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Under review as a conference paper at ICLR 2027

When Randomization Is Not Enough: Auditing Exposure in Network Experiments

Abstract

Randomized network experiments observe assignments and outcomes, but the physical exposure that defines a causal effect may be generated by an unknown mechanism. The same assignment–outcome law can then support exposure effects of opposite signs. We formulate active partial identification: bridge experiments measure physical exposure under selected assignments to narrow the union of candidate-implied causal targets. Under candidate completeness, outcome sufficiency, and calibrated invariant probes, candidate intervals and a structural e-process give a causal envelope valid throughout adaptive querying and stopping. Packing and feasible splits bound intrinsic audit complexity—the worst-case depth of a decision tree over causal targets—by causal-target geometry rather than by the number of mechanisms. For candidates with a common pre-audit law, heterogeneous-channel lower bounds separate search and confirmation costs; supplied ordered target cells with feasible cuts and a common binary-symmetric channel attain these scales up to universal constants. Experiments separate acquisition, calibration, and information-cost effects and quantify bridge sensitivity: target-aware auditing pays off when target and model geometries differ; public-data analysis illustrates the missing-anchor boundary left by unmeasured exposure.

Primary area:
causal reasoning
Keywords:
causal inference, network interference, partial identification, adaptive experimental design, anytime-valid inference, exposure mappings

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
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Paper summary

This paper study causal inference in randomized network experiments when the mechanism mapping treatment assignments to physical exposure is unknown. The paper show the same assignment & outcome distribution can support exposure effects of opposite signs, and proposes Target-Aware Bridge Auditing (TAB) to acquire additional exposure measurements. The paper also develops target-dependent query complexity bounds and search/confirmation results in structured settings. Validation includes synthetic experiments, non-oracle network simulations, and public-data analyses illustrating ambiguity when receipt is unobserved.

Critical strengths

The nonidentification construction establishes why randomization alone may not resolve the scientific target. This provides a concrete motivation for acquiring exposure measurements rather than simply collecting more assignment & outcome observations.

The nested retention rule supports causal coverage under adaptive querying and stopping, conditional on the stated assumptions. Hence, I think maintaining an envelope over plausible mechanisms is a useful alternative to selecting a single exposure map and ignoring structural uncertainty.

Critical weaknesses

My main concern is whether the certified intervals are informative in the settings where the method is intended to help. In Appendix F.3, the favorable width of 0.554 uses simulation oracle band. Replacing this with analytic bands on the recorded query paths gives a terminal mean width of 35.972, compared with a known effect-support diameter of only 1.8. I recognize that this replay does not rerun query selection under the analytic bands, but the gap is substantial. The non-oracle experiments also include vacuous results: Table 6 reports width 1.7927 against support diameter 1.8, while Table 12 reports width 2.000 against support diameter 2. I, therefore, remain unconvinced that the acquisition gains demonstrated with oracle calibration translate into useful certified inference without substantially more information from the main experiment.

I suppose that target-aware query selection does not offer a sufficiently consistent advantage over simple count balancing. In Table 12, count-based querying obtains essentially the same width as target acquisition (0.160 vs 0.161), using fewer labels (14.05 versus 16.10), with comparable empirical coverage. Table 8 provides another setting where count balancing gives a narrower interval, although at higher cost. Furthermore, the main non-oracle policy falls back to count balancing when the target score has zero 1 step gain. I acknowledge that target-aware acquisition performs better in other settings, but I find it difficult to separate its contribution from the fallback and improved interval calibration.

Questions for authors

I would ask the authors to prioritize addressing the concerns raised in weakness, especially the vacuous intervals and the inconsistent gains over simple baselines.

Question: Bridge labels test the assignment-to-exposure mechanism, but cannot establish outcome exposure sufficiency. If sender identity or dose affects outcomes beyond binary receipt, what justifies interpreting the narrowed envelope as evidence about the physical-exposure effect?

5 comments
AuthorsOpenReview ↗

Response to Reviewer aubW

We thank Reviewer aubW for examining whether the certified intervals are informative in the intended settings, whether target-aware querying adds value beyond count balancing, and how the exposure definition supports the causal interpretation. We distinguish main-trial information, bridge measurements, query allocation, and outcome exposure sufficiency.

A1. Informativeness of non-oracle intervals

Q: Are the certified intervals informative in the network-experiment settings where the method is intended to help?

A: Interval informativeness depends on both the main experiment’s randomized information and the exposure information supplied by bridge labels. The practical question is whether bridge auditing can make the causal envelope informative under the randomization structure available in the main experiment. The main experiment estimates effects under candidate mechanisms; bridge labels distinguish which mechanisms remain plausible. Theorem 5.3 guarantees coverage under adaptive querying and stopping, while the experiments assess interval width.

The experiments show that bridge audits can narrow the envelope when the main trial provides sufficient independent randomized information. Bridge auditing narrows the envelope when the main experiment provides enough independent randomized information, but cannot replace a design with too few effective independent blocks. Table 13 isolates auditing with main-trial information fixed; Tables 6 and 12 show how precision changes with randomized information.

EvidenceSetting and comparisonMean interval width
Table 6B=1B=1, support diameter 1.81.81.7927
Table 6B=96B=96 / B=256B=256, same 30-label budget0.2506 / 0.1195
Table 12n=4096n=4096: b=1b=1 / b=64b=640.161 / 1.196
Table 13Passive union / target-query anytime; active methods use 30 labels0.591 / 0.161

The results distinguish uncertainty that bridge auditing can reduce from precision governed by the main trial. When the main design has little independent randomized information, a valid envelope can remain wide. With more informative designs, bridge auditing narrows uncertainty from the unknown exposure mechanism. The experiments characterize when this reduction yields a useful interval; coverage alone does not guarantee narrowness.

