- Rating
- 3(+1)
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
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Paper summary
ALICE is an amortized causal discovery model trained on synthetic structural causal models to predict directed graphs from observational datasets. Its main contribution is a collection of augmentations and auxiliary objectives intended to improve consistency across datasets sharing the same causal structure. The paper also introduces target-conditioned averaging, subgraph voting, and post-processing with semantic information from an LLM. Experiments demonstrate competitive graph recovery and useful aggregation gains, although the causal validity of some components and the attribution of these improvements remain insufficiently established.
Critical strengths
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Improving the robustness of pretrained causal discovery models is a meaningful objective. ALICE obtains encouraging results across diverse benchmarks, including the best reported AUROC on the four real-world datasets in Table 1.
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The evaluation goes beyond aggregate accuracy to examine consistency, identifiability, graph width, and inference cost. Table 9 also provides a useful matched ablation showing that the auxiliary training objectives improve several metrics.
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Target-conditioned inference is an interesting design choice, and Figure 6 provides evidence that different targets produce complementary local improvements.
Critical weaknesses
- Subgraph voting needs a more careful causal justification. Section 3.4 uses the identity , which holds for an induced adjacency matrix but does not establish that the marginal dataset supports the same causal interpretation. For example, removing the mediator from leaves dependent variables whose relationship may be predicted as a direct edge; removing a common cause introduces latent confounding. Averaging these predictions can preserve systematic errors. Theorem 3.3 is a valid convex-loss averaging argument under its assumptions, but it does not resolve this issue or guarantee improved F1 over full-graph inference, as the authors appropriately acknowledge. There are also recent related works missing, for example:
Causal Discovery in the Wild: A Voting-Theoretic Ensemble Approach, ICLR 2026;
Efficient Causal Structure Learning via Modular Subgraph Integration, arXiv: 2601.21014
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The duplicate-parity objective raises a related concern about the correctness of the training labels. Appendix D states that a near-copy of a target’s parent is appended and labeled as another parent. If the original target-generating mechanism is unchanged, a noisy copy of a cause is not automatically another direct cause. Enforcing equal causal scores could therefore teach the model to confuse predictive proxies with causal parents. The paper needs to specify the augmented SCM and explain why these labels are valid.
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The distinctive contribution is not sufficiently isolated. AVICI already incorporates observation-permutation invariance, variable-permutation equivariance, alternating attention, and asymmetric edge scoring. ALICE’s novelty therefore rests substantially on its auxiliary objectives and target-conditioned inference. However, Table 9 removes the auxiliary losses together, including objectives involving additional mediator, confounder, and intervention supervision. This establishes the benefit of the combined training recipe, but does not distinguish consistency regularization from additional causal supervision. Moreover, the generic averaging theorem does not explain why these particular training losses improve aggregation efficiency.
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The semantic-fusion argument is not probabilistically justified. Giving numerical values to one model and feature names to another does not establish statistical independence between their predictions. Even independence would not, by itself, justify treating two estimates of the same edge event as . Empirically, Figure 8 shows that the LLM alone outperforms ALICE’s fused prediction on Tübingen, so the highlighted improvement over ALICE alone does not establish useful complementarity on that benchmark.
Questions for authors
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What assumptions make predictions from variable subsets comparable to the original graph’s direct-edge labels? Can you report errors specifically when mediators or common causes are omitted?
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For duplicate-parity training, is the target regenerated to depend causally on the appended variable? Please provide the corresponding structural equations.
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Can you separate consistency penalties from additional supervised augmentation while keeping training examples and compute matched, and evaluate these ablations on real-world benchmarks?
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How does semantic fusion compare with the stronger individual predictor and simple alternative fusion rules? Why does combining ALICE with the LLM reduce performance relative to the LLM alone on Tübingen?
Given these unresolved issues, my initial score is 2.
Raised to 3 after rebuttal.
