the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 24 Apr 2026
A Basin-Aware Global Framework for Computationally Efficient Surface Water Inundation Prediction
Abstract. Predicting surface water inundation at regional to global scales presents a fundamental tension: bespoke local models achieve high accuracy but require proprietary data and are difficult to scale, while globally trained systems offer broad coverage but demand substantial computational infrastructure and may lack flexibility for regional customization. We present the Basin-Aware Global Inundation Modeling framework (BAGIM), which addresses this gap by combining globally available, freely accessible datasets with basin-scale calibration to capture regional hydrological specificity. We evaluate six model architectures across eight geographically diverse basins to test three hypotheses: (1) that hydrologically meaningful feature engineering is more impactful than architectural complexity, (2) that basin-scale training mitigates regional biases in global datasets, and (3) that basin-aware models can generalize to extreme events beyond the training distribution. Our experiments demonstrate that tree-based ensembles (XGBoost, Random Forest) consistently outperform more complex deep learning architectures, achieving median F1 scores of approximately 0.5 against OPERA DSWx-S1 reference data, performance that approaches the inherent uncertainty ceiling imposed by disagreement among remote sensing products themselves in settings with small, shallow, and intermittent water bodies. We find that features commonly assumed essential for operational flood forecasting (i.e., coincident river-basin streamflow, Height Above Nearest Drainage, and elevation) are neither sufficient nor strictly necessary for reliable prediction, with well-engineered meteorological and terrain features achieving comparable performance without explicit streamflow inputs. This challenges a core assumption underlying many current operational flood forecasting systems. Cross-basin transfer experiments reveal limited transferability, reinforcing the importance of basin-aware calibration. Further, models trained exclusively on non-extreme events produce directionally correct predictions for out-of-sample extremes, though with conservative bias (higher precision, lower recall). We suggest that a design philosophy prioritizing feature engineering and regional calibration over architectural complexity enables accessible deployment without sacrificing predictive skill.
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Status: closed
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RC1: 'Comment on egusphere-2026-1527', Anonymous Referee #1, 03 Jun 2026
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AC1: 'Reply on RC1', Arik Tashie, 31 Jul 2026
We thank the referee for their rigorous review and helpful comments. Referee 1's comments prompt new analyses that will sharpen the physical interpretation of our results. Reviewer text is quoted in full below, followed by our responses and planned revisions.
COMMENT 1: "The training labels for inundation comes from OPERA DSWx-S1, which detects all open inland water on a given day without distinguishing flood inundation, and this is a major drawback in the workflow. Over a 14-month observation window, most positive-class pixels will be permanent and semi-permanent water bodies whose locations do not change (how the model can understand the seasonality?). Under this interpretation, the H3 experiment mainly indicates whether a model trained on surface water masks can predict flood inundation, and hence the observed pattern (precision increases, recall decreases) is then unsurprising: the model correctly identifies water that was present before, during, and after the flood (high precision in the channel) and misses floodplain inundation that did not exist in the training distribution. In my understanding, this could cause a huge class imbalance in wet to dry ratios. This analysis need to be rechecked and possibly rerun the model with proper justifications."
RESPONSE: We fully agree that the large class imbalance among perennially dry, perennially wet, and intermittently dry/wet parcels presents a challenge to this modeling framework. We do note, though, that predicting all open surface water, rather than flood-specific inundation, is a deliberate design decision: that is, we position BAGIM as a general surface-water extent modeling framework (floods, but also reservoirs, wetlands, and small and ephemeral water bodies), and H3 is intentionally an out-of-distribution stress test of that general model on extreme (out-of-sample) floods. Regarding seasonality, the model receives daily and antecedent (3-, 7-, and 14-day) meteorological forcings spanning a full annual cycle, so seasonal variation enters through physical drivers rather than through calendar features. And the wet/dry class imbalance is addressed via adaptive square-root subsampling (Sect. 2.4.2) and imbalance-robust metrics (MCC, PR-AUC; Sect. 2.4.3).
