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Under review as a conference paper at ICLR 2027

Counterfactual Intervention Validation and Decision Transition Learning for Graph and Hypergraph Neural Networks

Abstract

The decision processes of Graph Neural Networks and Hypergraph Neural Networks often rely on implicit structural propagation and distributed representations. It makes them difficult to interpret. And in multi class tasks, class imbalance and inter-class similarity can lead to ambiguous local decision boundaries. Make minority and easily confused classes difficult to learn.So we propose a counterfactual intervention validation and decision transition learning framework for GNNs and HGNNs. First, we introduce a two-stage counterfactual discovery and intervention validation method. It searches the structural space for key supports and estimates their contributions. The key supports drive a source state toward a restoration target. Node feature interventions are then applied to validate these candidate supports and to generate counterfactual samples. Second, we propose a dual target counterfactual decision transition learning method. Each source sample is paired with counterfactuals corresponding to a restoration target and a class-transition target. The model is jointly optimized using endpoint classification, decision-margin, transition-magnitude, and local decision-gradient alignment constraints.We evaluate on two public datasets using graph and hypergraph neural networks.On the TEP dataset, it improves Macro-F1 to 91.89% and Balanced Accuracy to 90.74%. And increase the restoration endpoint margins to 16.850 and transition endpoint margins to 13.954.On the Paderborn bearing dataset, the model maintains a Macro-F1 of 96.43%.The results show that the proposed method provides more reliable counterfactual explanations and geometrically meaningful decision directions.It generates counterfactuals with cross-intervention consistency. And we can use them to maintain or improve the classification performance of the base model, and improve the recognition of minority and similar classes.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
Graph Neural Networks, Hypergraph Neural Networks, Graph Counterfactuals, Counterfactual Samples, Intervention, Decision Transition Learning

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_AzhTOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper proposes a two-stage counterfactual learning framework for GNNs and HGNNs. It first identifies candidate supporting nodes through structural interventions. It then validates these nodes through node-feature interventions. The resulting counterfactual samples are used to constrain classification boundaries and decision-transition directions. The framework aims to make model decisions easier to interpret and improve performance on multi-class fault diagnosis tasks.

Critical strengths
  1. A coherent use of counterfactual information beyond post-hoc explanation. The paper connects structure-level support discovery, node-feature intervention validation, and subsequent decision-transition learning within a unified framework. The generated counterfactuals are used as structured supervision rather than only as post hoc explanations, which is an interesting direction.

  2. Relatively extensive empirical analysis. Beyond classification performance, the paper evaluates counterfactual validity, support sparsity, cross-stage intervention consistency, and several ablations. These analyses validate different components of the proposed framework.

Critical weaknesses
  1. The causal interpretation appears stronger than what the current evidence supports. The paper repeatedly refers to the identified supports as "causal" and interprets prediction changes following interventions as evidence of causal factors. The experiments show that intervening on these variables can affect the predictions of the fixed model, supporting an intervention-based explanation of the model's behavior. However, the current evidence does not provide sufficient support for a stronger causal interpretation beyond the model's predictive behavior. The distinction between model-level causal influence and real-world causality should be clarified, as this interpretation is central to the paper's claims.

  2. The justification for gradient-direction alignment is insufficiently established. Section 2.3 uses a first-order Taylor expansion, ΔR≈G⊤D\Delta R \approx G^\top D, to motivate alignment between the counterfactual direction DD and the gradient GG. This expansion establishes that their inner product determines the first-order change in the relative decision function, but it does not imply that the two directions must be aligned. The cosine-alignment objective may be a useful regularizer, as suggested by the ablation results, but its theoretical justification requires further clarification.

Questions for authors
  1. Could the authors clarify what notion of causality is intended by terms such as "causal supports" and "causal nodes"? Are these claims intended only with respect to the fixed model's prediction under input interventions, or also with respect to the underlying physical process? If the latter, what assumptions or evidence support this interpretation?

