acceptodds
Under review as a conference paper at ICLR 2027

Target-Specific Causal Recovery under Federated Support Fragmentation

Abstract

A federation can have enough information overall to resolve a causal target, such as an edge direction, while no client can form some required conditional-independence (CI) answers. We study a fixed set of answers sufficient to determine that target. Some losses leave it recoverable; others admit a graph with a different target answer. When unavailable queries abstain and available answers are correct, we identify the inclusion-minimal groups whose joint loss permits such an alternative. Recovery fails exactly when one such group is entirely missing. Queries with shared conditioning requirements rely on the same client counts. These counts determine when destructive losses occur and distinguish insufficient pooled support from failure caused solely by data placement. For clients with independently sampled data, we derive an exact failure probability accounting for dependent query losses. Individual missing rates generally do not determine this probability. Holding the same global counts fixed isolates risk caused only by repartitioning observations across clients; averaging these conditional risks recovers the overall failure probability. Controlled enumeration shows different risks with each query's missing probability held fixed. Paired and experiments isolate pure fragmentation. Added evidence improves recovery through alternatives that clients can support, and the exact law closely predicts the transition. In , these alternatives share a support bottleneck and yield no observed recovery gain.

Primary area:
causal reasoning
Keywords:
causal discovery, federated learning, conditional independence, causal identifiability, support fragmentation, reliability analysis

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_hQ6MOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

The authors study whether a specific causal target can still be recovered when data fragmentation makes some conditional independence evidence unavailable. They characterize the combinations of missing evidence that prevent recovery and analyze the associated failure probabilities.

Critical strengths
  1. The authors study how data fragmentation can prevent recovery of a specific causal target even when the combined sample has enough support. They separate this effect from ordinary sample scarcity, which helps clarify what goes wrong under their local testing setup.
  2. The authors explain why adding more CI queries does not always provide useful backup evidence, since different queries may depend on the same poorly represented groups of samples.
Critical weaknesses
  1. The authors introduce minimal destructive sets and an exact risk calculation, but do not clearly explain what Theorems 1–3 add beyond ruling out incompatible candidate graphs and standard reliability analysis.
  2. The authors require each CI query to have complete support within at least one individual client, but do not give a sufficiently concrete use case to explain why their stricter setup is needed.
  3. The authors compare C6, C12aug, and Q40, as well as local and aggregate support, but these are comparisons of evidence sets and interfaces. They do not evaluate an existing federated causal discovery method, so they leave unclear whether the analysis predicts failures when a practical method selects and combines its CI tests, or helps improve that process.
  4. The authors do not clearly explain the overall analysis or the key experimental settings and results, making the main text difficult to follow and weakening the overall presentation.
Questions for authors
  1. Could the authors explain how a user should choose the query set and its support thresholds when the true causal graph is unknown?
  2. Could the authors state what information each client must share to carry out the risk calculation? They should also explain how the joint support probabilities used in the analysis would be obtained in practice.
  3. Could the authors add an overview diagram and comparative experiments with federated causal discovery methods that fit their setting, to make the analysis easier to follow and its practical value clearer?
4 comments
AuthorsOpenReview ↗

Part 1 of 3 — Causal contribution and local evidence requirements (Weaknesses 1–2)

We provide the requested causal-to-support overview below and identify the precise evidence-formation interface. The submitted benchmarks and our historical/held-out CI comparisons follow evidence all the way to target recovery, but we do not equate these with running a published FedCSL/FedC2SL full learner or claim learner-level superiority.

Weakness 1 — What is added beyond graph elimination and reliability analysis?

The causal-to-support geometry is the contribution, not inclusion–exclusion. Proposition 3 gives two fixed-global configurations with the same query-wise erasure and blockwise support marginals but pure-fragmentation risk 1/3 versus 0. Corollary 2 strengthens this to matched margins with risk gaps tending to one. T1 derives the minimal joint CI-loss sets that admit target-discrepant DAGs; T2 maps them to shared conditioning-stratum blockers; T3 evaluates their union under joint client support-state laws. Per-query marginal reliability therefore cannot in general determine target risk, even for a fixed certificate.

In submitted Fig. 1(a), a causal five-variable target has 18 non-singleton minimal destructive sets, resilience 2, and identical single-query erasure probabilities 0.1. Avoiding, independent and aligned joint erasures yield 4.42% / 6.28% / 27.10% exact target risk. Submitted ALARM C12aug contracts 17 destructive sets → 12 shared-support regions → six undominated blockers. These are concrete structural examples, not a claimed general polynomial-time algorithm. The paper also proves inclusion-minimal certificates are singleton-fragile, so additional queries can create alternate exclusion routes, or fail to help when they share one support bottleneck (W2/W4).

Weakness 2 — Why assume complete support within one client?

This models a decision-only federation. Each client transmits a query ID and definite local CI label or abstention, not mergeable stratum counts/test statistics. Each query is therefore visible only if one client covers all required strata. Two clients at threshold mm with counts (m,m−1)(m,m-1) and (m−1,m)(m-1,m) are locally unready even though pooled counts are ready. This is a stated interface scenario, not an assertion that all existing learners use it or a claim of deployment.

If statistics are combinable and the pooled CI test preserves the target-certificate semantics (not automatic under heterogeneous mixtures), pre-test aggregation can remove this placement-only loss. Aggregate shortage and wrong CI labels may remain. The matched comparator quantifies the difference under the specified interface.

