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Under review as a conference paper at ICLR 2027

Proxy-HCD-IV: Bow-Capable Causal Discovery from Grouped Proxy Variables

Abstract

We study causal discovery when observed variables can be related by both direct effects and shared hidden causes, including cases where both occur simultaneously. Although the hidden causes are not observed, we assume that each is measured indirectly by a group of proxy variables, such as multiple noisy sensors or assays of the same underlying quantity. We propose Proxy-HCD-IV, which uses these grouped proxies to recover both direct causal relationships and relationships induced by shared hidden causes. The method learns a causal order and divides the proxies for each hidden cause into two independent groups, using one group as noisy regressors and the other as instruments for joint structural estimation. We establish identification and false-addition control under stated conditions, with extensions to nonlinear mechanisms. Experiments include FCI/RFCI, RCD, FoundCause, and matched proxy-aware controls. On an independent 40-graph equal-information benchmark with high proxy noise, Proxy-HCD-IV reduces graphs containing any false direct or hidden-effect selection from 30/40 to 3/40 relative to its matched OLS control, while directed F1 increases from .898 to .913, with lower bidirected F1 (.914 to .733). A semi-synthetic experiment based on real clinical feature distributions shows a similar trade-off. These results demonstrate how grouped proxy variables can provide additional information for recovering direct and hidden-confounding structure while substantially reducing false structural selections.

Primary area:
learning theory
Keywords:
Causal Discovery, Latent Confounding, Proxy Variables, Instrumental Variables

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

In this paper, the author proposes Proxy-HCD-IV which uses grouped proxies to recover both direct causal relationships and relationships induced by shared hidden causes. The model divides the proxies for each hidden cause into two groups, noisy regressor and its instrument. This framework could remove the measurement-error bias and isolate the hidden cause’s true effect on each observed variable.

Critical strengths
  1. The bidirected framework is well defined and appealing. The framework estimates directed and bidirected edges separately, and a pair can have both. This can provide a new view that methods such as FCI and RFCI cannot provide.

  2. The paper is well organized, and the assumptions and theory are stated clearly. Grouped proxies are common in practice, and the work has great potential applications.

Critical weaknesses
  1. The assumptions are too strong for this paper. The framework requires that each proxy group measures only its hidden cause and that the two views' measurement errors are independent. These assumptions are hard to hold in practice, and the authors should discuss them more and provide additional analysis.

  2. The baseline is weak. In the main paper and abstract, the author compared the proposed model to the OLS model. The OLS model performs poorly on noisy proxies, and the result (30/40) is expected. The author should include more up-to-date baselines.

Questions for authors
  1. I'm not quite sure why the author did not include all baselines presented in Table 1 (FCI, RFCI) in Table 2. This would make the comparison more comprehensive.

  2. Under the current setting, the proposed model performs better than the OLS-based model. What if the number of proxies for each hidden cause is small, like 2 or 3? Does the proposed model still outperform the OLS-based model?

5 comments

Thank you for recognizing the value of allowing direct and bidirected edges to coexist. We have added direct assumption-violation tests, official baselines on the same 40-graph cohort, and end-to-end comparisons with two and three proxies. The revised claims distinguish identification, finite-sample power, and false-addition control.

  1. How strong are purity and independent-view assumptions?

They are substantive measurement assumptions. A disjoint partition does not itself make measurement errors independent. The linear result requires exogeneity to the hidden causes and primary disturbances and the full cross-view condition E[νηT]=0E[\nu\eta^T]=0, including cross-group entries. We do not infer purity or independent errors from the data.

The revision adds a population sensitivity identity. Under the remaining exogeneity conditions, with regression error u=ϵ−ηTγ+Lu=\epsilon-\eta^T\gamma+L, γk=λk/ak\gamma_k=\lambda_k/a_k, D=E[νηT]D=E[\nu\eta^T], and nonsingular G=E[QRT]G=E[QR^T], the population IV bias is

