W1. The core formulation: dropping acyclicity and "projecting" afterwards is not a sound DAG estimator (main concern)
The central claim is that acyclicity is "the core source of nonconvexity" and can be deferred to a post-processing step. Removing the acyclicity constraint changes the statistical target, though, and the paper does not supply a sound way back.
Without the acyclicity constraint (and with self-loops excluded), problem (5) decouples into d independent regressions, i.e. neighborhood selection (Meinshausen & Bühlmann, 2006) with a fused-lasso penalty over time. In the linear-Gaussian case the population coefficient of X_i in the regression for X_j is \beta_ij = −\theta_ij / \theta_jj, where \theta is the precision matrix. Consequences:
- The population support of Stage 1 is the moral graph (parents, children and spouses), not the DAG, and it is symmetric: \beta_ij \neq 0 iif \beta_ji \neq 0. The support therefore carries no directional information. Tables 11 and 17 are consistent with this: the Stage-1 output is 0% acyclic, and roughly two thirds of its arcs belong to two-cycles even after regularization and thresholding.
- All directional information in the edge scores comes from ratios of conditional variances. The "net flow" ordering is then a function of these scale-dependent quantities, not of any identifiability principle. This is closely related to the varsortability / R²-sortability artifacts documented by Reisach et al. (2021; 2023).
Critically, the projection fails even in the population for a simple identifiable model. Take the chain X1 -> X2 -> X3 or the a v-structure X1 -> X3 <- X2 with weight b \neq 0 on both edges and unit noise variances. These are linear Gaussian with equal error variances, so they are identifiable by the paper's own Prop. 3.2(b). However, it seems like the paper's setup will fail in these simple examples.
Since the orientation is driven by conditional variances, the output is not invariant to rescaling the variables. As stated earlier, this is very similar to varsortability I would ask the authors to (a) report all results on standardized data and (b) compare against sortnregress and R²-sortnregress (Reisach et al., 2021; 2023). The synthetic protocol (equal unit noise variance, weights with |w| ≥ 0.5, ER graphs) is known to be highly varsortable.
The paper's own evidence points the same way:
- Table 10: the projection raises precision, the paper's stated priority. However, it reduces F1 relative to the unprojected Stage-1 output in all nine settings. App. E also reports that skeleton F1 changes by small amounts, so the projection mainly decides orientations, and Table 17 shows it often decides them wrongly.
- Table 17: after projection, 37–45% of retained edges are false positives, and 21–32% of removed edges are true edges whose reverse was kept. App. E concludes that the gap is "an orientation gap rather than a support gap". That is exactly the issue: Stage 1 recovers (roughly) an undirected moral graph, and Stage 2 orients it by a heuristic without causal justification.
- App. B.5 concedes that the population minimizer can "favor a directed supergraph over the true DAG" and that the Stage-1 objective cannot serve as a projection criterion (see also Remark B.3).
- Table 6 (\lambda1 = 0 rows): without the sparsity penalty, precision is about 0.08 regardless of \lambda2. Edge selection by \lambda1 and the threshold, not the structure of the estimator, appears to drive the reported precision.
Unconstrained regression followed by thresholding or ordering has been studied and critiqued before. Loh & Bühlmann (2014) explicitly estimate the moral graph via the inverse covariance and then search over DAGs consistent with it, using a proper score rather than a net-flow heuristic. Reisach et al. (2021) show that apparent DAG-learning performance on such benchmarks can come from scale artifacts, and Kaiser & Sipos (2021) show that NOTEARS-type outputs are not scale-invariant. Stage 1 is a basis-expanded variant of TV-penalized neighborhood selection for time-varying networks (Ahmed & Xing, 2009; Kolar, Song, Ahmed & Xing, 2010). The closest Gaussian analogue with abrupt changes is Kolar & Xing (2012). Related work on change points in graphical models includes the time-varying graphical lasso (Hallac et al., 2017) and the group-fused graphical lasso (Gibberd & Nelson, 2017). None of this literature is discussed, and it would substantially reframe the contribution: Stage 1 is a close relative of known estimators of time-varying undirected dependence structure, and the novelty would rest largely on Stage 2, which is the unsound part.
Unless the authors can give conditions, verifiable in terms of the SEM, under which net-flow ordering of neighborhood-regression coefficients recovers a topological order, and show that these conditions are not just varsortability, I do not think the method can be presented as a DAG / causal-discovery method. At most it learns time-varying Markov-blanket structure with a heuristic orientation.
W2. Theory is either standard or does not connect to the claims
- Thm 3.1 is the textbook Chambolle–Pock result applied to a convex problem. It guarantees convergence to the minimizer of a problem whose minimizer is not the target DAG (see above).
- Prop 3.2 restates LiNGAM, equal-variance and ANM identifiability (the proof says each part "restates an existing result"). It concerns the population distribution, not the estimator. Including it gives the impression that DACORD exploits these identifiability results, but none of them is used: the estimator never uses non-Gaussianity, equal variances, or residual independence. The three-node chain above is in setting (b) and the method fails there.
- Prop 3.3 is a triangle inequality given a uniform estimation error e, with no bound on e (no rate, no conditions on n_w, d, \lambda, design). The "reference sequence" W^0 is never tied to the SEM coefficients. As Remarks B.3 and App. B.5 indicate, the population regression target can include non-parent edges and is not the structural coefficient matrix, so even a consistent Stage 1 converges to something other than the structural W.