  2. Could the authors provide additional justification for requiring the counterfactual direction DD to align with the local gradient GG? In particular, the first-order Taylor expansion establishes ΔR≈G⊤D\Delta R \approx G^\top D, but does not appear to require cosine alignment between the two directions. Is the alignment loss primarily an empirically motivated regularizer?

3 comments
AuthorsOpenReview ↗

Clarification of Model-Level Causality and Gradient-Alignment Motivation

We thank the reviewer for the careful assessment and for identifying two places where our claims and motivation require clarification.

  1. Intended notion of causality. We agree that the identified supports should not be interpreted as physical causes of the underlying faults. In our framework, the graph and hypergraph serve as tools for organizing diagnostic knowledge: the TEP graph captures sensor dependencies learned from data, while the Paderborn hypergraph encodes engineering relations specified through domain knowledge. These structures therefore provide data- and knowledge-informed candidate relations rather than a physical structural causal model. Stage 1 identifies candidate supports within this structured representation, and Stage 2 evaluates whether feature interventions on these supports can induce the specified transition in the frozen predictor. Accordingly, (F) represents a data- and knowledge-informed, model-level intervention support for the prediction. Its causal relevance is defined operationally with respect to the frozen model’s input--output mechanism and should not be interpreted as physical causality in the underlying system. We will revise the terminology and make this distinction explicit.
  2. Motivation for gradient-direction alignment. We agree that the first-order Taylor expansion directly motivates the directional derivative ΔR≈G⊤D=∥G∥2∥D∥2cos⁡(G,D),\Delta R \approx G^\top D= \lVert G\rVert_2 \lVert D\rVert_2 \cos(G,D), but does not by itself make exact cosine alignment a necessary condition. The theory identifies the desired direction: the counterfactual intervention should have a positive projection onto the gradient of the target-versus-source relative score, i.e., G⊤D>0G^\top D>0. We implement this directional principle using the normalized alignment loss 1−cos⁡(G,D)1-\cos(G,D) Because DD is a fixed, validated counterfactual direction during enhancement training and its magnitude is constrained, minimizing Lalign\mathcal{L}_{\mathrm{align}} encourages the model’s local sensitivity to follow the observed transition. The normalization removes the effects of ∥G∥2\lVert G\rVert_2 and ∥D∥2\lVert D\rVert_2, preventing the objective from being satisfied merely by increasing the gradient or intervention magnitude. Thus, the first-order theory provides the desired direction, while cosine alignment is a scale-insensitive implementation of this directional principle rather than a mathematically necessary consequence of the Taylor expansion.

I appreciate the authors' efforts in addressing my concerns. The motivation for combining the different components could be better justified. The framework seems well suited to industrial fault diagnosis, but its applicability to broader graph learning tasks remains unclear.

AuthorsOpenReview ↗

Clarification on Framework Integration and Broader Applicability

We thank the reviewer for this constructive follow-up. We agree that the dependency among the components should be made more explicit. Our framework is intended as a closed loop of discovery, validation, and learning, rather than a collection of independent modules. Stage 1 identifies a compact structural support associated with the source prediction. Stage 2 restores the original graph structure and intervenes on the features of this support to test whether it can induce the specified target transition. The resulting model-valid source–counterfactual pairs are then used by dual-target learning to constrain both fault-to-normal restoration and fault-to-fault decision boundaries. Thus, Stage 2 converts structural attribution into intervention-backed evidence, while the learning stage converts validated counterfactuals from post-hoc explanations into structured supervision. Without Stage 1, the feature search lacks a compact prediction-relevant region; without Stage 2, the identified support is not interventionally validated; and without paired transition learning, the generated counterfactual relations are not exploited to refine decision boundaries. The support-selection, dual-branch, and objective-component ablations were designed to examine these dependencies. We will revise the motivation and method overview to present this closed-loop rationale more clearly. Regarding applicability, the optimization framework itself does not rely on TEP- or Paderborn-specific equations, sensor identities, or fault definitions. It requires a differentiable graph/hypergraph classifier, intervenable node features, and meaningful source–target class transitions. The experiments cover two distinct settings—a learned graph with GNN-TAM and a fixed, knowledge-informed hypergraph with HGNN—showing that the method is not tied to one graph construction or backbone. Nevertheless, we agree that both datasets are industrial fault-diagnosis benchmarks, so the current evidence does not establish empirical generality across all graph-learning domains. We will explicitly narrow the empirical claim to graph- and hypergraph-based fault classification and distinguish it from the broader methodological applicability of the framework. Extension to molecular, biological, and other graph-classification tasks will require domain-specific plausibility constraints and constitutes important future work. We appreciate the reviewer’s comments, which help us clarify both the necessity of the integrated design and the appropriate scope of our claims.