=G^{-1}\left(E[QL]-\binom{0}{D\gamma}\right).$$ Here $L$ represents an omitted structural contribution. Cross-view dependence and omitted confounding therefore affect the moments; poor conditioning can amplify the bias. Redefining the reported confounding target to include only measured roots does not restore direct-effect identification. We tested eight prespecified measurement conditions on 100 graphs at each noise level, using the true admissible order to isolate measurement misspecification. At noise SD 1.5, valid IV has false-final-graph additions in 3/100 graphs. Sharing a Gaussian measurement-error component across views with correlation parameter 0.1 or 0.3 raises this to 23/100 or 74/100. The corresponding within-view controls have the same population individual and view-average error variances but independent errors between views; their counts are 2/100 and 2/100. Thus this comparison separates cross-view invalidity from merely increasing the variance of the averaged proxies. Removing one proxy group while keeping its hidden cause in the structural equations produces 77/100 false-final-graph additions, including false directed edges in 68/100 graphs. Retained-root and full-confounding targets are reported separately. Cross-loading each proxy group on another root also disrupts labelled hidden-incidence recovery: at low noise and cross-loading 0.3, final-graph false additions occur in 94/100 graphs, but false directed edges in only 7/100. The revision explains this distinction: a common invertible mixing of all roots can preserve direct-effect identification while changing the meaning of individual proxy-group coefficients. We do not claim that every purity violation necessarily destroys every direct effect. These are sensitivity results, not robustness guarantees. They reinforce the need for externally justified proxy groups and independent measurement channels. The revised nonlinear theorem also now requires the stronger conditional assumptions and joint identification of the unknown direct function; its original proof gap is corrected.
  1. Published baselines on the same cohort, including proxy-augmented FCI/RFCI.

We agree that the original separate reference table was insufficient to answer the common-cohort question. We have now run official Tetrad 7.6.10 FCI/RFCI and LiNGAM 1.13.0 RCD on the exact 40 primary datasets underlying the main comparison. Each primary-only method receives all 1000 primary-variable rows, with no supplied order or proxy grouping. Primary data are identical across the two proxy-noise levels, so these are the same 40 primary-only fits, not separate noise-dependent runs. FCI/RFCI use Fisher-Z at 0.05 with unrestricted search depth; RCD uses its documented default configuration. No settings are selected using graph truth. Fisher-Z's Gaussian calibration is not guaranteed for the Laplace generator.

FCI and RFCI return PAGs, so we score adjacency and endpoint marks against the PAG obtained from the full generating DAG with the latent roots explicitly hidden. Mean PAG-adjacency F1 is 0.879 for FCI and 0.880 for RFCI; mean arrowhead F1 is 0.593 and 0.599. Their structural-pair overlaps are reported separately as descriptive quantities. We do not assign exact bow F1 to a PAG or interpret a PAG bidirected mark as the same target as a shared-root structural edge.

For RCD, mean structural directed/bidirected F1 is 0.510/0.417. Its native representation cannot encode a directed edge and a confounding flag simultaneously for the same pair; the reported bow F1 of zero is therefore a representation limitation, not a claim that RCD was designed for our exact output.

We also completed all 40 cases with the official November 2026 FoundCause checkpoint and ten default passes: mean directed/bidirected F1 is 0.622/0.390, with false final additions in 40/40 graphs. Two native outputs have directed cycles; the separate official DAG option gives F1 0.624/0.390. FoundCause receives XX only.

We additionally ran FCI/RFCI on XX plus all 15 raw proxies, using all 1000 rows and no grouping constraints or supplied order. This gives them the same raw observed variables, while our method additionally uses the scientific grouping and measurement model. Scoring the primary-variable restriction against a common exact augmented-DAG PAG reference gives mean PAG-adjacency F1:

At noise SD 0.35: FCI 0.707; RFCI 0.715.

At noise SD 1.5: FCI 0.826; RFCI 0.828.

All 160 proxy-augmented fits are reported. These results address the requested baselines and information-set comparison. They do not turn native PAG metrics into exact structural-edge metrics or establish that our method is uniformly preferable under other assumptions.

OLS remains a useful matched control for the effect of measurement-error correction, but the revision no longer uses it alone to characterize the broader baseline comparison. Moreover, we explicitly report threshold sensitivity: on a new learned-order N=250N=250 high-noise cohort, OLS at Holm threshold 10−610^{-6} has 5/100 false-final-graph additions versus 8/100 for IV at 0.10, with better directed and bidirected precision/recall. At that same fixed OLS threshold, known-order N=500,1000N=500,1000 give 30/100 and 76/100 false additions versus 3/100 and 5/100 for IV. These descriptive curves show that the claim concerns structural consistency under valid measurements, not dominance of every OLS operating point.

