Review of ‘Understanding drivers and biases of simulated CO emissions by the INFERNO fire model over South America’ by Veláquez-García et al.

General comments

Wildfires are an important part of the carbon cycle which are receiving much welcome attention from the climate modelling community at the moment. Advances are being made in the representation of fires within Earth System Models, and it is therefore important to evaluate the performance of fire models against observations so we can have confidence in their value as experimental tools. Wildfires are a particular concern in South America, and here the authors evaluate the performance of the JULES-INFERNO model against satellite-derived datasets using machine learning (ML). The authors find that the model exhibits spatial and temporal biases, attributing these to biases in key driving factors such as soil moisture and Plant Functional Type (PFT) coverage.

The paper addresses a knowledge gap and the motivation is clear. However, the analysis is excessively complex and difficult to follow, with very busy plots, occasionally inappropriate plotting choices, and a results section full of numerous acronyms specific to this study. Furthermore, there are some methodological issues with the work, in particular around the use of column CO to evaluate the performance of a land-only modelling setup.

1. The results and discussion section is incredibly dense and hard to follow. The authors have performed so many sensitivity tests and created so many acronyms for them that it is hard for the reader to understand what’s going on and the aims of the paper risk being buried. Additionally, many of the plots are very busy (although I appreciate that large-format versions would be available in the final online version of the paper). At the very least, I would suggest the authors seriously consider whether all the information in the results section is necessary to be included in the main section of the paper and consider moving some plots to the supplementary info. I would suggest splitting the results and discussion, which would enable the thread of the paper to be easier to follow. The paper would also benefit from a clearer statement of the objectives and demonstrating how each analysis section is designed to address them.
2. A large section of the paper is devoted to comparing different satellite-derived fire products against each other. While this is valuable, I think some of the finer detail could be moved to a methodological note in the supplementary info. As is often the case, the authors find that the differences between the observational products are about the same as differences between the model and the observations. With this in mind, the approach used which averages multiple fire datasets to produce a benchmark is not sufficiently justified. The authors exclude FINN (in which case, it could be removed from the analysis in the main text) but include GFED4 in the averaging even though it differs substantially from GFED5 (for example). The reasoning behind the averaging of multiple fire products needs to be more clearly explained.
3. It is unclear why total column CO observations are being used in this analysis. The modelling setup used produces CO emissions, but as it is a land-only model it is confusing to the reader to imply that atmospheric modelling has been done as well. To evaluate the model using TCCO you would need to simulate the atmosphere as well. Atmospheric transport of CO, a species with a long atmospheric lifetime, along with the topography and regional circulation of SA, means that TCCO is not necessarily co-located with peak CO emissions from fires. Additionally, some of the analysis is limited by the need to consider shorter timescales as a result of limitations of the TCCO datasets. I suggest the authors remove the TCCO analysis from the paper and stick to CO emissions. Using the emissions produced by INFERNO to force an atmospheric chemistry model, and comparing that to observed TCCO, would be a logical next step but would be beyond the scope of this paper.
4. I will confess that I am not an expert in the use of ML detailed in this work. However, the way in which certain variables were excluded from the ML model seems to be limiting. My understanding of this approach is that it can handle large numbers of covariates and indeed that this is a strength of the approach. It would be interesting to see if the results are sensitive to the choice of variables excluded, or to run the analysis with all variables. The use of soil moisture to represent leaf and wood carbon in particular is a concern – these variables strongly covary, but are calculated in very different ways in the land model. By using one set of processes to represent another, the authors may be limiting the power of the analysis especially given the goal is to evaluate model processes.
5. The paper contains a number of typos and instances of awkward wording, which are fixable with thorough proof-reading. I do not believe it is the responsibility of peer reviewers to perform the work of a sub-editor, though I have pointed some examples below.

Specific comments

Some of the authors’ names seem to be misspelled in the submission, based on the professional profiles found on the websites of their universities (‘Veláquez-García’ = Velásquez-García, ‘Chiperffield’ = Chipperfield).

Line 7: Specifically, this should say ‘carbon monoxide (CO) emissions estimates’.

Line 10: Remove ‘categories of’.

Lines 16-18: It is not immediately clear what the percentages in this sentence refer to.

Lines 26-27: Unclear wording (‘the success of fire-prone ecosystems is enhanced’).

Line 45: Suggest ‘represent’ or ‘simulate’ instead of ‘understand’.

Line 61: Where does the figure that SA represents 15% of annual fire carbon emissions come from? Over what time period?

Line 311: Should be Tg yr⁻¹.

Figure 2: The colour bar used for the annual mean emission plots is not perceptually uniform and features large non-uniform breaks at arbitrary intervals. Please use an appropriate colour bar – if these plots were made using Matplotlib, which they appear to have been, there are several available (see https://matplotlib.org/stable/users/explain/colors/colormaps.html). In addition, for the CO total column plots, the colour bar used is diverging which is inappropriate for displaying a continuous variable which is not a difference.

Line 364: ‘Andes’ rather than ‘Andean (mountain range)’ is sufficient.

Line 365: ‘Accumulates’.

Line 395: ‘Despite the peak of precipitation being…’, also there appears to be an incomplete citation here ‘(Grimm)’.

Table 3: The caption should explain why some of the numbers are in bold type. There is also a more general question here about whether short-term trends of <10 years are meaningful given interannual variability and the complex political environment in South America (which the authors describe well in this section from a fire perspective).

Figure 6: This figure would benefit from hatching/stippling to denote where the biases are statistically significant according to an appropriate test.

Line 509: ‘Differed’.

Line 515: ‘Has’, also ‘simulated’ rather than ‘estimated’.

Line 523: ‘Increased’ or ‘enhanced’, not ‘extenuated’ (this does not mean ‘extended’).

Figure 8: Should be ‘Spatio-temporal’.

Lines 591-592: There are words missing and therefore the sentence does not read correctly. ‘…landscape fragmentation, which represents both….and can lead to…fire suppression effects’.

Line 602: Remove ‘feature’.

Line 619: This sentence is incomplete: ‘Furthermore, agricultural expansion and landscape fragmentation.’. What about them?

Line 645: ‘TCCO’ (although I suggest removing this variable entirely).

Line 658: This should be ‘(broadleaf deciduous trees (BDT) and broadleaf evergreen tropical trees (BET-Tr))’.

Line 662: ‘Sensitivity’.

Line 663: ‘Small’ rather than ‘short’.

Line 664: ‘PFT’.

Line 664-665: Awkward phrasing. Try ‘Both improving PFT accuracy and incorporating representation of human land-use management, through variables such as land fragmentation, might help reduce biases’.

Line 677: ‘Cut’?

Line 677: It should be noted that this code is only accessible to people with a Met Office account; for me it returned a login page. If the underlying model code is not publicly accessible, a statement is required to explain why; additionally, there is no link provided to the model output which the journal also requires (or in the absence of this, a statement explaining why the data are not being made publicly available).

Line 678: ‘Are downloaded’; also, I suggest putting the dataset links in brackets.

Line 686: This doesn’t make sense: ‘Some assessments were done using the deforestation front for 2020 provided at and the ecoregion provided at’.

There are some typos in the reference list, and the DOIs are inconsistently stated with some references missing DOIs (e.g. Magahey and Kooperman 2023) and others having double entries e.g. line 872: https://doi.org/https://doi.org/10.1007/s10531-019-01720-z. Presumably these are artefacts introduced by reference management software but the reference lists that these produce should always be checked manually.