The vertical distribution of brown carbon is the crucial information to accurately assess its climate effects. The authors found significant amounts of secondary brown carbon in ascending air masses by the comprehensive field campaign performed at the mountain foot (MF) and mountain side (MS) of Mt. Hua, China. They attribute these findings to the formation of strong light-absorbing nitrogen-containing organic compounds (NOCs) leading to enhanced BrC absorption in the upper troposphere. Finally, the chemical element ratios obtained by AMS and isotopic results were proposed to further support that such abundant NOCs were mainly formed via ammonia-induced aqueous reactions (e.g., Maillard reactions). The work is well-conducted and interesting, corresponding results are of importance to the field. However, pending the resolution of a few minor questions, it is recommended that this study undergoes minor revisions before its final publication.

1. Page 7, line 141-146: The chemical element ratio is the key evidence in this manuscript, thus, please provide more information of offline AMS analyses, such as the RIE values that would affect the calculation results and make AMS results unreliable.

2. Page 10, line 215-216: The OSc value at MS site was merely ~0.06 higher than that at MF site, whether a significance test is conducted? This slight difference was farfetched to indicate a more oxidated atmosphere aloft; Thus, the authors should provide additional evidence to support hypothesis.

3. Any interpretation for these distinct relationship between OSc and abs365nm at two sites shown in Figure 3a and 3c? And why would atmospheric oxidation cause photobleaching in MF and absorption enhancement in MS?

4. In this work, the authors think that the aqueous reaction of dicarbonyl groups with NH4+/NH3 can significantly promote absorbing NOCs formation in lifting air mass and lead to the enhanced light-absorption in the upper troposphere; However, why does the author think these reactions are not significant on the ground? And the surface NH4+ and other precursors concentration are more abundant compared to that aloft.

5. Have the authors considered the time scales of vertical transport and chemical reactions mentioned in this work? The chemical-dynamic processes proposed in this work may be shorter than the transport time between the two sites.

6. In Figure 4(d), the amount of isotopic data is seemly less than the total of the campaign; Please provide more details for the isotopic measurement.

7. Please unify the units of OC, EC and WSOC in Table 1.

The manuscript by Wu et al. presents measurements of PM2.5 and some of its chemical constituents together with optical brown carbon measurements for two sites at different altitudes nearby Mt Hua, China. Generally, the manuscript is well-structured, reasonably well-written and the presented data is interesting and comprehensively discussed. My main concern is that major conclusions are based on the following two assumptions, which are not convincingly proven: 1) A direct connection of air masses between the two sites and 2) a lack of BrC sources in-between the sites. I give some details below, but these points need to be better addressed in a revision. In addition, some data analysis methods are not properly documented in the manuscript and need either be better explained or might even be removed, as further commented below. Overall, I recommend reconsideration after major revision.

Specific comments:

• Data from the mountain site are compared to another site at the mountain foot of Mt. Hua and any changes in chemical characteristics or BrC content are related to chemical processing taking place during the presumable quite short transport of air masses between the sites (8 km horizontally and 1 km vertically). No discussion, however, is provided to support the implicit assumption of connected air masses between the sites. What about wind direction for example? Was the mountain foot site indeed upwind of the mountain top site all the time? As for the anabatic valley breezes that are briefly mentioned: Is there any experimental evidence that such winds did indeed reach the mountain top site from the mountain foot site? And what about wind speeds and transport times? Could some of the observed differences in diurnal profiles be caused just by delayed arrival of valley pollution plumes at the mountain site?
• A second implicit assumption is the complete lack of any BrC sources between the sites. While this seems plausible for fossil sources, I wonder if it really holds for biomass burning sources as well? Are there no small villages along the path where people might burn wood or waste? What about agricultural fires or wild fires? Can these be ruled out as well for the campaign period in summer? In L220, the authors refer to their earlier Wu et al. 2020 study, but in this study, I could not find evidence for a lack of OA sources neither. In fact, in Fig. 8 of Wu et al. 2022, agricultural fires are included in the sketch as a possible source between the sites! Any biomass burning along the path would weaken the strong conclusion on chemical ageing between the sites.
• The application of the random forest analysis should be reconsidered. RF is a complex ML model typically applied for forecasting. While it can also be used to derive insight into data structure and relationship, there are quite some caveats that would need to be carefully addressed. First of all, care must be taken to not overfit the data and the exact model configuration would need to be documented (e.g. which RF implementation, which hyperparameter values and why they were chosen). Then, the method to interpret the RF model would need to be explained. Fig. 4b just says “RF analysis” and it remains completely unclear, what the given percentage values actually mean. There are a range of such interpretability methods and their outputs typically differ. On top of that, given the inherent randomness in RF, even the output from one and the same method can differ to some extent if repeatedly applied to the same data. Also, with correlated features – as in the given case – much care needs to be taken when interpreting the output of such methods. And lastly, the results shown do very likely just reflect the correlative structure of the data and this could much more easily be discussed by simple correlation coefficients. Another concern is that the authors might overinterpret the RF results in terms of causal dependence when in fact they just describes the statistical relationships between the variables.
• PMF results are shown in Fig. 2d, but the experimental details are only partially given in Text S2. How was the uncertainty matrix constructed? Was bootstrap resampling performed to assess the robustness of the solution? Were all variables included as “strong” or were some downweighted? These experimental details should be included in the main manuscript, not SI. The assignment of the factors to atmospheric sources should also be justified, instead of just displayed in the SI. Conceptually, I wonder what it means to combine abs365 with the PM constituents. What is actually apportioned by the PMF, if concentrations and optical properties are mixed and analyzed together? A more appropriate reference to the PMF model should be given, not the website of the user guide.
• The beginning of section 3.1 would benefit from some restructuring. It goes back and forth between discussing Figure 1 and Table 1 and is a bit difficult to follow.
• Table 1 indicates an increase in abs-BrC/abs-BC from MF to MS during daytime, which is taken as evidence of BrC formation. During night-time, however, an even stronger increase can be seen from the data in Table 1. I wonder how the authors interpret this? Night-time data is currently not discussed in the paper.
• Many results discussed throughout the paper are shown in the SI only, which sometimes makes it difficult to follow the reasoning without going back and forth between the paper and the SI. I recommend to critically assess which of this information is really needed. SI should not include entirely new data that is then still discussed as if it was part of the main manuscript.

Further comments:

• L31: Give reference for this earlier finding
• L81: Include reference for radiative forcing
• L122: Indicate the thermal protocol applied
• L170: How were pH and ALWC derived?
• L171: What is the difference between NH4+ and NH3(aq)? How was the ladder measured?
• L176: R2 would be the coefficient of determination, not correlation coefficient
• L178: R2 would need to have high values for good model performance, not small ones
• L197: If MAE at the two sites is really the same, does that not contradict the conclusion of higher BrC content at the mountain site?
• L275: Given the reported lack of correlation with NO2, I cannot follow the suggestion of NACs deriving from combustion sources. All combustion sources emit NO2.
• L279f: Not sure I agree. I would expect all anthropogenic pollutants to co-correlate at the mountain site. It would help to show all correlations in the SI.
• L283: A lack of correlation between NACs and ALWC does not necessarily indicate any specific formation mechanism. It also depends on the availability of precursors and whether the formation is volume-driven or concentration-driven. With low ALWC, aqueous concentrations might strongly increase.
• L285ff: What is the relevance of protonation for the formation process discussed here?
• L288: “explicit evidence” is quite a strong term for the discussed correlations, which might or might not be caused by the proposed processes.
• L292: As detailed above, the RF does certainly not quantify the contributions of different influencing factors. I suppose the given percentages are just a metric for the degree of correlation in the data. They can certainly not be used as causal quantitative contributions.
• L304: Experimental details of the isotopic analyses should briefly be included in the experimental section with reference to the earlier paper.
• L355ff: In China, total PM loads have decreased. I would therefore expect that ALWC might have decreased as well, not increased, as the authors seem to suggest. Is there any reference for this statement? The following paragraph would hold only if ALWC has indeed increased.
• Section 4: It is uncommon to refer to and discuss new Figures in the Conclusions section. Maybe consider to split “atmospheric implications” and “conclusions” into separate sections.
• S3: Is it r or R2 that is plotted in the Figure?
• S4: What about bootstrap uncertainty of the factor profiles?