The manuscript compares molecular-dynamics-derived nucleation, coagulation, and surface growth rates with empirical rate models in a premixed ethylene burner-stabilized stagnation (BSS) flame, focusing on their influences on the modeled particle number concentration and volume fraction. This is accomplished by solving the coupled mass, energy, and momentum transport equations using Fluent. Overall, this study is potentially interesting and relevant to the Aerosol Research. However, the presentation would benefit from significant improvement to better highlight the value of the work. The following comments are provided for the authors’ consideration and focus on selected aspects, although the authors are encouraged to carefully revise the manuscript as a whole, beyond the specific points listed below.

The methodology section would benefit from a more structured organization, for example by clearly separating geometry, governing equations, boundary conditions, and initial conditions. In addition, the descriptions should be more complete. For instance, although the temperature conditions can be inferred from Figure 1, all initial and boundary conditions for the flow, energy, and transport equations should be explicitly stated in the text. The manuscript provides the transport equations. It would also be beneficial to provide the exact flow and energy equations, as they are critical.

The manuscript would benefit from a clearer description of how the MD-derived rates are obtained. While readers may refer to the cited literature for details, it would be helpful to briefly summarize the underlying chemical and physical mechanisms, the types of systems used to derive these rates, and the conditions under which the rates are applicable.

The capabilities and limitations of the monodispersed model should be clarified. As currently described, it appears that the model is able to represent only the total particle number concentration, rather than size-resolved particle distributions. It would be beneficial to have more structured and involved discussions on this. 

In Line 105, Section 3.1.1, the text shows “Error! Reference source not found.” Please provide the correct reference.

In Line 124, the parameter C is introduced without a clear definition. In Equation (3) as well. Please clarify if C represents the total concentration of carbon species, or is individual concentration for different carbons. 

In Equations (2) and (3), the notation used for the source terms on the right-hand side may be misleading, as they resemble derivatives of the variables N and C, although they are not (they are source terms). Please consider revising the notation to avoid potential confusion.

In Line 140, the variables Wc and M should be defined when they are introduced.

Several variables listed in Table 1 have not been defined elsewhere in the manuscript. Please ensure that all variables appearing in the table are clearly defined.

This paper presents a simulation of a laminar premixed sooting flame with a CFD code coupled with a monodisperse soot model whose kinetics are derived by molecular dynamics (MD). The main contribution of the paper is in employing MD-derived kinetics in the context of a CFD simulation of a laminar flame. I applaud the authors' attempt, as I also think that the involvement of MD kinetics in soot and aerosol simulations is the way to go in the future. However, I think that the manuscript requires considerable revision in order to do justice to its cause. In the present form, the conclusions drawn do not seem to be adequately supported by the simulation results. This does not mean that the results are not publishable, but the discussion and conclusions should reflect the results and acknowledge the shortcomings, given that this is an early attempt, otherwise the aim of the authors in promoting the use of MD in sooting flame simulations will be compromised. I provide below a list of major points.

1. There is no detail at all on how the MD kinetics are derived, with the paper citing instead two works by the authors (one of them on surface growth still unpublished, so I cannot know how that model is derived). Even with the papers published, I feel that a summary of these works is required here, otherwise the paper cannot be comprehended without reading the other papers. This is important because the use of MD kinetics is the main contribution here and MD for soot is at a very early stage, so there are many open questions as to how MD kinetics could be derived and what would be their range of validity.

2. Related to point 1, in the abstract (and possibly elsewhere) it is implied that MD kinetics are superior in predictive power ('...does not rely on reaction kinetic modeling'). However, while MD simulations do indeed employ Newton’s laws at the basic level, they involve parametrised potentials that bring their own assumptions. In addition, there are many assumptions involved in the way statistical mechanics is used to relate the outcomes of MD simulations to macroscopic kinetics. At present, only very small sets of molecules can be simulated, often under conditions that are far from what would be encountered in real situations such as flames, and many more choices and assumptions are involved regarding boundary conditions etc., so there is no consensus as to how reliable ab initio kinetics can be obtained with MD. Given the fact that the MD model is not described at all here, the reader is left with uncertainty as to what is its range of validity.

3. In the same vein, it seems that the MD model used here relates soot to acetylene. This was the assumption of early soot models, such as the Brookes and Moss model, but now it is established that soot is mechanistically formed via PAH routes and the dependence on acetylene is a rather crude and indirect correlation. This does not mean that one cannot base a model on this correlation (after all early soot models had considerable success with it), but the deficiencies must be acknowledged given that MD is proposed here as an approach with predictive power. The lack of discussion of the derivation and assumptions of the MD model is again the root of the problem.

4. Again on the same point, given that the MD model is based on a crude correlation, the results on a single premixed flame leave open the question of the range of validity. This should also be acknowledged.

5. The base case that the MD is compared with, the Brookes and Moss kinetics, is a very old model, which should be acknowledged. Having said that, comparison is made also with a detailed kinetic-sectional model which is closer to the state of the art.

6. The main results do not seem to support the discussion that follows. The discussion outlines various improvements in several models that use different combinations of MD-derived kinetics (nucleation only, growth only or both) and the conclusions mention that ''... it [the MD-derived] captures the measured 𝑓𝑣 and 𝑑𝑚 reasonably well, resulting in even comparable predictions to those by a detailed sectional model in the post-nucleation flame region, at significantly lower computational cost'. However, this is not the impression one gets from Fig. 6. In (a) (number density) the detailed model is clearly seen to be the only one reasonably close to the experimental results with considerable difference from all the others, of which the early Brookes-Moss-HACA gives the best results. In (b) (volume fraction) again the detailed model follows closer the trend, although here it is difficult to draw conclusions as most models either overpredict or underpredict by a similar amount. These results should be better reflected in the discussion and conclusions.

7. Fig. 5 is not informative and even obfuscates the conclusions to be drawn from this study. To begin with, the information contained in these histograms is redundant as it is wholly contained in the radial profiles of Fig. 6. More importantly, histograms do not show trends unless one juxtaposes the two positions and tries to look at correlations. Since the radial profiles (the common way of presenting this information in sooting flame studies) are shown in Fig. 6, I think that this figure does not serve its purpose and this is aggravated by the fact that it is shown and discussed before Fig. 6.

8. In Fig. 7, results for the detailed model are not shown. Are results for mobility diameter not available for that model? If they are, they should be shown, otherwise a reason should be provided.

There also some minor points and typos:

• The model referred to as 'Moss-Brookes' would be better written as 'Brookes-Moss' given that this is the order of the names in the publication.
• Title: I would recommend '...by a monodisperse…’
• There is an undefined reference 'Section 3.1.1Error! Reference source not found.. '
• End of p. 4: 'd... iffusion'
• p.5 'denotes the velocity' there is a formatting issue there
• p.6 'detailed in (... - no parenthesis needed