This paper describes the application of a gradient boosted regression tree machine learning approach to derive a parameterization for tropospheric OH based on CCM simulations. The approach is shown to reproduce simulated OH well under current conditions even for cases it has not been trained on, and it behaves acceptably, albeit with increasing errors, when applied to future conditions outside the standard training set. There is substantial novelty in the approach taken, and the results offer a degree of interpretability that is very interesting. The paper is generally well structured, clearly written, and appropriately illustrated. The authors have been thorough in evaluating their approach, and it is particularly good to see robust testing of input variable choice and hyperparameter value selection.

The main weakness of the paper is that the potential applications of the approach are not clearly identified. What does the parameterization add beyond the simulated climatology that was used to generate it? The chemical inputs used for the parameterization are dependent on OH, and hence a full model simulation is required to capture the feedbacks. In its present form, the parameterization is not sufficient to replace CCM chemistry, and can only reproduce OH from existing simulations. If a full CCM simulation is required to generate the inputs to the parameterization, then what does the parameterization add?  If the approach is to be used as a simplified chemistry, like ECCOH, how will the oxidised inputs such as MHP and H2O2 be adjusted? A clear description of the application or purpose of the parameterization is needed, ideally with an example. Could the approach be applied with aircraft or satellite measurements to estimate OH concentrations? What is its value beyond simply reproducing existing simulations?

Overall, the methodological approaches developed here appear sound, and the parameterization has substantial potential, but practical application of the approach is not described. The paper is not suitable for publication in GMD until the authors have made the purpose and application clear to the reader.

Specific Comments:

Title: The paper describes a machine learning methodology, but does not convincingly demonstrate a tool to improve computational efficiency, as independent application of the approach is not described. The second half of the title should be dropped.

The approach is trained on an existing near present-day CCM simulation. Why was the approach not trained over a much wider range of conditions from preindustrial to possible future?  A more thorough and complete set of training data would permit generation of a much more robust parameterization that was applicable to a wider range of conditions. Weaknesses in reproducing simulated future OH with the same CCM and chemistry demonstrate the frailty of the approach.

Table 1 needs to be presented more tidily to conform to journal standards. Note also that isoprene is included twice; the first occurence should be ethane. Does UV albedo refer to UV surface albedo? Does cloud fraction apply to the column fraction above a given level or to the local fraction at that level? Optical depth above and below are separate inputs, while C4/C5 alkanes are combined; this is not clear from the Table, but is evident in Fig 5.

Line 232: What is the likely origin of the biases poleward of 30 degrees? Could this be related to averaging of cloud cover over the diurnal cycle, a factor lost when using daily-mean input variables?

The methane lifetime is matched well, but the small bias high is systematic throughout the year and indicates a consistent underestimate of mass- or methane-weighted OH (as also seen in Fig S5). Can the authors suggest why this arises?

Typos and Minor Issues

Lines 74-76: Sentence grammar needs revision (or remove "Though")

Line 174: "balance" would be clearer as "remainder" (or a similar word)

Lines 35, 219 and 436: "comports" is somewhat archaic; "accords with" would be clearer

Fig 3: Red percentage labels are difficult to read over color backgrounds. Please adjust the font color so that they are legible.

Fig 5: What do the colors represent?

Line 457: The citation for Shi et al. is missing the publication date (2018)

There is a Section 4.1 (with subsections) but no Section 4.2, so renumbering of sections is needed here.

The study ‘A machine learning methodology for the generation of a parameterization of the hydroxyl radical: ...’ by Anderson et al. presents the results of training boosted regression trees on the output of a chemistry-climate model simulation. Specifically, the goal is to predict OH concentrations as a function of meteorological and chemical variables, which could thereafter be used as a parameterization.

Mostly, this is a solid, well-written paper. In particular, most of the technical choices (following the initial choice of algorithm) are well-reasoned. However, I still have a few major and minor technical and scientific concerns, which I would like to see addressed before I would recommend publication. In particular, I am not sure how helpful such a parameterization would be if most of the chemical inputs cannot be simulated interactively. At the very least, this will help to clarify points that other readers will likely find confusing as well.

Major comments:

• My main concern relates to the motivation of building a standalone OH parameterization. I see that the authors cite several studies that used and developed OH parameterizations before and that certain inputs to those parameterizations are themselves simplified (e.g. simply time-varying climatologies). However, given the inputs for the parameterization here (e.g. NO2, ozone, VOCs) would this not pre-determine OH variations hugely, i.e. most of the expected variance in nature would not be included anyway? Is this then really just about capturing OH trends that scale with changes in CO, methane, O3? It seems to me that this is not the variance you primarily learn here, cf. your Gain values which show low contributions from e.g. CO, or CH4. If one only cares about the effect of OH on CH4, would a simpler way not be to predict long-term CH4 changes as a function of the anyway prescribed changes in CO and O3?
• The title is longer than necessary. Maybe consider shortening it? For example, are both ‘methodology’ and ‘tool’ needed in the same title? I am also not sure the main application of this tool would actually be in chemistry-climate model simulations. Surely, if you already run an interactive chemistry scheme it would not make a big difference to just replace OH by a parameterization? Maybe you mean something different, but it could confuse potential readers.
• Training and evaluating a parameterization offline is a completely different animal from predicting ‘online’ ie in operational mode, especially if suddenly the inputs won’t be provided by a consistent interactive chemistry model anymore. By now this is a well-known fact about machine learning parameterizations. This must be highlighted somewhere, i.e. that the study here is an offline test of the principle that requires further validation before being used operationally, especially if the OH feedbacks onto the system itself somehow (which I guess it ultimately should according to your paper title).

