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Withdrawn from ICLR 2027

CAUSAL REVERSAL AND IDENTIFICATION UNDER COEFFICIENT MODULATION

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

A coefficient that changes with the volatility state can reverse the direction preferred by causal discovery methods built for a fixed mechanism. We certify this reversal in a matched two-variable model: changing only the coefficient's state dependence makes both residual mutual information and the deployed DirectLiNGAM score prefer the wrong arrow. On a ten-variable benchmark, DirectLiNGAM, ICA-LiNGAM, VARLiNGAM and a constant-coefficient heteroskedastic-SEM score all fall below chance as positive modulation grows. Conditioning on the state does not settle the direction by itself: without a restriction on how the coefficient moves, a reverse model reproduces every state-conditional covariance. We then show how the same variation can identify a graph. When coefficients and relative noise variances are log-affine in an observed state, sinks have the smallest signed curvature of the log precision diagonal. This criterion recovers the DAG from three state-conditional covariances, provided coefficient growth does not exactly offset relative noise growth. We give a recursive estimator, HetCD-, with an exact-state recovery guarantee and a matching fourth-order lower bound near this balance condition. On the same benchmark, a fixed-window implementation reaches order accuracy under strong modulation of either sign, compared with and for DirectLiNGAM. These experiments also expose the limits of the repair: fixed windows lie outside the guarantee, one-signed modulation creates a variance-sorting shortcut, and an outcome-derived state proxy substantially reduces accuracy. A daily financial panel provides a consistency check only. The results specify when coefficient variation reverses a pooled criterion, when it identifies structure, and what state information that identification requires.

Primary area:
causal reasoning
Keywords:
causal discovery, causal identification, heteroskedasticity, time-varying volatility, non-stationarity, financial time series, coefficient modulation, model misspecification

Reviews

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Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_djpAOpenReview ↗
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1
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3
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Paper summary

The paper investigates causal structure identification and causal discovery using non-i.i.d. data. In particular, the authors consider a linear structural equation model in which both the edge coefficients and the noise variances are allowed to vary as functions of an additional variable. They first present a two-node example demonstrating that both residual mutual information and the score used by the DirectLiNGAM algorithm can incorrectly favor a causal direction opposite to the true data-generating process. The authors then propose an identification approach that is based on the curvature of the relationship between the additional variable and the corresponding conditional precision matrix.

Critical strengths

The paper addresses the sensitivity of existing methods to violations of constant coefficient and constant noise assumptions. To me, this is an interesting problem in causal discovery and I am not aware of work directly addressing it in the linear case.

Critical weaknesses

The presentation of the paper makes it very difficult to understand and assess the contribution. In its current form, it does not clearly communicate its findings to the reader. In the following, I state some examples from the first pages.

  1. It is not clearly articulated that the paper is about linear structural equation models.

  2. The central notion of coefficient modulation is introduced through the functional form b(v)=b0eκvb(v)=b_0e^{\kappa v}, without a clear conceptual explanation of the "modulation" phenomenon, its practical relevance, or why this particular parameterization is appropriate.

  3. Theorem 1 is a special example that shows that edge modulation can reverse the sign of the entropy. But the fact that this is an specific example needs to be inferred by the reader and is nowhere explicitly explained. The reader also has to infer that A=C=log⁡2,b0=1A=C=\log 2, b_0=1 and κ=mlog⁡2\kappa=m\log 2. Moreover, the parameter mm is not defined properly and terms like "equiprobable" remain unexplained.

  4. The last paragraph in Section 2 starts with the sentence "The packaged estimator placed XX first in 20/2020/20 constant-coefficient samples and 0/200/20 moving-coefficient samples at each n∈{500,2000,10000}n\in \{500,2000,10000\}". After reading multiple times I could infer that the numbers 20/2020/20 and 0/200/20 refer to the number of simulated datasets in which the correct causal ordering was recovered when running DirectLiNGAM on 2 variables with sample sizes n∈{500,2000,10000}n\in \{500,2000,10000\} without and with edge modulation. However, the exact data generating process is not described, and, this could have been stated much more clearly for me.

  5. Random variables are mixed upper and lower case.

  6. At the bottom of the first page the authors suppose that "coefficients and relative noise variances are log-affine in the observed state". There is no explanation on this assumption. Is it a strong assumption? When can it be justified? Is it necessary?

  7. Section 3 lacks clear explanations of intuition and there are no concrete examples.

Questions for authors

None.