Reviewer_bH8qOpenReview ↗
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2
Confidence
2
Informativeness
2
Presentation
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Soundness
2
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Paper summary

The paper proposes a framework combining counterfactual explanation with additional training for graph and hypergraph classifiers. First, it optimizes structural retention masks toward a restoration target, such as the normal class, and aggregates the resulting changes into node-level support scores. Second, it restores the original structure and searches for feature interventions, preferentially modifying the selected nodes. Successful interventions are categorized according to whether the selected support, auxiliary nodes, or their combination produces the target prediction.

The method then constructs source/restoration/class-transition triplets and fine-tunes the classifier using real-data supervision, endpoint classification, margin constraints, finite prediction-change constraints, and gradient–intervention alignment.

Experiments use GNN-TAM on TEP and an HGNN on Paderborn. The paper reports sparse interventions and improved TEP Macro-F1 from 90.15% to 91.89%, while Paderborn Macro-F1 remains unchanged at 96.43%. Ablations examine support selection, perturbation sparsity, training branches, and individual loss components.

Critical strengths
  1. The method uses the relationship between a source and its counterfactual as training information. Endpoint, finite-transition, and gradient-direction losses provide a concrete way to exploit paired interventions beyond adding synthetic examples independently. Table 6 includes relevant comparisons with naive counterfactual augmentation and component ablations; the full method obtains the highest reported TEP Macro-F1.

  2. The feature-intervention stage includes useful checks on the selected support. Evaluating primary-only, auxiliary-only, and combined perturbations distinguishes several ways an intervention can succeed. The size-matched Random-F comparison provides evidence on TEP that the structurally selected support is a better search region than random nodes: F-only validity is 93.18%, versus 84.09% for Random-F.

Critical weaknesses
  1. Cross-stage agreement is partly imposed by the optimization and does not establish the claimed causal validation. Stage 2 first searches exclusively within the Stage-1 support and subsequently penalizes auxiliary changes more strongly. High support-frequency correlation and concentrated intervention energy are therefore partly expected by construction. The Random-F experiment provides some independent evidence, but Paderborn achieves 100% validity with both random and selected supports.

Moreover, successful optimization within a support demonstrates that it can induce a model response; it does not establish that its nodes are necessary, uniquely explanatory, or genuine fault causes. The “F-only” category does not test whether auxiliary interventions could also succeed, and the causal-validity filter does not independently validate the synthetic target labels. The manuscript sometimes acknowledges model-level scope, but elsewhere concludes that the procedure identifies causal relationships between sensor states and faults. The evidence supports targeted model sensitivity more directly than these stronger claims.

  1. The evidence for improved classification and decision geometry is insufficiently controlled and documented. The final comparison in Table 6 gives no repeated-run uncertainty, despite the full method’s TEP advantage over naive counterfactual augmentation being 1.16 percentage points in Macro-F1 and 0.27 points in balanced accuracy. Paderborn shows no classification gain. A matched real-data-only continuation baseline is also needed to separate the benefit of counterfactual supervision from additional fine-tuning.

