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Under review as a conference paper at ICLR 2027

When Is It Safe to Borrow Across Treatments? Target-Aware Learning for Combinatorial Interventions

Abstract

Combinatorial interventions create an exponential treatment space from a modest number of components. The resulting sparsity motivates cross-treatment borrowing, but smoothing between neighboring bundles can attenuate interactions of interest. We introduce Treatment-Space Graph Selection (TSGS), which separates an immutable graph of feasible interventions from a target-indexed graph used only for statistical borrowing. The outcome surface is decomposed into prespecified structured variation and its orthogonal complement; only the latter is graph-regularized, and the graph and penalty are selected by an independent augmented inverse-propensity-weighted score for the desired contrast family. Our theory gives (i) an exact finite-sample contrast-risk decomposition, (ii) a sharp characterization of uniform dominance over all zero-sum causal contrasts by Loewner ordering on the contrast subspace, (iii) a Boolean spectral theorem explaining why edge effects and interaction effects weight the same smoothing error differently, and (iv) a finite-candidate oracle inequality. In projected graph-sequence experiments across 36 independently simulated support–roughness regimes, TSGS beats no borrowing in every cell, whereas indiscriminate full-graph smoothing is significantly harmful in five rough regimes; edge and synergy targets select different rules in 65.8% of repetitions. In the randomized ACTG 175 trial, target-selected borrowing reduces held-out contrast score by 0.7–1.7% relative to no borrowing across five clinical targets. The central conclusion is that treatment geometry specifies feasible interventions, but borrowing rules should be selected for the causal contrasts of interest.

Primary area:
causal reasoning
Keywords:
causal inference, structured treatments, bundle treatments, graph regularization, causal model selection

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_9KVeOpenReview ↗
Rating
4(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper presents Treatment-Space Graph Selection (TSGS), a framework for improving causal effect estimation in large, sparse combinatorial treatment spaces. Comparison methods smooth outcomes indiscriminately across similar treatments while TSGS instead selects information-sharing structures adaptively, guided by the causal contrasts of interest, so that meaningful treatment interactions are preserved. The framework decouples treatment feasibility from statistical borrowing and comes with theoretical guarantees. Across simulated settings, the author claimed that TSGS consistently outperforms no borrowing.

Critical strengths

The paper addresses an important problem in causal inference with combinatorial treatments, where the exponentially growing treatment space creates substantial data sparsity. The proposed TSGS framework offers an interesting perspective by distinguishing treatment feasibility from statistical information sharing and adapting the borrowing strategy to the causal contrasts of interest.

Critical weaknesses

The empirical analysis in the main paper is somewhat limited. I encourage the authors to provide more detailed insights into why the proposed method works, particularly in comparison with alternative approaches for combining information across treatments. A deeper discussion of the factors driving the observed performance differences would help strengthen the empirical evaluation.

Questions for authors
  1. For the real time evaluation, the ACTG 175 experiment provides useful evidence, but more details about the dataset, treatment combinations, and data sparsity would be helpful. Could the authors provide additional real-world evaluations or discuss the practical significance of these gains? Also, any evaluations to confirm the combination structure makes sense?

  2. How does TSGS perform when neighboring treatment combinations have substantially different effects or strong interactions? Could the authors include simulations on an ablation study varying treatment-effect heterogeneity to investigate when information borrowing becomes harmful and whether TSGS can adaptively avoid it?

  3. The experimental analysis could provide more insight into why competing methods underperform. Are the differences mainly driven by oversmoothing, or treatment sparsity? A more detailed comparison and component-wise ablation would help clarify the sources of improvement.

7 comments
AuthorsOpenReview ↗

Response to 9KVe — Part 1/7: External comparisons and selective borrowing

Our response is split into seven comments because of the character limit.

Q: [W1 — Critical Weakness] What explains the gains over other cross-treatment sharing methods?

A: TSGS beats all five original external baselines on both edge and square PEHE in the rough R2 benchmark. The original matched FullVal and target-alignment experiments show why: selecting where to borrow and which contrast to validate changes risk beyond simply tuning graph-penalty strength. Theorem 4.1 exposes the target-specific bias–variance cost of the chosen graph; Appendix H adds controlled edge-placement and penalty-location comparisons. The explanation is strongest where compatible and incompatible treatment relations coexist.

Original — comparisons with treatment-sharing methods (Tables 1 and 4). R1 and R2 use six binary components and 64 bundles. R1 has relatively smooth complementary variation; R2 introduces localized rough transitions, with 12 jump edges among 192 one-component geometry edges. This tests whether sharing can remain useful while preserving difficult local contrasts.

The first five baselines and TSGS were in the original submission; POUL is an Appendix H.2 adaptation added for this discussion. Results are edge/square PEHE, mean ± seed-level SE over seeds 201–210 (lower is better). We show R2 first because it tests selective borrowing across locally incompatible treatment relations:

R2 — localized rough transitions (primary advantage).

MethodEvidence sourceEdge PEHE ↓Square PEHE ↓
MultiHotMLPOriginal0.6961±0.00930.6961\pm0.00930.9987±0.01020.9987\pm0.0102
SharedBundleHeadOriginal0.4926±0.00430.4926\pm0.00430.6742±0.00750.6742\pm0.0075
SCPOriginal0.7299±0.00240.7299\pm0.00241.0295±0.00261.0295\pm0.0026
SIN-vectorOriginal0.5966±0.01700.5966\pm0.01700.6991±0.02040.6991\pm0.0204
VSROriginal0.4539±0.02970.4539\pm0.02970.5629±0.05320.5629\pm0.0532
POUL adaptationAdded, H.20.7364±0.00350.7364\pm0.00351.0340±0.00331.0340\pm0.0033
TSGSOriginal0.3292±0.00390.3292\pm0.00390.3670±0.00540.3670\pm0.0054

R1 — smooth complementary variation (cross-regime check).

