the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 12 May 2026
Reducing False Alarms in Small-Scale Slope Early Warning Systems via Deep Learning-Driven Asynchronous Displacement and Rainfall Data Fusion
Abstract. Real-time crackmeter-based warning systems for rainfall-induced small-scale slope failures suffer from prohibitively high false alarm rates. Across diverse geological settings, existing approaches relying on fixed thresholds or isolated rainfall–displacement relationships are highly sensitive to noise, lacking the robustness to reliably distinguish genuine deformation signals from spurious measurements. To address this operational bottleneck, this study reframes the early warning paradigm from a traditional fixed-threshold alerting process reliant on manual discrimination to an automated alert truth verification problem, proposing a real-time binary classification framework to isolate true early warnings from sensor-triggered false alarms. Utilizing a multi-source dataset of crackmeter displacement and rainfall measurements from diverse monitored slopes in Fujian Province, China, all true early warning instances were rigorously calibrated via field investigations. A patch-based dual-branch temporally-aware Transformer model was developed to explicitly address asynchronous multi-rate data fusion, strict temporal causality between rainfall and displacement, and stringent real-time decision constraints. By simultaneously capturing long-term rainfall-displacement interactions and high-resolution displacement dynamics, the model outperforms competitive baselines, achieving a precision of 90.91 %, a recall of 93.53 %, and an F2-score of 92.99 % in identifying true early warnings. Interpretability analysis reveals the model’s decisions are primarily driven by localized displacement trends and relative rainfall intensity, aligning with expert judgment. The proposed framework significantly curtails false alarms without compromising reliability, acting as a robust decision-support layer to enhance automated slope hazard monitoring. Future work will fuse additional sensor types to suppress false alarms via cross-validation of multi-physical responses.
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Status: open (until 06 Aug 2026)
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RC1: 'Comment on egusphere-2026-2352', Anonymous Referee #1, 21 May 2026
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RC2: 'Referee comment on egusphere-2026-2352', Anonymous Referee #2, 09 Jul 2026
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General Assessment
This manuscript proposes a dual-branch Transformer model (PatchDC) that reframes crackmeter alert validation as a binary classification problem ("true early warning" vs. "false alarm"), fusing asynchronous displacement and rainfall data. The operational motivation is well documented (a reported false-alarm rate below 0.03% over five years), and the proposed architecture — causal attention respecting the physical precedence of rainfall over displacement, and a hybrid fusion mechanism for correlated variables — is reasonably justified and convincingly validated through a well-designed ablation study. The interpretability analysis, and especially the dedicated failure-case section (Section 6.4), reflect a level of scientific transparency that is uncommon in this type of applied study.
However, the manuscript does not allow a full assessment of the internal validity of some of the reported results. The main concern relates to the construction of the positive dataset: expanding the 93 field-confirmed events to 255 samples by adding temporally adjacent points raises a circularity issue that is not discussed. A related concern involves the risk of information leakage through several normalisation steps computed "across the dataset", without the exact scope (training set only, or training+test combined) being specified. Both issues bear directly on the reliability of the performance metrics highlighted in the abstract and should be clarified before publication.
The manuscript is scientifically sound and likely publishable after revision. The comments below are intended to help the authors strengthen the internal validity of their results and the clarity of their evaluation protocol.
Major Comments
Comment 1 — Risk of circularity in the construction of the positive dataset. The initial number of field-confirmed true early warnings was only 93 (l. 199-200). To reach 255 samples, the authors added points temporally adjacent to these confirmed events, validated through a triple-blind review by three experts (l. 204-207). This procedure raises an important question that is not addressed: to what extent are these additional points independent of the original events in terms of signal (RDS, HMD)? If they share the same underlying displacement dynamics — which is plausible, since they were selected for their temporal proximity — the model may be learning an "episode signature" rather than generic early-detection features. Sensor-level isolation between training and test sets (l. 208-211) limits direct leakage but does not resolve this intra-episode homogeneity risk. If feasible, a sensitivity analysis training/evaluating the model on the original 93 events only would help demonstrate robustness.
Comment 2 — Ambiguous scope of global normalisation statistics. Several preprocessing steps rely on values computed "across the dataset": the four derived statistical features (IQR, ADM) are normalised by their "collective maximum value across the dataset" (l. 244-245), and RMR uses a global maximum across all stations as well as a regional five-year maximum (l. 265, 270). The text does not specify whether these maxima are computed on the training set alone or on the combined training+test set. In the latter case, this would constitute a minor but real information leak into the test set. Explicitly clarifying this point, and reformulating the pipeline to ensure these statistics are computed exclusively from training data (per cross-validation fold), would meaningfully strengthen the credibility of the results.
Comment 3 — Inconsistency between the two modes of reporting results. Section 5 selects the median run by recall among the five repetitions as the "representative" result (precision 90.91%, recall 93.53%, F2 92.99%), whereas Table 5 reports the mean ± standard deviation over 25 runs (precision 89.24±2.43%, recall 93.38±0.95%, F2 92.50±0.49%). These two sets of figures are close but not identical, and the use of two different reporting conventions in two places in the manuscript is not justified. The authors should harmonise their presentation, or otherwise clearly explain why each metric is used where it appears.
Comment 4 — Sampling uncertainty likely underestimated for the positive class. The test set contains only 139 "true early warning" samples (Table 4; confirmed by the confusion matrix: 130 TP + 9 FN). At this scale, a single additional misclassified sample shifts recall by roughly 0.7 percentage points. The inter-run standard deviation currently reported (Table 5) captures training-related variance, but not the sampling uncertainty inherent to a test set of this size. A bootstrap confidence interval on the reported metrics would give a more complete picture of their statistical reliability.