  2. Several reporting gaps prevent resolving these concerns: the split sizes are given without a clear recording/run-level split protocol; the provenance and partitioning of training versus evaluation triplets are not sufficiently specified; and Table 4’s dual-branch TEP Macro-F1 of 90.75% is not reconciled with Table 6’s 91.89%. Finally, larger raw logit margins can result from score scaling, so they do not alone establish improved boundary geometry.

Questions for authors
  1. Support validation: How does Stage-1 selection compare with size-matched random and attribution-based supports when all receive identical Stage-2 optimization budgets and penalties? How often can the complement independently achieve the same target transition?

  2. Experimental protocol: Please specify recording/run-level train/validation/test separation, preprocessing fitting, and the source partitions used to generate training and evaluation counterfactuals. Were held-out samples excluded from augmentation and model selection?

  3. Classification evidence: Can you provide paired repeated-seed results for Table 6, including a real-data-only continuation baseline with matched training budget? What configuration difference explains the dual-branch results in Tables 4 and 6?

  4. Counterfactual validity: What concrete plausibility constraints instantiate (L_{\mathrm{pl}}) on each dataset? Beyond changing the frozen model’s prediction, what evidence supports assigning the generated sample its target fault label?

1 comment
AuthorsOpenReview ↗

Causal Scope, Experimental Protocol, and Corrected Results

We thank the reviewer for identifying important limitations in the causal interpretation and experimental reporting. We agree that our evidence supports model-level intervention sensitivity rather than physical causality, and provide the following audits and corrections. 1.Support validation and scope. Cross-stage frequency agreement is partly induced by the Stage-2 search policy; we therefore treat it only as descriptive consistency. We additionally compare Stage-1 support FF, size-matched Random-FF, size-matched gradient-times-input support, and the independently optimized complement V∖FV\setminus F on the same held-out sources, using identical targets, optimization steps, feature bounds, and node penalties. On TEP, FF obtains 93.18% validity and 86.36% dual-target success with a 0.160 changed-node ratio. Random-FF obtains 84.09±1.6184.09\pm1.61% / 68.18±3.2168.18\pm3.21% / 0.143±0.0060.143\pm0.006, while gradient-times-input obtains 95.45% / 90.91% / 0.191. The complement obtains 81.82% validity and 63.64% dual-target success despite allowing 72.1% of nodes, versus 27.9% for FF, and changing 29.8%. Thus, FF is more effective than random support and more compact than the complement, although it is not universally superior to other attribution supports. On Paderborn, all supports reach 100%, indicating saturation. We will describe FF as a model-level causal candidate support. Stage 2 verifies its interventional relevance and sufficiency by showing that feature interventions restricted to FF can induce the specified prediction transition. The complement-restricted experiment further evaluates its conditional necessity under the same intervention budget and search procedure. However, these findings characterize interventional relevance only within the frozen model’s decision mechanism and should not be interpreted as establishing physical causality in the underlying system. 2. Split and counterfactual provenance. TEP is split by complete simulation run (1,904/336/560 train/validation/test runs); no windows from one run cross partitions, and scaling and intervention bounds are fitted on training runs only. Paderborn uses a recording-disjoint 14/3/3 split within each bearing-condition group. Recordings do not overlap, although the same bearing IDs may occur across splits; normalization and percentile bounds are training-only. Enhancement triplets are generated only from correctly predicted training sources (TEP: 50 per fault class, 1,400 total; Paderborn: 50 per fault class, 100 total). Validation data select checkpoints, test data are used only for final evaluation, and held-out audits/cases are never used for augmentation or model selection. 3. Repeated-seed audit and Tables 4/6. We reran all methods with paired seeds 42/52/62 under the same backbone, split, train-only CF pool, epoch budget, and validation rule. Corrected TEP Macro-F1/BA results are: real-only 90.73±0.06/90.55±0.2090.73\pm0.06/90.55\pm0.20, Mixup 90.67±0.06/90.56±0.4290.67\pm0.06/90.56\pm0.42, FLAG 90.60±0.06/90.79±0.2390.60\pm0.06/90.79\pm0.23, naive CF 90.72±0.04/90.51±0.0990.72\pm0.04/90.51\pm0.09, endpoint-only 90.75±0.04/90.61±0.1790.75\pm0.04/90.61\pm0.17, w/o finite transition 90.75±0.04/90.59±0.1690.75\pm0.04/90.59\pm0.16, w/o gradient alignment 90.74±0.04/90.60±0.1590.74\pm0.04/90.60\pm0.15, and ours 90.75±0.04/90.62±0.1590.75\pm0.04/90.62\pm0.15. Paderborn remains 96.43±0.0096.43\pm0.00 Macro-F1 and 96.91±0.0096.91\pm0.00 BA for all variants. The submitted Table 6 mistakenly aggregated nonmatching experiment records; its 91.89% entry is unsupported. We apologize and will replace it with the corrected table. The corrected Ours result matches Table 4. 4. Plausibility and target labels. Stage 2 fixes the restored graph/hypergraph, restricts edited nodes, constrains features to training-derived bounds (TEP: min--max and standardized change ±3\pm3; Paderborn: 1st--99th percentiles), and applies sparsity, magnitude, margin, and pruning constraints. These provide structural and distributional plausibility, not physical validation. We did not originally include model-external validation because our task is model-specific counterfactual explanation: validity is defined for the frozen classifier being explained, whereas requiring the same endpoint to flip another classifier tests the stronger, different property of model-agnostic target-sample validity. Nevertheless, the reviewer identifies an important distinction between explaining a model decision and validating a physical fault state. We will call the endpoints model-valid counterfactuals, avoid interpreting them as independently verified physical states, and investigate independent-model, simulator-based, and real-intervention validation in future work.