  1. Two or three proxies: completed end-to-end tests.

Two proxies can form a 1+1 split and three a 1+2 split. Identification under valid moments and rank does not require five proxies. However, under the equal-variance model, view-error variances are (σ2,σ2)(\sigma^2,\sigma^2) for two proxies and (σ2,σ2/2)(\sigma^2,\sigma^2/2) for three, compared with (σ2/2,σ2/3)(\sigma^2/2,\sigma^2/3) for five. Fewer noisy measurements can severely reduce power.

We extended the submitted 40-graph order study to full graph recovery with m=2,3,5m=2,3,5, the same 750/250 split, and Holm level 0.10. Every archived high-noise order-error count is reproduced. Within each setting, IV and OLS share raw data and learned order; IV uses balanced views and OLS the all-proxy average. These are new recovery results, whereas the submitted proxy-count table measured order accuracy only.

At noise SD 0.35:

m=2m=2: directed F1 is IV 0.991 versus OLS 0.986; bidirected F1 is 0.991 versus 0.994; false-final-graph counts are 3/40 versus 7/40.

m=3m=3: directed F1 is 0.983 versus 0.979; bidirected F1 is 0.978 versus 0.986; false-final-graph counts are 7/40 versus 9/40.

At noise SD 1.5:

m=2m=2: directed F1 is IV 0.417 versus OLS 0.787; bidirected F1 is 0.031 versus 0.840; false-final-graph counts are 1/40 versus 39/40.

m=3m=3: directed F1 is 0.667 versus 0.844; bidirected F1 is 0.249 versus 0.919; false-final-graph counts are 1/40 versus 37/40.

Thus IV retains high accuracy with two or three accurate proxies in this experiment, but does not outperform OLS in F1 with two or three noisy proxies. The small false-addition counts in the latter case accompany severe recall loss. A separate 100-replicate calibration study confirms this limitation rather than hiding it: with two proxies, correct order, noise SD 1.5, and N=250N=250, IV directed/bidirected recall is only 0.438/0.039.

The revised inference discussion distinguishes the original asymptotic Wald guarantee from an optional classical projected Anderson--Rubin procedure, whose finite-sample guarantee requires an admissible order fixed independently of the inference data and independent Gaussian, homoskedastic composite errors independent of the instrument design. That procedure is highly conservative. Neither this option nor the identification theorem provides a general recovery guarantee for weak proxy information.

We also addressed power with an optional all-proxy moment correction. This classical estimator averages all distinct-indicator cross products; it requires a common, possibly unknown, loading within each group and uncorrelated errors for all distinct indicators, including within-view pairs. We froze it before generating 100 fresh graphs with five proxies, noise SD 1.5, learned order, and a 750/250 split. At the same Holm level 0.10, directed/bidirected F1 improves from 0.903/0.739 for split IV to 0.965/0.920, with 8/100 false-final-graph events for both. The two prespecified paired F1 tests give Holm-adjusted p-values 1.23×10−51.23\times10^{-5} and 1.44×10−111.44\times10^{-11}. Strict OLS at the previously fixed 10−610^{-6} level gives F1 0.964/0.751 and 12/100 false-final-graph events. The proof and all 19 exploratory cells are included. This is a qualified efficiency improvement under stronger assumptions, not new estimation theory or a weak-instrument guarantee. Very noisy two-proxy cases remain weak; this extension does not establish general recovery with few proxies.

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Paper summary

This paper employs grouped proxy variables and instrumental variable (IV) estimation to recover both direct causal edges and latent confounding edges, allowing for their simultaneous presence. The authors provide identification results and error control guarantees for linear models, and also discuss non-linear extensions. Experimental results demonstrate that the proposed method reduces the selection of spurious edges in the presence of noise, albeit at the cost of some recall.

Critical strengths

The overall approach is clear: it leverages proxy variables and IV estimation to recover causal graphs that include "bow" structures (i.e., the coexistence of direct causal effects and latent confounding). The experimental evaluation is thorough, particularly in illustrating the trade-off between the false discovery rate and recall.