Comment 5 — No significance testing between competing models. The gaps between PatchDC and the best competitor (PatchTST) are sometimes small relative to the reported standard deviations — particularly for recall (93.38±0.95% vs. 92.95±1.24%, a gap of 0.43 points for standard deviations of comparable magnitude, Table 5). Without a paired statistical test (e.g., a t-test or Wilcoxon test across the 25 runs), this recall advantage could well be training noise rather than a genuine improvement, even though the precision gap (3.62 points) looks more robust.
Comment 6 — Geographic scope and generalisability insufficiently foregrounded. The authors acknowledge in the conclusion (Section 7) that the model has only been validated in a homogeneous geological and climatic context (Fujian Province, rainfall-triggered events exclusively). This is honestly stated, but it only surfaces at the very end of the manuscript; it should be flagged as early as the abstract and introduction so readers don't over-generalise, especially given that only 52 of the 429 sensors actually provided the true alerts used for training — a fairly narrow base of geological sites.
Minor Comments
Comment 7 — Typographical error. l. 642: "moder ate" should read "moderate".
Comment 8 — Striking figure insufficiently detailed. The 0.03% rate cited in the introduction (l. 132-134) is striking but presented without methodological detail on the exact period covered or the operational definition of "validated". A supplementary table would strengthen the credibility of this figure.
Comment 9 — Missing precision-recall curve. AUPR is presented as an important metric (Section 4.3), yet no precision-recall curve is shown in the main text. A figure would usefully illustrate the model's stability across decision thresholds, consistent with the Section 6.5 discussion of lowering the threshold to 0.4.
Comment 10 — Proposed but untested ensemble strategy. The "one-vote positive" strategy discussed in Section 6.5 as a future improvement is not empirically evaluated in this article, even though the five models required (one per fold) are already available. Adding this evaluation would strengthen the practical relevance of the discussion.
Comment 11 — Imprecise wording regarding the weighting ratio. The loss weighting ratio (10:1) is described as "strictly aligning with the actual class distribution ratio" (l. 367), whereas the actual ratio in the training set is closer to 9.3:1 (1082/116). A more cautious phrasing would be preferable.
Comment 12 — Sensor-level isolation within cross-validation. The manuscript states that the overall train/test split strictly respects sensor-level isolation (l. 208-211), but does not specify whether the same constraint applies to the 5 cross-validation folds within the training set. Clarifying this would remove any ambiguity regarding the hyperparameter optimisation procedure.
Recommendation
Minor Revision
This manuscript makes a useful methodological and operational contribution to a concrete false-alarm problem in geotechnical monitoring. The proposed architecture is well motivated and validated through a solid ablation study, and the failure-case analysis section reflects notable scientific rigour. However, the internal validity of some reported results depends on clarifications regarding the construction of the positive dataset and the exact scope of the normalisation steps — points that should be addressed prior to acceptance. Once these concerns are resolved, the manuscript has clear potential to make a valuable contribution to the field.
Citation: https://doi.org/10.5194/egusphere-2026-2352-RC2
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RC2: 'Referee comment on egusphere-2026-2352', Anonymous Referee #2, 09 Jul 2026
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Model code and software
The code of PatchDC Shubing Ouyang https://github.com/ShubingOuyangcug/PatchDC
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The manuscript addresses an important and relevant topic within landslide early warning systems, and the machine-learning/data-fusion methodology appears technically rigorous and competently validated.
However, the manuscript currently treats landslide early warning primarily as a signal-classification problem, without proper consideration of the geotechnical, geological and hydromechanical aspects.
The title, abstract and introduction should more clearly define the scope and contribution of the study. The novelty appears to lie mainly in the dataset manipulation and ML workflow.
The term “small-scale” is ambiguous and should be clarified.
A concern is the reliance on crack meters as the principal monitoring approach for shallow landslide warning. Crack opening is not necessarily representative of bulk slope deformation or impending instability, and the manuscript does not sufficiently justify this monitoring philosophy. Later sections imply that this approach has already been widely deployed across Fujian Province, and that the AI framework is intended to mitigate resulting false alarms. If so, this context should be introduced much earlier.
The manuscript also gives insufficient consideration to instrumentation placement and site characterisation. Sensor location relative to slope geometry, drainage, lithology and likely failure mechanism is critical to reliable interpretation.
The definition of “false alarms” remains unclear throughout the manuscript and requires substantial clarification. It is currently uncertain whether false alarms refer to:
These are fundamentally different phenomena with different implications for warning-system performance. Similar clarification is needed for Figure 4 and the “triple-blind review” discussed at line 205.
Figures 11–13 also require clarification. It is not clear whether the timing of actual landslide occurrence is shown relative to the issued alarms.
The statement that landslides are “most strongly associated with precipitation effects within a 6–10 day window” is overly broad and insufficiently justified. Slope response depends strongly on material type, permeability, drainage conditions and failure depth. However, the manuscript provides very limited information regarding geology, geomaterials or failure mechanisms.
The machine-learning workflow appears rigorous, but the manuscript does not compare the proposed framework against simpler or more conventional approaches that may already be sufficient to reduce false alarms. This raises the question of whether a highly sophisticated AI framework is being used to compensate for limitations in an oversimplified monitoring philosophy.
The discussion should also engage more critically with operational geotechnical practice: warning thresholds should generally be site-specific and informed by local geology and failure mechanisms, rather than applied uniformly across many slopes. Warnings are based not only on threshold exceedance, but also on trends in behaviour, rates of change, and engineering judgement.
The manuscript would benefit from discussion of the transferability of the proposed methodology beyond Fujian Province and to settings.