Reviewer_KVAHOpenReview ↗
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3
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

This paper tackles the issue of class imbalance and inter-class similarity making minority and easily confused classes difficult to learn in multi-class fault diagnosis tasks. The authors propose a counterfactual intervention validation and decision transition learning framework for GNNs and HGNNs including a two-stage counterfactual discovery and intervention validation method and a dual target counterfactual decision transition learning method.

Critical strengths

(1) The paper is well-motivated and easy to follow. (2) Instead of treating counterfactuals as post-hoc interpretation tools, the authors combines the counterfactual samples and the source-target relation to improve model training. (3) The experiments demonstrate that the proposed framework achieves promising improvements particularly on TEP.

Critical weaknesses

(1) The paper claims to tackle the issue of class imbalance, but there are no experiments designed to compare with existing class-imbalance methods. (2) The proposed framework includes a considerable number of hyper parameters. The effects of most of hyper parameters remain unclear, such as the contribution threshold for the causal candidate set and the target margin. (3) There are unresolved citations and references of figure and table.

Questions for authors

For excluded source sample without both a valid restoration counterfactual and at least one valid class-transition counterfactual, how likely is it a sample from minority classes or having complex multi-class decision boundaries?

1 comment
AuthorsOpenReview ↗

Clarifications and Additional Analyses

We thank the reviewer for the positive assessment. We agree that the submitted manuscript overstated the class-imbalance claim and did not sufficiently document hyperparameter effects and some references. We address these issues below.