Appendix F.3 isolates candidate-band calibration by replaying the recorded query paths with analytic bands. Appendix F.3 isolates candidate-band calibration by replacing the bands along recorded query paths. The mean width falls from 82.074 to 35.972, against an effect-support diameter of 1.8. Since paths are fixed, this is a calibration diagnostic, not a full adaptive rerun with analytic bands; it shows that candidate-band construction remains a precision bottleneck in this configuration. The oracle acquisition result addresses a different component.

Table 13 separates the contributions of adding labels, selecting queries, and using anytime reporting. With main-trial information fixed, Table 13 separates auditing, query selection, and reporting. The passive-union width is 0.591; 30 fixed queries with terminal reporting reduce it to 0.228. Target queries with terminal reporting give 0.194, isolating the query rule; anytime reporting on that path gives 0.161 with 0.983 path coverage.

Together, these comparisons identify the settings in which bridge labels improve the precision of the causal envelope. Bridge auditing is useful when the main experiment can estimate candidate-specific effects and much of the remaining uncertainty is structural. When effective independent blocks are too few, auditing cannot replace main-trial information. The experiments characterize this boundary: bridge measurements reduce mechanism uncertainty, while the main design governs precision.

A2. Independent contribution of target-aware querying

Q: What does target-aware querying add, and when does it improve on count balancing?

A: TAB’s practical contribution is to spend bridge labels on distinctions that change the causal effect. TAB is designed for a specific gap in randomized network experiments: randomization identifies who was assigned treatment, but the physical exposure—and thus the causal effect of interest—may remain ambiguous. Bridge measurements narrow the mechanisms and effects they imply. Under the stated assumptions, Theorem 5.3 guarantees envelope validity under adaptive querying and stopping. TAB preserves uncertainty across plausible mechanisms and directs limited audit effort toward measurements that distinguish effects.

Target-aware scoring allocates queries by their effect on the causal envelope, whereas count balancing allocates by mechanism counts. Count balancing splits mechanisms into similarly sized groups; TAB scores queries by expected reduction in worst-case causal-envelope width per unit information cost. Mechanism count can misrepresent causal uncertainty: many mechanisms may imply the same effect while a few imply different effects. TAB targets those effect differences, with count balancing as a fallback when no feasible query improves the envelope.

The theory explains when targeting causal geometry is useful and when count balancing is a good approximation. This broader objective has a theoretical basis. Theorem 5.4 measures difficulty by the packing of distinct causal targets and whether feasible queries separate them. Proposition D.10 shows count balancing is a valid approximation when child interval width scales with mechanism count. TAB thus covers count-aligned settings and the broader case where counts and causal targets diverge; the search-and-confirmation results characterize the information needed to locate and verify a target.

Figure 3 shows that target-directed queries reduce audit depth when model and target geometries are misaligned. Figure 3 shows the consequence: target-directed queries resolve the population effect with fewer exact queries when geometries are misaligned, while both methods require the same number in the aligned control.

The controlled comparison in Table 8 and the end-to-end comparison in Table 12 show how the gain depends on the setting. Table 8 holds candidate bands fixed: at budget 16, TAB has nearly the same width at lower cost; at budget 256, it is cheaper and narrower. Table 12 shows comparable non-oracle performance in another network configuration. Together with Figure 3, the comparisons show that target geometry helps when mechanism counts do not represent causal uncertainty.

SettingPlateau-aware TAB: width / cost or labelsCount balancing: width / cost or labels
Table 8, budget 160.8582 / 25.0460.8462 / 26.670
Table 8, budget 2560.1195 / 23.1070.1369 / 26.670
Table 12, non-oracle network0.161 / 16.10 labels; coverage 0.9830.160 / 14.05 labels; coverage 0.987

Taken together, the results position TAB as a target-centered extension of count balancing. TAB generalizes count balancing by retaining count-based allocation when counts reflect causal uncertainty and redirecting measurements toward effect-relevant distinctions otherwise. It couples this allocation rule with a valid envelope under adaptive querying and stopping.

A3. Outcome exposure sufficiency

Q: If sender identity or dose affects outcomes beyond binary receipt, how can the narrowed envelope be interpreted as a physical-exposure effect?

A: A causal interpretation starts by defining exposure to include the attributes that can affect the outcome. We would define exposure at the level that captures the treatment attributes relevant to the outcome. If sender identity and dose may affect outcomes, exposure should record receipt, sender, and dose. Aligning the definition, candidate mechanisms, and bridge labels distinguishes outcome-relevant states that a binary “received” indicator would pool.

Assumption 3.2 formalizes this requirement, and Theorem 5.7 supports sensitivity analysis for bounded departures. This is the interpretation required by Assumption 3.2, which represents outcomes as Yi(z)=YiE{Ei(z)}Y_i(z)=Y_i^E\{E_i(z)\}. If only a coarser measure such as binary receipt is available, scientifically justified bounds on unexplained outcome variation can enter a sensitivity analysis. Theorem 5.7 translates such a bound into an adjustment to candidate intervals. Thus, plausible sender or dose effects call for a richer measured exposure or a sensitivity-adjusted envelope based on an informative bound.