2 comments
AuthorsOpenReview ↗

RE: Official Review

Dear reviewer, thank you for your thoughtful comments and detailed review. We have revised the main text around the linear SEM, the matched reversal example, and the identification argument. Below we address your seven points in order.

  1. In regard to the model class being unclear, the first sentence now states that the paper concerns linear structural equation models. Section 1 immediately gives Xi=∑j∈pa(i)Bij(V)Xj+εi.X_i=\sum_{j\in\mathrm{pa}(i)}B_{ij}(V)X_j+\varepsilon_i. Conditional on the exogenous state VV, the equations are linear. The DAG stays fixed; coefficients and noise variances may change with the state.

  2. In regard to modulation appearing first as an unexplained formula, we now define it in words as a change in an edge's strength with the state, before introducing Bij(v)=βijeκijvB_{ij}(v)=\beta_{ij}e^{\kappa_{ij}v}. A one-unit increase in state multiplies the coefficient by eκije^{\kappa_{ij}}; κij=0\kappa_{ij}=0 gives a constant effect. This form preserves the sign and gives an affine log magnitude. It is a sufficient shape restriction, rather than a claim that real systems generally obey an exponential law.

  3. In regard to theorem 1's example and parameters being implicit, section 2 now introduces the construction explicitly: V,Ux,UyV,U_x,U_y independently take −1-1 and +1+1, each with probability 1/21/2; Zx,ZyZ_x,Z_y are independent standard Gaussians; and X=2(V+Ux)/2Zx,Y=2mVX+2(V+Uy)/2Zy.X=2^{(V+U_x)/2}Z_x,\qquad Y=2^{mV}X+2^{(V+U_y)/2}Z_y. Thus A=C=log⁡2A=C=\log2, b0=1b_0=1, and κ=mlog⁡2\kappa=m\log2. The scalar m≥0m\ge0 controls modulation. At m=0m=0 the coefficient is 1 in both states; at m=1m=1 it is 2 or 1/21/2. The noise process is identical. The theorem is now an existence result for this family, rather than a statement about every modulated model. It also certifies intervals, with the proof in Appendix AK.1.

  4. In regard to the simulation sentence was hard to interpret, we now directly state the data-generating process, the number of datasets, and what counts as success. On 200 independent datasets of size n=2000n=2000 from the displayed family, DirectLiNGAM puts the true cause XX first in 100% at m=0m=0, 72% at .5.5, 20% at .6.6, and 0% at the tested values m≥.8m\ge.8. Table 40 reports the sample-size comparison. These finite-sample results are separate from the population certificate.

  5. In regard to the overall notation being inconsistent, we have gone through and resolved these inconsistencies. Section 1 defines VV as a random state and vv as a value; XX is the random vector; tt indexes observations. The main theory uses B(v)B(v), Q(v)Q(v), Σ(v)\Sigma(v) and Ω(v)\Omega(v) consistently. Lower-case symbols in experimental appendices refer to generated or observed series.

  6. In regard to the log-affine assumption lacking clear interpretation, section 3 now explains its role through the reverse-implied coefficient. With unrestricted coefficient functions, both directions can reproduce every conditional covariance. Log-affinity rules out the reverse coefficient away from a specific balance condition. Appendix AK.2 extends the sink criterion to an anchorwise convexity condition, while retaining log-affine relative noise variances. Section 6 shows failures outside that sufficient class without claiming universal failure there.

  7. In regard to the identification argument lacking intuition and examples, section 3 now starts with the linear-prediction interpretation of the precision diagonal and a chain X1→X2→X3X_1\to X_2\to X_3. At three states its signed curvatures are (.115,.115,0)(.115,.115,0), identifying sink X3X_3. After removing it and recomputing the marginal precision, they are (.115,0)(.115,0), recovering the order. A common curved noise factor shifts every gap equally to (−.285,−.285,−.400)(-.285,-.285,-.400), showing why the minimum signed gap, rather than its absolute value, identifies the sink. Figure 1(b) illustrates the example.

We hope this makes the technical contribution substantially easier to assess. If any concern about the soundness of the results remains after these changes, we would be grateful to know which, so that we can address it directly.

I thank the authors for their response and for addressing the specific examples I raised. However, my broader concern remains: in its current form, the manuscript does not communicate its findings clearly enough to the reader. The examples I gave are just some of the instances where the presentation could be improved. As I said I consider the problem interesting, but I believe that substantial improvements to the presentation are needed before the paper is ready. I therefore maintain my recommendation and encourage the authors to revise the presentation for a future conference submission.