Critical weaknesses
  1. The proof for non-linear identification is questionable. Theorem 3 and Appendix C.8 appear to establish uniqueness under the assumption that the functions fjf_j are fixed (known). If fjf_j are also unknown, is it possible for the direct effects and the latent confounding effects to cancel each other out? The current conditions do not seem to rule out this possibility.

  2. The novelty of the work requires further clarification. Using independent proxy variables to construct instrumental variables is an established concept, and the estimation procedure presented here is relatively standard. The authors should better articulate what specific contributions this approach makes to graph recovery compared to standard IV-based methods.

Questions for authors
  1. Does Theorem 3 assume that fjf_j are known? If they are unknown, how is joint identification guaranteed?

  2. Could you report the precision and recall separately for the two types of edges (direct causal vs. latent confounding), as well as the number of spurious edges added to the final recovered graph?

  3. Given the same variable ordering, data partitioning, and testing configuration, what are the fundamental differences between this approach and standard multiple-indicator IV methods?

4 comments

Thank you for recognizing the graph-recovery formulation and its precision-recall trade-off. We have corrected the nonlinear theorem, separated final-graph errors from incidence errors, and clarified exactly what is classical and what the framework adds.

  1. The unknown direct-effect function is now identified jointly.

No, fjf_j is not assumed known. You are correct that the original proof held it fixed and therefore did not exclude transferring effects between direct and hidden components. The revised theorem expressly replaces bridge-only injectivity with joint injectivity and strengthens the conditional measurement assumptions.

For one equation, write X=f(C)+∑kgk(Hk)+ϵX=f(C)+\sum_k g_k(H_k)+\epsilon, center the bridges, and include the intercept in ff. Assume

E[\epsilon\mid H,V,C]=0.$$ For differences in the declared normalized function classes, require $$a(C)+E\left[\sum_k d_k(U_k)\mid V,C\right]=0 \quad\Longrightarrow\quad a(C)=0,\quad d_k(U_k)=0\ \hbox{for all }k.$$ The conditional assumptions imply the observed moment $$E\left[X-f(C)-\sum_k h_k(U_k)\mid V,C\right]=0.$$ Subtracting the moments for two candidate solutions proves simultaneous uniqueness of $f$ and the bridges. The direct function is allowed to change in this argument. Centering removes arbitrary transfers of constants. Hidden support additionally requires the bridge map to be injective at zero. Pairwise independence of the proxy views alone is not sufficient for these strengthened assumptions. For fixed bases, stack all direct and bridge features in $r$, choose instruments $q(V,C)$, and require $G=E[qr^T]$ to have full column rank. Then $E[qX]=G\beta$ identifies all coefficients jointly. The revision establishes this condition for an explicit nonlinear example: $H\sim N(0,1)$, $C=H+\zeta$, $U=H+\eta$, $V=H+\nu$ with mutually independent centered Gaussian noises independent of $H$, an independent mean-zero outcome error of finite variance, and $\operatorname{Var}(\zeta)=\tau^2>0$; both $f(C)$ and $g(H)$ contain unknown linear and centered quadratic terms. For the corresponding centered linear/quadratic features, $G$ has blocks $$1,\qquad \begin{pmatrix}s&1\\1&1\end{pmatrix},\qquad \begin{pmatrix}2s^2&2\\2&2\end{pmatrix},\qquad s=1+\tau^2.$$ The nontrivial determinants are $\tau^2>0$ and $4(s^2-1)>0$. This supplies a concrete joint identification example rather than assuming that bridge uniqueness already identifies $f$. The result remains conditional on an admissible order; no general nonlinear order-learning theorem is asserted. 2. Precision/recall by edge type and exact final-graph errors. We re-aggregated the archived per-graph counts and verified that they reproduce the submitted 40-graph table. The values below pool TP, FP, and FN across graphs; the paper's F1 values average per-graph F1 and therefore use a different aggregation. At proxy-noise SD 1.5: Directed precision/recall: IV 0.992/0.856; OLS 0.811/0.986. Bidirected precision/recall: IV 0.960/0.613; OLS 0.846/0.933. Bow precision/recall: IV 0.974/0.594; OLS 0.526/0.953. At proxy-noise SD 0.35: Directed precision/recall: IV 0.990/0.997; OLS 0.980/0.997. Bidirected precision/recall: IV 0.960/0.995; OLS 0.946/0.995. Bow precision/recall: IV 0.985/1.000; OLS 0.914/1.000. At high noise, IV makes 2 false directed and 5 false bidirected additions, compared with 67 and 33 for OLS. The exact number of graphs with any false final-graph addition is 3/40 versus 30/40; at low noise it is 4/40 versus 8/40. Separately, high-noise false hidden-incidence totals are 3 versus 17. Bow errors overlap edge errors and are not counted again in the final-graph total. We now distinguish the supports $(A,M)$ and the final graph $(A,B)$. Their observed any-error counts happen to agree in this cohort, but this is not automatic. The deterministic relation is $$\{\hbox{false addition to }(A,B)\} \subseteq\{\hbox{false addition to }(A,M)\}.$$ It transfers an upper bound, not an empirical equality.
  1. What differs from multiple-indicator IV?