Minor comments:

• l.94-98: Please also cite

Nowack et al. Using machine learning to build temperature-based ozone parameterizations for climate sensitivity simulations. Environmental Research Letters 13, 104016 (2018). https://iopscience.iop.org/article/10.1088/1748-9326/aae2be

Since this was the first study to suggest machine learning parameterizations in atmospheric chemistry. Note that the authors found that ridge regression outperformed random forest regression in their case, which might have to do with ridge regression allowing for some degree of extrapolation, which you find is a potential issue here (e.g. see also Nowack et al. AMT 2021 https://amt.copernicus.org/articles/14/5637/2021/amt-14-5637-2021.pdf).

Only trying out one algorithm is actually one of the main shortcomings of this study, given the aim to publish in GMD. Why not try at least a few different methods to compare their performance? This should be computationally feasible and it is well known that there is ‘no free lunch’ in machine learning, so just arguing that a method is chosen because others did the same before, often in very different applications, is certainly the (too) easy way out.

Another random forest application in atmospheric chemistry worth mentioning is Sherwen et al. ESSD (2019): https://essd.copernicus.org/articles/11/1239/2019/

• l. 101-104: yes, although the SHAP values could also be used for other methods, of course. Linear machine learning models such as ridge and Lasso are of course even more interpretable.
• l. 106-113: my main concern here is that you train your parameterization on a single simulation and mention, correctly, that the parameterization cannot extrapolate outside the training domain. Given that we are usually interested in transient climate change scenarios, I would strongly recommend training the parameterization on a wide range of simulations (ideally at least one extremely strong forcing and one strong mitigation scenario). This would mean that re-training is expensive, unless the data already exists. Maybe that should be highlighted instead, i.e. that you could usually learn from existing simulations that will be run anyway?
• l. 122: that’s a key concern: I doubt your current parameterization would work under climate change conditions, which makes it less useful. I think this point should be made very clear and highlighted prominently in the paper, ie that this is just a recipe to learn a parameterization but not a read-to-go product. Not all readers will be aware of this issue.
• l. 152: why not 2019? To avoid maximum extrapolation? I think it is good that you left out five years from the training data completely, this will reduce the risk of inflating performance measures due to spatial or temporal autocorrelation. I assume I understand your motivation correctly?
• Table 1: at this point it is still unclear to me how you consider the vertical dimension, so this should be clarified earlier on (unless I overread it somehow). Do you predict OH in each tropospheric grid box (from the near-surface to the upper troposphere)? Does you include only ozone, CO etc values from the same grid box you are trying to predict, or would, for monthly-mean training data, it not be best to include at least surrounding spatial predictors? I am also not sure if, especially for surface OH, it makes sense to build one parameterization that predicts all grid points simultaneously? Wouldn’t there be a spatial dependency of how e.g. ozone and OH relate, or do you think this will be sufficiently conditioned out by the other variables you include?
• l. 170: why separate by month and not by location? Should not June at a SH grid location be more different from June in the NH than, say, from July at the same grid point in the SH?
• l. 224: Random forests are known to often overpredict small values. Still wondering if this might partly be a result of throwing all data points independent of locations in one training basket?
• Figure 1: is this now tropospheric column-averaged OH? Surface OH? Please clarify. I read on: I now see that you say in the text that his is the PBL-500hPa average. Still, would add that info to the figure caption, too. Any particular reason to avoid the boundary layer? Is the spatial invariance not a good assumption there?
• At this point: do I understand correctly that you train and predict monthly-mean data? Your description in the data section was eventually somewhat confusing. So, do you train on monthly-mean data but use those functions to also predict daily OH? Might be worth highlighting again in the figure caption, for clarity.
• l .250-253: implies that you tried both, ie training on daily and monthly data. Here you say that daily performs better, but above you seem to imply that daily suffers from other problems with extrapolation. What would you recommend then? Please clarify.
• Figure 2: clarify that this is based on daily predictions (ie based on the model trained on daily data).
• Figure 3 should be larger, otherwise this becomes hard to read.
• Figure 5 and l. 351: again is this based on the model trained on daily or monthly-mean data? In any case, I would assume that CH4 has low predictability as it shows low variability on relatively short daily and monthly timescales, where other factors driving internal variability (rather than trends) are providing greater contributions to the predictions, thus showing greater feature importances. I suppose that would explain your initially maybe somewhat surprising result. If you predicted longer-term averages (e.g. decadal) I guess the picture would change dramatically. Anyway, this links to my major comment above and if much of the variability you capture will be negated if chemical inputs are derived from much simpler climatologies.
• l. 447: I see – was the motivation to exclude 2016 the specific El Nino event?
• l. 542-583: I think this is a very important discussion. Random forests cannot extrapolate, so this behaviour is not surprising (e.g. Nowack et al. AMT 2021). As a more general point, I would rephrase the entire paper, also the abstract, in the sense that you present a way to learn relationships, i.e. to show that this is possible, rather than a ready-to-go parameterization, see also my other points above.
• Section 4.1.2: again, not surprising because random forests cannot extrapolate. So, if you change the distribution mean, shape, and ranges, you will be in trouble. Again, selling your results as a recipe rather than a ready product, would address this point immediately.