That said, the reviewer's underlying question (how much of the reported skill reflects memorization of persistent water versus a genuinely dynamic, forcing-responsive representation) is important and testable. We appreciate the reviewer's attention to this potential source of bias, which we propose to robustly assess via a new suite of tests. Specifically, rather than retraining against a different (i.e., exclusively intermittently dry/wet parcels, aka "flood pixels") target, which would change the framework's intended predictand, the revised manuscript will answer it directly with two new analyses: (i) quantification of label dynamics (per-pixel wet/dry variability across the period of record), together with model skill reported separately for intermittently wet/dry pixels (including for the STURM extreme events) which decomposes the precision-up/recall-down pattern into its persistent-water and newly-inundated components; and (ii) a new figure mapping modeled inundation extent under dry, typical (climatological), and 100-year flood forcing, demonstrating that predictions are forcing-responsive rather than static. Section 3.4 and the H3 discussion will be revised around these results.
COMMENT 2: "Authors also claimed that streamflow features are 'neither sufficient nor strictly necessary for reliable prediction' and positioned as a challenge to the operational streamflow-driven flood forecasting. However, the ERA5 meteorological forcings and HydroATLAS-derived catchment attributes remain in the feature set of the 'No Streamflow' configuration. Removing modeled streamflow therefore does not remove independent information from the model. Streamflow at a given location is a lagged, response to upstream rainfall and if the inundation model already has access to those rainfall, temperature, and catchment-attribute features, the model can learn the rainfall-runoff transformation internally. I would suggest the Authors should redo the experiment by removing the meteorological forcings and report the results or properly justify the claim."
RESPONSE: We fully agree with the mechanism the reviewer describes, and we apologize for the lack of clarity in the description of our feature family tests. Indeed, we explicitly argue (Sect. 3.2) that the model internalizes the rainfall-runoff transformation from well-engineered meteorological inputs. Our claim is architectural, not informational: a separately trained streamflow model is not a necessary component of the system, which removes a modeling stage, its cost, and its cascading error. We will revise the abstract, Sect. 3.2, and Conclusions to state this precisely. And we will run the suggested experiment (full static stack plus modeled streamflow with all meteorological forcings removed) completing the ablation over the two dynamic input families, with results reported in the Supplement. One point of clarification: HydroATLAS attributes are not in the inundation models' feature set (they feed only the LSTM-FiLM streamflow model, Sect. 2.2.1; being basin-scale, they would be near-constants within any per-basin training domain).
COMMENT 3: "It has been found that BAGIM models do not generalize across basins. To deploy BAGIM in a new basin, a user must need to retrain the model which needs extensive work (get OPERA DSWx-S1 observations, construct the full 30-band static feature stack, extract ERA5 forcings, run the LSTM-FiLM streamflow model, and perform cross validation etc.). By contrast, Google Flood Hub and GloFAS are trained once globally and deployed everywhere with effectively zero local setup. How do the Authors justify this claim?"
RESPONSE: We agree that the submitted manuscript text does not clearly differentiate BAGIM from existing global products such as Google Flood Hub and GloFAS, and we welcome the opportunity to clarify. First, those systems deliver fundamentally different products: Flood Hub provides riverine forecasts at gauge/virtual-gauge locations with largely pre-computed inundation maps, and GloFAS provides coarse-resolution streamflow and threshold exceedance; neither provides daily 30 m extent for all surface water (including reservoirs and small, fragmented, ephemeral bodies). Second, neither Google Flood Hub nor GloFAS natively supports local recalibration or third-party data integration. Third, the per-basin setup is a single automated pipeline requiring roughly 20-30 minutes per watershed on commodity CPU hardware (non-specialized), and the streamflow (LSTM-FiLM) model is trained once globally, never per basin — and per Comment 2, the streamflow model can be omitted entirely without substantially degrading predictive skill. Fourth, globally trained empirical models do not escape the transfer problem shown by H2 (53 of 56 scenarios degrade); in any specific basin they are uncalibrated models with locally unquantified error. BAGIM makes the calibration cost explicit, small, and local, and additionally provides locally quantified, held-out error estimates for every basin in which it is deployed. To make this differentiation explicit in the manuscript, we propose to add a Discussion paragraph with a capability and deployment-cost comparison table, positioning BAGIM as complementary to existing global systems.