With the same R,QR,Q, order, split, and tests, nothing differs in the coefficient estimator: it is standard just-identified IV. The revised manuscript states this directly and credits the classical measurement-error/IV construction. Our contribution is the graph formulation and its conditional analysis: include all predecessors without requiring a supplied parent set, infer direct and hidden-incidence support together, induce a bow-capable bidirected layer, and propagate coefficient and order errors into a simultaneous graph guarantee. We do not claim that these results invent IV, Holm correction, or ICA order learning.

The matched OLS control receives the same raw measurements, order, split, and correction, but uses the mean of all five proxies. IV uses a two-proxy regressor view and a three-proxy instrument view. We have corrected the description so it does not imply identical noisy regressors. At the submitted operating point, sparse-order+IV has 40/40 graphs with false support additions, compared with 3/40 for all-predecessor IV; this isolates the importance of using an adequate structural context in addition to correcting measurement error.

We also checked whether the apparent advantage is only a threshold effect. On a new 100-graph learned-order cohort with N=250N=250 and noise SD 1.5, IV at Holm threshold 0.10 has 8/100 false-final-graph additions, directed precision/recall 0.972/0.853, and bidirected precision/recall 0.983/0.639. OLS at 10−610^{-6} has 5/100, 0.983/0.925, and 1.000/0.664, respectively. This is an important limitation: the submitted operating point does not establish dominance over threshold-adjusted OLS.

Keeping that OLS threshold fixed in the known-order sample-size comparison gives 30/100 and 76/100 false-final-graph additions at N=500,1000N=500,1000, versus 3/100 and 5/100 for IV. All threshold curves are reported. These are descriptive comparisons on paired simulations, not independently validated threshold choices. The defensible distinction is the valid structural moment and associated consistency under the measurement assumptions, not universal precision-recall superiority.

We also addressed power with an optional all-proxy moment correction. This classical estimator averages all distinct-indicator cross products; it requires a common, possibly unknown, loading within each group and uncorrelated errors for all distinct indicators, including within-view pairs. We froze it before generating 100 fresh graphs with five proxies, noise SD 1.5, learned order, and a 750/250 split. At the same Holm level 0.10, directed/bidirected F1 improves from 0.903/0.739 for split IV to 0.965/0.920, with 8/100 false-final-graph events for both. The two prespecified paired F1 tests give Holm-adjusted p-values 1.23×10−51.23\times10^{-5} and 1.44×10−111.44\times10^{-11}. Strict OLS at the previously fixed 10−610^{-6} level gives F1 0.964/0.751 and 12/100 false-final-graph events. The proof and all 19 exploratory cells are included. This is a qualified efficiency improvement under stronger assumptions, not new estimation theory or a weak-instrument guarantee.

  1. Additional evidence and limits.

The revision adds 100-replicate calibration cells over N=125,250,500,1000N=125,250,500,1000 and proxy-noise SD 0.35,1.5,3.0, plus small-proxy and assumption-violation tests. With correct order, five proxies and noise SD 1.5, IV directed/bidirected recall increases from 0.575/0.195 at N=125N=125 to 1.000/0.995 at N=1000N=1000, while false-support counts are 1,4,3,5 out of 100. Low-noise counts 14,15,11,10 out of 100 show why the original Wald statement remains asymptotic. Neither HC1 nor Holm makes weak-instrument Wald inference exact.