Reviewer_XJTdOpenReview ↗
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Paper summary

This paper investigates causal discovery in linear structural equation models where causal coefficients vary with an exogenous state that also influences noise variances. The authors first demonstrate that coefficient modulation can systematically reverse the causal direction preferred by conventional non-Gaussian causal discovery methods, particularly DirectLiNGAM. They provide a certified bivariate example showing reversal in both residual mutual information and the population DirectLiNGAM score. The paper then studies causal identification from state-dependent conditional covariance matrices. Under the assumption that structural coefficients and relative noise variances are log-affine functions of an observed state, the authors establish that sink nodes can be identified through the signed curvature of log-precision diagonal entries. Based on this result, they propose HetCD-Ω, a recursive algorithm that recovers the causal graph from three state-conditional covariance matrices.

Critical strengths
  1. The paper establishes an identification criterion for linear causal models with state-dependent coefficients and noise variances. The observation that sink nodes can be identified through signed curvature of log-precision diagonals is theoretically interesting. The characterization of the balance condition, together with the finite-sample recovery guarantees and the matching lower bound near this boundary, provides additional theoretical insights into the identification problem.

  2. The authors provide a concrete and mathematically certified example showing that coefficient modulation can reverse the direction preferred by residual mutual information and DirectLiNGAM. This goes beyond empirical observations of algorithmic failure and establishes a specific mechanism through which conventional causal discovery methods can produce systematically incorrect orientations.

Critical weaknesses
  1. The main identification theorem relies on restrictive functional-form assumptions. Specifically, both structural coefficients and relative noise variances are assumed to be log-affine functions of the same observed scalar state. The theorem also requires a separation condition. Although these assumptions make the identification result mathematically tractable, it is unclear how frequently they would hold in realistic causal systems.

  2. The empirical results do not sufficiently demonstrate that the proposed method provides a reliable solution for practical causal discovery problems. First, the main experimental results are obtained using fixed state windows, which are not covered by the theoretical recovery guarantees. Second, the method is highly sensitive to the quality of the observed stat but accurately observing the true modulating state may be difficult in real-world scenarios.

Questions for authors
  1. To what extent are the log-affine assumptions on structural coefficients and relative noise variances necessary for causal identification? Can the authors establish similar identification results under more general functional forms?

  2. any way to check whether the required log-affine relationships and separation conditions hold in real-life data?

  3. The theoretical guarantees concern exact state levels under i.i.d. sampling, whereas the main experiments use fixed windows and temporally dependent observations. Could you provide a more direct evaluation of the theoretically justified estimator?

2 comments
AuthorsOpenReview ↗

RE: Official Review (pt. 1/2)

Dear reviewer, thank you for your thoughtful comments and detailed review. We address your four weaknesses below.

Please note: we respond in two messages due to character length limits. This is the first of two responses.

Q1 / W1. Are log-affine coefficients necessary?

No. They are sufficient, and the revision gives a broader sufficient condition while keeping the restriction on relative noise variances.

Appendix AK.2 defines, for each edge j→ij\to i, ϕij(v)=2log⁡∣Bij(v)∣−(ai−aj)v.\phi_{ij}(v)=2\log|B_{ij}(v)|-(a_i-a_j)v. At anchors v1<v2<v3v_1<v_2<v_3 and t=(v2−v1)/(v3−v1)t=(v_2-v_1)/(v_3-v_1), require ϕij(v2)≤(1−t)ϕij(v1)+tϕij(v3)\phi_{ij}(v_2)\le(1-t)\phi_{ij}(v_1)+t\phi_{ij}(v_3). In each ancestral set, every non-sink must have an outgoing edge for which the three values are not all equal. Sinks are then exactly the minimizers of the same signed gap, and their precision rows identify their parents and coefficients at the anchors. The deterministic recovery argument and its distribution-specific sampling consequences continue to apply.

The proof uses log⁡Ωjj(v)+log⁡g(v)=affine+log⁡ ⁣(1+∑icieϕij(v)),ci>0.\log\Omega_{jj}(v)+\log g(v)=\text{affine}+\log\!\left(1+\sum_i c_i e^{\phi_{ij}(v)}\right),\quad c_i>0. The final expression is increasing in each argument and strictly convex because it includes the constant term. The anchorwise inequality and separation therefore give a strictly positive excess gap for every non-sink. Recursive removal identifies the graph.