Closing

These responses connect the practical value of TAB to its information requirements, query strategy, and exposure definition. We hope this response clarifies when the envelope is informative, what target-aware querying contributes, and how the exposure definition determines the causal interpretation. We appreciate the reviewer’s careful examination of these issues.

Reviewer_f8AFOpenReview ↗
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Paper summary

The paper considers the problem where even with perfect randomization, the effect of physical exposure can be unidentifiable when the mechanism linking assignment to exposure is unknown. The authors motivate this with an example: "in public-health messaging experiment, direct delivery, resharing, and feed ranking can produce different receipt events under the same assignment".

To tackle this issue, the paper then proposes a solution where Target-Aware Bridge Auditing is used where a sequential evidence process (e-process) allows for iterative elimination of candidate underlying mechanisms that the exposure provides evidence against. This approach chooses "probes" that is target aware and the method has the guarantee that the envelope covers the true effect w.h.p across all t, even under adaptive querying and stopping. The paper provides upper/lower bounds and wraps up with some synthetic experiments.

Critical strengths
  1. I think the paper's problem is well motivated, although I'm not an expert in this line of literature and so it is unclear to me to what extent prior works have already addressed the imperfect assignment -> exposure mapping problem.

  2. The proposed solution seems natural, including the use of e-processes for anytime inference/validity.

Critical weaknesses

The paper is quite dense and primarily theoretical in nature. It is reliant on assumptions that are not easy to verify (e.g. assumptions 3.3).

It also seems to me that the experimental section is a bit less detailed than the theoretical treatment in the paper. And no real world bridge experiment is run, although I understand that can be difficult to set up. Could the authors expand more on the tangible practical takeaways the theory in the paper offers?

Questions for authors
  1. As with a lot of works in causality, the proposed method rests on the underlying assumption needed to make the method work. Could the authors offer some motivation for the multiple assumptions needed (3.2-3.5) and if/how they might hold in practice?

  2. For the experiments, could the authors comment on what other baselines should be compared in the experiment section?

4 comments
AuthorsOpenReview ↗

Response to Reviewer f8AF

We thank Reviewer f8AF for asking how our assumptions guide study design and what the experiments support. We explain their practical roles, summarize the comparisons, and distinguish TAB’s exposure measurements from designs that collect additional outcomes.

F1. Motivation and practical basis for Assumptions 3.2–3.5

Q: What motivates Assumptions 3.2–3.5, and how might they hold in practice?

A: Consider an encouragement experiment where a public-health reminder can reach someone directly, through a friend, or through feed ranking. Assignment is observed, but physical receipt may not be.

Assumption 3.2 — Define a causally sufficient event. The restriction Yi(z)=YiE{Ei(z)}Y_i(z)=Y_i^E\{E_i(z)\} means assignments producing the same exposure must produce the same potential outcome. Receipt within a fixed window is a physical event, distinct from reading or persuasion. Fixing message, sender, dose, interface, and follow-up window supports sufficiency. If sender identity or repeated impressions matter independently, include them in a richer exposure or bound the residual with validation data.

Assumption 3.3 — Anchor the candidate class in delivery rules. A candidate g⋆g^\star must satisfy gi⋆(z)=Ei(z)g_i^\star(z)=E_i(z) for every relevant assignment. Direct send, one-hop forwarding, and feed delivery are interpretable rules; routing specifications, delivery logs, and verified receipts can inform the class before randomization. Example A.1 shows that an incorrect singleton may remain forever, even with an oracle interval, because its e-value stays one. Corollary C.4 allows a buffer for omissions bounded by certified receipt data.

Theorem 5.7 bounds the error for an approximate candidate g∘g^\circ. It gives ∣θn(g∘;P0)−τnE∣≤bn(g∘)|\theta_n(g^\circ;P_0)-\tau_n^E|\le b_n(g^\circ), where

bn(g∘)=1n∑i(2εi+Bi(γi1πi1(g∘)+γi0πi0(g∘))).b_n(g^\circ)=\frac{1}{n}\sum_i\bigl(2\varepsilon_i+B_i(\frac{\gamma_{i1}}{\pi_{i1}(g^\circ)}+\frac{\gamma_{i0}}{\pi_{i0}(g^\circ)})\bigr).

The terms capture outcome error, exposure mismatch, and inverse-support amplification.

Assumption 3.4 — Screen exposure support and dependence from the design. The known assignment law determines πie(g)=P{gi(Z)=e}\pi_{ie}(g)=P\{g_i(Z)=e\}, so positivity is checked before auditing. Bounded score residuals and a dependency graph covering shared randomized inputs yield valid main-data bands (Theorem C.2). Under block randomization, units using the same block belong to that dependence calculation, regardless of the friendship graph. Few effective blocks or rare exposure cells limit precision before labels are collected.

Assumption 3.5 — Preserve and calibrate the receipt mechanism. A feasible bridge query fixes the focal sender pattern and keeps the interface and exposure window comparable to the trial. Local rules need local control; global rules need a feasible global or calibrated-completion protocol (Appendix A.1). Each query qq has a calibrated conditional channel KqK_q and prespecified positive cost cqc_q. Independent gold receipts estimate query-error bounds; matched reference/probe cells check transport (Appendix A.2). Proposition D.3 and Theorem D.4 provide certified error and transport adjustments.

Precise coverage statement. Under 3.2–3.5, with main-band error budget α\alpha and structural-retention budget δ\delta, Theorem 5.3 states

P{g⋆∈Vt(δ) ∀t}≥1−δ,P{τnE∈Cn,t(α,δ) ∀t}≥1−α−δ.P\{g^\star\in V_t(\delta)\ \forall t\}\ge 1-\delta,\qquad P\{\tau_n^E\in C_{n,t}(\alpha,\delta)\ \forall t\}\ge 1-\alpha-\delta.

