Improvement of stomatal resistance and photosynthesis mechanism of Noah-MP-WDDM (v1.42) in simulation of NO2 dry deposition velocity in forests presents results of different model mechanisms for representing stomatal deposition of NO2. The authors conclude that they substantially improved upon the earlier Noah-MP-WDDM version and also assert that canopy stomata and leaf nitrogen-limiting mechanisms from various classic models cannot well express the diurnal changes in stomatal deposition.

This work is interesting and I recommend publication only following a reworking of the scope and conclusions of the manuscript. In my opinion the conclusions that the authors have substantially improved upon the earlier Noah-MP-WDDM version and that the results “emphasize importance of the canopy stomatal carbon dioxide compensation mechanism and the GPP-controlled leaf nitrogen-limiting factor for the simulation of nitrogen deposition” are overstated. The more interesting finding is that all classic model mechanisms do a fairly bad job at capturing the stomatal deposition of reactive nitrogen at the chosen site in China, indicating there are substantial gaps in our current understanding of in-canopy processes. This paper would be substantially improved with an expanded discussion of what those knowledge gaps are, and how this current study is able to identify areas where more research is needed. Although I think certain findings of Chang et al., are significant, they should also be better placed in the context of recent publications. I would like to see more discussion of the results of this paper in comparison with other models, observations, and laboratory findings. The lack of discussion as written limits the value of this current study to the wider scientific community.

Specific comments:

Additional proof reading of the manuscript is needed.

L49. what is meant by this?

L64. I would like to see some additional citations here of modelling papers that represent Rc. (e.g. Wolfe et al., 2011, Delaria and Cohen 2020, Simpson et al., 2012, Ganzeveld et al., 2002, etc.).

L 70. Would be good to discuss findings of the paper cited here, as the finding of Delaria and Cohen 2020 seem to tie in well with the purpose of this paper. This sentence as written just summarizes the introduction section of Delaria and Cohen 2020.

L 72. It seems you have missed a few recent papers that also support this finding and further discuss the compensation points and the roll of nitrogen availability on NO2 uptake (Delaria et al., 2018 and 2020). Place et al, 2020 may also be interesting for you to look at.

L101: why is it a better mechanism? Need citation for this? In what way is it "better"? Is this backed up by observational data?

L106: One might argue that these "key plant physiological parameters" result in model overparameterizations are too species- and possibly individual- specific to be useful at a regional scale. How may spatial and species deviations in these parameters introduce uncertainties into your conclusions? What advantage or disadvantage does this have compared to the Jarvis model?

L115. Rns is not defined. Please define.

L 146: How is it simplified? Why is this simplification not ideal?

L150: I am confused. Are you stating that the nitrogen leaf content changes just the photosynthesis rate, or changes the relationship between Gs and nitrogen Vd? I would recommend looking at Delaria et al. and Place et al. 2020.

L198: Observations of deposition velocity are difficult and subject to different uncertainties based on observation method. How is Vd calculated in your observation data? What uncertainties may be present in the observation data? Citation to data?

L208: Discussion of species present in the site considered is needed much earlier in the manuscript. Are you using species-specific parameters? If so, where are these parameters from and are there experimental data to support?

L214: Based on figure 2, even this scheme seems to have high stability of parameterization. It looks that it may even be anti-correlated with observed deposition velocity. From Figure 2 I would conclude that all mechanisms are bad at representing deposition velocity. It seems the goal of representing changes in Vd with different environmental conditions has failed, although diurnal cycles are captured seemingly better. I am curious what this data look like if you separate into different times of day (eg daylight hours only).

L225: I would like to see a time series of data over multiple days. Does your model not capture this turbulent exchange effect?

L281. I don't think you can conclude from the results presented that the new v 1.42 is much improved. I don't see much evidence in the diurnal cycles that the agreement with observations is significantly (statistically) different, and there doesn't seem to be much evidence that would allow you to assert which model scheme is "best". The important conclusions from this work are in lines 287-291.

Figure comments:

Figures 4---7: How are errorbars calculated?