This includes βcosh⁡(κv)\beta\cosh(\kappa v), βeκv+cv2\beta e^{\kappa v+cv^2} for c≥0c\ge0, and positive mixtures of exponentials, subject to separation. Unlike the log-affine case, three anchors do not identify an arbitrary coefficient function elsewhere.

All 16,000 sampled population graphs from the four included families were recovered. On the finite-sample benchmark, the cosh family gives about .90 order accuracy while slope sorting is near chance (.47 at κ=.6\kappa=.6). Clipped-linear, saturating, and step families give only 2–31% exact population graphs in the tested settings (Table 41). These are failures of unrestricted use of the criterion, not a claim that every non-log-convex function fails. With arbitrary coefficient and variance functions, both directions can reproduce the same conditional covariances; some restriction or additional information is needed for covariance-based identification. We do not claim log-affinity itself is necessary, nor relax the relative-noise restriction.

Q2. Can the assumptions be checked on data?

They have observable implications, but the proposed checks cannot certify them. Appendix AK.5 fits coefficients and residual variances in five state windows, conditional on the estimated graph, and examines coefficient curvature and η^ij=2κ^ij−(a^i−a^j)\hat\eta_{ij}=2\hat\kappa_{ij}-(\hat a_i-\hat a_j) using a moving-block bootstrap.

At a nominal 5% level, fitted-edge coefficient-curvature rejection shares are 4%, 4%, and 8% in the log-affine benchmark at κ=0,.3,.6\kappa=0,.3,.6. The negative-curvature flag detects 63% of clipped-linear and 78% of saturating datasets, but only 13% of step-law datasets. The selected graph is held fixed in the bootstrap, so these are exploratory diagnostics, not calibrated post-selection tests. A relative-noise check over-rejects and is not used.

In the financial panel, coefficient curvature is rejected on 0/11 fitted edges under either state; imbalance is distinguished from zero on 5/11 with MOVE and 3/11 with VIX. Non-rejection does not establish log-affinity, and these estimates do not certify separation over every ancestral subset. We therefore retain the panel only as a consistency check, without using the lower bound to infer a sample requirement for it.

AuthorsOpenReview ↗

RE: Official Review (pt. 2/2)

Dear reviewer, as mentioned, this is a continuation of our discussion to your raised points.

Q3 / W2. A direct evaluation of the theoretically justified estimator

The main text now includes Table 2, with the full comparison in Appendix AK.3. We retain the benchmark's heterogeneous noise and evaluate i.i.d. sampling at three exact levels and with a continuous state. At positive modulation κ=.6\kappa=.6:

Sampling and thresholdnnOrder accuracySHDExact graphs
Exact levels; m−1/4m^{-1/4}3,000.8614.3220%
Same30,000.9641.3965%
Same300,000.995.1893%
Shrinking windows; proved n−1/10n^{-1/10}3,000.8438.240%
Same30,000.9135.814%
Same1,000,000.9901.9522%
Same shrinking covariances; empirical mn−1/4m_n^{-1/4}1,000,000.990.3984%

The exact-level scale-mixture experiment tests the finite-fourth-moment consistency result; it does not meet the conditional-Gaussian assumption of the explicit sample bound. For shrinking windows, the proof uses n−1/10n^{-1/10} so the threshold dominates covariance bias. The faster threshold gives better empirical graph recovery, but is not justified by that proof. It does not change the order. Both are now reported explicitly.

At n=3000n=3000, fixed windows give .870 order accuracy with the benchmark's persistent state and .886 with an i.i.d. state. Persistence therefore does not account for the improvement over the pooled criterion. Negative and mixed-sign experiments show the same qualitative sampling trend (Table 42). Accuracy improves more slowly at weaker modulation, consistent with weaker separation; this heterogeneous sweep is not a direct verification of the minimax exponent.

Appendix AK.3 also extends the deterministic covariance perturbation argument to fixed windows, adding an explicit within-window bias. With stationary ergodic observations and sufficiently narrow windows, a suitable fixed threshold gives recovery. This does not establish consistency for the benchmark's .5 half-width, empirical mean anchors, and vanishing threshold. Section 4.3 now states that limitation.