For an admissible order fixed independently of the inference data, an optional classical projected Anderson--Rubin procedure supplies finite-sample control under independent Gaussian, homoskedastic composite errors independent of the instrument design, but it is highly conservative. At N=250N=250, five proxies and noise SD 1.5, its Gaussian-error directed/bidirected recall is 0.162/0.309, versus 0.894/0.659 for Wald. It is reported as a qualified inference alternative, not a power improvement or a new estimator.

The common-cohort baseline additions use official FCI/RFCI and RCD implementations, and FCI/RFCI also receive all raw proxy columns in an additional comparison. PAG adjacency and endpoint metrics are scored against an exact-DAG PAG reference; they are kept distinct from structural directed/bidirected/bow metrics. These additions strengthen the evaluation without suggesting that all methods identify the same target or use the same measurement assumptions.

We also completed all 40 cases with the official November 2026 FoundCause checkpoint and ten default passes: mean directed/bidirected F1 is 0.622/0.390, with false final additions in 40/40 graphs. Two native outputs have directed cycles; the separate official DAG option gives F1 0.624/0.390. FoundCause receives XX only.

Thank you for the detailed response and additional experiments. I have no further questions.

Thank you for taking the time to review our detailed response and additional experiments.

We appreciate your feedback. Could you please clarify whether our new results and explanations have addressed the main concerns underlying your initial assessment? If so, we would be grateful if you could reconsider your rating in light of the additional evidence. If any significant concerns remain, we would appreciate knowing which ones.

Thank you again for your time and consideration.

Reviewer_xiqZOpenReview ↗
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Paper summary

The paper studies causal discovery when observed variables are affected by both direct causal relationships and unobserved confounders, represented as directed edges Xi→XjX_i \to X_j and bidirected edges Xi↔XjX_i \leftrightarrow X_j. The hidden causes HH are unobserved but with noisy proxy variables. The method splits the proxies into two groups: WW (a noisy explanatory variable) and VV (an instrumental variable). It then regresses XjX_j on all earlier variables in the learned order plus WW, using VV as the instrument for WW (2SLS). Under independent measurement errors, this construction can correct measurement-error bias. The paper proves identification under a correct order, and asymptotic control of false edge additions through a Holm correction.

Critical strengths

Clean and clear linear identification result with a familywise false-edge guarantee.

Critical weaknesses

This paper is incremental. The individual components are largely established.

Strong assumption: every confounder has a proxy group. This is the most unrealistic one. In real problems we rarely know all the confounders, let alone have measured each one several times. Usually we have proxies for the one or two confounders we thought of in advance, and there are others we didn't think of.

Questions for authors
  1. The paper does not adequately demonstrate whether this inference is reliable in finite samples, particularly when proxies are noisy or instruments are weak.

  2. Potential gap in the proof of Theorem 3. The proof uses E[gkj(Hk)−hkj(Uk)∣V,Cj]=0\mathbb{E}[g_{kj}(H_k) - h_{kj}(U_k) \mid V, C_j] = 0. However, conditional independence of the proxy views given HkH_k alone does not guarantee this equality once we also condition on CjC_j; additional conditional-independence assumptions seem necessary. In addition, the proof assumes fjf_j is the same across candidate solutions. Can you show joint identification of the unknown fj(Cj)f_j(C_j) and the bridge functions?

4 comments

Thank you for recognizing the clear linear identification result. We agree that the original nonlinear theorem was incomplete and that the empirical claim needed stronger finite-sample evidence. The revision corrects the theorem, adds calibration and assumption-violation experiments, and narrows the performance claim.

  1. Contribution and scope.

Using indicators with independent measurement errors as instruments and just-identified IV estimation are classical. With the same regressor matrix, instruments, order, and tests, our coefficient estimator is standard IV. Our contribution is its use in a graph-discovery procedure that does not require known parent sets: estimate all forward direct coefficients and hidden-cause incidences jointly, construct a separate bidirected layer from shared incidences, allow bows, and connect simultaneous support selection to an independently learned order. The order and measurement assumptions are part of the result. The revised nonlinear result is conditional identification with an explicit joint-rank example, not a general nonlinear discovery guarantee.

The all-predecessor design matters empirically: the submitted high-noise comparison has false direct/incidence additions in 40/40 graphs for sparse-order+IV and 3/40 for all-predecessor IV. This supports the structural regression design, rather than a new IV estimation principle. We also now report official causal-discovery implementations on the same 40-graph cohort, including FoundCause and FCI/RFCI with raw proxies, rather than relying on OLS alone.