Citation: https://doi.org/10.5194/egusphere-2026-1527-AC1
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AC1: 'Reply on RC1', Arik Tashie, 31 Jul 2026
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RC2: 'Comment on egusphere-2026-1527', Anonymous Referee #2, 20 Jul 2026
I think this paper does a very good job framing global context in hydrological modeling. I think that the authors are overall fair and transparent about their experiments and interpreting the results. The overall quality of the presentation is good. The tables and figures are appropriate and helpful.
I have several significant high level concerns
- The introduction narrative needs citations or even anecdotal evidence. I don’t generally disagree with the contents of the introduction but many of the paragraphs are claims without evidence.
- I suggest you delete H1 entirely from the paper. It is about feature engineering being more important than model architecture. Famously the 2009 paper “The Unreasonable Effectiveness of Data” spurred on tons of additional papers testing the same thing. There are myriad papers in hydrology and other fields that pit model architectures against each other. Anecdotally, I point you to the evolution of commercial LLM services who keep making their models take ever wider context windows and billions more parameters. Furthermore, I don’t think that your experiments to explore the hypothesis makes a proper and robust effort to samples the wide range of datasets or model architectures on the table. The results spend more time discussing how this hypothesis was proven by changing model architectures rather than increasing the volume of data and improving or expanding the feature engineering. That quickly becomes a combinatorial explosion to test.
- Hypothesis 2 and 3 have more scientific value than H1. However I’m not convinced that the experimental design actually constitute evidence for your hypothesis. I elaborate in the following point about the methods.
- About 10 pages, all of sections 2.1-2.4, is generally describing choices of datasets and routine machine learning data preprocessing steps. Only in section 2.4.4 does the manuscript begin to describe an experimental design. This balance needs to be inverted. The simpler portions of data preparation and model selection can be relegated to an appendix or trimmed. I think they are necessary and helpful explanations but they do not help another scientist recreate the work being presented or justify the experimental design. Section 3.5 for instance presents ensemble methods for using model results which could form the foundation of exploring H2 and H3 but instead it receives only a figure and 2 paragraphs.
Citation: https://doi.org/10.5194/egusphere-2026-1527-RC2 -
AC2: 'Reply on RC2', Arik Tashie, 31 Jul 2026
We thank the referee for their thoughtful comments. Referee 2's comments prompt clearer hypotheses and a more readable manuscript. Reviewer text is quoted in full below, followed by our responses and planned revisions.
POINT 1: "The introduction narrative needs citations or even anecdotal evidence. I don't generally disagree with the contents of the introduction but many of the paragraphs are claims without evidence."
RESPONSE: We agree and will revise the Introduction paragraph by paragraph so every substantive claim is supported. In particular, we have identified the currently uncited "practical gap" paragraph (bespoke-local versus global trade-off) and the characterization of how operational global systems link streamflow to inundation via static masks or topographic thresholds as passages requiring support; both will be fully cited in the revised manuscript.
POINT 2: "I suggest you delete H1 entirely from the paper. It is about feature engineering being more important than model architecture. Famously the 2009 paper 'The Unreasonable Effectiveness of Data' spurred on tons of additional papers testing the same thing. There are myriad papers in hydrology and other fields that pit model architectures against each other. Anecdotally, I point you to the evolution of commercial LLM services who keep making their models take ever wider context windows and billions more parameters. Furthermore, I don't think that your experiments to explore the hypothesis makes a proper and robust effort to samples the wide range of datasets or model architectures on the table. The results spend more time discussing how this hypothesis was proven by changing model architectures rather than increasing the volume of data and improving or expanding the feature engineering. That quickly becomes a combinatorial explosion to test."
RESPONSE: We agree that H1 as stated reads as a general claim about feature engineering versus architecture. This broad claim is neither novel nor is it testable without the combinatorial sweep the reviewer rightly calls intractable. Rather than deleting H1, though, we propose to reframe it as the narrower, operationally motivated hypothesis our experiments actually test: that a computationally lightweight, tractable architecture is a viable alternative (equally performant, not superior) to complex and expensive architectures for basin-scale inundation prediction in this label-limited regime, which enables deployment without the specialized and costly infrastructure that is generally only available to large, well-resourced organizations. We propose to retain the experiments for three reasons: they justify the model selection used in H2/H3, which Reviewer 1 asks us to extend; the comparison is controlled (six architectures, identical features, cross-validation, and tuning budgets), with claims that will be explicitly scoped to this domain and regime; and the evidence cited by the reviewer (Halevy et al., 2009; LLM scaling) characterizes data-abundant regimes, whereas inundation labels are structurally scarce (~14 months of SAR snapshots), representing a tabular, label-limited setting where tree ensembles are documented to remain competitive with deep architectures (Grinsztajn et al., 2022; Shwartz-Ziv and Armon, 2022). Our contribution is confirming that this latter point holds for inundation prediction and (more importantly) assessing the operational consequences thereof. We will also state explicitly that we do not sample the data-volume axis and that deep architectures may close the gap with longer records.