Failure requires excluding the true map or the true candidate's band missing its target. Otherwise the band remains in every retained hull. The union bound allows adaptive queries and stopping without independence. If external calibration fails with probability at most ζ\zeta, Proposition A.3 gives coverage 1−α−δ−ζ1-\alpha-\delta-\zeta.

Empirical check on 3.5. Table 10 holds the bridge problem fixed while the sensor operates at the bound edge (error 0.35 throughout). Nominal likelihood assumes error 0.18; bounded-error betting uses a valid conditional upper bound.

Table 10 — Channel-calibration check at the bound edge.

Retention ruleTrue-map retentionFull-path causal coverageMean labels
Nominal BSC(0.18) likelihood0.7070.83228.20
Bounded-error betting (≤0.35\leq 0.35)0.9780.98051.95

Conditional calibration improves validity at a visible label cost. It matters under adaptive acquisition because average error over an unselected menu does not bound the chosen query’s error. Appendix Table 3 summarizes the checks and responses to violations.

F2. Practical takeaways and field application

Q: What practical takeaways do the experiments support, and what would a field bridge study add?

A: The scientific question is whether receiving a reminder changes behavior, not whether assignment creates an opportunity to receive it.

What main outcomes can identify. Theorem 5.1 constructs two models with identical assignment–outcome laws but physical-exposure effects +1 and −1, an ambiguity that persists with unlimited main-trial data. Theorem 5.2 characterizes the sharp identified set: {τnE(m):m∈Mn, Pm=P0}={θn(g;P0):g∈Gn(P0)}\{\tau_n^E(m):m\in\mathcal{M}_n,\ P_m=P_0\}=\{\theta_n(g;P_0):g\in\mathcal{G}_n(P_0)\}

The left side lists physical-exposure effects under submodels compatible with the observed assignment–outcome law; the right side lists contrasts implied by compatible mappings. Equality is sharp: every listed value is attainable. Thus randomization alone may leave effects indistinguishable, while valid bridge labels can eliminate incompatible mappings.

The practical question is which feasible receipt measurement resolves the remaining ambiguity.

Decision consequence (Theorem 5.3). At any almost-surely finite stopping time TT, declare a positive effect only if Cn,TC_{n,T} is nonempty and inf⁡Cn,T>0\inf C_{n,T}>0. Then P{positive declaration with τnE≤0}≤α+δP\{\text{positive declaration with }\tau_n^E\le0\}\le\alpha+\delta: on the theorem's simultaneous-coverage event, τnE∈Cn,T\tau_n^E\in C_{n,T}, so a false positive is impossible.

A concrete decision after two labels. Appendix A.2 considers three plausible delivery rules:

Delivery ruleCandidate effect intervalBridge-query prediction
Direct delivery (DD)[−0.06,0.10][-0.06, 0.10]0
One-hop receipt (RR)[0.04,0.18][0.04, 0.18]1
Feed-mediated receipt (FF)[0.12,0.25][0.12, 0.25]1

Before a bridge query, the union is [−0.06,0.25] and contains zero. A feasible local probe predicts (0,1,1) for (D,R,F). Under BSC(0.10) telemetry and δ=0.05\delta=0.05, two positive labels give relative likelihoods (0.01,0.81,0.81), excluding D. The retained hull becomes [0.04,0.25]: receipt has a positive sign even though R and F remain unresolved. That is the operational reason to target the effect instead of fully reconstructing delivery.

What the mathematical audit guarantee changes. Theorem 5.3 reports a simultaneous envelope with coverage at least 1−α−δ1-\alpha-\delta across all adaptive audit times. Appendix F.1 makes the distinction between terminal and pathwise validity visible:

ReporterTerminal coverageFull-path coverage
Retained candidate union0.9766—
Single selected map0.38990.9849

This shows that adequate terminal coverage can coexist with poor pathwise coverage when structural uncertainty is discarded.

Thus a reporter can look accurate at the final label while excluding the physical effect during intermediate policy decisions. Retaining structural uncertainty protects the entire decision path.

When will labels be useful? Precision depends on outcome information, receipt-label information, and certified measurement accuracy. For a connected-cycle design, the main-data half-width is bounded at scale π‾g−1log⁡(2/α)/J\underline\pi_g^{-1}\sqrt{\log(2/\alpha)/J}, where J=n/bJ=n/b counts randomized blocks. At n=256,b=64n=256,b=64 (only four blocks), Table 12 remains at the full width 2. At n=4096,b=1n=4096,b=1, the nonempty mean width is about 0.161. More labels remove candidate mechanisms; only adequate randomized support makes their effect intervals narrow.

Table 13 — Same main outcome data, varying audit and reporting procedure.

ProcedureAdded labelsNonempty mean width
Passive union00.591
Fixed-query, terminal300.228
Target-query, anytime300.161

This combines label value, placement, and reporting; matched-reporter controls in Table 14 (Q3) isolate query selection. In the target-anytime row, three empty reports enter coverage as failures; full-path coverage is 0.983.

What the real-data diagnostics tell a field experimenter. The 1,975-account Twitter archive records assignment opportunities and resharing proxies, not verified receipt. Its opportunity contrast is 0.0195; the binary-IV proxy-effect region [−0.1405,0.4823] spans both signs (Appendix F.6). A published Facebook randomization design yields exposure probability 3.2×10−93.2\times10^{-9} under a hypothetical five-neighbor threshold (F.7).