W3. Experimental design and fairness
- Missing baselines. (i) Pooled or per-window lasso + the same FAS step with no TV. The paper's own grid (Table 6, RBF10) is mixed here: at the default \lambda1 = 0.1, TV adds little, while at \lambda1 = 0.05 it helps substantially. A systematic comparison with the no-TV variant across settings is needed. (ii) sortnregress / R²-sortnregress. (iii) A simple two-step pipeline: an off-the-shelf multivariate change-point detector (e.g. on covariances) followed by a fast modern DAG learner per segment, e.g. DAGMA (Bello et al., which the paper cites but does not compare to), GOLEM, or PC with Fisher-z. These should be feasible at d = 200.
- Reports such as DYNOTEARS "too slow" at d = 100 within 10 h, and NTS-NOTEARS at 77 h for d = 200, need justification (implementation, tolerance 1e-8, CPU/GPU, number of threads). The 20–40x speedup compares a solver for an unconstrained convex problem to solvers for a constrained nonconvex problem, so it is not an apples-to-apples comparison of methods solving the same task.
- Unit-variance Gaussian noise, ER graphs and |w| \in [0.5, 2] is a highly varsortable regime (see Point 1). Results on standardized data, unequal noise variances, and scale-free graphs are needed.
References mentioned in this review
- Ahmed, A. & Xing, E. P. (2009). Recovering time-varying networks of dependencies in social and biological studies. PNAS.
- Gibberd, A. J. & Nelson, J. D. B. (2017). Regularized estimation of piecewise constant Gaussian graphical models: the group-fused graphical lasso. Journal of Computational and Graphical Statistics.
- Hallac, D., Park, Y., Boyd, S. & Leskovec, J. (2017). Network inference via the time-varying graphical lasso. KDD.
- Kaiser, M. & Sipos, M. (2021). Unsuitability of NOTEARS for causal graph discovery. Neural Processing Letters (arXiv:2104.05441).
- Kolar, M., Song, L., Ahmed, A. & Xing, E. P. (2010). Estimating time-varying networks. Annals of Applied Statistics.
- Kolar, M. & Xing, E. P. (2012). Estimating networks with jumps. Electronic Journal of Statistics.
- Loh, P.-L. & Bühlmann, P. (2014). High-dimensional learning of linear causal networks via inverse covariance estimation. JMLR.
- Meinshausen, N. & Bühlmann, P. (2006). High-dimensional graphs and variable selection with the lasso. Annals of Statistics.
- Reisach, A. G., Seiler, C. & Weichwald, S. (2021). Beware of the simulated DAG! Causal discovery benchmarks may be easy to game. NeurIPS.
- Reisach, A. G., Tami, M., Seiler, C., Chambaz, A. & Weichwald, S. (2023). A scale-invariant sorting criterion to find a causal order in additive noise models. NeurIPS.
Thank you for your careful review and thoughtful questions. In the revised manuscript, we have color-coded the changes by reviewer. Blue marks revisions addressing Reviewer Zmp7’s comments, green marks those addressing Reviewer ZrRA ’s, yellow marks those addressing Reviewer smsN’s, and red marks revisions addressing comments from multiple reviewers.
** W1. Window availability and the SNR interpretation.**
Section 4.2 now describes the dimension trend as sensitive to window construction. When one window covers a whole regime, no within-regime coefficient difference can be measured, although the sequence of windows across successive regimes remains available. The SNR explanation remains a hypothesis.
Q1. How much of the decrease is attributable to window construction?
In the linear-basis rows of Table 15, the default rule gives regime accuracy 0.467 at d=100 and 0.600 at d=200. Using two 125-sample windows per 250-sample regime gives 1.000 at both dimensions under the same knee-selected threshold procedure. This directly supports a window-construction effect in that experiment.
Q2. Do two windows per regime fully explain the outcome?
Every true boundary in the 250-sample design falls on the 125-sample grid, so the experiment tests detection on aligned boundaries. With the corrected proximal update and a half-maximum threshold, the same detection grid produced extra boundaries on nonlinear, medium-density graphs. Mean regime accuracy ranged from 0.667 to 0.950 across settings. Window count alone cannot explain the results across these protocols.
Q3. Which baselines completed at high dimension? At d=200, CD-NOD (Fisher-z) completed 32 of 36 original datasets, with two cancellations and two out-of-memory failures. RPCMCI completed 12 of 36, all at R=3. The records contain no jobs for its other 24 cases or for FANTOM at this dimension. The new DAGMA-linear comparisons also completed at d=200 with both true and estimated boundaries. Section 4.2 reports these results.
Q4. Why do the DACORD rows lack standard deviations? The graph table (submitted Table 1, revised Table 14) omits DACORD’s SD. Determinism for a fixed dataset does not justify that omission. The seed analysis (submitted Table 13, revised Table 12) reports variation across generated datasets, e.g., F1 0.403±0.06 at d=200, R=3 (revised Table 14 gives 0.469). In the separate threshold diagnostic in §4.2, F1 is 0.265±0.003 after averaging over R within each of three seeds and taking the sample SD across seeds. These SD estimates describe different summaries from the mean of 0.469 in revised Table 14.