MethodEvidence sourceEdge PEHE ↓Square PEHE ↓
MultiHotMLPOriginal0.1853±0.00090.1853\pm0.00090.1620±0.00130.1620\pm0.0013
SharedBundleHeadOriginal0.4738±0.00670.4738\pm0.00670.6442±0.01110.6442\pm0.0111
SCPOriginal0.2564±0.00230.2564\pm0.00230.2246±0.00350.2246\pm0.0035
SIN-vectorOriginal0.4105±0.00680.4105\pm0.00680.2866±0.00400.2866\pm0.0040
VSROriginal0.2550±0.00220.2550\pm0.00220.1838±0.00390.1838\pm0.0039
POUL adaptationAdded, H.20.2111±0.00220.2111\pm0.00220.1711±0.00110.1711\pm0.0011
TSGSOriginal0.2751±0.00430.2751\pm0.00430.2389±0.00340.2389\pm0.0034

Appendix F.2 documents the original implementations, including SIN-vector, the binary-vector adaptation of the generalized Robinson method in Causal Effect Inference for Structured Treatments.

Added — extended comparison (Appendix H.2). The POUL adaptation retains joint component/off–on embeddings, a nonlinear map after aggregation, a frozen nuisance in the orthogonalized stage and exact covariate-dependent centering under known assignment probabilities. Its architecture and training protocol were fixed before evaluation on the original generators: 3,000/3,000 training/validation observations, 5,000 evaluation covariates and seeds 201–210, followed by a separate two-stage refit.

In R2, TSGS lowers mean edge and square PEHE by 55.3% and 64.5% relative to this adaptation; the within-seed POUL-minus-TSGS edge-PEHE difference is +0.407205±0.005259+0.407205\pm0.005259, favoring TSGS in all ten seeds. POUL is better in smooth R1. The matched ablations below test the design choices directly.

Revision. Section 5.1 retains the original rough-regime and matched FullVal comparisons; Appendix H.2–H.3 supplies the POUL results and matched mechanism controls. The causal estimands and TSGS algorithm remain those of the submitted manuscript.

AuthorsOpenReview ↗

Response to 9KVe — Part 2/7: ACTG treatment structure and clinical contrasts

Q: [Q1 — Question for Authors] What treatments and support does ACTG contain, is the combination structure meaningful, and what practical evidence supports it?

A: The ACTG 175 study supplies four randomized regimens and three directly interpretable one-drug addition comparisons, scored across 100 prespecified held-out splits. The feasibility graph follows observed intervention composition, and the reference-span projection keeps shared treatment structure distinct from borrowable contrasts. Appendix H extends practical evaluation to measured five-component laboratory combinations. The combination structure is justified at three levels: intervention semantics defines valid comparisons, the protected function space states which variation is not directly graph-penalized, and held-out target evaluation tests whether borrowing is useful.

Original — ACTG cohort and geometry (Appendix F.15). The public ACTG 175 analysis comprises 2,139 participants, with week-20 CD4 change as the outcome:

Assigned regimenNumber of participants
AZT532
AZT + ddI522
AZT + ddC524
ddI561

Figure 11(A) depicts the three valid one-drug additions: AZT→AZT+ddI, AZT→AZT+ddC, and ddI→AZT+ddI. These edges follow treatment composition and have straightforward domain interpretations; their inclusion does not assume the corresponding effects are equal. Four randomized arms do not form a complete Boolean square, so we do not report a synergy requiring unassigned combinations. F.15 documents the data version, baseline feature construction, randomization propensity, graph/penalty choices and independent scoring protocol. With approximately 500 subjects per arm, ACTG is not an extreme-sparsity benchmark; scarce direct support is tested separately by H1 and F.13.

Structural rationale in the original model. The fixed geometry GgeomG_{\mathrm{geom}} encodes feasible intervention comparisons. The statistical borrowing graph GborG_{\mathrm{bor}} is chosen separately, because a scientifically meaningful comparison need not be suitable for smoothing. The prespecified dictionary B0B_0 gives a transparent regularization preference, not a claim that the outcome surface is confined to that dictionary: μ=P0πμ+Q0πμ\mu=P_0^\pi\mu+Q_0^\pi\mu retains all complementary variation.

ACTG specifically uses B0=14B_0=\mathbf1_4, rather than the full-cube degree-two dictionary. With b0=14/2b_0=\mathbf1_4/2 and a three-dimensional orthonormal contrast basis UU, the fitted arm-by-feature coefficients satisfy

\operatorname{tr}(H^\top L_GH) =\operatorname{tr}\{\Gamma(U^\top L_GU)\Gamma^\top\}.$$ Since $L_Gb_0=0$, the shared covariate-dependent treatment component is unpenalized by the graph term, while the three-dimensional treatment-contrast complement is eligible for smoothing (F.15). This gives the prior function family a precise role, without stipulating that the biological effects must be smooth. **Original — held-out clinical contrasts (Table 25).** The 100 original stratified ACTG splits evaluate different borrowing rules using the same clinical outcome features and scoring protocol. Table 25 reports: | Clinical contrast family | NoGraph | PredictiveCV | TSGS | TSGS wins among splits | |---|---:|---:|---:|---:| | All local additions | 110,487 | 109,171 | 108,987 | 86% | | Add ddI to AZT | 112,764 | 112,354 | 111,961 | 70% | | Add ddC to AZT | 89,899 | 88,535 | 88,479 | 89% | | Add AZT to ddI | 128,798 | 126,626 | 126,627 | 76% | | Combination vs. monotherapy | 54,674 | 53,973 | 53,922 | 79% | These are held-out conditional-contrast scores, not clinical-effect SEs. [Figure 11(B,D)](https://anonymous.4open.science/r/treatment-figures-review-630D/figure_11.png) connects target-dependent selected rules with held-out score differences, and Figure 11(C) shows the randomized clinical contrasts. PredictiveCV closely matches TSGS on individual targets. This directly supports target-conditioned statistical borrowing on the observed regimen geometry; the scientific structure is specified independently of outcome fitting.
AuthorsOpenReview ↗