POINT 3: "Hypothesis 2 and 3 have more scientific value than H1. However I'm not convinced that the experimental design actually constitute evidence for your hypothesis. I elaborate in the following point about the methods."
RESPONSE: We agree there is a gap in the H2 design: cross-basin transfer and the Transfer Ensemble are proxies for, not instantiations of, a globally uniform model. We will add the direct test: a single pooled model trained on all eight basins under the identical protocol, evaluated in each basin against its basin-specific counterpart. The pooled model benefits from roughly eight times the training data, making this a conservative test of H2; results will be reported whichever direction they take. For H3, the new analyses described under RC1 Comment 1 (change-pixel-conditioned metrics and the dry/typical/100-year regime-contrast figure) convert the evaluation into an explicit test of dynamic generalization beyond the training distribution.
POINT 4: "About 10 pages, all of sections 2.1-2.4, is generally describing choices of datasets and routine machine learning data preprocessing steps. Only in section 2.4.4 does the manuscript begin to describe an experimental design. This balance needs to be inverted. The simpler portions of data preparation and model selection can be relegated to an appendix or trimmed. I think they are necessary and helpful explanations but they do not help another scientist recreate the work being presented or justify the experimental design. Section 3.5 for instance presents ensemble methods for using model results which could form the foundation of exploring H2 and H3 but instead it receives only a figure and 2 paragraphs."
RESPONSE: We agree and will restructure accordingly: detailed preprocessing (terrain-metric derivations, soil and LULC feature construction, ERA5 extraction) and the LSTM-FiLM streamflow details (Sect. 2.3) will be moved to appendices, with the data-sources table and a condensed summary retained in the main text. The experimental design (currently Sect. 2.4.4) will be expanded into a full Methods section stating, for each experiment (including those added in this revision), the hypothesis addressed, the variable isolated, the controls held fixed, and the supported inference. The ensemble construction will move into the Methods with an expanded Results discussion, explicitly connecting the Transfer Ensemble to H2 as the reviewer suggests.
Citation: https://doi.org/10.5194/egusphere-2026-1527-AC2
Status: closed
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RC1: 'Comment on egusphere-2026-1527', Anonymous Referee #1, 03 Jun 2026
In this work, a basin-aware machine learning framework (BAGIM) is developed that combines globally available open-data products with basin-scale calibration to predict daily binary surface water extent at 30 m resolution. The authors evaluate six ML architectures across eight geographically diverse basins, test three hypotheses (H1: feature engineering over architectural complexity; H2: basin-scale training and regional bias; H3: generalization to extreme events), and report that tree-based ensembles (XGBoost, Random Forest) consistently outperform more complex deep-learning architectures. They also found that these models have limited cross-basin transfer, and that streamflow inputs are not necessary for reliable prediction.
However, there are some major concerns that Authors need to address before acceptance
Recommendation: Major revisions.
Comment-1
The training labels for inundation comes from OPERA DSWx-S1, which detects all open inland water on a given day without distinguishing flood inundation, and this is a major drawback in the workflow. Over a 14-month observation window, most positive-class pixels will be permanent and semi-permanent water bodies whose locations do not change (how the model can understand the seasonality?). Under this interpretation, the H3 experiment mainly indicates whether a model trained on surface water masks can predict flood inundation, and hence the observed pattern (precision increases, recall decreases) is then unsurprising: the model correctly identifies water that was present before, during, and after the flood (high precision in the channel) and misses floodplain inundation that did not exist in the training distribution. In my understanding, this could cause a huge class imbalance in wet to dry ratios. This analysis need to be rechecked and possibly rerun the model with proper justifications.
