In their manuscript “Impacts of summertime photochemical aging on the physicochemical properties of aerosols in a Paris suburban forest region”, authors linked OA factors identified from conventional AMS-PMF approach to airmass origins and photochemical activities, and highlighted the amplified BrC absorption observed during the ACROSS project. The study is on a topic of relevance and general interest to the readers of ACP. However, I found the description of the methodology partially insufficient and partially hindered the evaluation of the results. The below comments need to be addressed first before I could comprehensively evaluate Section 3.3 onward. Therefore, I recommend a major revision and am open to review the manuscript again if needed.

Specific comments:

1. Line 46-47, “Rapid urbanization and industrial activities had led to high levels of anthropogenic aerosol emissions in developed megacities (Shi et al., 2019)”. I am unable to find much information about “anthropogenic aerosol emissions” from your referred paper. Instead, its winter section stated that “PM2.5 and O3 each had similar temporal patterns at the urban and rural sites (Fig. 5), indicating a synoptic-scale meteorological impact” instead of “anthropogenic emissions”. Please make sure the reference is correct and relevant, or modify your sentence correspondingly. One megacity (Beijing) is also insufficient to serve the purpose of representing a generalized statement (developed megacities). 

2. Line 105: why near-ground measurements (5-m) can “facilitate a focused discussion on regional pollution within the boundary layer” better than the 40-m measurements, if both were available? Aren’t the lower measurements more affected by localized plumes or nearby human activities/events? If the PMF results from the below- and above-canopy measurements were consistent to each other throughout the entire campaign, then it could be less of a concern. Otherwise, it is recommended to separate the entire campaign period into episodes with vertical differences in NR-PM1 and those without to discuss separately, as shown in previous AMS-PMF study above- and below-canopy in Michigan, U.S. (Bui et al., 2021). Please clarify. 

3. More contexts should be provided to Section 2.2: 

3.1 HR-AMS section: Middlebrook et al. (2012) should be cited when you mention/use CDCE. How did you treat the RIE for OA since most of your analysis focused on the organics? Did you perform periodical filtered measurement for gas-phase CO2+ subtraction from your sampling and/or calculate species-dependent detection limits? 

3.2 HR-AMS section: a table of IE and RIE results, and five main species detection limits should be added to the SI.

3.3 HR-AMS section: “all factors exhibited distinct temporal and spectral characteristics until a six factor, and the spectra of the six factors were consistent with source spectra in the AMS spectral database (Jeon et al., 2023)”- please elaborate quantitatively on “distinct” and “consistent” in the SI. 

3.4: AE33 section: from your description, it seems that AE33 was sampling from another platform. Was the AE33 pm2.5-cycloned and Nafion dried as well? How did you treat the different collection efficiencies (line loss) of the two instruments at different platforms using different inlet systems before adding them together for a “total PM1 mass concentration”? 

3.5: What is your CAPS NO2 instrument model/type? 

3.6: Your net radiometer and wind monitor were mounted on the tower (40-m) while the aerosol instruments were described as near-surface. How did you account for the canopy interference to the solar radiation and wind before they reach the ground level for your subsequent analysis?

4. Much of the context in Section 3.2 should be put in the SI as an identification & justification of PMF OA-factors instead of as standalone scientific findings. Its corresponding figures are recommended to be combined with figures in Section 3.1 as an overview of campaign measurements (values reporting). For example, I see no reason why Figure 5 (diurnal of OA factors) and Figure 3 (diurnal of other species) are not combined, and why Figure 4 (TS of OA factors) are not combined into Figure 2 (TS of RH, T, bulk PM species). Having them separately is redundant and makes it harder to see general trends among different parameters. 

Technical corrections:

1. Line 58: please add “Aerodyne” in front of the Aerosol Mass Spectrometer as there are more than one kind of aerosol mass spectrometer (e.g. AToFMS, PALMS) for its first appearance in your manuscript. The Aerodyne AMS/ACSM is just the most widely used commercial one.

2. Line 60-62: please specify your “Source apportionment analysis” is “Positive Matrix Factorization” because there are many ways of doing aerosol source apportionment, and the nomenclature of HOA, BBOA, COA etc is mostly for AMS-PMF analysis. You should add reference to Ulbrich et al. (2009) and Zhang et al., (2011) to this sentence for naming these OA factors.   

3. Line 68: please consider rephrasing to “..., an important part of OA primarily emitted or formed through the oxidation of VOCs in the presence…”.