Submitted Fig. 1(b) illustrates the target-level effect. At ALARM K = 8, N = 160,000, for 5,000 paired within-trial fixed-global repartitions, Local C6 fails 100%, but prespecified C12aug and Q40 succeed 100%, with matched Aggregated success throughout. This is evidence about the causal choice of evidence family under this interface, not universal preference for it. The paper's Conditional Fixed-Global Disintegration distinguishes conditional placement risk from averaging across randomly realised global tables.

AuthorsOpenReview ↗

Part 2 of 3 — Practical method comparisons and experimental evidence (Weaknesses 3–4)

Weakness 3 — No comparison with practical federated methods

We do have end-to-end evidence-to-target evaluations, but not a published full-learner head-to-head. In submitted ALARM (K=9,N=160,000K=9,N=160{,}000, C12aug), 5,000 paired paths give 73.88% Local / 0% Aggregated clean-erasure failure under the fixed target decoder. For correct definite evidence, the difference decomposes into aggregate scarcity plus pure fragmentation. Submitted Fig. 1(b) additionally tests the C6 versus C12aug/Q40 evidence-family effect on the same target (W2).

A historical homogeneous-client comparison evaluates actual local voting, aggregated-count CI and visibility gating through target recovery.

CI interfaceDefinite-answer coverageWrong-definite shareExact target recovery
Local voting98.83%0.034%93.65%
Aggregated-count CI100%3.84%78.81%
Visibility gate41.86%0.044%5.89%

This illustrates how missing and incorrect evidence can have different downstream consequences; the historical arms are not matched to the held-out experiment and are not the complete published FedC2SL learner. A new held-out experiment is the strict same-sample, same-readiness-mask/decoder Oracle–actual-test comparison across 1,000 ALARM paths. Local/Aggregated failure 75.3%/0% Oracle, 75.5%/0.8% conditional MC G2G^2, 100%/100% original TV. With wrong labels the Local-minus-Aggregated risk difference is net, not necessarily pure fragmentation.

Complete FedCSL/FedC2SL learners have not been directly run under harmonised data/target metrics; their communication/statistical interfaces may differ. Thus we claim no complete-learner performance ranking, while emphasising that the existing evaluations do reach the downstream causal target output.

Weakness 4 — Experimental explanation and presentation

The requested overview is provided here, with the paper's running two-hospital example.

TARGET → edge direction / local target summary L_T
    | competing DAGs disagree on L_T
    v
SUFFICIENT CI CERTIFICATE → correct labels exclude competitors
    | T1 → which joint CI losses admit a discrepant DAG?
    v
MINIMAL DESTRUCTIVE CI SETS
    | each query I requires stratum-block counts above m_I
    v
T2 → SHARED SUPPORT-BLOCK CEILINGS
    | Hospital A (m,m-1), B (m-1,m) → neither locally ready;
    | pooled counts meet m on both strata.
    v
T3 → JOINT CLIENT SUPPORT LAW → CLEAN-ERASURE TARGET RISK
    | UNDER CLEAN ERASURE → Local failure = aggregate scarcity + pure fragmentation
    +→ non-IID clients | extended-access blockers | ALARM thresholds
    +→ historical CI interfaces | paired actual-CI/Oracle

The decomposition applies only under clean erasure; actual-CI experiments do not automatically inherit it when definite labels can be wrong. The diagram is provided in this reply, not in the submitted PDF. The submitted three-panel Fig. 1 shows (a) controlled 4.42%→27.10% matched-marginal risk separation, (b) paired ALARM C6 fails/C12aug-Q40 recover at K=8K=8, and (c) T3 predictions 26.31%/73.15% versus observations 26.62%/73.88% for the specified ALARM regimes. The submitted CHILD/GruntingReport contrast is also informative. All three queried families succeed at K=4K=4 and fail at K=5K=5 while Aggregated succeeds. Those are submitted results; the further CI/support audits are post-submission studies.

AuthorsOpenReview ↗

Part 3 of 3 — Query selection, information sharing and algorithmic comparisons (Q1–3)

Question 1 — How should users choose a query family and thresholds without the true graph?

Certificate verification need not identify the unique DAG. For correct CI reference labels, a declared candidate DAG class meeting Assumption 1, and a query family, require a nonempty compatible version space whose members are unanimous on the target summary. In finite oracle-audited benchmarks, reference-labelled enumeration plus redundant-query deletion can yield an inclusion-minimal certificate, but not a guaranteed minimum-cardinality, unknown-data trustworthy or efficiently scalable construction.

Choose readiness threshold mIm_I before looking at test results, from the selected CI test's per-stratum sample/power requirements, then report sensitivity. Our ALARM threshold test shows that even ±5% shifts can drive a sharp transition. This threshold controls availability, not automatic label correctness; heterogeneous pooling must additionally preserve common certificate CI semantics.

Practical lesson from W2/W4. ALARM C6 is sufficient and minimal but fragile at K=8K=8, while C12aug/Q40 add alternative routes and recover. By contrast, CHILD C5/C8aug/Q40 share a Disease support bottleneck and all fail at K=5K=5. Query count alone cannot choose the family. Within an adequate declared class, verify target sufficiency, map destructive sets/shared support blocks, and compare their readiness. This is guidance within the paper's stated assumptions, not a generic automatic query-selection algorithm.

Question 2 — What must clients share, and where do the joint support probabilities come from?