Response to 9KVe — Part 3/7: Additional real-world evaluations

A (continued — Q1):

Added — measured combinations (Appendix H.5, Table 33). We analyzed the published in-vitro combination-growth measurements of Lozano-Huntelman et al. (2021): 56 five-component panels, 243 dose contexts per panel, three technical repetitions, and 31 measured nonempty combination nodes. The observed structure contains 75 activation edges, 70 complete squares, and five four-to-five-component terminal additions. The degree-two dictionary has rank 16 and a rank-15 complement. This additional application uses the projected-sequence/linear TSGS specialization on observed laboratory growth measurements. Train/validation/test roles retain physical-well identity to avoid duplicate-well leakage.

The prespecified terminal decision is whether to add the fifth component. The actual held-out measured-growth results are:

MethodTerminal contrast MSE ↓Local growth reduction (pp) ↑
Raw NoGraph0.11753412.672
Target-tuned complement ridge0.10978012.565
Predictive-tuned complement ridge0.11015612.542
LowOrder0.12150811.755
FullVal0.10954612.578
PredictiveCV0.10988412.534
TSGS0.10862812.612
Same-density RandomGraphVal0.10958012.586
TotalSurfaceVal0.10681412.703

TSGS's local-gain increment is +0.0338+0.0338 pp over FullVal (exploratory date-cluster interval [0.0009,0.0696][0.0009,0.0696]) and +0.0780+0.0780 pp over PredictiveCV ([0.0184,0.1482][0.0184,0.1482]). Raw NoGraph and TotalSurfaceVal achieve higher mean local gains. All-edge MSE is nearly tied between TSGS and PredictiveCV. The increments over tuned controls are therefore small; these are measured laboratory growth outcomes with repeated technical measurements rather than patient clinical endpoints.

Added — ACTG decisions (Appendix H.4). A separate out-of-fold policy check estimates a local CD4 gain of 43.144 cells/mm$^3$ for TSGS, against 42.861 for FullVal and 42.697 for PredictiveCV; a training-mean fixed policy obtains 46.891. The values are out-of-fold AIPW policy estimates under a separate protocol, with the fixed-policy comparator retained.

Revision. The revised §2–§3 clarifies scientific edges and the protected function space; the original F.15 remains the primary ACTG protocol. Appendix H adds the distinct measured-combination and policy checks, including stronger comparators and their limits. Scientific plausibility of a comparison and statistical usefulness of borrowing are kept separate.

Reviewer_i6fSOpenReview ↗
Rating
3(+2)
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

This paper tackles combinatorial treatment problem where there is limited data for each treatment. They propose to solve this by separating an immutable graph of feasible interventions from a target-indexed graph used only for statistical borrowing.

Critical strengths

None

Critical weaknesses

To be honest, this paper is extremely convoluted and hard to read. Undefined concepts and phrases appear at multiple locations in the paper, throughout the paper. Examples include 'valid activation edge' (line 148) 'E_geom' (line 148) 'square-face synergies' (line 160) 'esidual branch ' (line 221) 'oriented geometry edge' (line 242) 'covariant trunk' (line 270); 'it satisfies the required overlap condition' (line 187) - no overlap condition was clearly stated earlier in the section, etc...

For this reason, it's not possible for me to judge the motivation and correctness of the paper.

Questions for authors

None

5 comments
AuthorsOpenReview ↗

Response to i6fS — Part 1/4: Original definitions (activation edges and synergies)

Our response is split into four comments because of the character limit.

For each cited term, we give its original definition or formula and the corresponding revised location. Line numbers refer to those printed in the respective PDFs.

Q: [W1.1, reviewer cites original line 148] Where was “valid activation edge” defined, and what effect does it define?

A: Original submission (§2, lines 141–150 and 155–156). The feasible edge set was defined immediately above (lines 141–146). The contextual-effect paragraph then stated:

“For a valid activation edge (a,a+ej)∈Egeom(a,a+e_j)\in E_{\mathrm{geom}}, where eje_j is the jjth standard basis vector, define”

τa,j(1)(x)=Δjμ(x,a):=μ(x,a+ej)−μ(x,a).\tau^{(1)}_{a,j}(x)=\Delta_j\mu(x,a):=\mu(x,a+e_j)-\mu(x,a).

The original also specified the activation direction at lines 155–156:

Ej={(a,a+ej)∈Egeom:aj=0}.E_j=\{(a,a+e_j)\in E_{\mathrm{geom}}:a_j=0\}.

Thus the original gives both the finite-difference effect (line 150) and the condition that component jj is initially inactive (line 155). Revised manuscript (§2, lines 149–159): we put aj=0a_j=0 directly into the first defining sentence (lines 149–151) and state explicitly that the edge contrast is a contextual CATE (lines 156–159). The interpretation is unchanged: add component jj at a feasible background aa, keeping xx and all other components fixed.

Q: [W1.2, reviewer cites original line 148] Where was EgeomE_{\mathrm{geom}} defined, and how is it different from the borrowing graph?

A: Original submission (§2, lines 141–146):

“The graph Ggeom=(Af,Egeom)G_{\mathrm{geom}}=(A_f,E_{\mathrm{geom}}) contains scientifically valid one-component transitions: (a,b)∈Egeom(a,b)\in E_{\mathrm{geom}} only if a,b∈Afa,b\in A_f and ∥a−b∥0=1\|a-b\|_0=1, after removing domain-invalid toggles when needed.”