4. Figure 6(c) has one duplicated label (LO-OOA2). 

Reference:

Bui, A. A. T et al., Transport-driven aerosol differences above and below the canopy of a mixed deciduous forest, Atmos. Chem. Phys., 21, 17031–17050, https://doi.org/10.5194/acp-21-17031-2021, 2021.

Middlebrook, A. M., et al., Evaluation of composition-dependent collection efficiencies for the Aerodyne aerosol mass spectrometer using field data, Aerosol Sci. Tech., https://doi.org/10.1080/02786826.2011.620041.

Ulbrich et al., Interpretation of organic components from Positive Matrix Factorization of aerosol mass spectrometric data, Atmos. Chem. Phys., 9, 2891-2918, 10.5194/acp-9-2891-2009, 2009.

Zhang et al., Understanding atmospheric organic aerosols via factor analysis of aerosol mass spectrometry: a review, Anal Bioanal Chem. 2011., https://doi.org/10.1007/s00216-011-5355-y.

This manuscript presents the impacts of the photochemical process on aerosol physicochemical and optical properties in a suburban forest near Paris. The authors characterize major PM1 components and gas-phase species, identify OA factors under different air mass origins, and investigate OOA evolution and their optical properties. The topic is relevant to ACP readers, and the idea of quantifying photochemical aging is interesting in principle. However, the current methodology has significant limitations, and some conclusions are not fully supported by the presented results, as detailed below. Therefore, I do not recommend the publication of this paper in ACP.

Major Comments

1. The key analysis relies on photochemical age, but I don’t think it works for the sampling environment. The method works if one tracks the same air parcel from emission to downwind. But at this ground site, the airmass constantly changes. The method is heavily biased by the fresh plume close to the site.

Many results may be confounded by the diurnal trend of calculated photochemical age. Why does isoprene concentration increase with photochemical age?

2. OA is normalized to BC to account for dilution, but this approach only works if the species originates from the same source as BC. It may not be the case in this study. Line 220.

3. Section 3.2 on source apportionment should be revised to make the conclusions convincing:

3.1 The correlation between OA factors and tracers is generally low. For example, the correlation between LO-OOA1 and isoprene is only 0.43. The comparison matrix in Fig. S9 should be moved to the main text.

3.2 Be careful when correlating aerosol with gas species because they have different lifetimes.

3.3 Line 274. The evidence to suggest marine emissions sources needs to be strengthened.

3.4 Fig. S9 shows a stronger correlation between isoprene and MO-OOA (r = 0.65) than with LO-OOA1 (r = 0.43). Why is isoprene plotted only with LO-OOA1 in Fig. 4b?

3.5 Line 265. The reported “good correlation” between LO-OOA and MVK+MACR should be quantified explicitly by providing the r value.

Minor Comments

1. In general, more contexts should be provided for clarity beyond referencing previous literature. For example:

1.1 Line 178. Describe more about the CIMS OH measurements.

1.2 Line 103. Briefly describe the sampling site and its surroundings.

2. Line 115. Does the 0.1 L/min flow rate meet the cutoff specification for a PM2.5 cyclone, and would this low flow rate lead to potential sampling losses?

3. Eqn 5 to calculate BrC. They didn’t consider the lensing effect.

4. Line 330. It is strange that O:C does not increase. Further clarification is needed.

5. Line 349. How to define the background CO?

6. Section 3.4. Cite Washenfelder et al., GRL, 2015.

7. The manuscript uses coefficients from multiple linear regression to estimate MAC. A comparison between these estimated MAC values and directly measured MAC values from the literature should be included. The discussion should also address potential reasons for discrepancies across different factors. Additionally, interpreting correlation coefficients as contributions requires caution (i.e., variable standardization, multicollinearity, etc.). More statistical details should be provided to support this analysis.

Technical Corrections

1. A few typos were noted (e.g., “person correlation coefficient” in Line 248 and Fig. S9 caption; two “LO-OOA2” labels in Fig. 6a).

2. The use of abbreviations is occasionally inconsistent. In some cases, terms are introduced without an abbreviation where one would be expected (e.g., aerosol mass spectrometer, Line 82), while in others the full term is unnecessarily repeated (e.g., the definition of PM1, Line 142).

3. In Fig. 4a, please include labels to identify factors, such as HOA, LO-OOA1, etc., for improved readability.