- Rating
- 3(+1)
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 3
- Soundness
- 2
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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
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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.
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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
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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.
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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
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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.
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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
- 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 only.
We additionally ran FCI/RFCI on 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 high-noise cohort, OLS at Holm threshold 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 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.
- 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 for two proxies and for three, compared with for five. Fewer noisy measurements can severely reduce power.
We extended the submitted 40-graph order study to full graph recovery with , 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:
: 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.
: 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:
: 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.
: 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 , 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 and . Strict OLS at the previously fixed 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.
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.
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]=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+L, γk=λk/ak, D=E[νηT], and nonsingular G=E[QRT], 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.