The manuscript presents observations of OH, HO2, RO2 and OH reactivity made in the Yangze River Delta region in China during a prolonged ozone pollution event. The radical observations were compared to model simulations using the RACM2-LIM1 mechanism. The base model scenario underpredicted the observed OH, HO2 and RO2 concentrations during the high ozone episode and several additional model scenarios were run (that have previously been considered in the literature to help resolve model measurement discrepancies). These scenarios included a) the addition of an unknown species X to the model which recycled RO2 to HO2 and HO2 to OH, b) introduction of monoterpenes into the model and c) reduction of the RO2 self reaction. The impact these scenarios made to P(Ox) and the ratio of HO2:OH, RO2:OH and HO2:RO2 as a function of NO is also presented. Despite these analyses, the manuscript, as written, does not expand on the current scientific understanding of factors controlling oxidation processes in urban environments. The writing style is poor and many sentences/sections are difficult to understand and so one is left trying to guess at the point the authors are trying to make in many places. I, therefore, do not think the manuscript, as it stands, is suitable for publication in ACP.

Major points:

Line 180: LIF groups now routinely use inlet-pre-injectors to chemically remove ambient OH prior to sampling (to determine their background signal for subtraction) to ensure an interference-free OH measurement. Wavelength modulation does not allow distinction between ambient OH and any OH internally generated within the reaction cell. A previous comparison exercise with a second LIF instrument at a different location does not ensure that the instrument (and the OH measurement presented here) is free from interferences. This needs to be acknowledged when discussing the model measurement comparison.

Section 2.2.2: the description of the OH reactivity instrument lacks adequate detail. How is OH generated? Via the photolysis of ambient or generated ozone? What was the initial OH concentration generated? Flow rate and pressure in the flow-tube?

Section 2.3: A comprehensive list of model constraints should be provided. Which NMHCs were measured?

Line 223: Was the model unconstrained to O3 and NO2 in this scenario?

Fig. 4 highlights that OVOCs contribute significantly to OH reactivity. Given that one of the major conclusions of the manuscript is that future measurement campaigns should target more OVOCs, the individual OVOCs that are considered in this class should be provided. It would be beneficial to list all the VOCs that have been considered in all the different groups in a table. The calculated reactivity seems to compare well with the observed OH reactivity at the start of the measurement period, but then there is evidence of missing OH reactivity after the 10^th, why is this? Was the contribution model-generated intermediates make to the calculated OH reactivity considered?

Line 444-455: This section discusses the inclusion of monoterpenes in the model. The authors need to describe how RACM2 treats the oxidation of alpha-pinene and how this compares to the MCM mechanism for alpha pinene.

Section 4.3: I found this section particularly difficult to follow. What do the authors mean by ‘Special HCHO’? Could the authors provide the model predicted HCHO concentration (when left unconstrained to HCHO) relative to the HCHO concentration measured? The main conclusion of this section seems to be that other OVOC (that can act as a source of RO2) should be measured, but there is no discussion on what OVOCs were measured beyond HCHO; this detail needs to be included.

Minor points:

Line 38: Define ‘ChL’

Line 232 and 235: the different notations used in (2) and (3) need to be defined.

Written style needs to be improved substantially throughout.

The study by Hu et al. focuses on the analysis of measurements of OH, HO₂, RO₂ radicals and OH reactivity performed in the Yangtze River Delta region in China. Measurements of radicals, in particular RO₂, remain quite sparse as few groups have the needed instrumentation.

Measurements are compared to model results using the RACM-LIM1 mechanism and some sensitivity tests are done to try and bring model and measurements in agreement.

I fully agree with Referee #1 that in the current status the paper requires language checking and editing as many sentences are not correct and this makes it sometime difficult to understand what point the authors are trying to make. I also agree that, in the current status, it is difficult to see the advancement in our knowledge on radical cycle and chemistry.

Following are some general points that the authors should consider addressing.