The originally selected setting was also rerun on 200 held-out seeds. Its positive-modulation accuracy is .87 rather than the submitted .90; the abstract, Figure 1(c), and Table 1 now use the held-out results.

W2. Sensitivity to state quality

The revision measures intermediate state quality rather than only exact and outcome-derived states. With exogenous white measurement noise and population correlation rr with the true state (200 seeds; Table 44):

rr1.95.90.80.70
κ=.6\kappa=.6.87.83.77.65.55
κ=−.6\kappa=-.6.86.86.84.79.73
Mixed ±.6\pm.6.88.87.83.77.70

We also correct the outcome-derived proxy's correlation from .87 to .70–.75. The held-out proxy accuracy is .58 at positive modulation, close to exogenous noise at a similar correlation, but this does not make the two measurement mechanisms equivalent. The guarantee assumes the state is observed on a coordinate satisfying the model laws; an arbitrary monotone transformation need not preserve the criterion. The sensitivity curves are benchmark-specific, not a universal correlation requirement. Inferring a suitable state from the outcomes remains outside the guarantee.

Finally, all three reviews motivated a revision of the introduction and the identification exposition, including a three-node worked example and a new overview figure.

We hope the revised scope and evidence address the practical and theoretical distinctions raised in your review.

Reviewer_ZwiBOpenReview ↗
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Paper summary

The paper proves that when a coefficient changes with some underlying state, standard causal discovery methods like LiNGAM can pick the wrong causal direction. It then shows that if the coefficients and noise variances change with the state in a log-affine way, you can recover the whole causal graph from covariances at just three state levels, and it proposes a method for this (HetCD-Ω). The paper tests this on a synthetic 10-node benchmark, varying how strongly the coefficients change with the state, whether they increase or decrease with it, and whether the method gets the true state or an estimated one. And they compare their method against baselines in terms of causal ordering accuracy and graph reconstruction across each settings, and further evaluate its consistency on real-world financial data. LiNGAM-like methods fall below chance as the coefficients change more strongly. Their method reaches 0.90 ordering accuracy when the state is measured and the change is strong, but it does much worse when the change is small or the state has to be estimated.

Critical strengths
  1. In my view, identification theories are accurate and the core idea is realistic.

  2. Distributional assumptions are mild, and because it is invariant to variable scaling, it cannot exploit varsortability.

  3. A matched example certifies that changing only the coefficient reverses the DirectLINGAM decision.

Critical weaknesses
  1. The evaluated fixed-window estimator lies outside the recovery guarantee, its window setting was tuned on the evaluation seeds, and the benchmark’s highly persistent state (AR(1), φ = .97) departs from the i.i.d. sampling the theory assumes.

  2. The reversal is certified for only one discrete example and a 10⁻⁴ neighborhood, so its generality rests on numerical evidence alone.

  3. the paper mentions “added after review” and “earlier versions of this work,” keeps superseded results (Table 35), and quotes claims that appear nowhere in the paper.

  4. The notation is imprecise for a theory paper. The symbol v denotes both a scalar argument and the whole state process, V is used elsewhere and so on.

Questions for authors

Please see the weaknesses.

4 comments
AuthorsOpenReview ↗

RE: Official Review (pt. 1/2)

Dear reviewer, thank you for your thoughtful comments and detailed review. We address your four weaknesses below.

Please note: we respond in two messages due to character length limits. This is the first of two responses.

W1. Window selection, fixed-window bias, and temporal dependence

Window selection. Your concern was justified: the setting was chosen on the original evaluation seeds. We froze it and evaluated 200 held-out seeds. The main comparison now reports those results:

Order accuracy (mean ± 95% CI half-width)κ=.6\kappa=.6κ=−.6\kappa=-.6mixed ±.6\pm.6
Fixed-window HetCD-Ω\Omega, measured state.870 ± .017.863 ± .016.881 ± .013
DirectLiNGAM.307 ± .018.511 ± .022.472 ± .022

The submitted values were .90/.90/.88. The observed reduction at positive modulation is about .03; selection optimism and seed variation can both contribute. The abstract, Figure 1(c), and Table 1 use the held-out evaluation. Appendix AK.3 reports all nine settings without choosing a new winner. At positive modulation, held-out graph recovery gives SHD 4.6, directed F1 .81, and 35/200 exact graphs.