The decision-only CI interface and T3 risk inputs are different. Under decision-only reporting, clients send CI labels or abstentions, not mergeable stratum-level test statistics. T3 separately requires a joint support-state model, given by client kk's CDF Fk(z)=Pr⁡(Zk≤z)F_k(\mathbf z)=\Pr(\mathbf Z_k\leq\mathbf z) at blocker-ceiling intersections, or a sampler for complete support vectors. Such inputs may be specified by a sampling law or estimated from joint support states; CI labels alone and per-query readiness marginals do not determine them (Proposition 3; Corollary 2). If full joint laws are unavailable, Corollary 6 (Sec. 4.4/App. B.4) supplies marginal-information bounds, not exact point risk.

In principle, clients could share only selected estimated joint CDF evaluations at those intersections rather than raw observations. Alternatively, given a verified blocker family and a sampler for complete client support vectors, event-indicator Monte Carlo avoids explicitly expanding the up-to-2b−12^b-1 inclusion–exclusion terms. The submitted 17→12→6 ALARM reduction (W1) illustrates why only selected ceilings matter. These are conditional calculation routes, not demonstrated private estimators or communication protocols; statistical accuracy and blocker discovery remain separate challenges.

The paper's Conditional Fixed-Global Disintegration averages placement-conditional risk over realised global tables; the T3 product of distinct client CDFs assumes independent client support-state vectors. One must not use that product solely because pooled counts have been conditioned upon.

Question 3 — Could the authors add an overview and compatible algorithm comparisons?

The overview is already supplied in W4, and the same-target comparisons are explicit in W2/W3. They comprise submitted ALARM matched Local/Aggregated and certificate-family comparisons, natural count-threshold variation, historical local-vote/aggregated-count/visibility-gate CI interfaces through target recovery, and held-out same-path Oracle, TV, asymptotic G2G^2 and conditional MC G2G^2 using the same ALARM readiness and decoder. W3 reports answer coverage, wrong-definite share and target recovery together for the historical interface comparison rather than treating recovery percentages as unexplained rankings.

These validate evidence-formation and target-output consequences within their respective contracts, not an independent evaluation of complete FedCSL/FedC2SL learners. We do not rank such learners. These additional evaluations were conducted after submission, not included in the submitted PDF. The overview is provided in W4 of this response, rather than in the submitted PDF.

Thank you again for your thoughtful questions and suggestions. We have now uploaded the revised manuscript, including a clearer causal-to-support theoretical roadmap, the held-out finite-sample CI results, additional comparisons between local and aggregated evidence interfaces, and more explicit guidance on certificate verification, query selection, and the assumptions underlying the recovery-risk analysis.

We would appreciate your feedback on these revisions and would be grateful if you could reconsider your assessment and score in light of the clarifications and additional results. We would be glad to address any remaining questions.

Reviewer_ojzhOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper studies target-specific causal recovery when conditional-independence evidence becomes unavailable because the required support is fragmented across federated clients. Given a fixed target-sufficient certificate and a candidate DAG class, it characterizes minimal destructive query losses, maps these losses to client support conditions, and derives an exact recovery-risk expression under independent client sampling. The evaluation includes controlled erasure experiments and support-based experiments on selected ALARM and CHILD target scopes.

Critical strengths

The distinction between insufficient aggregate support and failure caused purely by data placement is useful. The paired experiment, which holds each realized global count table fixed while changing its allocation across clients, provides a clean control for isolating fragmentation. The exhaustive matched-partition analysis also strengthens the controlled demonstration that equal query-wise erasure probabilities can produce different target-recovery risks.

Critical weaknesses
  1. The experimental setup provides limited validation of the framework’s broader relevance.
  • Oracle evidence excludes a central source of uncertainty in causal recovery. The experiments assign every available query its reference CI label, with the observed data determining only whether the query passes the prescribed support threshold (Section 5; Appendix D.1). The certificates are also explicitly described as oracle-certified experimental fixtures. Consequently, the reported recovery rates quantify ambiguity induced by the assumed support-erasure mechanism, without evaluating finite-sample CI errors or uncertainty in obtaining a sufficient certificate.
  • The main benchmark calculations do not substantially exercise the full joint-support risk law. A central contribution concerns dependence among support blocks. However, the principal ALARM risk calculation is almost entirely determined by one LVEDVOLUME block.
  • Task coverage and computational scalability remain limited.
  1. The presentation needs clearer explanations and more informative visual support.
Questions for authors
  1. How informative are the predicted recovery risks when available CI answers are estimated from finite samples and can be incorrect?

  2. How sensitive are the reported transitions to the readiness thresholds, total sample size, and imbalance or heterogeneity across clients?

6 comments
AuthorsOpenReview ↗

Part 1 of 3 — Experimental validation and oracle assumptions (Weaknesses 1–2)

We agree that the original natural-ALARM experiment alone is narrow. The submission also contains controlled joint-erasure, a second CHILD target and exact T3 risk calibration; Further post-submission experiments test independent non-IID clients, a controlled two-blocker extension, threshold sensitivity, historical CI interfaces and matched finite-sample CI. They use distinct assumptions.

Weakness 1 — Limited broader experimental validation

The submitted evidence already extends beyond a single natural-ALARM curve. Fig. 1(a) gives a controlled five-variable causal target (18 non-singleton destructive sets, resilience 2) with all ten individual erasure probabilities fixed at 0.1. Changing only joint erasure dependence yields exact failure 4.42% / 6.28% / 27.10%. Submitted CHILD/GruntingReport, at fixed N=160,000N=160{,}000, moves from 5,000/5,000 Local exact recoveries for each of C5/C8aug/Q40 at K=4K=4 to 5,000/5,000 failures at K=5K=5, with matched Aggregated always successful. The shared Disease support bottleneck makes this a useful negative contrast to ALARM, where evidence-family augmentation helps (Fig. 1(b)). It is not proof of general cross-network performance.

