Dear Dr. Sato,

Thank you for submitting your manuscript to PLOS ONE. After careful consideration, we feel that it has merit but does not fully meet PLOS ONE’s publication criteria as it currently stands. Therefore, we invite you to submit a revised version of the manuscript that addresses the points raised during the review process.

Please address several comments raised by the reviewers. Also, please address these issues: a). random forests classification and overfitting and hyperparameter tuning issues; b). cross validation issues; c). use of very few grid cells from the global datasets: d). providing additional accuracy metrics; e). poor predictions for some of the classes in the model; f). figure modifications, etc.

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Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Author

1. Is the manuscript technically sound, and do the data support the conclusions?

Reviewer #1: Yes

Reviewer #2: No

Reviewer #3: Partly

Reviewer #4: Yes

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2. Has the statistical analysis been performed appropriately and rigorously? -->?>

Reviewer #1: Yes

Reviewer #2: No

Reviewer #3: N/A

Reviewer #4: Yes

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3. Have the authors made all data underlying the findings in their manuscript fully available??>

The PLOS Data policy

Reviewer #1: Yes

Reviewer #2: Yes

Reviewer #3: Yes

Reviewer #4: Yes

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4. Is the manuscript presented in an intelligible fashion and written in standard English??>

Reviewer #1: Yes

Reviewer #2: Yes

Reviewer #3: No

Reviewer #4: Yes

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Reviewer #1:  Major Revisions

The manuscript attempts to apply different machine learning techniques to classify biome under present and future climate scenarios. This research topic is relevant and holds significant potential for impactful insights. Below are some suggestions which can help improve the clarity and rigor of the manuscript.

Figures

1. For the figures 1, 2, 3, 4, and 5, please increase DPI. Use at least 300 for Image Exports. In the current form, the legend is unable to read.

2. Please include a north arrow and scale bar in the spatial maps.

Tables

1. In Table 1, please consider introducing the abbreviation for the units - C or mm - before the first appearance in the table.

2. In Table 2, the abbreviations must be redefined in the Table caption or as a footnote to provide a better readability.

3. The tables 3, 4, and 5 can be combined into a single big table to reduce the visual clutter as the three tables share a same input variable combination and 4 models. Perhaps even, using a color-coding schema for train, test and overfitting accuracies could help? This could also reduce the overall number of figures and tables.

4. The same as above can be said for Table 6 and 7

Typos

1. Page 19, Line 311: “to an RF” must be changed to “to the RF”

2. The term “pseudo-predicting” must be changed to “pseudo-predictive”. The latter seems more reasonable

Suggestions and Questions

1. While the authors acknowledge the issue of overfitting in RF, the conclusion refers to it as ‘robust’. Given that RF achieves 100 percent training accuracy and significant overfitting, calling it robust appears inconsistent with the results. It maybe helps to rephrase this statement altogether to avoid confusion.

2. I believe the authors should have done hyper parameter tuning, even if it is at minimal, for a more even model comparison.

3. Could the authors clarify if the image conversion from climatic variables performed only to train CNN or, to even test and predict? Could the authors also clarify why they chose the method from Sato and Ise? Are there any advantages to it over other methods?

4. The study lacks a feature sensitivity analysis. Thus, it is not clear which climate variables are driving predictions. If the authors note this addition, it would be helping the study.

5. The authors trained using the climate data from years 1970-2000 and then tried to project for years 2061-2080. Could the authors provide details on the intermediatory validation between the years 2000-2060 and account for this gap? This would also help to assess the model’s temporal generalization.

Reviewer #2:  The manuscript is relevant and shows an interesting approach. I have some suggestions for improvement:

- The first sentence of the abstract was too direct. I suggest making it more explanatory.

- In the abstract, I suggest including the accuracy value mentioned so that the phrases “marginally decreased model accuracy” and “improved accuracy slightly” are not vague. How many % of accuracy?

- The last sentence of the abstract could be left in a way that recommends not using extreme climate data. Using “should not” ends up establishing a rule, which is complicated considering only one or a few studies.

- The introduction could be more detailed and show other examples on the topic. I suggest increasing it a little and referencing studies that have already been done.

- Usually, the largest amount of data is intended for training. Why was only 25% used in this study? Using little in training could be the reason for overfitting in the end. Despite the justification and that there were tests for using 25%, have other studies adopted this methodology? Is it reproducible?