W1. Scope of the class-imbalance claim. TEP has an overall normal-to-per-fault frequency ratio of approximately 10.7:1, but all 28 fault classes contain the same number of training windows. In Paderborn, the two fault classes also have comparable sizes (671 outer-race and 616 inner-race training samples), while the smaller class is healthy (336). Thus, neither benchmark provides a controlled long-tailed distribution among fault classes. In the three-seed TEP evaluation, several difficult classes improve, including IDV23 (+10.23±0.73+10.23\pm0.73 F1 points) and IDV16 (+4.41±0.34+4.41\pm0.34), while IDV9 and IDV22 decrease. Because the fault classes are equally represented, these changes are more directly associated with class difficulty and local boundary ambiguity than with fault-class frequency. Our original imbalance motivation also came from a separate industrial Winder dataset with 1,590 normal samples and 84--471 samples per fault class. There, the full model changes Balanced Accuracy from 87.96 to 88.09±0.1288.09\pm0.12 and Macro-F1 from 83.73 to 84.25±0.1984.25\pm0.19 over three seeds. We regard this only as domain-specific supporting evidence, not as proof of a general class-imbalance solution. We will revise the abstract, introduction, experiments, and conclusion to remove claims of solving class imbalance or generally improving minority classes, and instead focus on intervention validation and local decision-boundary learning. Comparisons with specialized long-tail methods are left for future work. W2. Hyperparameter effects. We now distinguish the Stage-1 contribution threshold τ\tau, the generation margin mcfm_{cf}, and the training margins mep/mΔm_{ep}/m_\Delta. On the same 875 Stage-1-pass TEP sources, τ=0.02/0.05/0.10\tau=0.02/0.05/0.10 gives support ratios of 0.413/0.302/0.230, captures 99.1/98.8/82.9% of intervention energy in FF, and yields complete dual-target rates of 93.26/91.43/80.23%. Thus, τ=0.05\tau=0.05 substantially reduces support while retaining 98.8% of the intervention energy. Re-evaluating the same endpoints with mcf=0/0.05/0.10/0.20/0.50m_{cf}=0/0.05/0.10/0.20/0.50 gives strict-validity rates of 98.40/98.34/85.66/82.29/76.51% and complete dual-target rates of 93.60/93.49/70.51/65.14/56.69%. The default mcf=0.05m_{cf}=0.05 removes zero-margin cases with negligible loss, whereas larger margins reject many otherwise valid transitions. We will add these results, parameter definitions, and the complete settings to the appendix; existing ablations separately test the endpoint, finite-transition, and gradient-alignment terms. W3. Citations and cross-references. We will add the missing TEP and Paderborn citations, repair the Appendix table and decision-trajectory figure references, and correct RCExplainer to Bajaj et al. (2021), rather than Tan et al. (2022). We will recompile the manuscript until no undefined references remain. Q. Which source samples are excluded? Here, “excluded” means omitted only from the complete counterfactual-triplet pool; the samples remain in real-data training and test evaluation. We select 50 correctly predicted sources per fault class: 1,400 for TEP and 100 for Paderborn. Hence, exclusion is not caused by unequal source sampling. On TEP, 800/1,400 sources form a strict-and-causal-valid dual-target pair. Of the 600 omitted sources, 525 fail Stage 1 and 75 pass Stage 1 but fail the complete-pair requirement. All 875 Stage-1-pass sources have at least one valid fault-to-fault endpoint, so the latter failures are driven by restoration. Reachability is class-dependent despite equal sampling: IDV8 and IDV13 each yield 1/50 complete pairs, whereas IDV5 and IDV16 yield 50/50. On Paderborn, 85/100 form complete pairs; the 15 omissions are split nearly evenly between outer-race (8) and inner-race (7). The omitted samples are not conventional low-confidence boundary cases. On TEP, they have a larger source-vs-runner-up margin (9.50 vs. 8.97) and lower entropy (0.095 vs. 0.125) than included samples. Instead, they are farther from normal (source-vs-normal gap 21.68 vs. 17.01) and require denser Stage-1 support (32.89 vs. 14.98 nodes). Paderborn shows the same trend. Thus, the main failure mode is a high-confidence fault state requiring broader restoration, rather than minority status or ordinary boundary ambiguity. We will report this limitation and investigate partial-triplet or failure-aware training. We appreciate the reviewer’s comments, which helped us clarify the scope, strengthen the analyses, and correct the reference issues.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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