The next sentence states that geometry is fixed by intervention feasibility and semantics, not by outcomes or empirical support. The original §3 opening (lines 201–204) separately specified that the learner regularizes the complementary component over Gbor⊆GgeomG_{\mathrm{bor}}\subseteq G_{\mathrm{geom}} and chooses the borrowing rule by target-specific AIPW validation. Revised manuscript: the geometry definition remains at §2, lines 142–147, and the borrowing-graph distinction is reiterated in §3, lines 205–208. EgeomE_{\mathrm{geom}} specifies meaningful intervention comparisons; EborE_{\mathrm{bor}} specifies the subset on which statistical smoothing is applied. Selecting a sparser borrowing graph does not discard an otherwise identified contrast.

Q: [W1.3, reviewer cites original line 160] Were square-face synergies defined in the original paper?

A: The original submission defines square-face synergy immediately after the edge effect (§2, lines 151–154):

“when the four required vertices are feasible, define the square-face synergy”

\tau^{(2)}_{a,jk}(x)=\Delta_j\Delta_k\mu(x,a) ={}&\mu(x,a+e_j+e_k)-\mu(x,a+e_j)\\ &-\mu(x,a+e_k)+\mu(x,a). \end{aligned}$$ Original lines 154–161 further explain that $x$ stays fixed and that $C_{\mathrm{sq}}$ stacks the feasible square contrasts. **Revised manuscript (§2, lines 153–157):** the four-cell equation is retained, and lines 156–157 explicitly explain it as a *difference between two contextual CATEs across treatment backgrounds*. The four required vertices must be feasible and, for causal identification, overlap-safe. This makes the interpretation visible next to the original mathematical definition.
AuthorsOpenReview ↗

Response to i6fS — Part 2/4: Original definitions (residual branch and overlap)

For W1.4–W1.7, the original submission gives the residual branch in lines 266–269, the edge orientation in lines 241–250, the shared encoder in lines 213–215 and 270, and the overlap condition in lines 132–139.

Q: [W1.4; reviewer cites original line 221] What is the residual branch, and why was its definition hard to follow?

A: Original submission: §3.1 line 221 first refers to “a flexible residual branch,” after introducing the structured head but before defining the complementary projection. The raw signal was actually parameterized later in §3.2, lines 266–269:

“let rϑ(x)∈RKr_\vartheta(x)\in\mathbb R^K be a raw feasible-node signal parameterized by neural parameters ϑ\vartheta”

The same original passage defines μ^comp(x)=Q0πrϑ(x)\widehat\mu_{\mathrm{comp}}(x)=Q_0^\pi r_\vartheta(x) and the complete predictor. We agree the raw signal should have been defined at the first mention. We have moved that definition to revised §3.1, lines 226–228, where the text now states:

“We parameterize this branch by a raw node vector rϑ(x)∈RKr_\vartheta(x)\in\mathbb R^K.”

Revised §3.2, lines 273–276, retains the projected output and full predictor:

\widehat\mu(x,a)=\phi_0(a)^\top g_0(\Phi_X(x))+[Q_0^\pi r_\vartheta(x)]_a.$$ At a fixed covariate profile $x$, the raw branch gives one value per bundle. The projection removes the part the structured head can already represent. The graph penalty acts on differences between the remaining values along the selected edges. Here *residual* denotes the complementary function component, rather than the observed response residual. The model and objective are unchanged. **Q: [W1.5; reviewer cites original line 242] Where was “oriented geometry edge” defined?** **A:** **Original submission (§3.2, lines 241–250)** states: > “For an oriented geometry edge $e=(a,b)$, define $\Delta_e f:=f(b)-f(a)$” It immediately gives $\tau_e(x)=\mu(x,b)-\mu(x,a)$ and the complementary edge difference $\delta_e(x)$. The same section defines an **undirected** weighted borrowing graph and its Laplacian (original lines 247–250). **Revised manuscript (§3.2, lines 247–256)** retains these definitions and adds “fixing the difference sign” at line 248. Orientation therefore sets the *sign* of the effect contrast; the graph penalty is a weighted sum of squared differences and is invariant to reversing an edge. **Q: [W1.6; reviewer cites original line 270 as “covariant trunk”] Where was the trunk introduced?** **A:** The original term is *covariate trunk*. **Original submission (§3.1, lines 213–215)** already defines the shared encoder: > “Let $\Phi_X:\mathcal X\to\mathbb R^{d_z}$ be the shared covariate encoder and $g_0:\mathbb R^{d_z}\to\mathbb R^{p_0}$ the structured head.” The later sentence at **original §3.2, line 270** reads: > “The branches may share the covariate trunk; output-space projection enforces functional separation.” Thus *trunk* refers to the already-defined $\Phi_X$, not to a separate module. **Revised manuscript (§3.1, lines 216–219; §3.2, lines 277–278):** we consistently use “shared covariate encoder $\Phi_X$,” replacing the informal trunk wording at the later mention. This is a terminology clarification, not an architectural change. **Q: [W1.7; reviewer cites original line 187] Was the overlap condition stated before the identification theorem?** **A:** The overlap condition appears before Theorem 2.1: original §2 defines the bundle propensity $e_a(x)=P(A=a\mid X=x)$ and overlap-safe support (lines 131–133), then imposes the support condition in Assumption 2.1 (lines 136–139): $$A_{s,\eta}=\{a\in A_s:e_a(X)\ge\eta\quad P_X\text{-a.s.}\},\qquad\eta>0.$$ In particular, original Assumption 2.1 states: > “(iii) identified validation and causal reporting use only contrasts supported on $A_{s,\eta}$.” Theorem 2.1 at original lines 184–187 uses that assumption to identify a finite-difference contrast when each required bundle vertex meets the overlap condition. **Revised manuscript (§2, lines 132–140; Theorem 2.1, lines 187–190):** the same support restriction remains explicit in Assumption 2.1, and the theorem now refers directly to $A_{s,\eta}$ and Assumption 2.1 rather than saying only “the required overlap condition.” The explanatory paragraph at revised lines 195–198 distinguishes strict positivity for point identification from the stronger uniform floor used for stable AIPW validation.
AuthorsOpenReview ↗

Response to i6fS — Part 3/4: Scientific motivation and method

Q: [W1.8] What is the scientific motivation, nontrivial mathematical contribution, and correctness argument?