- Were there no tests performed with changes to the algorithm parameters? The use of default parameters is generally not recommended for all analyses and all algorithms. It is interesting to test whether there was any change in performance and to find the hyperparameters. It is said that default was used, but cross validation and other techniques help to ensure that the models are reliable.

- The figures and map captions are blurry. I suggest making them clearer.

- When you say that "while CNN employed graphically converted climate data, preventing a conclusive determination of the superior approach" you limit the comparison with other algorithms and it would be interesting to better justify why you continued with the 4 algorithms.

- The conclusion could be more explanatory, it is very direct.

Reviewer #3: Overview of the Study

This study explores the use of machine learning (ML) models to simulate and project global Potential Natural Vegetation (PNV). The models were trained on baseline climate data from 1970 to 2000 and used to predict future vegetation distributions for the period 2061–2080 under the RCP 8.5 scenario from the IPCC's Coupled Model Intercomparison Project Phase 5 (CMIP5). Four ML algorithms—Random Forest (RF), Support Vector Machine (SVM), Naïve Bayes (NB), and Convolutional Neural Network (CNN)—were tested across six configurations of four climate-related datasets, yielding 24 distinct model scenarios. These datasets included averaged monthly temperature and precipitation, averaged monthly climate indices, climate extreme indices, and a reduced version of the climate extremes dataset with six variables excluded. The author concludes that CNN achieved the best performance. The inclusion of climate indices slightly decreased model accuracy, whereas the use of climate extreme indices led to a slight improvement.

Writing and Organization

Although the manuscript has been reviewed by two native English speakers and is grammatically sound, it lacks logical structure and clarity. The flow of ideas is often difficult to follow, making it challenging for readers to grasp the author's main points. It is recommended that the manuscript be reviewed by a scientific copy editor who can improve coherence, enhance conceptual clarity, and ensure that the writing is logically organized and accessible.

Machine Learning Methodology

The methodological choices in the study raise several concerns. The global dataset consists of 52,297 grid cells, yet only 25% of these were used for training while the remaining 75% were allocated for testing. This deviates from standard ML practice, where typically 70–80% of data is reserved for training. The author repeated this process 10 times to obtain average results, but no explanation is provided for the reversed training-test split or the repetition strategy.

Additionally, the confusion matrices presented in Tables S2 to S4 lack important context. It is unclear whether they correspond to training, test, or full datasets. Examination suggests they were computed on the full dataset, as the total number of records in the matrices is 52,303, which does not match the documented dataset size of 52,297. Furthermore, the matrices are mislabeled, with both rows and columns titled "Predicted Class," without identifying the true labels, which undermines interpretability.

Evaluation Metrics and Imbalanced Data

The manuscript reports only overall accuracy as the evaluation metric across the 24 model configurations. While this metric is commonly used, it is insufficient for imbalanced datasets such as this one, which involves 13 PNV classes based on the International Geosphere-Biosphere Programme classification. Overall accuracy can obscure poor performance on minority classes and misrepresent model effectiveness. To address this issue, the author should include additional performance metrics such as class-level precision, recall, and F1 scores, as well as aggregated measures like Cohen's Kappa and metrics such as the Area Under the ROC Curve (AUC-ROC). These metrics would provide a more robust and informative comparison of model performance. The use of techniques to address class imbalance, such as SMOTE (Synthetic Minority Over-sampling Technique), is also strongly recommended.

Abstract and Supporting Materials

The abstract is not sufficiently informative. It mentions only two of the four ML algorithms and omits any reference to the comparison of the 24 model-dataset configurations. As a result, readers must progress through a significant portion of the manuscript to understand the scope of the study. The abstract should be revised to clearly summarize the methodological design and key findings.

Other Issues

Several minor but important issues were noted. The figures lack adequate resolution, and Figures 6 through 9 are referenced in line 282 but are missing from the manuscript. The citation style is inconsistent; in some cases, the first two authors are named followed by a reference number, even when more than three authors are involved. Long URLs and access dates appear in the body of the text and should instead be properly formatted as references, in accordance with journal guidelines. There is also an inconsistency in the definition of the future projection period: while the study defines this period as 2061–2080, Supplementary Figures S8 to S11 appear to show data for the year 2100. This discrepancy requires clarification. Finally, the author does not justify the choice of CMIP5 data over the more recent CMIP6 datasets, which are increasingly favored in contemporary climate studies. Providing a rationale for this choice is essential.