Original numerical calibration is also explicit. Fig. 1(c) reports T3 clean-erasure predictions versus observations 26.31%→26.62% (ALARM C6, K=7K=7) and 73.15%→73.88% (C12aug, K=9K=9). Our additional experiments address different questions. An independent non-IID test uses independently sampled client support laws (one IID reference, three non-IID settings; 5,000 trials each; T3 error ≤0.91 pp); A controlled two-blocker extension isolates a matched-marginal two-blocker effect under a deliberately extended access gate (10.32-pp Local contrast, not a natural count-only ALARM test); A natural ALARM threshold test measures the sharp natural ALARM threshold transition; A historical CI-interface comparison follows historical actual CI interfaces through target output (Local voting 93.65%, aggregated-count 78.81%, visibility gate 5.89% exact recovery); and A held-out paired CI-test experiment compares same-path Oracle versus estimated-CI target recovery (details in W2/Q1).

These controlled, benchmark and historical audits expand mechanism and statistical validation, but are not a wide benchmark survey, independently varied total-NN study or complete published federated-learner head-to-head.

Weakness 2 — Oracle evidence and certificate uncertainty

Oracle CI labels deliberately isolate the clean-erasure estimand proved by T1–T3; they were not asserted to represent universally error-free finite-sample CI inference. Given correct reference labels, an Assumption-1-adequate candidate DAG class, and a nonempty compatible set unanimous on the target, sufficiency can be checked without identifying a unique DAG. The finite benchmark certificates were constructed/audited with reference structure and labels; they do not solve unknown-data trustworthy-label acquisition or high-dimensional certificate search.

A held-out actual-CI experiment addresses the empirical finite-sample gap in the current ALARM setting. Over 1,000 held-out paths, Oracle fails 75.3% Local / 0% Aggregate, versus conditional fixed-margin MC G2G^2 75.5% / 0.8%, using exactly the same samples, readiness and target decoder. The matched test evaluates four CI rules, readiness-preserving client selection and per-path target outcomes. The original fixed-TV test fails 100% / 100% because 13 truly dependent queries have population plug-in TV below its fixed 0.15 threshold; these do not satisfy the original Δind≥0.30\Delta_{\mathrm{ind}}\geq0.30 strong-signal premise. This does not refute a conditional guarantee. Conversely, MC null calibration does not guarantee universal power against weak dependence.

Under the submitted Maximal Componentwise Soundness result, disagreement in a nonempty version space requires abstention from a definite target component; AMBIGUOUS and INCOMPATIBLE outputs are distinct from a definitively WRONG causal conclusion. Q1 gives the resulting classification. The held-out study remains an empirical actual-versus-Oracle comparison, not a new exact T3 formula with incorrect labels.

AuthorsOpenReview ↗

Part 2 of 3 — Support bottlenecks, scalability and clarity (Weaknesses 3–5)

Weakness 3 — ALARM's single dominant support block

We agree. In 5,000 submitted natural ALARM K=9K=9 paths, Local failure coincides with the LVEDVOLUME support-loss event. The joint-blocker theorem is broader than this particular numerical regime, and we tested a non-degenerate case rather than relabelling that dominant event as joint dependence.

Our controlled two-blocker experiment augments count readiness with a controlled support-block-shared query-access gate. Access acts jointly on all queries using a block, preserves the within-block threshold nesting, and its randomness is included in the effective support state FkF_k. It is therefore an extension of the original count-only Defs. 5–6, not an unmodified ALARM allocation. With all individual access marginals fixed at 0.55 and three joint-dependence patterns (5,000 matched paths each).

Gate dependence (joint q11)T3 predicted LocalObserved LocalAggregatePure fragmentation
Negative (0.1200)82.33%82.82%80.00%2.82%
Independent (0.3025)77.93%77.82%70.24%7.58%
Positive (0.5000)72.74%72.50%60.06%12.44%

Each blocker has ≥14% exclusive contribution. Negative versus positive access gives 10.32 pp paired Local risk difference (95% CI 9.10–11.54 pp; numeric T3 difference 9.59 pp). Yet Aggregate risk also changes by 19.94 pp, and pure fragmentation changes by −9.62 pp. Therefore the 10.32-pp Local contrast must not be called pure fragmentation.

Independently, the submitted Fig. 1(a) is a controlled, unextended causal-erasure example of the joint-loss phenomenon (4.42/6.28/27.10%; W1), whereas submitted ALARM C12aug has 17 query destructive sets → 12 support regions → six undominated blockers despite a single dominant realised bottleneck at K=9K=9. The three settings support different aspects of the claim; we do not substitute one for another.

Weakness 4 — Target coverage and computational scalability

The submitted 84-target census (App. D.8/Table 14) separates applicability constraints. 14 exceed the five-node degree budget; 26 lack an adequate five-node scope; 20 of the remaining 44 are target-unidentifiable even under complete CI evidence. Thus 24/84 pass both prerequisites (15 at conditioning order ≤1; 9 require order 2–3). The census uses reference true-DAG scopes and population CI labels for benchmark assessment. It does not implement unknown-system automatic-scope discovery. This distinguishes scope inadequacy, complete-evidence non-identifiability and subsequent fragmentation; five nodes are a computational audit choice, not a theorem restriction.