  1. Must all confounders have proxies?

The required restriction is that omitted contributions must not invalidate the moments. It is not enough to define the reported bidirected graph using only supplied proxy groups. If an omitted common cause contributes LL to an equation and E[QjL]≠0E[Q_jL]\ne 0, direct effects and incidences can both be biased. The revised setup states this explicitly. Independent node-specific disturbances remain allowed, and an absent bidirected edge cannot certify absence of unmeasured confounding.

We tested this directly on 100 new graphs per noise level, using a known admissible order to isolate the measurement assumptions. Removing one proxy group while retaining its hidden cause in the data-generating equations increases IV false-final-graph additions from 3/100 to 77/100 at noise SD 1.5; 68/100 graphs then contain a false directed edge. The retained-root incidence/bidirected target and the full confounding target are scored separately. Thus these experiments demonstrate the consequence of incomplete confounder coverage; they do not establish robustness to it. The intended application remains a scientifically justified repeated-measurement setting.

  1. Finite-sample reliability and weak proxies.

We added a fixed simulation grid with 100 graph/data replicates per cell, balanced between random and collider graphs. The existing HC1 standard errors and Holm level 0.10 are unchanged. Four inference sample sizes, three noise levels, and a two-proxy stress case are evaluated. Known-order experiments isolate coefficient inference; separate learned-order experiments use 750 development and 250 inference rows. All unfavorable settings are retained.

With five proxies and noise SD 1.5, the known-order results are:

N=125N=125: IV/OLS false-support graphs 1/100 versus 57/100; IV directed/bidirected recall 0.575/0.195.

N=250N=250: 4/100 versus 74/100; recall 0.864/0.632.

N=500N=500: 3/100 versus 96/100; recall 0.982/0.923.

N=1000N=1000: 5/100 versus 100/100; recall 1.000/0.995.

Here support means (A,M)(A,M) and recall pools edge counts. Average marginal 95%95\% coefficient coverage for IV is 0.973, 0.967, 0.959, and 0.956, respectively; the corresponding OLS values are 0.782, 0.752, 0.723, and 0.707. These results distinguish estimation consistency from a favorable threshold choice.

With the learned order at N=250N=250, noise SD 1.5, IV has 8/100 false-support graphs versus 76/100 for OLS, and 8/100 false-final-graph additions versus 74/100. The order is admissible in 96/100 graphs. IV marginal coverage is 0.960 versus 0.744, with directed/bidirected recall 0.853/0.639 versus 0.985/0.946. The Wilson 95%95\% interval for IV's 8/100 rate is [0.041,0.150]; this is Monte Carlo evidence, not a finite-sample guarantee.

The limitations are substantial. At noise SD 3.0 and N=250N=250, five-proxy IV with the correct order has directed/bidirected recall 0.315/0.002. The median minimum residualized cross-view canonical correlation drops from 0.822 at noise SD 0.35 to 0.183 at 1.5 and 0.030 at 3.0. Low false-addition rates and wide intervals do not imply useful recovery. At low noise, known-order IV false-support counts are 14,15,11,10 out of 100 as NN increases; the first three point estimates exceed 0.10. The submitted semi-synthetic result also has 5/20 false-support graphs. We therefore retain the asymptotic scope of the original Wald guarantee.

We additionally implemented classical projected Anderson--Rubin tests (Dufour and Taamouti, 2005), projecting over all nuisance hidden coefficients before Holm correction. For an admissible order fixed independently of the inference data, under the extra assumption of independent Gaussian, homoskedastic composite errors independent of the instrument design, the full-vector F pivot and projection argument give finite-sample control without an instrument-strength condition. This is an optional classical inference procedure, not a new estimator or a correction of invalid instruments. In 200 known-order Gaussian-error graphs at noise SD 1.5, five proxies, and N=250N=250, its false-support rate is 2/200, but directed/bidirected recall is only 0.162/0.309, versus 0.894/0.659 for Wald. Laplace-error experiments are reported separately and do not receive the exact Gaussian guarantee.