The authors “test” what has been proposed in the past:

• Species X to match the observation. This is nothing more than a fitting exercise and does not really help us understanding what mechanism might be behind. Could be removed.
• Introduction of more monoterpenes which might sustain a lower-than-expected HO₂ to RO₂ ratio due to the chemistry of complex alkoxy radicals. This in the current version of the paper is not well explained though. How does the RACM-LIM1 treats the alkoxy radicals formed from alpha-pinene and limonene? Did the author modified the mechanisms including available SAR? How is the organic nitrate yield treated? A recent study by Färber et al. (2024) shows that it might be difficult to sustain a lower than 0.6 HO2-to-RO2 ratio due to termination reaction for complex RO₂ such as formation of organic nitrates. The section in the paper showing the sensitivity test including monoterpenes should give more information.

The last “manipulation” of the mechanisms is not really clear to me. In the text it is mentioned: “Manipulating the self-reaction rate of peroxy radicals by approximately five-fold, and the extended lifetime counterbalance their supplementary consumption by non-traditional regeneration mechanisms” (Page 18 lines 465-467). I have no idea of what this means practically in the mechanism. This needs to be explained in a clearer way.

As mentioned by Referee #1 many more details on how the model simulations are performed are needed. In the manuscript it is mentioned that species listed in table S1 are used to set the boundary conditions for the base scenario. Which NMHC are included? From the kOH budget it appears a large variety of different VOC was measured. It would be good to list them. Is the precision, accuracy and limit of detection the same for all the different VOCs and OVOCs measured? Focusing on the kOH budget plot I would recommend separating the contribution of HCHO (which I assume now is included in the OVOC label) as I would guess it might be the largest fraction of the OVOCs.

It would be good to add the experimental budget for ROx as looking at table S1, all the species contributing substantially in the modelled budget (Fig 5) are measured. Or is Fig. 5 showing the experimental budget? And why did the author only analysis ROx and not OH, HO₂ and RO₂ separately?

Co-authors of this study just recently published a new mechanisms that could explain the missing OH source at low NO (Yang et al., 2024). This could be a good sensitivity test rather than species X and I would recommend the authors to try it.

Minor comments.

As mentioned, the paper needs careful language check. As far as I can tell it is not grammatically wrong but many sentences seem extremely complicated and the meaning is lost:

“The full-chain radical detection untangled a gap-bridge between the photochemistry and the intensive oxidation level in the chemical-complex atmosphere, enabling a deeper understanding of the tropospheric radical chemistry at play.” (Page 2, Lines 42-45)

“Moreover, the closure experiment, incorporating field campaigns and box model, has proven to be an effective method for verifying the integrity of radical chemistry at local to global scales.” (Page 3, Lines 70-72). I do not know what the closure experiment is?

References.

Färber, M., Fuchs, H., Bohn, B., Carlsson, P. T. M., Gkatzelis, G. I., Marcillo Lara, A. C., Rohrer, F., Vereecken, L., Wedel, S., Wahner, A., and Novelli, A.: Effect of the Alkoxy Radical Chemistry on the Ozone Formation from Anthropogenic Organic Compounds Investigated in Chamber Experiments, ACS EST Air, https://doi.org/10.1021/acsestair.4c00064, 2024.

Yang, X., Wang, H., Lu, K., Ma, X., Tan, Z., Long, B., Chen, X., Li, C., Zhai, T., Li, Y., Qu, K., Xia, Y., Zhang, Y., Li, X., Chen, S., Dong, H., Zeng, L., and Zhang, Y.: Reactive aldehyde chemistry explains the missing source of hydroxyl radicals, Nat Commun, 15, 1648, https://doi.org/10.1038/s41467-024-45885-w, 2024.