A prospective bridge can address these obstacles with a feasible local sender-pattern intervention, independent gold receipt checks, matched interfaces and windows, and pre-collection exposure-probability screening. Reporting can stop when all retained intervals lie on the same side of a prespecified decision threshold (Section 7).

F3. Baseline comparisons

Q: Which baselines are compared, and what does each comparison test?

A: Holding outcome data and thirty receipt-label queries fixed, we ask which policy yields the most useful causal interval. Two added policies test whether target awareness helps beyond label collection and map learning.

  • Uniform-random feasible queries test the value of thirty labels without directing measurements to informative mechanisms or effects.
  • Posterior information gain tests map-recovery learning. Starting with equal weights on six candidate maps, it updates wt(g)=Lt(g)/∑hLt(h)w_t(g)=L_t(g)/\sum_hL_t(h) and selects the probe maximizing the binary-label information score h(0.18+0.64∑gwt(g)aq(g))−h(0.18)h(0.18+0.64\sum_gw_t(g)a_q(g))-h(0.18). TAB instead scores worst-case contraction of the retained causal interval, with count-based acquisition on flat target scores.

Matched-budget protocol. All three policies use the same eleven connected-network designs, 600 paired trials per setting, fixed main-data candidate intervals, the same four-query menu, precomputed query-indexed BSC(0.18) labels, thirty unit-cost queries, α=δ=0.05\alpha=\delta=0.05, structural e-process retention, and the same anytime union reporter. The changed variable is query selection alone. Empty terminal reports count as coverage failures and receive width loss 2, the full bounded effect range. An independent probability-domain implementation replayed all 13,200 additional baseline paths and 409,200 reporting prefixes without discrepancies (Appendix F.5).

Table 8 — Acquisition controls under fixed candidate bands.

SettingPlateau-aware TAB: width / cost or labelsCount balancing: width / cost or labels
Budget 160.8582 / 25.0460.8462 / 26.670
Budget 2560.1195 / 23.1070.1369 / 26.670
Non-oracle network (Table 12)0.161 / 16.10 labels; coverage 0.9830.160 / 14.05 labels; coverage 0.987

At budget 16, widths are similar and TAB costs less; at 256, TAB is narrower and cheaper. In the non-oracle setting, count balancing is marginally narrower and uses fewer labels. Table 14 — Mean terminal width loss. Lower is better; bold marks the row minimum.

nnbbEffectTABRandomInfo gain
25610.300.64690.74910.6706
25640.301.19241.39381.2036
256640.302.00002.00002.0000
1,02410.300.32130.40370.3639
1,02440.300.64100.75780.6834
1,024640.301.77651.85731.7773
4,09610.050.16460.19220.1881
4,09610.300.17030.23140.1924
4,09640.300.32980.39670.3711
4,096640.051.27631.47741.2721
4,096640.301.19981.37991.2103

TAB has the smallest or tied-smallest loss in 10/11 settings: it beats random in ten (one tie) and information gain in nine (one tie, one reversal). At n=4096,b=1n=4096,b=1, effect 0.30, TAB's 0.1703 loss is 26.4% lower than random's 0.2314. At n=4096,b=64n=4096,b=64, effect 0.05, information gain is ahead by 0.0042, within corrected Monte Carlo uncertainty. When n=256,b=64n=256,b=64, all procedures incur full loss: the randomized main trial supplies too little effect precision for acquisition alone to help.

Statistical evidence for the representative design. Differences are paired TAB-minus-baseline width losses for n=4096,b=1n=4096,b=1, effect 0.30, with 95% Monte Carlo intervals corrected across 22 comparisons.

ComparisonMean loss differenceAdjusted 95% interval
TAB − Random−0.0612[−0.0888, −0.0335]
TAB − Info gain−0.0221[−0.0535, 0.0093]

The reduction versus random is significant after correction; the information-gain contrast is uncertain. Empty counts for TAB/random/information gain are 3/5/10, with full-path coverage 0.9833/0.9817/0.9833. Empty reports count as failures, avoiding survivor-only width comparisons.

What the baselines isolate. Count balancing and fixed cycling test candidate-count and nonadaptive acquisition; target-only and score/pricing ablations test components of TAB (Table 8). Passive, fixed-terminal, Bonferroni, and anytime procedures test the reporter and added measurement budget (Table 13). Because Table 13 varies more than query choice, Table 14 is the requested controlled acquisition comparison. Theorems 5.4–5.6 predict the mechanism: map distinctions have value only insofar as they separate causal targets and feasible probes can reveal them. Information gain can identify a map without materially shrinking the effect hull; TAB directs the budget toward distinctions that change the causal decision.

F4. Relation to prior work

Q: To what extent has prior work studied assignment-to-exposure mapping, and how does this paper differ?

A: Exposure mappings are established in interference research. Here receipt is defined, but its assignment-to-receipt rule is unknown; we ask which measurements resolve the resulting causal ambiguity.

The deeper identification conflict (Theorem 5.1). Let Z1,Z2Z_1,Z_2 be independent Bernoulli(1/2) assignments. Model A has exposure (E1,E2)=(Z2,Z1)(E_1,E_2)=(Z_2,Z_1) and YiE(e)=eY_i^E(e)=e, so the physical exposure effect is +1. Model B has exposure (1−Z2,1−Z1)(1-Z_2,1-Z_1) and YiE(e)=1−eY_i^E(e)=1-e, so the effect is −1. Yet both generate (Y1obs,Y2obs)=(Z2,Z1)(Y_1^{obs},Y_2^{obs})=(Z_2,Z_1) under every randomized assignment. They induce the same observable law, so no amount of main-trial data distinguishes the signs, even before sampling error or network dependence.