A: Scientific question. Given limited direct information for many feasible bundles, which treatment relations should share statistical information to estimate a specified conditional causal contrast accurately? The target may be the effect of adding one component, a square-face interaction, or another prespecified zero-sum contrast. Those are already defined in §2, before the learner or graph penalty.

The fundamental tension. Pooling information reduces variance when neighboring bundles have compatible outcome variation, but can introduce bias across genuine local changes. Scientific adjacency does not imply statistical compatibility: all one-component cube edges have the same Hamming distance, while their complementary differences may be very different. There is also a target conflict: estimation errors may cancel under one signed contrast and reinforce under another. Thus neither a single similarity graph nor generic factual-prediction accuracy is automatically optimal for every causal question.

Added explanation — a numerical example (Appendix H.1). Fix xx and consider

μ(a)=a1+2a2+4a3+4a1a2a3.\mu(a)=a_1+2a_2+4a_3+4a_1a_2a_3.

(a1,a2)(a_1,a_2)μ(a1,a2,0)\mu(a_1,a_2,0)μ(a1,a2,1)\mu(a_1,a_2,1)
(0,0)04
(1,0)15
(0,1)26
(1,1)311

The effect of adding component 1 is 11 from (0,0,0)(0,0,0) but 55 from (0,1,1)(0,1,1). The square effect for components 1 and 2 is 00 with component 3 absent and 44 with it present. These are different treatment backgrounds at fixed xx; covariate heterogeneity arises additionally when the contrasts vary with xx.

In the a3=0a_3=0 column, the two gains from adding component 1 are 1−0=11-0=1 and 3−2=13-2=1, so their difference is zero. In the a3=1a_3=1 column, the gains are 5−4=15-4=1 and 11−6=511-6=5. Each addition changes just one bit, so the Euclidean distance between the two bundles is always 1. Suppose the gains in this last column were estimated as 2 and 6. Both edge effects would be one unit too high, yet the estimated square synergy would still be exactly right, 6−2=46-2=4.

Original method — the role of each construction. The scientific graph first records feasible comparisons; it is not learned from outcomes. A prespecified dictionary B0B_0 then identifies a functional span to protect from direct graph penalization. With reference weights WπW_\pi,

P0π=B0(B0⊤WπB0)−1B0⊤Wπ,Q0π=I−P0π.P_0^\pi=B_0(B_0^\top W_\pi B_0)^{-1}B_0^\top W_\pi,\qquad Q_0^\pi=I-P_0^\pi.

Proposition 3.1 gives the unique functional decomposition f=P0πf+Q0πff=P_0^\pi f+Q_0^\pi f with B0⊤WπQ0πf=0B_0^\top W_\pi Q_0^\pi f=0 under its rank condition. The default Boolean span contains intercept, singleton and pairwise terms: degree two is the smallest explicit polynomial order with nonzero pairwise square differences. The complement retains higher-order departures, so the full outcome model remains expressive beyond the protected degree-two span. For constrained feasible spaces, a full-rank basis of the same span defines the same projection.

A training-only NoGraph pilot next ranks complementary edge differences and builds a finite nested graph family. Factual candidate fits and the validation nuisance use training data. Independent, target-specific AIPW validation selects the graph and penalty, which are frozen for refit. The graph acts through a complementary output-space penalty, and selection uses observed training/validation data. Figure 2 displays the two output branches and selection procedure together.

Reviewer_w6EVOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes Treatment-Space Graph Selection (TSGS) for cross-treatment borrowing in combinatorial interventions. The key idea is to separate treatment geometry from statistical borrowing by first specifying the causal contrasts of interest and then selecting borrowing rules accordingly. This helps prevent borrowing from oversmoothing or distorting the treatment effects and interactions of interest. The authors establish theoretical guarantees and demonstrate the benefits of the proposed method through simulations and a real-data application.

Critical strengths

The paper proposes a general and flexible graph-based framework that provides a useful way to distinguish scientific targets from statistical borrowing. I particularly appreciate the idea of aligning borrowing strategies with the causal questions of interest, rather than allowing the borrowing structure to determine which effects are preserved. The theoretical development is also rigorous, with core algebraic results independently machine-checked in Lean 4.

Critical weaknesses

In the ACTG 175 application, the improvement in held-out contrast scores is relatively modest (0.7–1.7%). I wonder how these improvements translate into gains in estimation precision or statistical power. It would also be helpful to understand under what conditions more substantial efficiency gains can be expected.

Questions for authors

Could the authors elaborate further on the impact of the proposed borrowing framework on downstream tasks, such as heterogeneous treatment effect (HTE) estimation and individualized treatment rule (ITR) learning, compared with methods without borrowing or with alternative borrowing strategies? It would be interesting to see whether the gains in contrast estimation translate into improved performance in these downstream tasks.

4 comments
AuthorsOpenReview ↗

Response to w6EV — Part 1/4: ACTG scores and borrowing gains

Our response is split into four comments because of the character limit.

Q: [W1 — Critical Weakness] How do the ACTG score gains translate into precision or power, and when are larger efficiency gains expected?

A: The original ACTG results improve all five prespecified held-out contrast scores relative to NoGraph (0.7–1.7%). The much larger gains arise when direct support is scarce but suitable relations can be borrowed: in the original R2 matched comparison, TSGS reduces edge and square deployment MSE by 26.6% and 41.5% versus target-tuned FullVal. Theorem 4.1 explains the required variance–bias balance; Appendix H.4 separately quantifies the ACTG marginal-effect precision.