Reviewer #4: The author presents a study on modelling biome distribution at global scale using machine learning. The performances of four machine-learning algorithms driven by six combinations of four current climate datasets are compared. The performances of each of the 24 resulting models (i.e., algorithm-climate dataset combinations) are assessed based on its ability to reproduce the current observation-based potential vegetation map produced by Beigaite et al. (2022) with limited overfitting, and its consistency with other models when predicting future potential natural vegetation under a Representative Concentration Pathway 8.5 (RCP8.5) climate scenario. Based on such comparisons of model performances, the author recommends using the CNN algorithm from Sato and Ise (2022) and excluding extreme climate data when building models to predict global-scale biome distribution.

I believe this is an interesting and timely study that aims to clarify and compare the current potential of different machine learning methods for predicting vegetation distribution on a global scale. Overall, while I think the study has the potential to be published, several major revisions are required. I find that the manuscript would particularly benefit from (1) a clarification of the research question, (2) a better contextualisation, and (3) a better description and justification for the methods, products, and programs used. I also find that the manuscript tends to rely too little on the literature, which leads to a certain amount of unsourced methodological choices and statements.

Major comments

(1) Stating a clear question along with some hypotheses from start would improve the readability. Several questions are addressed, and I'm having trouble identifying the real focus: is the priority to identify the best-performing ML algorithm, to assess the value of not summarising climate data into climate indices, to study the potential of incorporating extreme climate indices, or the potential of machine learning to predict the future distribution of biomes in the context of climate change?

(2) To better emphasise the value of the issues addressed in this study, I would find it helpful to describe from the start the general approach of machine learning and the interest of using it to predict the distribution of vegetation. In particular, what are the advantages of using machine learning compared with other existing approaches such as other correlative models or more process-based models. For example, Beigaite et al. (2022) and Bonannella et al. (2023) provide some details in their introductions that could be mentioned here. It is suggested on L40-52 that the main advantage of machine learning is the ability to use a larger amount of climate data, but it is not stated how this gives the machine learning an advantage in terms of its performance over other approaches. In general, I find it difficult to identify use cases for such models, given that biome/land-cover maps derived from satellite observations seem more relevant for mapping current distribution, and that the present manuscript demonstrates the difficulties of such models for predicting future vegetation distribution on a global scale. This point requires further attention and justification.

Bonannella, C., T. Hengl, L. Parente, and S. de Bruin. 2023. Biomes of the world under climate change scenarios: increasing aridity and higher temperatures lead to significant shifts in natural vegetation. PeerJ 11:e15593.

(3) Most of the products and programs used are treated as “black boxes” (machine learning algorithms and their default parameters, the potential natural vegetation map, climate data). Generally, little or nothing is said about the data and methods used to construct and validate them, the assumptions associated with them and the reasons for selecting them for this study. I find that this blurs the implications and conclusions of this study.

(4) The manuscript would benefit from a better description of the fundamental similarities and differences between the four machine learning approaches compared in this study, and the hypotheses associated with them. Hengl et al. (2018) included other machine learning algorithms in the comparison (from Friedman 2002, and Venables and Ripley 2002). Why choose to compare these four in particular? So far, although some specific aspects are being discussed, the algorithms generally appear to be black boxes and it is difficult to understand the origin of the differences observed. Before drawing general conclusions, it would be interesting to detail, at least in the form of hypotheses, the potential reasons why a model outperforms another, and what does it mean for the associated sets of data and assumptions.

Friedman, J. H. 2002. Stochastic gradient boosting. Computational Statistics & Data Analysis 38:367–378.

Venables, W. N., and B. D. Ripley. 2002. Modern applied statistics with S (Fourth Edition). New York: Springer-Verlag.

(5) The performances of the models are compared against their ability to predict the PNV map of Beigaite et al. (2022) which is itself derived from IGBP-MODIS from Friedl et al. (2010). The reasons for this choice are not given, although there are many other biome maps and classifications with numerous differences (reviewed for example in Mucina 2019, Beierkuhnlein and Fischer 2021, Hunter et al. 2021, Fischer et al. 2022, Champreux et al. 2024). After reading the manuscript, the potential effects of the choice of this product on the results and conclusions remain unclear.

Beierkuhnlein, C., and J.-C. Fischer. 2021. Global biomes and ecozones – Conceptual and spatial communalities and discrepancies. Erdkunde 75:249–270.

Champreux, A., F. Saltré, W. Traylor, T. Hickler, and C. J. A. Bradshaw. 2024. How to map biomes: Quantitative comparison and review of biome-mapping methods. Ecological Monographs 94:e1615.

Fischer, J.-C., A. Walentowitz, and C. Beierkuhnlein. 2022. The biome inventory – Standardizing global biogeographical land units. Global Ecology and Biogeography 31:2172–2183.

Hunter, J., S. Franklin, S. Luxton, and J. Loidi. 2021. Terrestrial biomes: a conceptual review. Vegetation Classification and Survey 2:73–85.

Mucina, L. 2019. Biome: evolution of a crucial ecological and biogeographical concept. New Phytologist 222:97–114.

(6) The unequal spatial coverage of the different biomes does not appear to be considered in the manuscript. The model performances are assessed via the percentage of correct answers. Because of its simplicity, such a measure seems to facilitate interpretation. However, it does not consider the variability of the areas covered by the different biomes. The choice of this metric over other common map comparison metrics such as Cohen’s kappa (Cohen 1960, Monserud and Leemans 1992) or the quantity-and-allocation agreement (Pontius and Millones 2011) thus requires better justification. It also seems obvious to me that the models should tend to better predict the most extensive biomes on a global scale since the models necessarily receive more data on them during the training phase. This is perhaps one of the potential reasons for the poor performance of the models in predicting the “Wetland” and “Closed Shrubland” biomes as stated on L236-244, respectively representing 0.5 and 0.2 % of the grid cells according to S1 table. The differences observed in future predictions are also likely to be affected by this unequal distribution of biomes. While the poor prediction of biomes covering smaller total areas globally affects current predictions less, their potential expansion in the future is likely to be poorly captured and to mechanically increase the disparities among models.

Cohen, J. 1960. A Coefficient of Agreement for Nominal Scales. Educational and Psychological Measurement 20:37–46.

Monserud, R. A., and R. Leemans. 1992. Comparing global vegetation maps with the Kappa statistic. Ecological Modelling 62:275–293.

Pontius, R. G., Jr, and M. Millones. 2011. Death to Kappa: birth of quantity disagreement and allocation disagreement for accuracy assessment. International Journal of Remote Sensing 32:4407–4429.

Minor comments

(7) L18. I would find it helpful to mention the four machine learning algorithms compared in the abstract.

(8) L40. “To date, many methods have been proposed to model biome distributions” Sato and Ise (2022) is cited here to support this statement, but also citing other sources reviewing the various methods to model biome distributions in greater details would be more appropriate. Generally, the statements in this paragraph should refer more to existing literature.

(9) L84-85. I wonder why eliminating only grid cells with 100 % human activity. Keeping in the analysis other highly impacted areas could possibly strongly affect the outputs. For example, Champreux et al. (2024) suggested that human activities could cause disagreement among biome maps including among PNV maps. Anyway, providing the percentage of grid cells that were eliminated due to the “100 % human activity” criteria would be helpful.

(10) L130-140. The models are trained with current, observation-based climate datasets but future predictions are made with simulated data that are associated with more uncertainties. Although these methodological differences are obviously unavoidable, I wonder whether they are likely to bias the assessment of model performances in future predictions. For example, it is not stated if the variables used have a standard definition that is common to both current and future datasets, or if some equivalencies have been performed.

(11) L134-135. “The Representative Concentration Pathway (RCP) 8.5 was the only used.” The choice of this single scenario should be justified.

(12) L144. Reference for CNN (Sato and Ise, 2022) is missing.

(13) L150-151. The author state “Simplicity was maintained and potential overfitting was mitigated by using the default settings in these commands”. This statement needs to be better justified.

(14) L154-158. This statement needs to be associated with supporting literature.

(15) L181. While I understand that model robustness was assessed based on the consistency among models for future predictions, this part of the analysis is not described in the method section, except for the presentation of the BIOCLIM data on L130-140. Describing it in the “Data analysis” section would be appropriate.

(16) L190. It is unclear if the selected value of 25% corresponds to standards of the discipline or was decided due to other reasons. Justifying it is important as it probably impacts the differences in overfitting scores of the models in the end, especially considering the 100% training accuracy of the RF models mentioned on L256-257.

(17) L199-200. “precisely” should be defined, as no decision threshold was provided in the method section.

(18) L204-205. “all grids at the same latitude were assigned the most frequent PNV at that latitude” This statement is unclear.

(19) L242. I guess that “The incorrectly identified biomes” is a typo that should be replaced with “The incorrectly identified grid cells”.