General comments

As a whole, the paper is interesting as it compares the performance of various combinations of stomatal conductance models and nitrogen-limited photosynthetic schemes. I think the paper should be published as it brings new and useful information to the scientific literature. However, the presentation has to be improved before publication. The authors should pay attention to details (see below). On the other hand, I am concerned about the fact that the authors did not show results of the Aphalo and Jarvis (1993) scheme (simulation BN-31-BN-33) on Figures 4-7 despite the fact that this scheme present among the lowest bias (MBM-3 in Figure 3). It would be interesting to include results from Aphalo & Jarvis model in Figs. 4-7 as well. Finally, the discussion section is absent and more interpretation of the results should be done including uncertainties and knwoledge gaps.

From the point of view of the English language, the authors should ask the help of a native English speaker to review and correct the manuscript because at times we see poor English. Moreover, proof editing is needed since there are a lot of typographical errors in the submitted manuscript.

Specific comments

- In the methodology section it is necessary to make clear that model output interpolated at one point (at the measurement tower site) is not necessirily comparable with a measurement point.

- A discussion section should be added to discuss several weakness and uncertainties of inputs and results.  For exemple, tower measurement is made at one location not necessary spatially representative of a whole model grid tile (whereas model output are average over a bigger area). The authors should also mention the resolution (grid spacing) of the model used and should discuss the validity and uncertainties of measurement versus model.  What about scale dependency of dry deposition ?. A discussion section should be added to review the results and provide further interpretation and describe uncertainties and knowledge gaps in a better way.

-Lines 93-97: not clear to what refers option 1. For those not very familiar with this model, it is hard to follow. More details are needed concerning options description and model characteristics.

-Section 2.2 Coupling of stomatal resistance scheme. Not clear how the coupling is done. Please explain.

-Stomatal resistance or stoma resistance ? Throughout the document you should use stomatal resistance or stomatal conductance. E.g. line 13 please replace stoma resistance à stomatal resistance

-In models of stomatal conductance,   Gs = k A*RH/[CO2], inputs for RH and A are available but how did you obtain [CO2] ?. By measurement ? CO2 is usually not available from numerical models. Please clarify.

- Line 233-234 “smallest simulation deviation”. This is poor English.

-The reference to simulation BN1-BN76 should also be better explained there in reference to Table 3.  I suggest putting the name of the simulation (BNx) in Figure 3 (just below the bias values). It would become clearer for the reader and allow a direct comparison and consistency with the following figures 4-7 where simulation name BN are used.

-Table 3 and Figure 3 are presented in different order (columns and rows are inverted). Please transpose the matrix in Table 3 to be consistent with Figure 3.

-Figures 4-7. Why not putting results of simulation from Aphalo and Jarvis (1993) model in the figures (Sim BN31-BN36) ? It would have been interesting to present also simulation of  BN31-BN33 in your figure since they show the lowest bias in Figure 2.

Minor

Line 9 and 11 Nitrogen-limitings -> nitrogen-limiting

Line 34 deviation -à ??? standard deviation ?

Lines 42 and 44  typo. Please correct.

Lines 45  Equ. -à Eq.

Figure 5,6 and 7. Units needed in the legend (s/cm ? or s/m?). Please specify.

Line 169, 170. 212 Typos. Please correct.

Line 205   typo.  0.05 cms à 0.05 cm/s

Line 215, 234, etc.:   deviation ? you mean standard deviation of what ? please clarify.

Line 216 need space between number and units (typo)

Lin 226  English could be improved, e.g. The black line in Fig 4 is BN-11 and the green line is BN-23 à The black line in Fig. 4 corresponds to experiment BN-11 and the green line to BN-23, respectively.

Line 227 This sentence does not make sense. “Vd simulation upward” à “simulated Vd values are increased”.

Line 227-230 badly worded. Please re-write.

Line 233 smallest deviation (standard deviation ?)

Line 234 bias 0.001 cm/s ? where does it come from ?

Line 245 s/m or s/cm ? in other parts of the manuscript s/cm units are used.  Why here use s/m ? Please be consistent with units used elsewhere in thee document. Do not mix units it is confusing for the reader. Either s/m in the whole document or s/cm but not both.

Section 3.4.1 badly written

Line 126. Later, the method of Lohammar et al (1980). This does not make sense. The authors just previously talk about a reference Leuning (1990). Year 1980 comes before 1990 not later. This poor English. Please reword.