Original — ACTG contrast estimation (Table 25). The original analysis reports the following held-out target scores over 100 repeated stratified splits of the same 2,139-participant cohort (lower is better):

TargetNoGraphPredictiveCVTSGSPaired TSGS − NoGraphPaired SETSGS wins
All local additions110,487109,171108,987−1,50013786%
Add ddI to AZT112,764112,354111,961−80319270%
Add ddC to AZT89,89988,53588,479−1,42014189%
Add AZT to ddI128,798126,626126,627−2,17229376%
Combination vs. monotherapy54,67453,97353,922−7539979%

The paired differences are calculated before rounding. The paired SE summarizes repeated splits of one cohort; it is distinct from the SE of a clinical treatment-effect estimator. PredictiveCV is competitive on individual targets. Figure 11 also shows that distinct clinical contrasts can select different graph/penalty rules.

The score has a precise statistical meaning. For a fixed training-fitted candidate, independent validation and correct propensities give (§4.2)

=R_C^{\mathrm{sel}}(\theta)+\kappa_C,$$ where $\kappa_C$ is candidate-independent. Expected score differences therefore compare conditional-contrast prediction risks. The score level also contains candidate-independent pseudo-outcome noise. Consequently, the score's percentage change is a conditional-contrast validation improvement; the marginal-effect SE change is measured separately below. **Original theory — the bias–variance mechanism (Theorem 4.1).** The conditional risk of an admissible projected graph-sequence rule is squared target bias plus target variance: $$R_C(\theta)=B_C^2(\theta)+V_C(\theta).$$ When the zero-penalty estimator is admissible, it is unbiased in this restricted model. Rearranging the submitted theorem gives the criterion now stated explicitly in Appendix H.1: $$\boxed{R_C(\theta)<R_C(\mathrm{NoGraph}) \iff B_C^2(\theta)<V_C(\mathrm{NoGraph})-V_C(\theta).}$$ This is a **necessary and sufficient condition within the stated model**: the variance saved by borrowing must exceed its squared-bias cost. The bias contains $-\lambda CUA_{G,\lambda}^{-1}U^\top L_Gh_0$, so the cost depends jointly on which relations are smoothed, the complementary signal along them, and the target $C$—not on Hamming proximity alone. Proposition 4.1 makes this tangible. For a relation with true difference $d$, unsmoothed estimation variance $v$, and retained-difference fraction $s$, $$R(s)=(1-s)^2d^2+s^2v,\qquad R(s)<R(1)\iff(1-s)d^2<(1+s)v\quad(0\le s<1).$$ The accompanying numerical illustration in Appendix H.1 uses $s=1/2$: if $(d,v)=(1,9)$ the risk falls from $9$ to $2.5$; if $(d,v)=(3,1)$ it rises from $1$ to $2.5$. A noisy, nearly compatible relation offers substantial variance savings; shrinking a reliable, genuinely different relation destroys signal. TSGS regularizes complementary differences, not necessarily the full treatment-effect difference. **Original — sparse support and rough transitions (Tables 5 and 8).** In the original H1 rare-support intervention, rare-edge PEHE is reported as mean ± SE: | Observations retained per target bundle | NoGraph | Full borrowing | |---|---:|---:| | 1 | $0.586\pm0.029$ | $0.280\pm0.005$ | | 2 | $0.573\pm0.022$ | $0.280\pm0.002$ | | 5 | $0.498\pm0.017$ | $0.280\pm0.004$ | | 8 | $0.464\pm0.013$ | $0.279\pm0.005$ | | Natural support | $0.338\pm0.011$ | $0.260\pm0.006$ | The gain is greatest when direct support is scarce.
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Response to w6EV — Part 2/4: Selection and precision

A (continued — W1):

Figure 3 connects support, the R2 error decomposition, and jump/non-jump effects; Figure 6 crosses support with roughness. In that controlled 6×6 sequence grid, target-selected borrowing has lower mean risk than NoGraph in all 36 tested cells, while strong full-graph borrowing can be harmful in rough cells.

In the neural benchmarks, R1 and R2 use six binary treatment components and 64 bundles. R1 has relatively smooth complementary variation; R2 has localized rough transitions, with 12 designated jump edges among 192 one-component edges. The original R2 decomposition (Table 8) shows why selective borrowing can win despite bias:

MethodSquared seed-mean errorAcross-seed variationOverall edge MSE
NoGraph0.035810.104170.13998
Full0.084990.088320.17331
TSGS0.037900.070640.10854

Full saves across-seed variation but incurs a larger squared seed-mean error; TSGS achieves a more favorable balance of these components.

Original theory — realizing a candidate gain through selection (Theorem 4.4). A good candidate must also be identified reliably. The deployed risk bound is

