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Paper summary
This paper proposes SEQ2CAUSE, a framework for causal discovery in discrete event sequences with large vocabularies. It organizes the problem into four regimes: event-to-event versus event-to-outcome discovery, each at the level of an individual sequence or a population of sequences. A pretrained autoregressive event model, together with an outcome head, supplies conditional probabilities for information-gain and conditional-independence calculations. The framework uses randomized intermediate events for lagged event effects and an error-corrected minimum-description-length criterion to aggregate evidence into population graphs. The theoretical contribution is a claimed connection between autoregressive prediction error, conditional-mutual-information estimation, and causal graph recovery. Experiments include nonlinear synthetic sequence generators with vocabularies up to 8,000 and vehicle diagnostic data with 29,100 event types and 474 outcomes. The reported results are promising, including 91.3% F1 for the synthetic sample-level task and 56.8% F1 for population-level outcome boundaries. My main concern is whether the probability comparisons and available error estimates support the specific causal objects and guarantees claimed.
Critical strengths
S1 A useful computational approach to a difficult event-sequence setting. The paper addresses a practical setting in which the event vocabulary is large, sequences are relatively short, and many classical conditional-independence procedures have poorly populated contingency tables. Reusing a learned sequence distribution across many tests is a sensible way to amortize density estimation. The four-regime organization also helps distinguish questions that are often conflated, such as a time-indexed dependency in a particular trace and a type-level dependency across traces. The parallel construction in Appendix G provides a concrete implementation idea rather than only a conceptual analogy between prediction and causality. If the causal interpretation can be established, this could make structure exploration considerably more accessible for systems with rich event logs. S2 The experiments provide encouraging evidence of practical signal and investigate meaningful failure modes. Table 2 compares the proposed sample-level event method with alternatives using the same LLaMA backbone, which helps separate the proposed scoring procedure from representation quality. The vehicle outcome experiments are also relevant to the intended application and go beyond a small synthetic demonstration. The difference between corrected and uncorrected population aggregation is substantial: the reported synthetic population precision increases from 4.2% to 81.5%. The vocabulary, sequence-length, mediator-sampling, and context-truncation analyses help characterize computational behavior. These findings make the method worth investigating even if the present theoretical claims need revision. I view the empirical evidence as support for a useful dependency-scoring procedure; whether it validates direct causal structure requires the clarifications below.
Critical weaknesses
W1 The proposed tests do not yet establish recovery of the direct causal objects defined in the paper. The most concrete problem is in the event-to-outcome regime. Section 4.3 states that intermediate-event randomization is unnecessary because outcomes have no children or spouses. However, an outcome being a sink does not eliminate mediation by later events. Consider an unconfounded, temporally ordered chain in which the first event causes the second event, and the second event causes the outcome, with no direct edge from the first event to the outcome. With an exact probability model, observing the first event still changes the outcome distribution relative to the preceding prefix. Consequently, the sequential information-gain test can be positive even though that event is not in the outcome's parent set or Markov boundary. Conditioning on the second event would remove this association, but conditioning only on the history before the candidate event does not. This counterexample satisfies the autonomous event chain and terminal-outcome structure assumed in Equation 2, so it cannot be dismissed solely by invoking the two-chain factorization. The proof in Appendix D.4 does not resolve this issue. It writes the conditioning history as the entire prefix before the target time while also testing an earlier event contained in that history; taken literally, the candidate indicator is then already determined by the conditioning set, and the conditional mutual information is zero for parents as well as nonparents. If the intended conditioning set instead stops before the candidate, the mediated-outcome example above applies. The event-to-event implementation in Appendix G, which changes prefixes and randomizes intermediate tokens, also needs an explicit connection to the conditional-independence statement used in the theorem. These are consequential distinctions between a direct parent, an ancestor, and an informative observation. They affect both the claimed sample Markov boundaries and the root-cause traversal in Corollary 1. I would need a precise conditioning/intervention definition and a corrected soundness argument before accepting the central identification claim. W2 The prediction-error guarantees are not adequately connected to the available diagnostics or to the implemented decision rules. Assumption 1 bounds the event model's next-event conditional KL error. It does not explicitly bound the separately trained outcome conditional probabilities, although Theorems 1 and 2 are presented as covering both event and outcome targets. A perfect event predictor does not by itself make the outcome head accurate. In addition, Equation 8 and Proposition 1 average over histories generated by the model, whereas the proof of Theorem 1 in Appendix D.3 explicitly treats histories as fixed and says they are not sampled from the model's joint distribution. The relevant distributions, and any accumulation of error across a generated history, therefore need to be specified consistently. The practical calibration problem is equally important. Appendix H.2 estimates the unknown entropy floor by the best converged validation loss. If that checkpoint retains approximation error, subtracting its loss removes the residual error rather than certifying an upper bound on it. A dataset-average validation loss also does not certify the local error for each target and conditioning context, particularly under the randomized histories queried by the algorithm. Proposition 2 establishes that a binary projection cannot increase KL divergence; it does not establish the approximately frequency-proportional error allocation used in the rare-event example on page 18. Finally, the sample experiments report small fixed thresholds without the corresponding certified local errors, while the theorem uses an error-derived threshold, and Equations 12 and 14 appear to use inconsistent conventions for whether the MDL coding penalty has already been subtracted. These gaps matter because soundness and calibration without additional tuning are central contributions. The empirical success of a threshold would still be interesting, but it should be distinguished from a verified error-controlled causal-discovery rule.
Questions for authors
Q1 Direct outcome parents — clarification and a minimal validation. For the simple mediated chain described in W1, what exact conditional distributions does the implemented event-to-outcome test compare, and which events enter the recovered boundary? Please show the result with an exact oracle, so that model approximation cannot explain any discrepancy. If the method is intended to identify ancestors or sequential information contributions rather than direct parents, how should Definitions 1–2, Theorem 2, and Corollary 1 be revised? Q2 Theoretical and implemented estimands — clarification. Please specify the conditioning set, distribution over history particles, intervention distribution, and fixed realized values for each regime. In particular, how are the cause-containing conditioning set in Appendix D.4, the sampled histories in Equation 8, the fixed-history argument in D.3, and the staircase comparisons in Figure 6 reconciled? This would materially affect my assessment of whether the proof applies to the reported algorithm. Q3 Error estimates and actual thresholds — clarification and reporting from existing experiments. What assumption controls the outcome-head error, and how are per-target errors estimated or upper-bounded without knowing the true distribution? Please distinguish raw KL error from the normalized oracle score in Equation 42 and report the thresholds actually used for Table 2 and Figure 2. Is the approximately frequency-proportional binary-error scaling an additional assumption? If the theoretical bound was not used directly, please state which claims remain empirical. Q4 Population objective — clarification. Does the quantity on the left of Equation 14 denote the raw accumulated log-likelihood gain or the penalized gain defined in Equation 12? Please state the inclusion criterion in one convention. Also, Appendix D.5 drops under-resolved probability terms: is the resulting guarantee for the full-data objective or only for the retained positions, and why does the stated MDL gain sum over matched positive occurrences rather than all affected observations? Q5 What is validated by the reported graphs — clarification of existing evaluation. Appendix H.1 says that evaluation is always on a summary graph, whereas the main claims include recovery of sample-time graphs. Could you identify which reported numbers validate each object and provide the time-edge result if it already exists? For the vehicle boundaries, please explain the expert annotation protocol, which parts are incomplete, and how unlabeled candidate causes are treated in precision and recall. This determines whether the results assess direct causal boundaries, broader diagnostic relevance, or both.