increasing WSON/WSOC_p ratio is invalid. Since WSOC accumulates substantially via secondary formation of non-nitrogenous organics during haze, this ratio merely signals the relative enrichment of nitrogenous species, not absolute NOC formation. Additionally, attributing higher daytime WSON to photochemistry lacks supporting precursor/radical data. Dismissing the clean-day trend as a "lack of photochemistry" is inconsistent, as radicals persist on clean days; diurnal variations are more plausibly explained by boundary layer dynamics and emission patterns.
• Lines 242-264: The assertion that photochemistry rapidly generates WSONg during the daytime is not supported by precursor or radical data. The ALWC during the daytime may also influence the partitioning of WSON. Furthermore, the claim of "no significant correlations (R < 0.3)" between F_p and T, RH, or pH fails to specify whether Pearson (linear) or Spearman (monotonic) coefficients were used. Explaining the modest ALWC–Fp​ correlation in Chengdu via an "organic shell hindering gas transfer" is speculative.
• Lines 319-355: Again, the correlation analysis fails to specify the type of correlation coefficient used and address non-linear relationships, particularly for S-curve interpretations.
• Section 3.3: The observation that MA and DMA shift to the particle phase during polluted periods is presented without mechanistic depth. The authors discuss ALWC, pH, and T as factors for MA/DMA partitioning, but treats amines as a bulk class and omits species-specific controls: protonation equilibrium, effective Henry's law constants, dicarbonyl-driven consumptive partitioning to imidazoles, organic-phase partitioning under high OM/inorganic ratio, aerosol aging time, and ionic-strength effects on activity coefficients. Without these, the conclusion that "ALWC is the key factor" remains a single-variable approximation of a multi-parameter thermodynamic problem.

Technical corrections:

• Author list appears to list Rui Li twice (positions 3 and 9), please confirm whether it is a metadata duplication.
• The unit of N should be consistently formatted as “μgN m⁻³” throughout the manuscript.
• Abbreviations (e.g., WSON, SOA，MA, DMA, ALWC) should be preceded by full names at their first appearance in the main text not only in the Abstract.
• To avoid ambiguity, it is recommended to rephrase this expression "WSON transfer process" to "WSON partitioning process".
• “the decrease in FWSON during the daytime may be attributed to the increase of WSONg exceeding that of WSONp” merely restates the mathematical definition. Please delete it or replace it with a mechanistic explanation.
• The manuscript uses three different designations for the sampling location: "Chengdu", "CD", and "SCB". The authors should standardize the nomenclature throughout the text, tables, and figures.