7 comments
(W1) Related Works
We thank the reviewer for these references and will add both. Vo et al. [1] combine different classical algorithms to hedge against their individual assumptions, whereas VISTA [2] aggregates one classical algorithm over Markov-blanket subgraphs for scalability. Neither involves amortized pretraining. ALICE, similar to CDFM, TabCausal, and FoundCause, addresses the assumption problem through pretraining on diverse SCMs, and its subgraph voting is similar to VISTA’s. The difference is that ALICE’s invariance losses during training enable consistency across subgraph views, whereas VISTA considers a fixed base learner and relies on the voting rule to filter inconsistent subgraph predictions. ALICE is complementary to both: it can serve as one of the experts in Vo et al.’s ensemble, and VISTA’s Markov-blanket decomposition can be used to further reduce omission bias in ALICE’s subgraph voting.
[1] Causal Discovery in the Wild: A Voting-Theoretic Ensemble Approach, ICLR 2026
[2] Efficient Causal Structure Learning via Modular Subgraph Integration, arXiv: 2601.21014
(W2 and Q2) Clarifying Duplicate-Parity Penalty
The duplicate-parity objective targets redundant measurements of the same quantity, for example, two calibrated sensors reading the temperature that a controller acts on (). In such settings, a model should treat the two measurements symmetrically rather than arbitrarily favoring one of them.
Starting from the original SCM, and , we select a parent of the target , generated by its own mechanism . We append , with independent of all other variables. inherits ’s parents and, up to a small measurement noise, its exact realization. Accordingly, the two are siblings and share no edge between them, and we label both as parents of y. The parity penalty enforces that both and should be equally identified as parents of the target.
The target mechanism is left unchanged after is appended and y is not regenerated. So strictly, depends on and not on . However, since , the observational samples are nearly indistinguishable from those of the equivalent target mechanism , in which y depends symmetrically on both measurements. For such near-duplicates, the direct parent is practically non-identifiable from observational data with finite/limited samples, and consequently, our parity penalty enforces the symmetric interpretation rather than arbitrarily choosing one.
(Q3, W3) Isolating the Contribution of the Invariance Losses
We thank the reviewer for this careful comparison. We agree that ALICE’s backbone follows established amortized designs: AVICI already uses alternating row-column attention, permutation symmetries over observations and variables, and asymmetric edge scoring. ALICE differs in two respects. First, these architectural symmetries cover only the reordering of rows and columns. ALICE additionally enforces invariances that architecture cannot guarantee, to new realizations, different mechanisms, added irrelevant variables, and duplicated parents, through dedicated training losses. Second, ALICE introduces target-conditioned inference and test-time aggregation, whose effects are isolated in Figure 6.
We now address the reviewer’s central question: Do ALICE’s gains come from the invariance penalties themselves or from the additional supervised samples they require?
To separate the contribution of the invariance losses from additional supervised augmentation, we trained a third matched model. It sees exactly the same augmented consistency samples as full ALICE and is supervised on them with the edge loss, but it omits the invariance penalties between views. All three models share architecture, size (~2M parameters), and training steps.
| Metric | No Augmentation | Consistency Samples Augmentation without Invariance Losses | Consistency Samples Augmentation with Invariance Losses |
|---|---|---|---|
| Synthetic suite AUROC (null) | 0.8772 | 0.8715 | 0.8860 |
| Synthetic suite F1 (null) | 0.4489 | 0.4407 | 0.4866 |
| Ensembling gain, synthetic AUROC | +0.0413 | +0.0434 | +0.0474 |
| Ensembling gain, synthetic F1 | +0.0829 | +0.0825 | +0.1138 |
| Causal Chambers AUROC | 0.9651 | 0.9615 | 0.9665 |
| Sachs AUROC | 0.7388 | 0.6521 | 0.7577 |
| Tübingen weighted acc. | 0.4588 | 0.6096 | 0.6431 |
| Avg. identifiability deviation | 0.1921 | 0.1650 | 0.1133 |
| Avg. consistency (invariance tests) | 0.7544 | 0.7691 | 0.8061 |
Table 2: Consistency penalties vs. supervised augmentation. All models are matched in size and training steps. Ensembling gains are for subgraph voting on the synthetic suite. Table 9 (Table 11 in the updated manuscript) has been updated with the detailed results.