The submitted Fixed-Budget Local Capacity Boundary supplies a sufficient deterministic criterion for Local failure when, for some minimal destructive set, every query's required stratum capacity exceeds the largest client size. With remainder-balanced splitting and fixed NN, sufficiently large KK can force failure. The Remaining Fragmentation Resilience result describes how aggregate-unavailable but nonfatal queries reduce the margin against subsequent Local loss. The CHILD K=4→5K=4\to5 transition (W1) illustrates a sharp allocation effect, but is not proof that this particular capacity sufficient condition triggered there.

Candidate enumeration, certificate/blocker search and joint-support probability estimation may still be expensive; event-indicator Monte Carlo bypasses an already-constructed blocker's inclusion–exclusion expansion, not blocker discovery. No general scalable high-dimensional algorithm is claimed.

Weakness 5 — Explanation and visual clarity

A self-contained causal-to-support overview is provided here.

Target-discrepant DAGs → minimal destructive CI losses (T1)
    → shared conditioning-stratum support blockers (T2)
    → joint client support-state events and clean-erasure target risk (T3)
    → under clean erasure → Local failure = aggregate scarcity + pure fragmentation

Submitted Fig. 1(a/b/c) separately visualises controlled matched-marginal erasure, within-trial fixed-global ALARM repartition/certificate choice, and fixed-KK numeric-versus-empirical T3 calibration. CHILD supplies a contrasting negative target (W1).

For interpreting new evidence, our experiments address independent non-IID clients, controlled extended access, natural ALARM threshold sensitivity, historical actual-CI interfaces, and held-out matched actual-versus-Oracle CI. Their sampling laws and interfaces differ, so the rates are not directly comparable. These are post-submission experiments, not results from the submitted PDF. Nor do these studies constitute a direct complete FedCSL/FedC2SL learning-algorithm benchmark.

AuthorsOpenReview ↗

Part 3 of 3 — Actual CI testing and sensitivity analysis (Q1–2)

Question 1 — What does the risk mean when finite-sample CI answers can be wrong?

Held-out ALARM experiment: Oracle→MC target failure: 75.3%→75.5% Local, 0%→0.8% Aggregated (fixed TV 100%/100%). This is a setting-specific empirical match, not a wrong-label T3 formula. T3 covers clean erasure. Wrong definite CI labels may exclude the true DAG, empty the compatible set or yield wrong target summaries, beyond T1–T2 erasure blockers. Exact wrong-label risk needs the joint law of readiness, CI errors and decoder outcomes. Appendix C.1 Proposition 9 bounds these events; with identical support/abstention masks and decoder, ∣Ractual−Rerase∣≤Pr⁡(Ewrong)|R_{\mathrm{actual}}-R_{\mathrm{erase}}|\leq\Pr(E_{\mathrm{wrong}}) follows by coupling, not stated verbatim there.

Matched-test protocol: held-out natural ALARM, K=9,N=160,000K=9,N=160{,}000, seeds 53–62, 100 trials each, fixed Q40; 1,000 matched federation paths.

CI evidenceLocal target failureAggregated target failure
Oracle correct labels75.3%0%
Original fixed TV (τ=0.15\tau=0.15)100%100%
Asymptotic G2G^275.7%0.9%
Fixed-margin conditional MC G2G^275.5%0.8%

Protocol. Count-only readiness is determined before test outcomes. Local takes the ready client with the largest minimum stratum count, ties by smallest client ID, uses its one label (no voting or result-dependent selection); Aggregated builds pooled stratum statistics. All ready queries are tested with Bonferroni α/40=0.00125\alpha/40=0.00125. Conditional MC uses up to 1,999 fixed-margin random tables, with full-simulation p=(1+#{Gsim2≥Gobs2})/2000p=(1+\#\{G^2_{\mathrm{sim}}\geq G^2_{\mathrm{obs}}\})/2000. It may stop early only for certain non-rejection once two exceedances occur, then records a bound rather than a fictitious full-BB p-value. The conditional-MC test was selected following a separate population-signal diagnostic and evaluated on held-out seeds. Null-conditional calibration handles sparse chi-square concerns but cannot ensure power for all weak alternatives.

Pathwise error and outcomes. MC has 4/29,745 wrong definite Local queries and 10/40,000 wrong Aggregate queries; these are on 4/1,000 Local and 10/1,000 Aggregate paths with any wrong surfaced label. All 14 wrong ready-query/interface decisions are false dependences (a true CI labelled dependent), not missed dependences; the original TV test instead repeatedly misses weak dependences. Exactly 2 and 8 Oracle-success paths, respectively, become MC target failures; zero transitions run in reverse. On C12aug the MC decoder yields Local 245 EXACT / 754 AMBIGUOUS / 0 WRONG / 1 INCOMPATIBLE, versus Aggregate 992 / 1 / 0 / 7. Q40 has the same category counts on these paths, not independent replications. The 95% Clopper–Pearson intervals for the empirical additional-failure rates are 0.024–0.721 pp (2/1,000 Local) and 0.346–1.570 pp (8/1,000 Aggregate) under the stated independent-path model.

This is an actual-CI-versus-Oracle empirical calibration, not a fresh numerical evaluation of the T3 joint-CDF formula. The submitted Fig. 1(c) separately checks 73.15% predicted vs 73.88% observed for clean-erasure ALARM C12aug, K=9K=9, on different paths (W1). Local-minus-Aggregated under wrong labels is only a net failure contrast, not a pure-fragmentation probability. One paired path has Local success but Aggregated failure.