(20) L298-301. “Default parameter settings were used for all methods adopted in this study, and the models except the CNN were trained with climate data, while CNN employed graphically converted climate data, preventing a conclusive determination of the superior approach.” The implications of this methodological difference are unclear. It would be interesting to elaborate a bit more on this.

(21) Did Hengl et al. (2018) consider this overfitting issue with the RF algorithm?

(22) L322-325. If this statement means that the RF model is still showing strong overfitting despite these considerations, this calls into question the recommendations of Fourcade et al. (2018) and deserves to be discussed.

(23) L335-338. The consistency among future predictions is considered here as a proxy of model robustness. However, it also highlights the weaknesses of the machine learning algorithms for predicting future biome distributions where extremes are supposed to become more frequent and unprecedented. This point is discussed in the subsequent paragraphs, but the use of the consistency metric to assess model robustness is not questioned.

(24) L351-353. This is a rather strong statement justifying the use of machine learning over DGVMs for future biome map predictions. The statement is only supported here by citing Pugh et al. (2020). However, while Pugh et al. (2020) did compare several DGVMs and show several output and mechanism discrepancies, the study did not focus on predicting biome distribution, and did not provide such a conclusion.

(25) L364-367. This statement may be helpful in the introduction section to justify testing the incorporation of extreme climate variables for predictions at larger spatial scales (here biomes).

(26) L383-384. “thus, the CNN model is preferable”. This conclusion seems paradoxical given the earlier claim suggesting that CNN's performance is difficult to compare with that of other models, on L299-301: “the models except the CNN were trained with climate data, while CNN employed graphically converted climate data, preventing a conclusive determination of the superior approach.”

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Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Author

Reviewer #1: All comments have been addressed

Reviewer #4: All comments have been addressed

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2. Is the manuscript technically sound, and do the data support the conclusions??>

Reviewer #1: Yes

Reviewer #4: Yes

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3. Has the statistical analysis been performed appropriately and rigorously? -->?>

Reviewer #1: Yes

Reviewer #4: Yes

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4. Have the authors made all data underlying the findings in their manuscript fully available??>

The PLOS Data policy

Reviewer #1: Yes

Reviewer #4: Yes

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5. Is the manuscript presented in an intelligible fashion and written in standard English??>

Reviewer #1: Yes

Reviewer #4: Yes

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Reviewer #1: I thank the author for addressing my previous comments, and I am satisfied with the responses. The figures and tables have been improved, and the manuscript is now clearer and sound. I recommend acceptance.

Reviewer #4: The author presents a study on modelling biome distribution at global scale using machine learning under present and future climate scenarios. This is the second time I read the manuscript, which has been largely revised, greatly improving its quality compared to the previous version. The author has made an effort to respond carefully to all comments. In particular, the overall research questions are stated more clearly and most of the methodological choices are now better justified.

I only have a few minor comments :

- L86-88. I still question the relevance of retaining in the analysis grid cells that are highly impacted by human activities but do not reach 100%. The manuscript states that "grid cells partially affected by human activity were retained, on the assumption that the relative proportions of natural vegetation remain stable despite these changes. However, it has been shown that PNV maps disagree when human activities are high, suggesting that the proportion of remaining natural vegetation is not sufficiently informative in these grid cells. I therefore find the justification insufficient.

- L93-94. While the manuscript explains the importance of using a PNV map over maps derived from satellite imagery, and describes the product used, the choice of this specific PNV map for this study over others is insufficiently justified. The statement « this dataset was selected because it is particularly well suited for global climate-vegetation modeling » is not associated to any argument.

- L352-366. The paragraph justifying the choice of these four specific ML algorithms and explaining their differences appears in the Discussion section. As it highlights one of the strengths of the study and illustrates well how the manuscript adresses the overall research questions, it would be more appropriate in the ‘Methods’ section under ‘Machine learning algorithms’.

- L392-402. The manuscript recommends not including extreme climate data since it reduces robustness (here, consistency among models) under forecast climate conditions. However, the differences observed in predictions of the future state of vegetation also make it possible to define a universe of possibilities and therefore seem rather interesting. The fact that this extreme climate data improves test accuracy, even slightly, makes this observation even more interesting. The possibility that only one of these models accurately predicts the response of biome distribution to climate change remains plausible, although unprovable. The choice of whether to include or exclude this data therefore seems to me to depend on the research question, and would thus benefit from more discussion.

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Reviewer #1: No

Reviewer #4: No

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Predicting dominant terrestrial biomes at a global scale using machine learning algorithms, climate variable indices, and extreme event indices

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Dear Dr. Sato,

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