Invariance losses enable gains in consistency and prediction. Adding the consistency samples without the penalties gives only small changes in consistency and slightly lowers AUROC on the synthetic suite. Adding the penalties on the same samples improves consistency, reduces identifiability deviation, and gives the best AUROC on the synthetic suite as well as real-world benchmarks.
Connection to aggregation efficiency. The reviewer correctly notes that Theorem 3.3 holds for any estimator and therefore does not by itself explain why these losses help aggregation. However, our argument is about the finite-sample approximation of the aggregate. A Monte Carlo average over views converges faster when the predictions across graph-preserving views vary less, and the invariance penalties directly reduce this view-induced variation (Table 2, page 6). With identical training samples, the model trained with penalties is the most consistent across views and also gains the most from subgraph voting.
We thank the reviewer for their careful observations and detailed feedback. The reviewer acknowledged the improvements that stem from the proposed target-aware design and the extensive evaluation. Below, we address the weaknesses and the questions raised by the reviewer.
(W1 and Q1) Possible Bias in Subgraph Voting
We agree with the reviewer. The identity ASij=Aij holds for the induced subgraph, but it does not imply that DS supports the same causal interpretation. Removing a variable k from DS does not remove its effect on the remaining variables. If k is a mediator (i→k→j) or a common cause (i←k→j) of a nonadjacent pair, then i and j seem dependent in DS with k no longer present to explain that dependence, and the estimator may predict a spurious edge. Theorem 3.3 and the per-edge averaging bound do not address this bias, since it is shared across subgraphs. Accordingly, we have revised Section 3.4 (lines 370-375) and Limitations (lines 491 and 492) to state this explicitly.
When are subgraph predictions comparable to the original direct-edge labels?
A subgraph prediction for (i,j) targets Aij when S retains the variables that explain any dependence between i and j other than a direct edge, such as mediators and common causes. When we omit such a variable, the prediction may include a spurious edge, and averaging retains this error in proportion to how often we omit the variable. However, omitting variables does not remove a dependence created by a true edge, so the bias mainly produces false positives rather than missed edges.
Quantifying errors when mediators or common causes are omitted.
We evaluate ALICE on all 450 synthetic-suite graphs with 50 or 100 variables, covering 5,619 nonadjacent endpoint pairs and 8,161 tests of an individual mediator or common cause. In each test, both endpoints appear in all 64 width-30 subgraphs, the target is fixed, and we control the fraction of subgraphs from which the explanatory node is omitted. All conditions use the same frozen threshold calibrator. Probe accuracy is the fraction of tests in which neither i→j nor j→i is selected.
Table 1: Omitting mediators and common causes increases spurious edges locally but has a limited effect on overall graph recovery. Probe accuracy measures how often ALICE correctly rejects an edge between two nonadjacent variables as the fraction of subgraphs omitting their mediator or common cause increases.
Probe accuracy decreases from 88.4% to 68.3% as the omission rate increases. However, the effect remains local. Whole-graph AUROC and F1 are nearly unchanged up to 75% omission. Also, random sampling of 30-feature subgraphs achieves the best whole-graph AUROC and F1, since it covers all variable pairs with many votes.
The gap between random sampling and the 0% omission condition (72.7% vs. 88.4%) suggests that sampling strategies that first identify likely mediators and common causes of each pair, for example, from ALICE’s own full-graph scores or from an estimated Markov blanket as in VISTA [1] (Sun et al., 2026), and use that information in sampling could reduce these spurious edges. We leave this to future work and have added this discussion and the analysis above in Appendix G.
[1] Efficient Causal Structure Learning via Modular Subgraph Integration, arXiv: 2601.21014