Relation to existing information structures (Appendix Table 2).

Research lineInformation availableInferential objective
Aronow–Samii (2017)Supplied exposure mappingDesign-based causal interval
Sävje (2024)A mapping defining an estimand, with sufficiency examined separatelyMeaning of mapping-based effects
Schröder et al. (2026)Fixed data and propensity-sensitivity restrictionsDirect/spillover effect bounds
Ailer et al. (2024)Adaptively acquired treatment–outcome observationsNarrow a causal functional
Nowak (2011)Feasible binary testsRecover a binary-valued function
TABFixed randomized outcomes plus adaptive physical-receipt labelsAnytime union interval for the physical effect

TAB combines design-based candidate bands, e-process retention, and noisy-search query-cost tools to adaptively measure physical receipt effects. Appendix A.3 contrasts its data and costs with outcome-acquisition designs.

Sharp identification and valid sequential reduction. Theorem 5.2 gives the sharp, attainable set of physical effects compatible with the main-data law; bridge labels remove incompatible receipt predictions. Theorem 5.3 guarantees that the true map survives every time with probability at least 1−δ1-\delta and the causal envelope covers the effect with probability at least 1−α−δ1-\alpha-\delta. Modelwise true-candidate coverage suffices; simultaneous confidence for every pseudo-target is unnecessary. At B=96B=96, modelwise betting cuts mean terminal width by 28.1% versus simultaneous betting, with 0.9917 path coverage (Section 6).

Theorem 5.4 — exact target-resolution complexity. Let Nϵ(V)N_\epsilon(V) pack causal targets separated by more than 2ϵ2\epsilon, Dϵ⋆(V,Qn)D^\star_\epsilon(V,Q_n) be the smallest worst-case exact-query depth, and Δn(V)\Delta_n(V) their diameter. Then$\left\lceil\log_2 N_\epsilon(V)\right\rceil \le D^\star_\epsilon(V,Q_n).$

If every reachable nonterminal node admits a feasible query contracting target diameter by a factor at most 1−ρ1-\rho, then for Δn(V)>2ϵ\Delta_n(V)>2\epsilon,Dϵ⋆(V,Qn)≤⌈log⁡{Δn(V)/(2ϵ)}−log⁡(1−ρ)⌉.D^\star_\epsilon(V,Q_n) \le\left\lceil \frac{\log\{\Delta_n(V)/(2\epsilon)\}}{-\log(1-\rho)} \right\rceil.

When Δn(V)≤2ϵ\Delta_n(V)\le2\epsilon, depth is zero even if many candidate maps remain. This is the counterintuitive point: the causal target may be resolved before the physical map is identified.

Theorems 5.5–5.6 — information price and an attaining procedure. For KK targets separated by more than 2ϵ2\epsilon, sharing the same pre-audit information law, Theorem 5.5 lower-bounds average search cost by FK(δ)/CF_K(\delta)/C, where FK(δ)=log⁡K−h(δ)−δlog⁡(K−1)F_K(\delta)=\log K-h(\delta)-\delta\log(K-1) and CC is the best channel capacity per query cost. It separately lower-bounds pairwise confirmation cost by kl(1−δ,δ)/K(g,h)\mathrm{kl}(1-\delta,\delta)/\mathcal K(g,h), where K\mathcal K is the best pairwise KL information per cost. These are distinct necessary bounds. Under supplied ordered target cells, feasible cuts and fresh BSC(η\eta) observations, Theorem 5.6 constructs a search-and-confirmation procedure with sup⁡gEgT≤A0log⁡KCη+A1log⁡(1/δ)κη.\sup_g E_gT\le A_0\frac{\log K}{C_\eta} +A_1\frac{\log(1/\delta)}{\kappa_\eta}.

Here A0,A1A_0,A_1 are universal constants. Figure 3 illustrates this geometric distinction: target-aware and count-balancing probes tie when effect and map partitions align, but target-aware needs fewer probes when they differ. Table 14 extends the test to matched network trials against random querying and map-information gain. The design principle is to measure distinctions that change the causal decision.

Closing

We hope this response clarifies how the assumptions translate into study-design checks and how the experiments separate the contributions of exposure measurement, query allocation, and valid reporting. We thank the reviewer for prompting us to make these practical connections explicit.

Reviewer_bUVwOpenReview ↗
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Paper summary

Summary: with my best ability, I cannot understand what the paper's research core is. And I cannot find a compact logic flow. I can only guess maybe the work is about a protocol design of who can receive the message to reduce the uncertainty.

Critical strengths

Strength: With my judgment to this work, I choose not to discuss the strength of the work. I sincerely suggest all experts in this channel to read only the abstract of the work, then you will understand my argument here.

Critical weaknesses

Weakness: I will use the following as some examples, I did this just to let the peers and the ACs/SACs see my efforts and I respect this reviewing process.

  • What's the "exposure mechanism" and "active partial identification". For the researchers with formal academic training, for this over 50-page submission, a clear definition is a must, especially, they seem like the central objects of the paper.
  • How should I understand the research gist of this submission? I cannot read any useful information even after I reached page 3. I still cannot grasp the context.
  • What's the paper doing with those theorems ? Which one is your main theorem?
  • There are too many notations / symbols used with no clear definition. e.g., eq.13, what's {}_{+} ?
Questions for authors

i have stated my questions in the Weakness section.

4 comments
AuthorsOpenReview ↗

Response to Reviewer bUVw

We thank Reviewer bUVw for identifying the points where the paper’s central concepts, research flow, theorem structure, and notation need to be easier to locate and understand. We address each point below and connect our explanations to the relevant definitions, results, and locations in the manuscript.

B1. Core concepts and definitions

Q: What do “physical exposure,” “exposure mechanism,” and “active partial identification” mean?

A: We respectfully note that the manuscript already defines them: Section 3.3 defines the exposure mechanism, and the Abstract formulates active partial identification.

A messaging experiment illustrates the difference between treatment assignment and actual physical exposure. Consider a study that randomly selects social-media accounts to receive a vaccination message. Some people see it directly; others see it after a friend reshares it. The assignment records who was selected, while physical exposure records who actually received the message. Formally, as we define it in Section 3.3, an exposure mechanism maps treatment assignments to physical exposures. Thus, “count direct delivery only” and “count both direct delivery and resharing” are two candidate mechanisms: two rules mapping the same assignment to actual receipt.

Because the exposure mechanism is unknown, the same observed data can support multiple causal effects. This distinction determines the causal target. The study may record assignment and vaccination outcomes without recording receipt; for example, it may show higher vaccination among targeted accounts without revealing which receipt pathway produced that difference. The causal target is the effect of the specified physical exposure on the outcome. When several exposure mechanisms remain compatible with the observed data, the target is partially identified: the data determine a set or interval of possible effects rather than a single value. Theorem 5.1 makes the consequence precise by constructing observationally equivalent models with physical-exposure effects of opposite signs.

Active partial identification uses selected bridge measurements to narrow the set of effects compatible with the data. In our Abstract, we define active partial identification as using bridge experiments that measure physical exposure under selected assignments to narrow the union of candidate-implied causal targets. In the example, a bridge label records whether a person actually received the message under a selected assignment. TAB chooses assignments whose labels are informative about differences among candidate causal targets. The calibrated e-process accumulates evidence from these labels to update the retained candidates, and the causal envelope is the hull of their effect intervals. Theorem 5.3 establishes the envelope’s coverage guarantee under adaptive querying and stopping, subject to Assumptions 3.2–3.5.

B2. Research core and logical flow

Q: What is the paper’s research question, and how does the method address it?

A: The paper asks how to infer the effect of actual exposure when random assignment does not reveal who was exposed. We appreciate the reviewer’s request for a clear account of our research question. We study how to estimate the effect of actual physical exposure in a randomized network experiment when the assignment-to-exposure process is unknown. In the vaccination-message example, researchers randomize which accounts to target, but direct delivery, resharing, and feed ranking may produce different receipt patterns under the same assignment. Theorem 5.1 shows why this creates a fundamental identification problem: two mechanisms can produce the same observed assignment–outcome distribution while implying exposure effects with opposite signs. More observations of assignment and outcomes alone cannot resolve which exposure effect the data support.

TAB uses targeted bridge measurements to update candidate mechanisms and report an anytime-valid envelope of their effect intervals. Target-Aware Bridge Auditing (TAB) addresses this problem by adding selected measurements of actual exposure while keeping the main assignment–outcome sample fixed. For each candidate mechanism, the main-trial data first produce an effect interval. TAB then selects a bridge query according to how much it is expected to distinguish the candidate causal targets, accounting for label reliability and query cost. The observed bridge labels update the retained mechanisms through a calibrated e-process, and the reported result is the hull of the effect intervals for the retained candidates. Theorem 5.3 establishes coverage of this envelope throughout adaptive querying and stopping under Assumptions 3.2–3.5.

The experiments test both the coverage value of retaining multiple mechanisms and the query-efficiency value of targeting causal effects. The experiments evaluate the two central claims behind this design. The structural-validity experiment shows why the method retains multiple mechanisms during the audit: the union envelope achieves 0.9766 full-path coverage, while a single-map procedure achieves 0.3899, despite terminal coverage of 0.9849. The target-geometry experiment shows when adaptive measurement can reduce audit effort: in a setting where model and target geometries are misaligned, target-directed querying resolves the causal target in 1.875 exact queries on average, compared with 5.875 for count balancing; when the geometries align, both use six queries. These results illustrate the method’s two-part logic: preserve coverage across plausible exposure mechanisms, then use measurements chosen for their relevance to the causal target.

B3. Main theorem and roles of the theorems

Q: Which theorem is the main result, and what do the other theorems establish?

A: The main inferential result is Theorem 5.3, “Anytime-valid active partial identification.” The other theorems lead to this result and then explain how much auditing is needed.

The identification theorems explain why the analysis must retain a set of causal effects rather than select one exposure map. The logic begins with an identification problem. In a messaging experiment, two delivery mechanisms may produce the same observed assignment–outcome distribution while implying opposite effects of actual receipt. Theorem 5.1 establishes this sign ambiguity; Theorem 5.2 characterizes the full set of causal targets compatible with the main experiment and audit history. Together, they explain why we retain a set of candidate effects instead of reporting the result under a single presumed mechanism.

