Review of Intensive photochemical oxidation in the marine atmosphere: Evidence from direct radical measurements

General comments:

The manuscript presents OH and HO2 observations and model comparisons from a marine site which was influenced by air masses both from the ocean sector and from the land sector. The manuscript compares the radical observations to those previously made at other marine locations. Given the low wind speeds experienced and the impact of local emissions (as evidenced from the isoprene concentrations reported from the ocean sector) is this region really representative of coastal marine environments in general? The HONO concentrations reported are much higher than typically observed at other marine sites and the major sources of OH differ, so these differences should be highlighted and it should be acknowledged that these processes may be unique to this particular study. The impact of halogen chemistry and heterogenous reactions have previously been shown to be important to the chemistry occurring at marine sites. The authors consider the impact of bromine chemistry in one particular model scenario, but the reactions considered and products from the bromine scheme need some revision (see later comment). The impact of heterogenous uptake of HO2 and other species should be included in the model – this can’t simply be ignored because the modelled and measured HO2 agree without it. I have made quite a few specific comments that should be addressed before final publication.

Specific comments:

In section 2, the authors should describe how the OCM and LAM sectors were assigned – by wind direction or trajectory analysis? Some of this description is provided in lines 261 – 270 and I suggest this is moved to section 2.

Section 2.1: some description of the vegetation type in the surrounding forest should be provided, so the reader can ascertain if other biogenic emissions such as monoterpenes were likely present that could influence the local chemistry.

Section 2.2.1: Some further details on the HOx radical detection and calibration methods should be provided:

Line 132: ‘..via chemical transformation’ add ‘by addition of NO’. Please also state the purity of the NO and concentration of NO in the detection cell.

Line 147: Is this a single pass laser configuration or multi-pass? Please state

Line 155: change ‘avoid’ to ‘reduce’

Line 159: The ozone interference as a function of ambient ozone and H2O (v) concentration and laser power determined from the laboratory experiment should be provided.

Line 160 -164: The previous good agreement reported for OH measurements by this system and the PKU-LIF in a previous study doesn’t translate to an interference-free OH observation in the present study. Chemical removal of ambient OH using an inlet pre-injector is now seen as standard practice for LIF OH instruments. In the absence of this, the authors should provide some information on the chemical environment (ozone, alkene, NOx concentrations) were the instrument was deployed during the intercomparison and explain how this contrasts with the current environmental conditions.

Line 166: The authors need to state the percentage interference from an alkene-derived RO2 under these operating conditions (it won’t be zero).

Line 169: How much OH and HO2 was produced in the calibration? Was the calibration performed using a turbulent flow? How was the lamp flux determined? These details should be included in the manuscript.

Section 2.2.2: Given the importance of HONO as an OH source in this study, some comments on possible instrument artefacts/or how interferences were corrected for should be discussed.

Line 183: Which of the measured photolysis rates were used as model constraints?

Section 2.3:

Line 204: Did the modelled OH and HO2 reach a steady state concentration during this time – what was the % difference between day 2 and day 3 radical concentrations?

Line 208: Could the authors explain their choice of the 18 he lifetime? Were any model tests performed to assess how well the model predicted HCHO for example (if left unconstrained to HCHO) with an 18 hr lifetime? How sensitive were the modelled OH, HO2 and modelled kOH to the choice of this lifetime?

Line 211 – 217: What was the modelled BrO concentration when the model was run with Br2 chemistry? I think some comment on the potential impact of iodine chemistry should be included in this section (as other papers which focus on the chemistry of the marine boundary layer consider both iodine and bromine chemistry).

With regards to the Tables S2 and S3 provided in the SI, what are the expected products from the photolysis reactions in S2? HOBr photolysis is a source of OH, was this included as the photolysis product in the model? For S3, ‘ACD’ and ‘MO2’ need defining. Were heterogeneous loss processes for HOBr considered? In Bloss et al., ACP, 2010, the reaction of CH3O2 + BrO produces HOBr + CH2O2 (which dissociates to CO and H2O). Could the authors explain/provide a reference for their choice of products (HOBr, HO2 and HCHO) from this reaction? As it is written, the reactants and products don’t balance. As it stands, the halogen scheme included seems incomplete and I suggest this is reviewed before final publication.

Line 233: ‘exhibited good consistency..’ it would be useful to provide typical concentrations of CO and PM2.5 to aid comparison to the previous campaigns referenced.

Section 3.1.1: As the paper is trying to contrast LAM and OCM sectors, I think it would be useful from the start of this section to provide concentrations for the species discussed (e.g. NMHCs, NOx, CO, O3) from both sectors rather than campaign averages.

Line 235: I don’t think it is ‘conventional belief’ that marine ozone would necessarily be at background levels. At coastal sites which are influenced by land emissions, as is the case at the YMK site, I don’t think it is unexpected to observe net ozone production given the NOx concentrations reported. I think it would be valuable to highlight, perhaps in Table 1, contrasting marine environments – for example, some of the referenced literature are from marine sites which are considered representative of the open ocean (RHaMBLe, SOS, ALBATROSS), whereas others, including YMK, are coastal sites which, depending on the wind direction, could be influenced by local land emissions.

Line 246: provide typical concentrations of alkenes and aromatics.

Line 260: The wind speed during the campaign is low, so I would expect local emissions could have impacted the concentrations of the precursor species to a certain extent. 0.5 ppb isoprene was observed in the OCM sector (fig.2) which, to me, suggests some local influences which should be acknowledged.

Line 319: In previous literature, e.g. Whalley et al., ACP, 2010, the inclusion of halogen chemistry led to an increase in modelled OH concentrations and a decrease in modelled HO2 concentration, so the decrease in the modelled OH concentration reported here is a little surprising – perhaps the differing levels of NOx between this study and RHaMBLe play a role? Could the authors provide a little more detail on the dominant reactions in the halogen scheme that are contributing to OH destruction?

Fig. 4: This figure could be removed as figure 6 is more instructive.

Line 335 – 346: I’m not sure this case study adds anything to the paper as it stands and could be removed to make the paper more succinct.

Line 358: I don’t think the good agreement between modelled and measured HO2 should be used as an argument to exclude heterogeneous reactions in the model. If the inclusion of heterogeneous processes did reduce the modelled HO2 concentration, this could highlight missing HO2 sources in the model (or may indicate that some RO2 species present were detected as HO2) and so warrants investigation.

Line 371: Given the model slightly overestimates HO2 and the calculated OH reactivity could be an underestimate of the total OH reactivity actually present, a missing OH source may be masked.  A comment on these points should be provided.

Line 394: D(OH) should be considered a lower limit as it uses calculated rather than measured kOH. This should be made clear.

Line 421 – 423: Again, following on from my earlier comments, without a measurement of kOH, the absence of unknown OH recycling pathways can’t be confirmed here.

Fig. 10, line 532 - 539: Some further details on how the model was run when it was used to predict ozone are needed. What model constraints were changed to variables other than ozone (presumably NO2 was also changed to a variable)? Why was the atmospheric lifetime changed from 18 hrs to 15 hrs and what was the rate of the first order loss term used? How did modelled OH, RO2 and HO2 change when the model was unconstrained to HONO?

Line 547 - 548: I’m not sure the findings from this study support this closing statement. Although the impact of HONO in this particular marine environment is interesting, the elevated HONO concentrations are somewhat of an anomaly compared to the other marine environments. In regions where HONO concentrations are elevated, the sources of HONO would need to be identified to aid pollution mitigation policies.

Line 564 – 567: These statements need to be supported by evidence or removed.

Minor comments:

Line 84: ‘..heterogeneous iodine-organic chemistry’ Could the authors provide the specific reactions they are referring to here.

Line 155: change ‘avoid’ to ‘reduce’

Line 183-184: I’m not sure about the terminology used here ‘conventional pollutants’, ‘secondary pollutant precursors’ and ‘destruction products’. I suggest just listing all these species and not attempting to categorise them.

Line 183: ‘carbonic oxide’ to ‘carbon monoxide’

Line 198: change ‘radical related secondary pollution’ to ‘ozone’

Line 199: remove ’conventional’

Line 249: ‘grooved distribution’ is strange terminology, I would delete.

Line 252: ‘extremely high..’ ‘significantly affect..’ need to be more specific.

Line 277 – 278: This needs rewording, as it is written, it could be interpreted as meaning the ozone and HONO concentrations were higher during the OCM period.

Line 280: ‘..changed greatly’ I would be explicit, i.e. T increased..From figure 2, J(O1D) is very similar between the two sectors.

Line 360 -368: Suggest referencing section 4.1 here

Line 448: ‘loss’ to ‘production’

Fig 11: The YMK campaign is labelled as STORM-II in this fig. Change to YMK for consistency.

This manuscript reports an investigation of free radical (OH & HO2) chemistry & budget in a coastal environment (Pearl River Delta) impacted by anthropogenic emissions from ships and transported pollution plumes from China.  While the campaign duration is short (only 11 days), this dataset and the conclusions reached in this study will be of interest for the scientific community. The manuscript is well structured and clear. This reviewer recommends publication after the authors address the following comments:

Comments:

• L 32-34: Average concentrations of OH and HO2 are provided for the LAM period in the abstract. For comparison, please also provide values for the OCM period.
• L38-41: “After a sensitivity test, HONO-related chemistry elevated the ozone production rate by 33% and 39% during the LAM and OCM periods, respectively, while the nitric acid and sulfuric acid formation rates were 52% and 35% higher, respectively.” – Please clarify the last part of this sentence. Are the nitric acid and sulfuric acid formation rate increases for the OCM or LAM period?
• L41-43: “The simulated daytime HONO and ozone concentrations were reduced to a low level (~70 ppt and ~35 ppb) without the HONO constraint.” – Are the reported concentrations for LAM, OCM or both periods together? For comparison, please also provide values simulated when HONO is constrained.
• L157-159: “A wavelength modulation for the background measurement that periodically switches from an on-resonant state to a non-resonant state has been widely used to obtain spectral zero.” – Did the authors also used a chemical modulation approach as done now on most LIF-FAGE instruments to make sure that OH measurements are free from interferences? If so it should be discussed here. If not, the authors should comment on potential interferences on OH measurements.
• “The ozone photolysis interference was subtracted according to laboratory experiments.” – What was the contribution of this interference to the total measured OH signal (interference + ambient)? 
• “The ozonolysis interference on the measurement consistency of both systems was excluded under high-NOx and high-NMHC conditions, confirming the general applicability under complex atmospheric pollution.” – What do the authors mean by “ozonolysis interference”? What type of interference is it? The authors indicate that they could rule out interferences under high-NOx and high-NMHC conditions from a comparison with an interference free instrument. What about low-NOx conditions as encountered in the MBL? Why do the authors consider PKU-LIF to be free of interferences? 
• L164-167: “For HO2 measurement, the NO concentration corresponding to a conversion efficiency of ~15% was selected to avoid RO2→HO2 interference (especially from RO2 radicals derived from long chain alkanes (C ≥ 3), alkenes, and aromatic hydrocarbons.” – The authors optimized operating conditions to minimize this interference. However, to this reviewer’s knowledge, it is not possible to completely eliminate this interference. The authors should comment on the level of interference that is still expected from the most abundant RO2 radicals at the measurement site. If a significant interference is expected, the authors should report this measurement as HO2* and should compare it to modelled HO2* values instead of HO2.
• L175: “measurement errors were 13% and 17%” – Please clarify in the text how these values were assessed? If these values are derived from uncertainties associated to the generated radical concentrations it should read “measurement accuracy”
• L185-191: The authors should provide more details on the measured VOCs in the supplementary material. What were the most abundant species in each category (alkanes, alkenes, aromatics, OVOCs)? What was the campaign averaged concentration of each category? Etc.
• L191: “All of the instruments were located close to the roof of the fourth floor” – It was not indicated in the text before that there is a building at the measurement site. Please provide some details in the site description section.
• L202-204: “The overall average during the observations was substituted for large areas of missing data due to instrument maintenance or failure.” – How long were these time periods? They should be highlighted in Figure 3. It is interesting to note that while using campaign average data when ancillary measurements are missing could lead to improper model constraint , it does not appear to have a significant impact on the model-measurement agreement.
• L210: “the simulation accuracy of the model for the OH and HO2 radicals was 50%” – Please specify if this is 1 or 2 σ
• L211-217: The bromine chemistry is included in the chemical mechanism to test the HOx sensitivity. What about the iodine chemistry? Is there a specific reason why it was not included in the mechanism as well?
• L301-302 & Fig. 3: How does the modelled kOH compare to that calculated from the model constrains? How much OH reactivity does the model generate from unconstrained OVOCs? Since VOCs are constrained as lumped groups in RACM, OH reactivity from unmeasured OVOCs may be underestimated. Could the authors comment on this?
• L311-313: “The base model slightly overestimated the OH radical, suggesting that a radical removal pathway was missing.” – The authors should remove this statement. The measurement/model agreement is well within uncertainty. In addition, this is only observed on the first 2 days and a model underestimation is observed on 10/23 & 10/24.
• L314-327: Model sensitivity to halogen chemistry - What was the range of BrO concentrations simulated by the model? Is it comparable to BrO concentrations measured in the MBL? As mentioned in a previous comment, iodine chemistry was not added in the model. Why? Could the authors comment on the potential impact of this chemistry?
• L331-346 & Fig. 5: This reviewer does not see the added value of this section and thinks that it moves the reader’s focus away from the main results. It is suggested to remove it.
• Eq. 3: The second term on the right-hand side should include the organic nitrate yield from RO2+NO. The authors may need to recalculate P(Ox) values displayed in Fig. 9 if the organic nitrate yield was not considered.
• L529-542: Please provide details on the time dependent box model in the supplementary material.

Edits:

• L183: “carbonic oxide” should read “carbon monoxide”
• L271: “Serval observation campaign” should read “Several observation campaigns”
• L299: Since a range of concentrations is given for both OH and HO2, “The average daily maximum” should read “The daily maximum”. Other instances in the text.
• L332: Please define ROx
• 2: Please define the different parameters
• L447-448: “As the only known gas-phase source, OH + NO accounted for a negligible proportion of the HONO loss.” Should read “As the only known gas-phase source, OH + NO accounted for a negligible proportion of the HONO production rate.”
• L455: “Peroxyl radical” should read “Peroxy radical”. Other instances in the text.
• L573: “peroxynitrite” should read “peroxynitrate”
• Fig S2: Please indicate the color code for back-trajectories