Question 2 — Sensitivity to thresholds, sample size and heterogeneity

Thresholds. We reprocessed natural ALARM K=7K=7–10, C6/C12aug/Q40 and five multipliers (0.90–1.10) on the original count paths. At K=9K=9, C12aug/Q40 Local failure is 0% / 73.88% / 100% at multipliers 0.95 / 1.00 / 1.05, a critical transition, not robustness. Heterogeneity. A separate experiment tests one IID reference and three independent non-IID client configurations, with T3 numerical risk within 0.91 pp of observation and forced IID approximation error up to 25.73 pp.

Sample-size sensitivity remains limited. We have not run an independently resampled total-NN sweep. Threshold reprocessing is not one. Client-size imbalance was also not independently varied. The non-IID test changes distributions at equal client sizes; the threshold test uses original counts without a new unequal-size allocation experiment. The submitted ALARM Fig. 1(b) reallocates each realised global table at fixed N=160,000N=160{,}000 and varies the certificate. At K=8K=8, C6 fails 100% locally while C12aug/Q40 succeed 100%, and Aggregated succeeds. The separate CHILD target, at the same fixed NN, changes from all-success at K=4K=4 to all-failure at K=5K=5 (W1). The submitted fixed-budget capacity result offers a sufficient deterministic failure criterion under splitting, not a substituted independent NN experiment.

Reviewer_VTZHOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies the restoration problem for specific causal objectives (such as the direction of an edge) in a federated scenario. The experiment validated the failure geometry, fragmentation transition, and risk prediction on controlled five variable instances, ALARM, and CHILD.

Critical strengths
  1. The paper presents an interesting and often overlooked phenomenon: federal aggregate data is sufficient to support causal conclusions, but due to the distribution of data among clients, no individual client can form the necessary evidence.
  2. The theoretical chain is complete, from the minimum destruction set to the support block failure area and then to the precise risk formula. Each link has a complete proof, and counterexamples are used to illustrate that the target risk cannot be determined solely by the missing rate of a single query.
Critical weaknesses
  1. The core theorem is relatively straightforward in terms of technology: failure characterization is essentially a minimum cut set argument, and the risk formula is the product of independent events plus the principle of tolerance and exclusion. These are standard tools in reliability theory, and the novelty at the methodological level is limited.
  2. The target-sufficient certificate is considered as an external given, while in the experiment it relies on exhaustive search of all candidate DAGs and obtaining reference labels. In practice, this is equivalent to knowing the answer in advance, and exhaustive search only applies to a local range of about five nodes, which raises doubts about the operability of the framework.
  3. The assumption that the available answers are necessarily correct avoids the core difficulty of conditional independent testing errors under limited samples. In the experiment, it can be seen that queries are directly assigned reference labels without running real tests, so the experiment is essentially just verifying the combination behavior of counting thresholds.
  4. The local query interface requires a single client to independently cover all conditional layers, which is similar to a weak interface set by humans. Existing methods such as FedC2SL can make judgments after summarizing statistical data, and fragmentation issues are mostly absent in these methods. Therefore, the practical significance of the conclusions in the paper is limited.
  5. The experimental scale and heterogeneity are insufficient: there are only five node target ranges and two benchmark targets, and the client is divided by independent and identically distributed multivariate sampling, without involving distribution heterogeneity in the real federation. Among the 84 objectives, only a minority meet the applicable conditions.
  6. There are numerous writing symbols, nested concepts, and a large number of conclusions in the main text rely on appendices, resulting in poor readability and difficulty for readers to quickly grasp the main contributions.
Questions for authors
  1. How to obtain sufficient target certificates in actual federated scenarios without knowing the reference image? Is there a construction method that can be extended to a larger set of variables?
  2. What modifications need to be made to the failure geometry and risk formula if the assumption that the available answers are necessarily correct is relaxed and the error of real finite-sample testing is introduced?
  3. If clients are allowed to contribute statistics separately based on conditional layers and merge them on the server side, will fragmentation failures basically disappear?
  4. Can the precise risk formula with a fixed number of clients still be used when there is heterogeneity in client distribution, and it does not meet the criteria for independent and identically distributed partitioning?
  5. How to efficiently calculate or approximate the risk of failure when the scale of tolerance and exclusion calculation increases exponentially with the number of blocked areas?
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AuthorsOpenReview ↗

Part 1 of 4 — Causal novelty and certificate validity (Weaknesses 1–2)

The contribution is causal target-recovery geometry under federated support constraints, not a new inclusion–exclusion identity. Below we distinguish the submitted paper's exact results (T1–T3; Fig. 1), post-submission support and finite-sample CI experiments, and the unresolved boundaries of real-world certificate construction and full-learner comparison.

Weakness 1 — Novelty relative to reliability theory

The novelty is not inclusion–exclusion. Proposition 3 (Sec. 4.3) gives a causally realisable five-variable target with two fixed-global allocations having identical client sizes, aggregate readiness, conditioning-block histograms and single-query erasure probabilities, yet pure-fragmentation risks 1/3 versus 0. Corollary 2 gives matched-marginal instances with target-risk differences tending to one. Thus query-wise support reliability does not determine target recoverability, with target and certificate fixed within each paired instance.

T1 derives the minimal joint CI losses allowing target-discrepant DAGs; T2 turns those losses into shared conditioning-stratum support blockers; T3 evaluates the resulting blocker union under joint client support laws. Standard reliability algebra combines the events, but does not supply the causal discrepancy sets or the map to shared federated support blocks.