Comment-2
Authors also claimed that streamflow features are “neither sufficient nor strictly necessary for reliable prediction” and positioned as a challenge to the operational streamflow-driven flood forecasting. However, the ERA5 meteorological forcings and HydroATLAS-derived catchment attributes remain in the feature set of the “No Streamflow” configuration. Removing modeled streamflow therefore does not remove independent information from the model. Streamflow at a given location is a lagged, response to upstream rainfall and if the inundation model already has access to those rainfall, temperature, and catchment-attribute features, the model can learn the rainfall-runoff transformation internally. I would suggest the Authors should redo the experiment by removing the meteorological forcings and report the results or properly justify the claim.
Comment-3
It has been found that BAGIM models do not generalize across basins. To deploy BAGIM in a new basin, a user must need to retrain the model which needs extensive work (get OPERA DSWx-S1 observations, construct the full 30-band static feature stack, extract ERA5 forcings, run the LSTM-FiLM streamflow model, and perform cross validation etc.). By contrast, Google Flood Hub and GloFAS are trained once globally and deployed everywhere with effectively zero local setup. How do the Authors justify this claim?
Citation: https://doi.org/10.5194/egusphere-2026-1527-RC1 -
AC1: 'Reply on RC1', Arik Tashie, 31 Jul 2026
We thank the referee for their rigorous review and helpful comments. Referee 1's comments prompt new analyses that will sharpen the physical interpretation of our results. Reviewer text is quoted in full below, followed by our responses and planned revisions.
COMMENT 1: "The training labels for inundation comes from OPERA DSWx-S1, which detects all open inland water on a given day without distinguishing flood inundation, and this is a major drawback in the workflow. Over a 14-month observation window, most positive-class pixels will be permanent and semi-permanent water bodies whose locations do not change (how the model can understand the seasonality?). Under this interpretation, the H3 experiment mainly indicates whether a model trained on surface water masks can predict flood inundation, and hence the observed pattern (precision increases, recall decreases) is then unsurprising: the model correctly identifies water that was present before, during, and after the flood (high precision in the channel) and misses floodplain inundation that did not exist in the training distribution. In my understanding, this could cause a huge class imbalance in wet to dry ratios. This analysis need to be rechecked and possibly rerun the model with proper justifications."
RESPONSE: We fully agree that the large class imbalance among perennially dry, perennially wet, and intermittently dry/wet parcels presents a challenge to this modeling framework. We do note, though, that predicting all open surface water, rather than flood-specific inundation, is a deliberate design decision: that is, we position BAGIM as a general surface-water extent modeling framework (floods, but also reservoirs, wetlands, and small and ephemeral water bodies), and H3 is intentionally an out-of-distribution stress test of that general model on extreme (out-of-sample) floods. Regarding seasonality, the model receives daily and antecedent (3-, 7-, and 14-day) meteorological forcings spanning a full annual cycle, so seasonal variation enters through physical drivers rather than through calendar features. And the wet/dry class imbalance is addressed via adaptive square-root subsampling (Sect. 2.4.2) and imbalance-robust metrics (MCC, PR-AUC; Sect. 2.4.3).
That said, the reviewer's underlying question (how much of the reported skill reflects memorization of persistent water versus a genuinely dynamic, forcing-responsive representation) is important and testable. We appreciate the reviewer's attention to this potential source of bias, which we propose to robustly assess via a new suite of tests. Specifically, rather than retraining against a different (i.e., exclusively intermittently dry/wet parcels, aka "flood pixels") target, which would change the framework's intended predictand, the revised manuscript will answer it directly with two new analyses: (i) quantification of label dynamics (per-pixel wet/dry variability across the period of record), together with model skill reported separately for intermittently wet/dry pixels (including for the STURM extreme events) which decomposes the precision-up/recall-down pattern into its persistent-water and newly-inundated components; and (ii) a new figure mapping modeled inundation extent under dry, typical (climatological), and 100-year flood forcing, demonstrating that predictions are forcing-responsive rather than static. Section 3.4 and the H3 discussion will be revised around these results.
