The authors present a model study to investigate the effect of ammonia on the formation of particulate mass and specific constituents in the North China Plain during a test case in 2017. The first step of the study is the incorporation of an WRF-Chem model and the comparison with measurement data to establish a base line and investigate the model bias as well as a prediction gap for single species. In a second step, the uptake of ammonia is implemented in the model and the effect on the prediction quality is investigated and discussed. As the aim of this study is a better understanding of the uptake process on the air quality, this study is very important to better reflect multiphase chemistry in model frameworks.

Unfortunately, the implementation seems to be done hastily and deserves far more attention and discussion. The authors vary the uptake coefficient itself, but leave the fate of ammonia in the particulate phase fixed. Moreover, instead of leaving the most important pathway of ammonia uptake the formation of ammonium, a huge assumption is made that all NH3 forms nitrogen-containing organic compounds (NOCs), which just does not seem justified. In the current form, the paper should not be published. If the authors improve on the setup of the model implementation of the uptake and can convincingly address the following comments, the manuscript should be re-evaluated carefully. I would expect many of the key findings to change drastically. As a result, large sections of the results part should be re-written.

Critical comments:

• 1.) As the authors state correctly, the uptake coefficient is considered to be the probability of a molecule to be transferred to a particle after collision. However, not only chemical reactions are considered here, but also solvation processes. Furthermore, the process could be separated into gas-phase diffusion, surface accommodation, solvation and reaction. Of course, implementing a full model framework for the uptake mechanism would be out of the scope of this study, but to account for only the reaction as a sink to the bulk of the total uptake does not seem justified. The process should be discussed following respective studies such as follows: https://doi.org/10.5194/acp-10-9059-2010
• 2.) If only the reaction sinks are discussed, then at least the acid base reaction leading to ammonium should be part of the sink whenever there is a bit of aerosol liquid water (ALW). Arguably, even in dry aerosol conditions, the reaction with residual sulfuric acid should be a main sink. That would lead to ammonium sulfate. As a result, the shown plots in Fig. 4-8 would significantly change. It is also not discussed, if at such high formation rated of NOC would not be limited by the carbonyl fraction available for the reaction.
• 3.) Most of the results are discussed in a way that the implemented effect changes the model result away from observation and, as a result, the effect is best represented if the impact is tuned down as far as possible. The discussion if the implemented mechanism represents the current understanding and improves the results at all, are largely missing. The authors should add an additional section to the results, after the model setup and before the variation of the uptake coefficient where the general effect with a conservative estimation of the uptake coefficient is discussed. That way the reader could see the importance of the implementation of such a pathway, before the kinetic constant is tuned.

Further comments:

• 4.) The authors use the term nitrogen-containing compounds (NOCs) and include all kind of NOCs, but the formation mechanism of this compound class is very variable. Ammonia uptake would likely be able to contribute to the formation of imidazoles, if sufficient concentrations of di-carbonyl compounds are available, and to the formation of imines with other carbonyls, but the formation of organonitrates is probably not a direct result of ammonia uptake. Yet, the authors cite the paper of Liu et al. 2015 to compare the behavior of the uptake coefficient. A clear distinction should be made here.
• 5.) Could the authors investigate the formation of clusters of ammonia and sulfuric acid in the gas-phase and related new-particle formation events and compare that to the uptake and subsequent formation of ammonium sulfate in the particle phase? A high dependency of the local sulfuric acid concentration and ALW would be expected here. This might help to investigate the effect of various uptake coefficients.
• 6.) In line 205 the authors write: ‘The increase in NH3 concentration due to the uptake reaction can also observed…’ An uptake is an additional sink for NH3, as a result the concentration should not increase. This really should be reconsidered and discussed thoroughly

 Minor comments:

1. 86 should read: the y of NH3 on SOA is assumed to be in the range of
2. 251: should read: much higher
3. L.205 should read: can also be observed in FIG.reference
4. Figure references should be unique and clear. E.g. Fig 4b instead of S(-3)
5. In the SI, some of the abbreviations are not introduced to the reader

This paper uses 3D chemical transport modeling (WRF-Chem) over the North China Plain to examine how heterogeneous uptake of gas-phase NH3 onto secondary organic aerosol (SOA) affects NH3 levels, PM2.5 burden, and the formation of nitrogen-containing organic compounds (NOCs) during a November 2017 pollution episode. The authors evaluate the baseline simulation against multiple observational datasets, including field measurements, routine monitoring, and satellite retrievals. They then conduct sensitivity runs with three assumed uptake coefficients (γ = 10^-3, 10^-4, 10^-5) and diagnose resulting changes relative to the baseline, including decreases in ammonium and nitrate and indirect effects such as reduced sulfate formation via aerosol pH changes. They conclude that γ = 10^-5 yields NOC concentrations most consistent with observations and may represent a reasonable upper limit, which is associated with small impacts (<1%) on NH3 and overall PM2.5 burden.

Major comments:

Although the manuscript is well written, focuses on an important research question, and presents the results clearly, I recommend major revision to address several fundamental issues:

First, the key conclusion from this paper (i.e., γ = 10^-5 is a reasonable upper limit) is not sufficiently justified. It seems the sole reasoning is “NOCs concentrations simulated with the γ of 10^-5 are the closest to observations” (line 290). However, given the simplifying assumption that all NH3 uptake on SOA leads to NOC formation (line 115), I would expect that the model substantially overestimates NOC production for any given uptake coefficient. In that case, tuning γ downward to match observed NOCs could simply compensate for an overly efficient NOC yield, and the resulting “best-fit” γ may not be physically meaningful.

More broadly, I encourage the authors to reconsider and clarify the paper’s central objective. I do feel the sensitivity experiments are valuable and convincingly show that NH3 uptake on SOA can trigger cascading impacts on NH3, inorganic aerosol, and PM2.5, with a sublinear dependence on the assumed uptake coefficient. Several aspects (e.g., induced changes in aerosol–radiation interactions and potential dynamical responses) are interesting and could also be explored further. The current attempt to observationally constrain γ using NOCs, however, does not yet appear robust. If the authors aim to reduce the uncertainty in γ, substantially more work is needed to provide a stronger, more defensible constraint.

Another concern is the model setup and documentation. Since this is primarily a modeling study, inaccuracies or inconsistencies in the model description are particularly concerning. The manuscript states throughout that WRF-Chem is used, yet the Supporting Information says “aerosols are modeled in CMAQ using a modal approach…”. This is confusing because CMAQ and WRF-Chem are two distinct modeling systems. Please clarify whether this is an editing error or whether CMAQ is actually involved, and explicitly state in the main text which aerosol module/configuration is used. Also, the manuscript states that a “SAPARC-99” mechanism is used for gas-phase chemistry. Did you mean SAPRC-99? If so, this is an older mechanism, and SAPRC has undergone major updates since then (e.g., SAPRC18). Because the conclusions, especially those involving oxidant levels, sulfate/nitrate formation, and aerosol acidity, can depend strongly on the chemical mechanism and aerosol module, these choices need to be accurately described and clearly documented. Relatedly, as the study compares simulated NOC against observations, it is also important to clarify how the primary emissions of NOC are treated in your simulations. All these key model details are unclear in the current manuscript.

Minor comments: