In this manuscript, Caram and colleagues present the reactive halogen chemistry in the chemistry-climate model LMDZ-INCA, focusing on the sensitivity of tropospheric ozone. This work emphasizes a long-standing issue in the climate community that the impacts of halogen chemistry on key short-lived climate forcers (such as ozone and methane) have not been fully accounted for in most climate models. 

The method section of this manuscript lacks key details of the model (LMDZ-INCA) that are relevant for the scientific goal of this work. For example, acid displacement is a major source of reactive chlorine in the atmosphere. To properly model acid displacement, several key processes need to be properly implemented in the model, such as the emissions, dry/wet depositions, and transport of sea salt, as well as its physical and chemical properties (especially acidity), not to mention the acidic gas(es) to displace HCl (e.g., nitric acid). It remains unclear how these processes are implemented in this model LMDZ-INCA. It does appear that the model uses highly simplified HCl emissions to account for this process, yet no details are given (i.e., spatial/temporal variability of such emissions). Similarly, debromination is a major source of reactive bromine in the troposphere. Yet, how this process is implemented in LMDZ-INCA is unclear. Fig 3 looks like the model only recycles HBr produced from other reactive bromine species (not a net bromine source); if this is indeed the case, essentially the only source of the reactive bromine is the organobromines. Key details like these should be clearly stated.

This work does take other more established models as benchmarks, especially GEOS-Chem and CAM-Chem. The halogen chemistry implemented in this model (LMDZ-INCA) appears to be much simpler than GOES-Chem or CAM-Chem. The measurement-model (LMDZ-INCA) comparison is not adequately transparent and contains almost no specifics. A few major issues: the measurements and observations are not presented in consistent manners; the comparisons completely ignore the spatial and temporal variabilities revealed in the observational datasets. The level of detail presented in these comparisons does not adequately justify the performance of this model. Please see the next section for details. It is my opinion that this manuscript is not well written either, with numerous vague/confusing statements, which I will elaborate later. In light of these, it is unclear in the current manuscript what new scientific insights this study offers, compared to other models such as GEOS-Chem and CAM-Chem, which are more comprehensive and have been rigorously evaluated against a wide variety of observations.

The way that the pre-industrial simulations are configured is based on key assumptions that are unverified/unjustified. For instance, this study essentially assumes several key processes of the Earth system (e.g., lightning, biomass burning, biogeochemistry in the ocean) remain the same between the pre-industrial period and the present-day. I am not fully convinced. One specific example is again acid displacement largely driven by HNO3, which, may be different between pre-industrial periods and present-day. These key assumptions need to be justified.

Therefore, I do not recommend this manuscript for publication in Geosci. Model Dev. Please find my specific and technical comments below:

Line 26: Indeed the earliest study of the reactive halogen chemistry in the troposphere was perhaps a decade later than that for the stratospheric halogen chemistry, but since then there have been quite a few large-scale, comprehensive field experiments focusing on the tropospheric halogen chemistry. Therefore I do not think “…halogens in the tropospheric chemistry had been investigated but to a lesser extend…”

Line 40: reactive halogen species also greatly affect the chemical transformation of atmospheric mercury.

Line 51: halogen chemistry is also active in polluted atmosphere, e.g., Thornton et al 2010.

Line 58-59: please define HTAP, ACCMIP, and AerChemMIP. This is a great point. Please also elaborate how these model intercomparison projects have been used to evaluate the effects of international policies. 

Line 87: consider deleting non-methane hydrocarbons (NMHC) since this category overlaps with volatile organic compounds.

Line 89: define ORCHIDEE.

Line 101: heterogeneous chemistry on sea salt: is this simply halogen recycling (i.e. not a net source) or debromination (net source)? Please clarify.

Line 105: “ice chemistry” is vague. What type of ice? What kind of chemistry on ice? What microphysics option/package is used? Please clarify. Also, I do not quite follow how discarding ice chemistry can *ensure* bromine cycling in the MBL.

Line 106-107: Does this mean that the model cannot reproduce bromine-mediated ozone loss if the so-called “ice chemistry” is included? This may be important information for the community.

Line 135: rephrase.

Line 181-196: in this section (chlorine), only a few ratios are roughly compared to a single model (GEOS-Chem) on the global scale (I guess the numbers are global means). Indeed the GEOS-Chem study cited here (Wang et al., 2019) is fairly comprehensive and probably state-of-the-art, but the level of detail presented in this manuscript does not adequately justify the performance of this model (LMDZ-INCA). Note that the GOES-Chem study cited here (Wang et al., 2019) have been evaluated using a wide variety of observations (ground-based: particulate chloride, gaseous HCl, HNO3, ClNO2; airborne: HCl, ClNO2, HOCl, Cl2). I fail to understand why the rich reactive chlorine dataset used for model evaluation in Wang et al. (or even a subset of it) is not used to evaluate this model (LMDZ-INCA).

Line 186: “atomic chlorine evolves… ” this is confusing and inaccurate from the chemistry perspective. Consider rephrasing to something like “atomic chlorine has two main sinks/reaction pathways/…”

Line 202: What is considered as “efficient”? How is this efficiency quantified in this model and in the cited GEOS-Chem studies? Note that the bromine schemes are very different in these GOES-Chem studies (Parella et al., 2012, Schmidt et al., 2016; Zhu et al., 2019).

Line 210: This entire paragraph is problematic: 1) “Since our goal is to simulate the impact on global and ground-level ozone, rather than simulating a state-of-the-art partition within inorganic bromine…” I fail to follow the logic here. What is a point of simulating the impact on global and ground-level ozone if the model does not represent the state-of-the-art understanding of bromine chemistry? Especially, the “impacts on global and ground-level ozone“ have been examined using more comprehensive models (like GOES-Chem and CAM-Chem). 2) “… we make sure that the bromine cycle is chemically active…” This sounds like a very low bar. One can have an active bromine chemical mechanism as long as a few key reactions are included. 3) “…even though reaction fluxes are a factor of 1 to 2 smaller…” please clarify what fluxes the authors are referring to here.

Line 222: “the concentrations of HI, INO2, and O2 are lower…” where can the readers find the concentrations of these compounds??

Line 230: if the authors do not bother to clarify how geographical representation of organic/inorganic iodine sources affect iodine burden, might as well delete this sentence because it serves no purpose as currently written.

Figure 2-4: these schematic diagrams are so simplified that they are very difficult to follow and may be confusing for readers who are not experts in this area. I’ll list a few here: 1) Many important pathways are not shown (e.g., the production of HBr, BrNO2 chemistry). 2) In Fig 3, BrO photolysis and the reactions with other compounds (NO, BrO, ClO) are not separated and some reactions may lead to a net loss of ozone (or odd oxygen) but some don’t. 3) In Fig 3, Br (a very short-lived radical), Br2 and BrCl (both stable compounds) are placed in one box, and it’s unclear where some of the arrows are pointing at. 4) it is not immediately clear how the bottom center box (HOI, INOx, N2O5) affects chlorine (Fig 2) and bromine budget (Fig 3). 5) It remains absolutely unclear what “physical loss” is and how it works, e.g., is this wet or dry deposition?? What compound(s) exactly? 6) the number formatting is very confusing. For instance, the Cl burden in Fig 2 is written as “3,0.10^-4”. I am aware that comma is also commonly used to separate the integral part of the number from the decimal part (which is perfectly fine), but then the full stop is used in the scientific notation (not even the dot multiplication symbol). All together it looks like two numbers (3 and 0.10^-4). Please follow the commonly accepted number formatting in scientific publications as well as journal guidelines. 7) The percentage values in the square brackets are not defined. 8) In Fig 4, not one single reaction rate is given (while Figs 2 and 3 do list a few rates) and what exactly are “gas phase reactions”??

Line 247-248: this sentence offers virtually no specifics. Where are these sites located? Where are the ClNO2 comparisons presented? 

Table S5: the last four reactions appear to rely on underlying assumptions. Essentially the yields and branching ratios used in these four reactions need to be justified. Also, some of these reactions do not obey mass conservation, e.g., HOI -> 0.85 ICl + 0.15 IBr + HNO3. This reaction makes chlorine, bromine, and nitrogen out of nothing, which might not be complete nonsense under very specific conditions but are certainly dangerous and should be avoided in modern chemical transport models.

Table S9: The way the comparisons are conducted in this table does not make much sense and definitely is not “satisfactory” (Line 251). 1) Is Cl* the sum of total reactive chlorine or some individual compound (Cl2, HOCl, ClNO2, ClNO3)? Either way, such comparison offers practically no scientific insights. I fail to understand why the comparisons are not conducted for each individual compound.2) if the measurements and are shown as 24-hour means, please also show standard deviation or something like that to represent the variability of these observations. 3) I do not understand why monthly means (modeled) are compared to 24-hour means (measured)? 

Line 253: Table 2 is also problematic. 1) the measurements are shown in very different styles: some given in a range, some with a plus/minus (unclear what these are), and some are given a single value. The table caption does not help. 2) the use of “<” is also confusing. It says in the caption that this symbol indicates that mixing ratios are below detection limit, yet in the table the symbol appears to be used differently. For instance, in the first line of the table reads like the measured BrO was below 2.0 ppt. 3) many of the observations contain rich information on the spatial variability (vertical, geographic) which is wasted completely here. Why don’t the authors show a few vertical profile plots for the airborne measurements and a few time-series or alike for the ship-based measurements? 4) again it makes no sense to compare the modeled diurnal averages to the measured daily max.

Line 279: averaged across the entire atmosphere or troposphere or what?

Line 282: why ozone column carries the unit of ppbv?

Line 303-304: the total ozone chemical annual loss decreased by 2.4% in the simulation with halogen chemistry, I assume?

Line 347: please provide evidence (perhaps a few citations) to support this statement.

Line 349: what is this “NOx concentration threshhold”?

Line 350: “… NOx from 24-27 pptv to 39-41 pptv” it is completely unclear what these values are.

The paper in review for GMD by Caram and co-workers is a first attempt to include tropospheric halogen chemistry within the global chemistry-climate model LMDZ-INCA. This is a very interesting and well intended effort. But, the current version and modeling fall short of the high standard of GMD. I agree with reviewer #1 on all points, but come to a different conclusion that if the modeling and the presentation within the paper are improved, this can eventually be published in GMD with major revisions.

The main problem with the paper at present is that there are no new scientific conclusions that can be drawn from this modeling effort. I suppose that GMD papers can be based mainly on descriptions of new model implementations, but in the case that this is acceptable, then the model description has to be significantly improved in it’s clarity and some errors and omissions must be addressed for this to be acceptable.

Specific major comments are detailed below:

L35 - VSLS are not the only source of reactive halogens, this is a mistake. Halogens are also released from sea salt aerosols and iodine is released via ozone deposition to the ocean surface. These should be discussed and included in the modeling. These are mentioned later (around L135), but this must be clarified here. Polar specific halogen activation mechanisms (snow, blowing snow sea salt aerosols, etc) may not need to be included here for the first global modeling study with LMDZ-INCA, but should at least be mentioned. 

L101 - The heterogeneous chemistry on sea salt and sulfate aerosols needs to be more clearly detailed. The basic aerosol chemistry within LMDZ prior to adding this must be described in some detail in order to know if what has been added is reasonable. The aerosol chemistry in the two established global models (CAM-Chem and GEOS-Chem) are significantly different. The method implemented here follows the CAM-Chem methodology.  However, this implementation seems to only include recycling on sea salt and sulfate aerosols, rather than actual degassing of HCl and HBr triggered by aerosol acidification (or another proxy for acidity, for example sea salt aerosol age). This approach for reacative halogen cycling is already used in CAM-Chem, but it is not correct compared to what is known to happen in the atmosphere. This is particularly important for chlorine release from sea salt aerosols globally. One early example of modeling HCl emissions from sea salt aerosols is:

Erickson III et al., JGR, 1999: https://agupubs.onlinelibrary.wiley.com/doi/abs/10.1029/98JD01384

Other processes that liberate photochemically active halogens from sea salt aerosols are also known, see for example the early review of Finlayson-Pitts and Hemminger, J. Phys. Chem. A, 2000:

https://doi.org/10.1021/jp002968n 

L105: I do not understand the discussion of ice chemistry here, is this ice/mixed phase clouds, snow, or sea ice. What does it mean to ensure bromine recycling in the MBL?