COMMENT 2: "Authors also claimed that streamflow features are 'neither sufficient nor strictly necessary for reliable prediction' and positioned as a challenge to the operational streamflow-driven flood forecasting. However, the ERA5 meteorological forcings and HydroATLAS-derived catchment attributes remain in the feature set of the 'No Streamflow' configuration. Removing modeled streamflow therefore does not remove independent information from the model. Streamflow at a given location is a lagged, response to upstream rainfall and if the inundation model already has access to those rainfall, temperature, and catchment-attribute features, the model can learn the rainfall-runoff transformation internally. I would suggest the Authors should redo the experiment by removing the meteorological forcings and report the results or properly justify the claim."
RESPONSE: We fully agree with the mechanism the reviewer describes, and we apologize for the lack of clarity in the description of our feature family tests. Indeed, we explicitly argue (Sect. 3.2) that the model internalizes the rainfall-runoff transformation from well-engineered meteorological inputs. Our claim is architectural, not informational: a separately trained streamflow model is not a necessary component of the system, which removes a modeling stage, its cost, and its cascading error. We will revise the abstract, Sect. 3.2, and Conclusions to state this precisely. And we will run the suggested experiment (full static stack plus modeled streamflow with all meteorological forcings removed) completing the ablation over the two dynamic input families, with results reported in the Supplement. One point of clarification: HydroATLAS attributes are not in the inundation models' feature set (they feed only the LSTM-FiLM streamflow model, Sect. 2.2.1; being basin-scale, they would be near-constants within any per-basin training domain).
COMMENT 3: "It has been found that BAGIM models do not generalize across basins. To deploy BAGIM in a new basin, a user must need to retrain the model which needs extensive work (get OPERA DSWx-S1 observations, construct the full 30-band static feature stack, extract ERA5 forcings, run the LSTM-FiLM streamflow model, and perform cross validation etc.). By contrast, Google Flood Hub and GloFAS are trained once globally and deployed everywhere with effectively zero local setup. How do the Authors justify this claim?"
RESPONSE: We agree that the submitted manuscript text does not clearly differentiate BAGIM from existing global products such as Google Flood Hub and GloFAS, and we welcome the opportunity to clarify. First, those systems deliver fundamentally different products: Flood Hub provides riverine forecasts at gauge/virtual-gauge locations with largely pre-computed inundation maps, and GloFAS provides coarse-resolution streamflow and threshold exceedance; neither provides daily 30 m extent for all surface water (including reservoirs and small, fragmented, ephemeral bodies). Second, neither Google Flood Hub nor GloFAS natively supports local recalibration or third-party data integration. Third, the per-basin setup is a single automated pipeline requiring roughly 20-30 minutes per watershed on commodity CPU hardware (non-specialized), and the streamflow (LSTM-FiLM) model is trained once globally, never per basin — and per Comment 2, the streamflow model can be omitted entirely without substantially degrading predictive skill. Fourth, globally trained empirical models do not escape the transfer problem shown by H2 (53 of 56 scenarios degrade); in any specific basin they are uncalibrated models with locally unquantified error. BAGIM makes the calibration cost explicit, small, and local, and additionally provides locally quantified, held-out error estimates for every basin in which it is deployed. To make this differentiation explicit in the manuscript, we propose to add a Discussion paragraph with a capability and deployment-cost comparison table, positioning BAGIM as complementary to existing global systems.
Citation: https://doi.org/10.5194/egusphere-2026-1527-AC1
-
AC1: 'Reply on RC1', Arik Tashie, 31 Jul 2026
-
RC2: 'Comment on egusphere-2026-1527', Anonymous Referee #2, 20 Jul 2026
I think this paper does a very good job framing global context in hydrological modeling. I think that the authors are overall fair and transparent about their experiments and interpreting the results. The overall quality of the presentation is good. The tables and figures are appropriate and helpful.
I have several significant high level concerns
- The introduction narrative needs citations or even anecdotal evidence. I don’t generally disagree with the contents of the introduction but many of the paragraphs are claims without evidence.
- I suggest you delete H1 entirely from the paper. It is about feature engineering being more important than model architecture. Famously the 2009 paper “The Unreasonable Effectiveness of Data” spurred on tons of additional papers testing the same thing. There are myriad papers in hydrology and other fields that pit model architectures against each other. Anecdotally, I point you to the evolution of commercial LLM services who keep making their models take ever wider context windows and billions more parameters. Furthermore, I don’t think that your experiments to explore the hypothesis makes a proper and robust effort to samples the wide range of datasets or model architectures on the table. The results spend more time discussing how this hypothesis was proven by changing model architectures rather than increasing the volume of data and improving or expanding the feature engineering. That quickly becomes a combinatorial explosion to test.