The submitted Fig. 1(a) independently instantiates this geometry. A five-variable target with 18 non-singleton minimal destructive sets and resilience 2 has exact failure risks 4.42%, 6.28%, 27.10% under avoiding, independent and aligned erasure dependence, respectively, while all ten single-query erasure rates stay at 0.1 (a 6.13-fold aligned-versus-avoiding contrast; 2,800 group partitions enumerated in the appendix). This is exact controlled erasure, not a finite-sample CI-test or unmodified natural-ALARM experiment. In submitted ALARM C12aug, T2 reduces 17 minimal CI-erasure sets to 12 support regions and six undominated blocker ceilings, an instance-specific structural reduction, not a general polynomial-time guarantee. A separate post-submission extended-access two-blocker test varies joint blocker dependence under controlled access marginals.

Weakness 2 — Oracle certificate and operationality

Verification, benchmark construction and unknown-data discovery are different tasks. Given correct CI labels and a candidate DAG class meeting Assumption 1 (target-scope adequacy), form the compatible set; it must be nonempty, and all its DAGs must agree on the target summary. This verifies sufficiency relative to that declared class without recovering a unique DAG. Exhaustive finite-candidate enumeration and redundancy deletion implement this condition in the audited small benchmark scopes; their reference labels and candidate-class adequacy were established using oracle information. They do not constitute an automatic, trustworthy certificate learner for unknown observational data.

The submitted ALARM Fig. 1(b) demonstrates what choice of verified evidence family changes. For K = 8, N = 160,000, in 5,000 paired trials (the same realised global table is repartitioned within each trial), the inclusion-minimal C6 fails locally 5,000/5,000, while prespecified C12aug and Q40 recover 5,000/5,000; matched Aggregated recovery succeeds throughout. Although C6, C12aug and Q40 all have erasure resilience of 1, augmentation changes the destructive geometry and improves recovery in this ALARM setting. Thus inclusion-minimality alone does not determine recovery risk; redundancy can provide alternative exclusion routes, but need not help (cf. CHILD in W5). Maximal Componentwise Soundness further establishes that, for a nonempty version space, a definite target component is sound precisely when all compatible candidates agree; otherwise an always-sound decoder abstains.

Remaining boundary. Obtaining trustworthy labels, validating Assumption 1 without oracle structure and finding certificates/blockers efficiently at large scale are not solved. The conditional target-risk results apply once a specified certificate and valid evidence model are available.

AuthorsOpenReview ↗

Part 2 of 4 — Finite-sample CI errors and evidence aggregation (Weaknesses 3–4)

Weakness 3 — Finite-sample CI errors

T1–T3 are exact for clean erasure. Every surfaced definite CI label is correct. Appendix C.1, Proposition 9 gives an event-inclusion/risk bound for incorrect evidence. With the same support/abstention mask and decoder, no wrong surfaced definite label implies identical actual and Oracle outputs; consequently ∣Ractual−Rerase∣≤Pr⁡(Ewrong)|R_{\mathrm{actual}}-R_{\mathrm{erase}}|\leq\Pr(E_{\mathrm{wrong}}) is a same-mask coupling consequence, not an equation printed verbatim in Proposition 9. Wrong definite labels can also exclude the true candidate, produce an empty version space or force an incorrect target conclusion; unlike erasure, their exact risk is not determined by the original T1–T3 blocker family (see Q2).

A new matched actual-CI experiment uses natural ALARM with K=9,N=160,000K=9,N=160{,}000, seeds 53–62 × 100 trials and fixed Q40, with matched samples, readiness masks, ready-client selection and decoder. Oracle target failure is 75.3% Local / 0% Aggregated; fixed-margin conditional Monte Carlo G2G^2 is 75.5% / 0.8% (Bonferroni α/40=0.00125\alpha/40=0.00125, at most 1,999 random tables); asymptotic G2G^2 is 75.7% / 0.9%, and the original fixed-TV rule gives 100% / 100%. For MC there are 4/29,745 wrong ready Local labels and 10/40,000 wrong Aggregate labels, occurring on 4/1,000 and 10/1,000 federation paths. Across both interfaces, all 14 wrong definite query decisions mislabel population-independent queries as dependent; none misses a population dependence. By contrast, fixed TV repeatedly misses 13 weak dependent queries. The paired decoders have 2 Local and 8 Aggregated Oracle-success→MC-failure paths and no reverse changes. Local selects the ready client with the largest minimum stratum count (ties by ID), without voting or test-result selection. This is empirical actual-versus-Oracle evidence, not a wrong-label T3 theorem.

The TV failure is a signal-assumption limitation, not a universal counterexample. A population-signal audit identified 13 truly dependent queries whose population plug-in TV statistic is below the fixed 0.15 threshold; those cases do not meet the original strong-dependence premise of Δind≥0.30\Delta_{\mathrm{ind}}\geq0.30. The conditional-MC test was selected following a separate population-signal diagnostic and evaluated on held-out seeds. Its conditional-null calibration does not promise power for arbitrary weak dependence.

The submitted Fig. 1(c) separately calibrates T3's clean-erasure numerical risk, with 26.31% predicted / 26.62% observed for ALARM C6 at K=7K=7 and 73.15% / 73.88% for C12aug at K=9K=9 (prediction within the reported 95% Wilson interval [72.64%,75.08%]). A separate experiment tests independent non-IID client laws. These three calibrations answer different questions. Moreover, MC failures need not mean wrong causal directions. For C12aug the Local outcomes are 245 EXACT / 754 AMBIGUOUS / 0 WRONG / 1 INCOMPATIBLE, and Aggregate 992 / 1 / 0 / 7; Q40 gives the same counts. Most Local failures are non-identification, not confidently wrong output.