This paper presents measurements of OH, HO2, RO2, and total OH reactivity in the Yangze River Delta in China. Measurements were conducted before and after an elevated pollution event, and the measured radical concentrations were compared to predictions from a 0-D model incorporating the RACM2-LIM1 mechanism constrained to observed concentrations of O3, NOx, and VOCs. Similar to other studies, the authors find that the model tends to underestimate the measured radical concentrations, most significantly during the elevated pollution event. And similar to that proposed in other studies, the authors find that including an unknown species that enhances OH radical recycling (the “X” mechanism) improves the agreement of the model with the measurements. Furthermore, similar to that proposed in other studies, the authors find that the addition of multiple RO2 isomerization steps that could compete with reaction with NO, as well as reducing the rate of the terminating RO2 self-reaction improves the agreement of the modeled RO2 radical concentrations with the measurements. The authors find that the addition of multiple RO2 isomerization steps into the mechanism also helps to explain the observed HO2/RO2 ratio changes with changes in HCHO.

While the paper provides additional measurements of radical chemistry in polluted environments, it is not clear that the analysis “enabled a deeper understanding of the tropospheric radical chemistry at play” (line 597). As referenced in the paper, the unknown “X mechanism” has been proposed in several similar studies in an attempt to explain the model/measurement discrepancy. Similarly, the RO2 isomerization reactions have been proposed previously in an attempt to explain the observed peroxy radical concentrations. Thus, this paper as written doesn’t really provide new insights to explain the model measurement discrepancies. The paper might be acceptable for publication if the authors address the following comments in a significant revision.

1. The authors did not conduct any testing for potential interferences associated with their OH measurements. While it is clear that some LIF-FAGE instruments are more sensitive to interferences than others, testing for interferences is still important, especially in complex chemical environments given that the source(s) of the interference have yet to be identified. The authors should acknowledge the possibility that unknown interferences may have contributed to their OH measurements and may explain some of the discrepancy with their model. It is unfortunate that the authors did not conduct interference testing during the “heavy” pollution episode. This would have provided confidence that the elevated OH concentrations during this period were free from interferences.
2. There is very little discussion of the OH reactivity measurements. Figure 4 shows the measured reactivity with that calculated from major OH sinks, but it isn’t clear whether these are the measured OH sinks or whether they include the reactivity of unmeasured modeled oxidation products. During the “heavy” pollution episode, the calculated reactivity appears to be higher than that during the “semi” periods, while the measured reactivity appears to be similar. Given that the greatest discrepancy between the radical measurements and the model occurred during the “heavy” episode, the modeled OH reactivity (including the reactivity of unmeasured modeled oxidation products) should be discussed in much more detail.
3. As noted in the manuscript, there have been several studies where the “X mechanism” has been incorporated in order to explain the underprediction of the measured OH concentration by the model (Table 1). However, similar to these previous studies, the authors do not provide any new insight on what “X” might be. Some of these authors have recently published a theoretical study suggesting that reactive aldehyde chemistry may explain the missing source of OH (Yang et al., Nature Communications, 15, 1648 (2024). https://doi.org/10.1038/s41467-024-45885-w). Incorporation of this proposed mechanism into their model would provide some new insights into the potential missing radical chemistry and provide a test of whether the proposed mechanism can explain the measured radical concentrations during the heavy pollution episode.
4. The final section of the paper is very confusing. The authors appear to suggest that the base model constrained to the measured formaldehyde overestimates the HO2/RO2 ratio by increasing the production of HO2 relative to RO2. However, unconstraining the model to the formaldehyde concentrations results in lower HO2/RO2 ratios that are in better agreement with the measured ratio, presumably because the model underestimates the measured formaldehyde. However, including monoterpene chemistry that have multiple RO2 isomerization steps increases the modeled RO2 concentration so that the modeled HO2/RO2 ratio is in better agreement with the measurements when HCHO is constrained. The authors suggest that additional measurements of OVOCs are necessary, but the connection between unmeasured OVOCs and the different model scenarios discussed in this section is not clear. This section of the manuscript needs considerable revision in order to clarify the points that the authors are trying to make.