- Hypothesis 2 and 3 have more scientific value than H1. However I’m not convinced that the experimental design actually constitute evidence for your hypothesis. I elaborate in the following point about the methods.
- About 10 pages, all of sections 2.1-2.4, is generally describing choices of datasets and routine machine learning data preprocessing steps. Only in section 2.4.4 does the manuscript begin to describe an experimental design. This balance needs to be inverted. The simpler portions of data preparation and model selection can be relegated to an appendix or trimmed. I think they are necessary and helpful explanations but they do not help another scientist recreate the work being presented or justify the experimental design. Section 3.5 for instance presents ensemble methods for using model results which could form the foundation of exploring H2 and H3 but instead it receives only a figure and 2 paragraphs.
Citation: https://doi.org/10.5194/egusphere-2026-1527-RC2 -
AC2: 'Reply on RC2', Arik Tashie, 31 Jul 2026
We thank the referee for their thoughtful comments. Referee 2's comments prompt clearer hypotheses and a more readable manuscript. Reviewer text is quoted in full below, followed by our responses and planned revisions.
POINT 1: "The introduction narrative needs citations or even anecdotal evidence. I don't generally disagree with the contents of the introduction but many of the paragraphs are claims without evidence."
RESPONSE: We agree and will revise the Introduction paragraph by paragraph so every substantive claim is supported. In particular, we have identified the currently uncited "practical gap" paragraph (bespoke-local versus global trade-off) and the characterization of how operational global systems link streamflow to inundation via static masks or topographic thresholds as passages requiring support; both will be fully cited in the revised manuscript.
POINT 2: "I suggest you delete H1 entirely from the paper. It is about feature engineering being more important than model architecture. Famously the 2009 paper 'The Unreasonable Effectiveness of Data' spurred on tons of additional papers testing the same thing. There are myriad papers in hydrology and other fields that pit model architectures against each other. Anecdotally, I point you to the evolution of commercial LLM services who keep making their models take ever wider context windows and billions more parameters. Furthermore, I don't think that your experiments to explore the hypothesis makes a proper and robust effort to samples the wide range of datasets or model architectures on the table. The results spend more time discussing how this hypothesis was proven by changing model architectures rather than increasing the volume of data and improving or expanding the feature engineering. That quickly becomes a combinatorial explosion to test."
RESPONSE: We agree that H1 as stated reads as a general claim about feature engineering versus architecture. This broad claim is neither novel nor is it testable without the combinatorial sweep the reviewer rightly calls intractable. Rather than deleting H1, though, we propose to reframe it as the narrower, operationally motivated hypothesis our experiments actually test: that a computationally lightweight, tractable architecture is a viable alternative (equally performant, not superior) to complex and expensive architectures for basin-scale inundation prediction in this label-limited regime, which enables deployment without the specialized and costly infrastructure that is generally only available to large, well-resourced organizations. We propose to retain the experiments for three reasons: they justify the model selection used in H2/H3, which Reviewer 1 asks us to extend; the comparison is controlled (six architectures, identical features, cross-validation, and tuning budgets), with claims that will be explicitly scoped to this domain and regime; and the evidence cited by the reviewer (Halevy et al., 2009; LLM scaling) characterizes data-abundant regimes, whereas inundation labels are structurally scarce (~14 months of SAR snapshots), representing a tabular, label-limited setting where tree ensembles are documented to remain competitive with deep architectures (Grinsztajn et al., 2022; Shwartz-Ziv and Armon, 2022). Our contribution is confirming that this latter point holds for inundation prediction and (more importantly) assessing the operational consequences thereof. We will also state explicitly that we do not sample the data-volume axis and that deep architectures may close the gap with longer records.
POINT 3: "Hypothesis 2 and 3 have more scientific value than H1. However I'm not convinced that the experimental design actually constitute evidence for your hypothesis. I elaborate in the following point about the methods."