Weakness 4 — Local whole-query interface versus pre-test aggregation

The Local model has a concrete decision-only workflow. Each client sends a query identifier and either its definite CI label or abstention, not mergeable stratum counts/test statistics. A whole query is reportable only if one client has enough data in every conditioning stratum. Two clients with (m,m−1)(m,m-1) and (m−1,m)(m-1,m) are individually unready but pooled counts are ready. This is an explicit interface contract, neither a claimed deployment nor an assertion about every federated causal learner.

When required statistics can be combined before testing and the pooled test preserves the same target-certificate CI semantics, placement-only fragmentation may disappear; aggregate scarcity and statistical errors can remain. That semantic clause matters for heterogeneous mixtures. An independence shared within clients need not hold after pooling. Our matched comparator quantifies the removable support-placement channel under the stated interface. FedC2SL pre-test aggregation is not our Local whole-query contract; historical CI-to-target variants and paired actual-CI checks are interface/estimator evaluations, not complete FedC2SL/FedCSL algorithm runs.

In submitted Fig. 1(b), each trial fixes one realised global count table, then compares its paired client repartitions and matched Aggregated evidence. The paper's Conditional Fixed-Global Disintegration distinguishes such conditional placement risk from its expectation over randomly realised global tables; it does not extend T3's independent-client product law to dependent fixed-global allocations.

AuthorsOpenReview ↗

Part 3 of 4 — Heterogeneity, applicability and certificate construction (Weaknesses 5–6; Q1)

Weakness 5 — Heterogeneity, scale and applicability

Independent does not mean identically distributed. Assumption 3 (Sec. 4.2) fixes the certificate-CI truth but allows different client marginals, support, parameters and off-certificate mechanisms; T3 (Sec. 4.3, Eqs. 17–18) requires independent client support vectors, permits distinct joint CDFs FkF_k and arbitrary within-client support-block dependence. A separate non-IID experiment evaluates one IID reference and three independent non-IID ALARM-structured client configurations (5,000 trials each). T3-versus-observed discrepancy at most 0.91 pp, versus up to 25.73 pp error from a forced IID approximation. This experiment uses a C6 recovery certificate; Q40 was an additional population-CI semantic audit (480 labels, zero mismatch), not its recovery certificate. Observed IID/mild/strong/extreme risks are 45.46% / 31.60% / 31.00% / 29.30%, against respective T3 predictions 44.92% / 32.51% / 30.74% / 29.33%. This supports independent non-IID populations, not cross-client dependence.

Scope coverage has distinct causes. The submitted 84-target census (App. D.8/Table 14) found 14 beyond the five-node degree budget, 26 lacking an adequate five-node scope and, among the remaining 44, 20 not identifiable even under complete CI evidence; 24/84 pass both prerequisites (15 at conditioning order ≤1, 9 at order 2–3). This is an oracle benchmark census using reference DAG scopes and population CI labels, not an unknown-data automatic-scope or certificate-search procedure. The general theorems are not five-node-specific; the study does not establish efficient high-dimensional enumeration.

The submitted CHILD/GruntingReport target provides a contrasting negative case. At fixed N=160,000N=160{,}000, C5/C8aug/Q40 all achieve 5,000/5,000 exact Local recoveries at K=4K=4, and 5,000/5,000 failures at K=5K=5, while matched Aggregated recovery succeeds throughout. Alternative queries still share a Disease support bottleneck; adding queries need not improve resilience. This is distinct from the separate CHILD/Disease complete-evidence insufficiency entry in the census.

The submitted Fixed-Budget Local Capacity Boundary gives a sufficient deterministic failure criterion when every query in a minimal destructive set requires more stratum capacity than the largest client can supply; under remainder-balanced splitting, sufficiently large KK at fixed NN can force Local failure. This is not a complexity guarantee or an independent NN-sweep experiment.

Weakness 6 — Readability

A causal-to-support overview is given here.

Target-discrepant DAGs → minimal destructive CI losses (T1)
    → common conditioning-stratum support blockers (T2)
    → joint client support states / blocker event risk (T3)
    → Under clean erasure → Local failure = aggregate scarcity + pure fragmentation

Submitted Fig. 1(a–c) already supplies, respectively, controlled matched-marginal separation, paired ALARM certificate comparison and numeric-versus-empirical T3 calibration; CHILD supplies a different target. Additional post-submission experiments separately test non-IID support laws, controlled extended access, threshold shifts, historical CI interfaces and held-out finite-sample CI; they must not be conflated. The overview above is provided in this reply and is not part of the submitted PDF.

Question 1 — How can certificates be obtained without knowing the true DAG?

As distinguished in W2, one can verify sufficiency without uniquely identifying the true DAG, but only relative to correct reference CI labels, an Assumption-1-adequate candidate class, a nonempty compatible set and unanimous target summaries. In a finite oracle-audited benchmark, start with a sufficient labelled family and remove redundant queries to obtain an inclusion-minimal (not necessarily minimum-cardinality) certificate. A finite-candidate audit, for example, exhaustively checks all 64 erasure masks for the six-query ALARM C6 certificate against the finite decoder. The submitted C6→C12aug comparison illustrates robustness under different prespecified evidence sets (W2).

These procedures neither derive trustworthy labels from arbitrary unknown observational data nor certify that a chosen candidate class contains the true target structure; general efficient certificate/blocker construction remains open. This is the precise operational boundary, rather than a claim that the conditional sufficiency test itself requires knowing a unique true DAG.

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

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