L133: How is HCl emitted from sea salt? 

L181 - Section 3.1.1 - This section is poorly written and I cannot tell what is being compared with what. There is not enough information or numbers in this section for this to be considered a chlorine model evaluation. The information in this section should be provided in figures, such as a plot of total Cly in LMDZ-INCA compared with CAM-Chem or GEOS-Chem for the same years/conditions as a function of latitude and altitude.

L201 - Section 3.2.1 - Same comments as for Section 3.1.1. (above).

In addition, the discussion of wanting to capture the impact on ozone rather than the actual chemistry is a puzzling and problematic argument. The focus on ground level ozone, while also discussing the entire tropospheric chemistry cycle for ozone at the same time is also a problem.

L218 - Section 3.1.3 - Same comments as for Section 3.1.1 (above). I don’t understand why there is a separate iodine flux section, while the bromine and chlorine fluxes are not discussed. I believe this flux section is actually a chemical budget, but the writing is unclear.

L247 - Industrial emissions of chlorine are known to be important for ground level reactive chlorine cycling (see Thornton et al., 2010, https://www.nature.com/articles/nature08905). Why are they left out here?

L252 - I don’t understand how the measurements and model are compared in Table S9. Where are the measurement sites, what model grid cells are used? What does it mean that the measurements are a 24 hour average while the model uses an average over months?

L255 - Table 2 - I understand that the model values are diurnal averages, but more is needed on the measurements (timing of measurement). Are you comparing a monthly average from the observation in some cases with a diurnal average from the model? The wording is unclear and it is possible that the model and observations cannot be comparabled in this way. 

L269 - Section 4 - This section shows why the discussion earlier regarding the main goal of the study is to capture ozone chemistry near the surface is not accurate. In this section the whole troposphere is discussed (however this is not well defined).

L289 - The discussion of the factors that result in different tropospheric ozone burdens from different NMVOC emissions needs to be expanded and discussed in more detail. Is the difference due to NMVOC emissions even larger than due to inclusion of halogen chemistry? If yes, then why were the same NMVOC emissions not used for these runs?

L371 - Section 5 - I do not see any new conclusions compared to past work. This should be improved. The main problems are that (1) the modeling is not advanced compared to past work and (2) there are no new conclusions. Therefore, this paper does not fit the aims of GMD at present. However, maybe the GMD editorial team can agree to accept new descriptions of models without these two criteria being met. In general, it is very good to see more models including halogen chemistry. Therefore, it would be a dissapointment if this review process ended with the result that there is no halogen chemistry available in LMDZ-INCA in the future.

Comments regarding citations, co-authorship, and code availability:

• There is a persistent issue of self citations within the paper, while ignoring the wider literature. Examples are on lines 33 and 45, only including self citations for the authors’ own groups is not appropriate for these sentences.
• For co-authorship - the description of the author contributions is interesting, but may not rise to the level of the GMD co-authorship guidelines (https://www.geoscientific-model-development.net/policies/obligations_for_authors.html, point 9). Specifically, serving as a scientific advisor for the manuscript may not fit within this description from GMD.
• The code availability on google drive is not standard and this code should be archived on GitHub and Zenodo as noted by the GMD executive editor.

Minor comments:

L19 - halogens should not have an s here

L40-41 - halogens both change the partitioning of NOx and also react with NO2 to form species that remove NOx from the system via deposition or other loss processes. While this is said in the next paragraph, this statement is not quite complete/right here.

L184 - halogens’ should be halogen