Finally, we tested whether stricter OLS thresholds can reproduce the precision advantage. On the new learned-order high-noise cohort, OLS at Holm threshold 10−610^{-6} has 5/100 false-final-graph additions versus 8/100 for IV at 0.10, and better directed/bidirected precision and recall. We disclose this result and make no claim that IV dominates the entire precision-recall curve. Holding that OLS threshold fixed in the known-order sample-size study gives 30/100 and 76/100 false-final-graph additions at N=500,1000N=500,1000, versus 3/100 and 5/100 for IV. These are descriptive sensitivity comparisons, not thresholds selected and validated on independent cohorts.

We also addressed power with an optional all-proxy moment correction. This classical estimator averages all distinct-indicator cross products; it requires a common, possibly unknown, loading within each group and uncorrelated errors for all distinct indicators, including within-view pairs. We froze it before generating 100 fresh graphs with five proxies, noise SD 1.5, learned order, and a 750/250 split. At the same Holm level 0.10, directed/bidirected F1 improves from 0.903/0.739 for split IV to 0.965/0.920, with 8/100 false-final-graph events for both. The two prespecified paired F1 tests give Holm-adjusted p-values 1.23×10−51.23\times10^{-5} and 1.44×10−111.44\times10^{-11}. Strict OLS at the previously fixed 10−610^{-6} level gives F1 0.964/0.751 and 12/100 false-final-graph events. The proof and all 19 exploratory cells are included. This is a qualified efficiency improvement under stronger assumptions, not new estimation theory or a weak-instrument guarantee.

  1. Corrected nonlinear identification.

You are correct on both proof issues. Pairwise view independence given HkH_k does not justify conditioning additionally on CC and the full VV. Also, uniqueness with ff fixed does not establish joint identification. We replaced the theorem and proof rather than treating these as notational omissions.

Write X=f(C)+∑kgk(Hk)+ϵX=f(C)+\sum_k g_k(H_k)+\epsilon. Center the bridges and place the intercept in ff. The revised sufficient conditions include E[hk(Uk)∣H,V,C]=gk(Hk),E[ϵ∣H,V,C]=0.E[h_k(U_k)\mid H,V,C]=g_k(H_k),\qquad E[\epsilon\mid H,V,C]=0. For example, the first equality follows from the bridge equation and UkU_k independent of (H−k,V,C)(H_{-k},V,C) given HkH_k. For differences within the specified normalized function classes, require

\quad\Longrightarrow\quad a(C)=0,\quad d_k(U_k)=0\ \hbox{for every }k.$$ The strengthened conditional assumptions give $$E\left[X-f(C)-\sum_k h_k(U_k)\mid V,C\right]=0.$$ Subtracting this equation for two candidate solutions gives the joint condition above, proving uniqueness of the unknown $f$ and all bridges together. Hidden-support identification additionally requires the bridge map $h\mapsto E[h(U_k)\mid H_k]$ to be injective at zero. The assumptions are stronger than the original statement, and this correction is acknowledged explicitly. The revision also gives a nonvacuous quadratic example. Let $H\sim N(0,1)$, $C=H+\zeta$, $U=H+\eta$, and $V=H+\nu$, with mutually independent centered Gaussian noises independent of $H$, an independent mean-zero outcome error of finite variance, and $\operatorname{Var}(\zeta)=\tau^2>0$. Set $s=1+\tau^2$, $s_U=\operatorname{Var}(U)$, and $s_V=\operatorname{Var}(V)$. Allow unknown $$f(C)=\theta_0+\theta_1C+\theta_2(C^2-s),\qquad g(H)=\lambda_1H+\lambda_2(H^2-1).$$ The bridge is $h(U)=\lambda_1U+\lambda_2(U^2-s_U)$. For $r=(1,C,U,C^2-s,U^2-s_U)^T$ and $q=(1,C,V,C^2-s,V^2-s_V)^T$, $E[qr^T]$ has an intercept block 1 and blocks $$\begin{pmatrix}s&1\\1&1\end{pmatrix},\qquad \begin{pmatrix}2s^2&2\\2&2\end{pmatrix}.$$ Their determinants are $\tau^2$ and $4(s^2-1)$, both positive. Thus all direct and hidden quadratic coefficients are jointly identified despite noisy proxies. This verifies the condition for a concrete class; it does not claim arbitrary nonlinear channels satisfy it. The linear theorem does not rely on the corrected nonlinear proof.

Thank you for response and additional experiment. I have raised my score accordingly.

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