\min_{\theta\in\Theta}R_C^{\mathrm{refit}}(\theta) +2\zeta+2\Delta_{\mathrm{refit},C}.$$ For a baseline in the candidate family, a best-candidate refit-risk advantage $\gamma_C>2\zeta+2\Delta_{\mathrm{refit},C}$ is sufficient for the bound to imply improvement. Appendix H.1 identifies this as a sufficient deployment-risk condition under Theorem 4.4; its validation and refit terms are explicit. Useful borrowing opportunities must exceed validation noise and the possible refit shift; the estimated-nuisance extension is in E.8. **Added — marginal precision (Appendix H.4, Table 32).** We used each model's own out-of-fold outcome predictions in an AIPW estimator of prespecified marginal clinical contrasts, rather than the common pseudo-outcome used to rank candidates. Two distinct five-fold protocols were evaluated. Working SEs are in CD4 cells/mm\$^3\$: | Marginal contrast | NoGraph, 16 rules | TSGS, 16 rules | Ridge-tuned NoGraph, 64 rules | TSGS, 64 rules | |---|---:|---:|---:|---:| | Add ddI to AZT | 6.9886 | 6.9854 | 7.0521 | 7.0734 | | Add ddC to AZT | 6.2074 | 6.1750 | 6.1909 | 6.2688 | | Add AZT to ddI | 7.4902 | 7.4902 | 7.5447 | 7.6196 | | Combination vs. monotherapy | 4.8536 | 4.8354 | 4.8721 | 4.9018 | Under fixed ridge, the separately selected scalar targets show 0–0.52% lower working SE; joint addition-family selection changes one component's SE by +0.087%. In the expanded ridge-tuned protocol, the four scalar SE comparisons favor NoGraph (Table 32). The main ACTG improvement remains the held-out conditional-contrast score, and marginal-effect precision is evaluated separately. As a scale illustration, a 0.52% reduction in SE changes approximate two-sided 5%-level Wald power from 80.0% to about 80.4% at a fixed standardized signal, under the normal approximation. Appendix H.4 also explains why contrast prediction and AIPW precision need not track one another. For a fixed independently trained predictor $g$, correct propensity $e_a(x)$, scalar contrast $c$, and $u_a=g_a-\mu_a$, the AIPW score satisfies $$\operatorname{Var}\{\Gamma_c(g)\}-\operatorname{Var}\{\Gamma_c(\mu)\} =\mathbb E\left[\sum_a\frac{c_a^2u_a(X)^2}{e_a(X)}-\{c^\top u(X)\}^2\right].$$ Under the fixed-fit conditions, this extra variance—not contrast MSE alone—is the relevant precision criterion. Two arm predictions can share an error that cancels in their difference but still increases the AIPW score variance. Thus the observed SE differences support a modest precision effect in the initial protocol and imply correspondingly small approximate power changes at a fixed effect size. **Revision.** Section 5.1 now points to the gain criterion; Appendix H.1 spells out consequences of the original risk theorems and gives the numerical example. Appendix H.4 adds the marginal-precision analysis with tuned comparators. The revised text keeps held-out conditional-contrast scores and marginal-effect precision as separately quantified endpoints.
AuthorsOpenReview ↗

Response to w6EV — Part 3/4: HTE estimation and alternative borrowing

Q: [Q1 — Question for Authors] Does target-aware borrowing improve heterogeneous treatment effects and individualized treatment decisions versus alternative strategies?

A: The paper directly estimates heterogeneous conditional treatment effects. In rough R2, those estimates support lower local-addition regret: 39.8% below NoGraph in the archived-fit replay and 77.2% below the specified POUL adaptation in a separate comparison. The original target-selection experiment already tests heterogeneous edge and square effects; Appendix H.4 evaluates the corresponding decision consequences.

For a valid transition (a,b)(a,b),

=\mathbb E[Y(b)-Y(a)\mid X=x].$$ This is a contextual pairwise CATE. A square-face contrast is the difference between two contextual CATEs. PEHE and contrast MSE therefore directly evaluate conditional HTE functions over covariates; they are not simply marginal ATE errors. **Original — target-aligned HTE estimation (Table 19).** R3 here denotes a synthetic experiment, not Reviewer 3. Holding the 26 fitted candidates fixed while changing the selection target gives the following results for seeds 201–210: | Selector | Edge MSE | Square MSE | |---|---:|---:| | Edge-AIPW | $0.1111\pm0.0028$ | $0.2074\pm0.0059$ | | Square-AIPW | $0.1139\pm0.0044$ | $0.1822\pm0.0066$ | | PredictiveCV | $0.1112\pm0.0026$ | $0.2236\pm0.0025$ | **Square-target selection lowers mean square MSE by about 18.5% relative to PredictiveCV.** The edge-target comparison is nearly tied. This isolates target alignment without changing the candidate learner. [Figure 5](https://anonymous.4open.science/r/treatment-figures-review-630D/figure_5.png) shows the paired target-transfer comparisons. **Added — conditional effects and matching decisions (Appendix H.2, Table 26).** The new comparison uses the original R1/R2 generators described above. We added a paper-based binary-bundle adaptation of POUL, retaining joint component/off–on embeddings, a nonlinear map after aggregation, an orthogonalized outcome stage, and exact centering with the known assignment probabilities. Choices were fixed before formal evaluation. With 3,000 training, 3,000 validation and 5,000 evaluation covariate rows (seeds 201–210), we obtain: | Regime | Method | Edge PEHE | Square PEHE | Local regret | Global regret | |---|---|---:|---:|---:|---:| | R1 | POUL | 0.2111 | 0.1711 | 0.012628 | 0.103378 | | R1 | TSGS | 0.2751 | 0.2389 | 0.020017 | 0.127653 | | R1 | NoGraph | 0.3471 | 0.4188 | 0.029708 | 0.178640 | | R2 | POUL | 0.7364 | 1.0340 | 0.087231 | 1.367481 | | R2 | TSGS | 0.3292 | 0.3670 | 0.019865 | 0.103749 | | R2 | NoGraph | 0.3740 | 0.4657 | 0.028096 | 0.055823 | Entries are means; Table 26 gives seed-level SEs. In R2, **TSGS reduces mean local regret by 77.2% relative to the declared POUL adaptation**, with paired difference $-0.067366\pm0.002491$ and lower regret in all ten seeds. The R1 comparison favors POUL, and the R2 comparison favors TSGS. Both regimes are retained, making the rough-regime advantage and smooth-regime crossover explicit.
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Response to w6EV — Part 4/4: Local decision regret and measured outcomes

A (continued — Q1):

Added — decisions from archived fits (Appendix H.4, Table 31). A separate endpoint evaluation of archived R2 fits, seeds 401–410, compares the same selected/refitted surfaces under local and global decision rules:

MethodEdge MSELocal-addition regretGlobal-bundle regret
NoGraph0.15296±0.004270.15296\pm0.004270.03184±0.001060.03184\pm0.001060.08114±0.008000.08114\pm0.00800
FullVal-Edge0.15618±0.005290.15618\pm0.005290.02942±0.001300.02942\pm0.001300.16033±0.028440.16033\pm0.02844
PredictiveCV0.11559±0.002390.11559\pm0.002390.01943±0.000610.01943\pm0.000610.15361±0.018130.15361\pm0.01813
TSGS-Edge0.11466±0.002440.11466\pm0.002440.01917±0.000470.01917\pm0.000470.15553±0.019150.15553\pm0.01915

TSGS lowers mean local regret by 39.8% relative to NoGraph and 34.8% relative to target-matched FullVal. Its paired difference from NoGraph is −0.012671±0.001105-0.012671\pm0.001105. PredictiveCV is nearly tied (−0.000257±0.000650-0.000257\pm0.000650). The outcomes are new evaluations of previously fitted models; seeds and deployment protocols are reported separately from the POUL comparison.

Mechanism — local decisions. For a binary addition with no treatment costs, choose the addition when τ^(x)>0\widehat\tau(x)>0. A wrong sign incurs ∣τ(x)∣|\tau(x)| and implies ∣τ^(x)−τ(x)∣≥∣τ(x)∣|\widehat\tau(x)-\tau(x)|\ge|\tau(x)|. Under the same edge/covariate distribution as the estimation target,

\le\mathbb E|\widehat\tau-\tau| \le\sqrt{R_{\mathrm{edge}}}.$$ Appendix H.4 gives this link from conditional-effect accuracy to a matching local decision. The empirical ranking need not follow the bound: errors that do not change a decision have little immediate decision cost. Global optimization over 64 bundles depends on ranking the best bundles and is a different objective; its less favorable results remain in both decision tables. **Added — measured outcomes (Appendix H.4–H.5).** In the separate five-fold ACTG policy check with 64 candidates, TSGS's estimated local CD4 gain is 43.144 cells/mm\$^3\$, versus 42.861 for FullVal and 42.697 for PredictiveCV; a training-mean fixed policy achieves 46.891. The ACTG values are AIPW-estimated policy outcomes under that protocol. The laboratory combination study directly measures held-out growth reduction from adding a fifth component: TSGS achieves 12.612 percentage points versus 12.578 for FullVal and 12.534 for PredictiveCV, while raw NoGraph obtains 12.672 and total-surface smoothing 12.703. These measured laboratory increments over tuned controls are small and describe a distinct in-vitro terminal-addition decision. **Revision.** Section 2 now identifies activation-edge contrasts as contextual CATEs. Section 5.1 points to the local-decision evaluation; Appendix H.2 and H.4 report the new comparison and archived-fit evaluation under their distinct protocols. The downstream conclusion is specific to matching local treatment additions in the evaluated rough regimes, with global and clinical decision endpoints also reported.

Comments on the paper

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General Response to Reviewers and Area Chairs — Summary of Revisions

We thank the reviewers for their constructive comments. We have addressed their concerns through clearer definitions, expanded theoretical explanations, and targeted empirical analyses, with the new results documented in Appendix H.

Below, we summarize the main revisions and their correspondence to the reviewer responses.

1. Clarification of Definitions, Scientific Motivation, and Theoretical Contributions (i6fS)

  • Definitions and identification: Traced all seven questioned concepts to their original definitions or equations, providing both original and revised manuscript locations. Clarified activation edges, square-face interactions, graph orientation, covariate encoding, and overlap, moved the raw residual-branch definition closer to its first mention (i6fS–W1.1–W1.7).
  • Scientific motivation and novelty: Explained the fundamental tension between variance reduction through borrowing and bias from smoothing genuine treatment differences. Clarified how TSGS separates scientific treatment geometry, protected functional structure, and target-specific borrowing.
  • Mathematical contributions: Connected the projection construction, exact contrast-risk characterization, target-dependent dominance results, and finite-candidate selection guarantee to this scientific problem (i6fS–W1.8, Appendix H.1).

2. Understanding the Sources of TSGS's Improvements (9KVe–W1/Q2/Q3, w6EV–W1)

  • Original evidence: Brought together the existing sparse-support experiments (H1), rough-transition analysis (H2), bias–variance decomposition, matched FullVal comparison, and cross-target selection experiments to explain when and why selective borrowing improves causal-contrast estimation.
  • Additional comparisons: Extended the treatment-sharing baselines and analyzed performance on localized rough transitions (Appendix H.2).
  • Controlled mechanism studies: Added same-density random-graph comparisons, complementary versus whole-surface regularization, interaction-strength and covariate-heterogeneity stress tests, and localized versus dispersed roughness experiments (Appendix H.3). These analyses distinguish the effects of borrowing location, structural protection, and target alignment.

3. Real-World Evidence, Estimation Precision, and Downstream Decisions (w6EV–W1/Q1, 9KVe–Q1)

  • ACTG 175: Clarified the four randomized treatment arms, scientifically valid drug-addition comparisons, and interpretation of the original five held-out clinical contrast results (Appendix F.15).
  • Precision and decision evaluation: Added AIPW marginal-effect precision analyses and local/global treatment-decision evaluations, connecting conditional-effect estimation to downstream decision performance (Appendix H.4).
  • Measured combination outcomes: Added an evaluation of five-component laboratory intervention combinations, including held-out contrast estimation and local addition decisions (Appendix H.5).

The revisions clarify the central contribution of TSGS: treatment geometry determines which causal comparisons are scientifically meaningful, while target-aware graph selection determines where statistical borrowing is beneficial. Our reviewer-specific responses provide the supporting mathematical arguments, experimental evidence, and precise manuscript references.

Thank you again for the time and care invested in these reviews. We welcome further questions and would be happy to discuss any aspect of the revision.

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

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