Sampling schemes aligned with the theory. Table 2 now compares the benchmark design under exact-level and shrinking-window sampling. The following entries are order accuracy / SHD / exact-graph proportion at κ=.6\kappa=.6:

Sampling and thresholdnnResult
Fixed windows, AR(1) coefficient .973,000.870 / 4.6 / .175
Fixed windows, i.i.d. state3,000.886 / 3.9 / .23
Three exact levels, i.i.d.; m−1/4m^{-1/4}3,000.861 / 4.32 / .20
Same300,000.995 / .18 / .93
Shrinking windows; proved n−1/10n^{-1/10}1,000,000.990 / 1.95 / .22
Same covariance estimates; empirical mn−1/4m_n^{-1/4}1,000,000.990 / .39 / .84

The exact-level scale-mixture experiment evaluates the finite-fourth-moment consistency argument, not the Gaussian concentration bound. The two shrinking-window rows have identical orders but different graphs. Only the slower threshold is covered by the stated shrinking-window proof. At ϕ=.99\phi=.99, fixed-window accuracy falls to .83: persistence does not explain its gain. Results for other modulation signs and sample sizes are in Appendix AK.3.

What the window extension proves. Theorem 6's covariance perturbation argument is deterministic. For fixed windows Wk⊆[vk−h,vk+h]W_k\subseteq[v_k-h,v_k+h], if −ΛΣ(v)⪯Σ′(v)⪯ΛΣ(v)-\Lambda\Sigma(v)\preceq\Sigma'(v)\preceq\Lambda\Sigma(v), their covariance bias is bounded by factors e±Λhe^{\pm\Lambda h}. Composing this with relative sampling error ρs\rho_s gives ρ=(1+ρs)eΛh−1\rho=(1+\rho_s)e^{\Lambda h}-1. Recovery follows when this error is small relative to both ordering and edge gaps. Stationary ergodicity supplies convergence to the window covariances; a suitable fixed threshold then yields recovery.

This does not certify the benchmark's half-width .5, empirical window-mean anchors, or vanishing threshold. Sections 4.3 and AK.3 now state these distinctions. The extension quantifies the bias rather than claiming that arbitrary fixed windows are consistent.

AuthorsOpenReview ↗

RE: Official Review (pt. 2/2)

Dear reviewer, as mentioned, this is a continuation of our discussion to your raised points.

W2. Generality of the certified reversal

The revised Theorem 1 certifies a continuum in the same two-state family. With b0=1b_0=1, the residual-MI contrast is positive for ∣m∣≤.49|m|\le.49 and negative for .52≤∣m∣≤3.52\le|m|\le3. The packaged DirectLiNGAM population statistic is positive for ∣m∣≤.54|m|\le.54 and negative for .56≤∣m∣≤3.56\le|m|\le3. The upper endpoint is part of the claim; we do not assert reversal for every larger modulation strength.

Appendix AK.1 also certifies intervals for b0∈{.5,.7,1.4,2}b_0\in\{.5,.7,1.4,2\}. The new tool is a perturbation bound for the entropy of a centred Gaussian scale mixture: its derivatives with respect to log component variances are nonnegative and sum to 1/21/2. Thus an interval bound on the log variances extends a rigorous point entropy enclosure to a whole parameter interval. Arb quadrature and adaptive subdivision then establish the reported signs. The supplementary code contains the certificate programs and their outputs; we reran the b0=1b_0=1 residual-MI and population DirectLiNGAM certificates and confirmed the reported sign bounds.

The result remains a certified existence family. Gaussian-state and other-family sweeps provide broader numerical evidence, not a universal reversal theorem. The certificate encloses sign transitions but does not prove uniqueness of a zero inside the undecided intervals.

W3. Draft-history language and superseded results

We agree that this material distracted from the scientific account. The revised manuscript removes the internal-draft/review wording and the quoted unsupported justification. The superseded rate columns are removed from the oil-family table (Table 35 in the submission, now Table 36); the oil-family result remains because it is still discussed, explicitly outside the DAG assumptions. The appendix now has a question-based guide, and the new certificates and confirmation studies are collected in the final appendix (AK), so that earlier appendix and table numbering is nearly unchanged. Relevant distinctions between pre-specified and exploratory experiments are retained.

W4. Notation and presentation

Section 1 gives the notation convention: random state VV, value vv, observed vector XX, and observation index tt. The main model and theory consistently use state-dependent functions B(v)B(v), Q(v)Q(v), Σ(v)\Sigma(v) and Ω(v)\Omega(v). The two-variable section uses QX(v),QY(v)Q_X(v),Q_Y(v). Lower-case symbols in the experimental appendices denote generated or observed series.