RESPONSE: We agree there is a gap in the H2 design: cross-basin transfer and the Transfer Ensemble are proxies for, not instantiations of, a globally uniform model. We will add the direct test: a single pooled model trained on all eight basins under the identical protocol, evaluated in each basin against its basin-specific counterpart. The pooled model benefits from roughly eight times the training data, making this a conservative test of H2; results will be reported whichever direction they take. For H3, the new analyses described under RC1 Comment 1 (change-pixel-conditioned metrics and the dry/typical/100-year regime-contrast figure) convert the evaluation into an explicit test of dynamic generalization beyond the training distribution.
POINT 4: "About 10 pages, all of sections 2.1-2.4, is generally describing choices of datasets and routine machine learning data preprocessing steps. Only in section 2.4.4 does the manuscript begin to describe an experimental design. This balance needs to be inverted. The simpler portions of data preparation and model selection can be relegated to an appendix or trimmed. I think they are necessary and helpful explanations but they do not help another scientist recreate the work being presented or justify the experimental design. Section 3.5 for instance presents ensemble methods for using model results which could form the foundation of exploring H2 and H3 but instead it receives only a figure and 2 paragraphs."
RESPONSE: We agree and will restructure accordingly: detailed preprocessing (terrain-metric derivations, soil and LULC feature construction, ERA5 extraction) and the LSTM-FiLM streamflow details (Sect. 2.3) will be moved to appendices, with the data-sources table and a condensed summary retained in the main text. The experimental design (currently Sect. 2.4.4) will be expanded into a full Methods section stating, for each experiment (including those added in this revision), the hypothesis addressed, the variable isolated, the controls held fixed, and the supported inference. The ensemble construction will move into the Methods with an expanded Results discussion, explicitly connecting the Transfer Ensemble to H2 as the reviewer suggests.
Citation: https://doi.org/10.5194/egusphere-2026-1527-AC2
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- 1
In this work, a basin-aware machine learning framework (BAGIM) is developed that combines globally available open-data products with basin-scale calibration to predict daily binary surface water extent at 30 m resolution. The authors evaluate six ML architectures across eight geographically diverse basins, test three hypotheses (H1: feature engineering over architectural complexity; H2: basin-scale training and regional bias; H3: generalization to extreme events), and report that tree-based ensembles (XGBoost, Random Forest) consistently outperform more complex deep-learning architectures. They also found that these models have limited cross-basin transfer, and that streamflow inputs are not necessary for reliable prediction.
However, there are some major concerns that Authors need to address before acceptance
Recommendation: Major revisions.
Comment-1
The training labels for inundation comes from OPERA DSWx-S1, which detects all open inland water on a given day without distinguishing flood inundation, and this is a major drawback in the workflow. Over a 14-month observation window, most positive-class pixels will be permanent and semi-permanent water bodies whose locations do not change (how the model can understand the seasonality?). Under this interpretation, the H3 experiment mainly indicates whether a model trained on surface water masks can predict flood inundation, and hence the observed pattern (precision increases, recall decreases) is then unsurprising: the model correctly identifies water that was present before, during, and after the flood (high precision in the channel) and misses floodplain inundation that did not exist in the training distribution. In my understanding, this could cause a huge class imbalance in wet to dry ratios. This analysis need to be rechecked and possibly rerun the model with proper justifications.
Comment-2
Authors also claimed that streamflow features are “neither sufficient nor strictly necessary for reliable prediction” and positioned as a challenge to the operational streamflow-driven flood forecasting. However, the ERA5 meteorological forcings and HydroATLAS-derived catchment attributes remain in the feature set of the “No Streamflow” configuration. Removing modeled streamflow therefore does not remove independent information from the model. Streamflow at a given location is a lagged, response to upstream rainfall and if the inundation model already has access to those rainfall, temperature, and catchment-attribute features, the model can learn the rainfall-runoff transformation internally. I would suggest the Authors should redo the experiment by removing the meteorological forcings and report the results or properly justify the claim.
Comment-3
It has been found that BAGIM models do not generalize across basins. To deploy BAGIM in a new basin, a user must need to retrain the model which needs extensive work (get OPERA DSWx-S1 observations, construct the full 30-band static feature stack, extract ERA5 forcings, run the LSTM-FiLM streamflow model, and perform cross validation etc.). By contrast, Google Flood Hub and GloFAS are trained once globally and deployed everywhere with effectively zero local setup. How do the Authors justify this claim?