In regard to presentation, the organization has improved: the first paragraph identifies the linear SEM; modulation is defined before its parameterization; the reversal theorem is introduced as an explicit example; and Section 3 gives a numerical three-node explanation of signed curvature and recursive sink removal.

Thank you for the detailed response. The held-out evaluation resolves my concern about window selection, and Theorem 15 addresses W2.

However, Corollary 18 cannot cover the benchmark. With h=0.5h = 0.5, even at the best case (Λ=0.5\Lambda = 0.5) requires γ>1.34\gamma > 1.34, whereas γ≤1.14\gamma \le 1.14 for any non-sink at κ=0.6\kappa = 0.6. Hence no graph from the generator satisfies the condition.

And the current manuscript still quotes claims that doesn't appear in the paper (e.g., p.30 "We allow an arbitrary..."), reuses symbols with different meanings in the main text (tt, SS, mm).

So, I maintain my score.

Thank you for checking the condition so carefully.

You are right: at h = 0.5 the bound in Corollary 18 cannot hold for any graph from the generator. It does not cover the benchmark setting, and the empirical results at h = 0.5 have no theoretical guarantee. We will say this explicitly in Section 4.3 rather than only that the benchmark is “not certified”.

We also thank you for spotting the leftover quoted phrase in the CHOD comparison of the appendix, which we will remove, and the reuse of t, S and m in the main text, which we will separate.

We appreciate your feedback.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Revision summary

We thank the reviewers for identifying two central weaknesses: the presentation obscured the contribution, and the evaluated fixed-window implementation was not directly covered by the recovery theorem.

We have revised the exposition and added evidence that separates population identification, statistical guarantees, and empirical performance. Below is a detailed mapping of these revisions.

A clearer account of the contribution. Section 1 now states the linear SEM immediately, defines coefficient modulation before parameterizing it, and distinguishes three claims: (1) a pooled criterion can reverse (2) structured variation can identify a graph (3) estimation requires additional conditions. Figure 1 illustrates these three claims. Section 2 presents the certified result as an explicit two-state family, with every parameter defined. Section 3 explains sink removal through linear prediction and gives a numerical three-node example, including why curvature must be signed.

A more direct evaluation. Table 1 uses 200 held-out seeds and the frozen submitted window setting. At positive modulation κ=.6\kappa=.6, order accuracy is .870±.017.870\pm.017 (95% interval), compared with the submitted .90.90; at negative modulation it is .863±.016.863\pm.016. DirectLiNGAM gives .307.307 and .511.511. The original broader baseline comparisons remain visible and are identified as a separate 30-seed evaluation. The full nine-setting window sweep is reported, without choosing a new setting from the held-out results.

Table 2 brings the sampling comparison into the main text. With i.i.d. observations at three exact state levels, the finite-moment estimator reaches .995.995 order accuracy and 93% exact graphs at n=300,000n=300{,}000. Shrinking windows reach .990.990 order accuracy at n=106n=10^6. Their graph results depend on pruning: the proved threshold n−1/10n^{-1/10} gives 22% exact graphs; the faster empirical threshold mn−1/4m_n^{-1/4} gives 84%. We explicitly distinguish these thresholds and do not claim that the latter graph result is covered by the stated proof.

Extensions and limits. Appendix AK gives interval certificates for the reversal, an identification extension to anchorwise log-convex signal ratios, and deterministic covariance-bias bounds for fixed windows. The fixed-window bound does not certify the benchmark implementation. Additional experiments examine coefficient laws outside the sufficient class, noisy states, and exploratory model diagnostics.

Corrections. We replace the headline .90.90 by the held-out estimate, correct the outcome-derived proxy's correlation with the true state from .87.87 to .70.70--.75.75, and distinguish the shrinking-window thresholds. We also standardized the main notation, and state the limitations of the diagnostics and coefficient-law experiments more precisely.

Where to find the changes: Sections 1-3: exposition and identification; Section 4.3: sampling assumptions; Section 5 and Tables 1-3: held-out, theory-aligned, and broader comparisons; Section 6: assumptions, state information, and external evidence; Appendix AK.1-AK.5: certificates, extension, sampling studies, measurement error, and diagnostics. The accompanying supplementary package contains the code, frozen outputs, and a reproducible verification record.

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