Theorem 5.3 is the central guarantee for that set-valued report. Under Assumptions 3.2–3.5, an e-process controls the chance of ever removing the true mechanism, even when bridge queries are chosen adaptively. Combining that retention guarantee with the candidate-specific effect intervals gives an envelope that covers the physical-exposure effect throughout the audit and at any almost-surely finite stopping time, with probability at least 1−α−δ1-\alpha-\delta. For example, we can inspect the envelope after each new receipt label and stop when it is sufficiently narrow without reallocating an error level at every look.

The audit-complexity results determine the measurements needed to resolve distinct causal effects, without requiring identification of every mechanism. The remaining results ask how efficiently the audit can narrow the envelope. Theorem 5.4 bounds the required query depth using the separation among causal targets and the availability of queries that split them. This makes the complexity target-dependent: if 100 candidate mechanisms imply only two distinct effect values, a query separating those two target groups can suffice; identifying every mechanism is unnecessary for resolving the effect. Theorem 5.5 gives information-per-cost lower bounds for searching among targets and confirming a separated alternative. Theorem 5.6 provides a search-and-confirmation algorithm for ordered target cells under feasible cuts and a common binary-symmetric channel. Finally, Theorem 5.7 quantifies sensitivity to approximation and departures from outcome exposure sufficiency.

Thus, Theorem 5.3 is the main inferential theorem; Theorems 5.1–5.2 establish why its target must be set-valued, Theorems 5.4–5.6 characterize and attain audit-efficiency scales, and Theorem 5.7 describes sensitivity. Figure 2 maps this progression onto our workflow.

B4. Notation in Equation (13)

Q: What does x+x_+ in Equation (13) mean?

A: Appendix A of our manuscript defines and indexes the notation used throughout. Table 1 lists each symbol, its meaning, and the location where it is first defined or used as a result. This includes the positive-part operator in Equation (13), x+=max⁡�0�x_+=\max�0�.

Closing

We hope these clarifications make the paper’s definitions, argument, and notation easier to follow. We appreciate the reviewer’s careful attention to these points.

AuthorsOpenReview ↗

Thanks for the review and here is the response

We sincerely appreciate the time, care, and thoughtfulness you have devoted to reviewing our work. As the deadline for this stage is now less than two days away, we would be more than happy to address any further questions and will respond promptly.

We sincerely hope that our clarifications and additional results have addressed your concerns. If so, we would be truly grateful if you would consider the re-evaluation and rating.

Thank you again for your time, expertise, and invaluable feedback. Your contribution has been instrumental in helping us improve this work.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response and Summary of Revisions

General Response to All Reviewers and Dear AC

We thank Reviewers bUVw, f8AF, and aubW for their comments. The revised manuscript clarifies the paper’s research question and algorithmic workflow (bUVw), explains how the assumptions guide study design and causal interpretation (f8AF, aubW), and reorganizes the experiments around the questions they answer (f8AF, aubW).

We revised the manuscript in response to the points below:

  1. Framework and presentation (Reviewer bUVw). The Introduction now gives a concise method workflow: the main experiment forms candidate-specific effect intervals, TAB selects target-aware probes, bridge evidence updates the retained candidates, and the paper reports the interval hull. We also added a local definition of the positive-part operator at Equation (13).
  2. Assumptions and causal interpretation (Reviewers f8AF and aubW). We clarified the distinct roles of bridge labels and outcome sufficiency, linked Assumptions 3.2–3.5 to the practical checks in Appendix Table 3, and connected departures from outcome sufficiency to the sensitivity analysis in Theorem 5.7.
  3. Experimental design and findings (Reviewers f8AF and aubW). Section 6 now explains each experiment’s purpose and takeaway alongside its setup and results. We report non-oracle precision across randomization-information levels, add the target-only comparison with count balancing, describe the incremental information from bridge labels with the main data fixed, and clarify the fixed-path analytic-band replay in Appendix F.3.

These revisions make the paper’s method, assumptions, and experimental findings easier to follow.


Reviewer–Revision Map

Anonymous ReviewerIssue and responseManuscript revision
bUVwDefinitions and research flow: The exposure mechanism and active partial identification are already defined in the paper. The Introduction now makes the TAB workflow explicit.Clarified the TAB workflow in the Introduction.
bUVwTheorems and notation: Theorem 5.3 is the main inferential result. The other theorems establish identification, audit complexity, and sensitivity results. x+=max⁡(x,0)x_{+}=\max(x,0).Added a theorem roadmap and defined x+x_+ beside Equation (13).
f8AFAssumptions in practice: Assumptions 3.2–3.5 address outcome sufficiency, candidate coverage, randomization support and dependence, and bridge calibration. The response links these conditions to study-design checks and sensitivity analysis.Added practical context for Assumptions 3.2–3.5 and linked them to Appendix Table 3.
f8AFExperiments and baselines: The experiments test coverage, query allocation, non-oracle precision, and latent-receipt sensitivity. Comparisons include count balancing, fixed cycling, target-only acquisition, and alternative reporting procedures.Expanded the experiment summaries and baseline comparisons in Section 6.
f8AFPrior work: The response distinguishes supplied exposure mappings, mapping-sensitivity analyses, and methods that acquire outcome data from TAB’s adaptive acquisition of exposure labels with the main sample fixed.Clarified the paper’s positioning in Related Work.
aubWNon-oracle precision: F.3’s analytic replay remains wide in its tested configuration. Tables 6 and 12 show precision varying with randomized-block information; Table 13 isolates bridge-audit gains with the main data fixed.Clarified the analytic replay and non-oracle precision results.
aubWTarget-aware acquisition: Table 12 shows a setting where count balancing performs slightly better. Table 8 and the F.3 ablation provide controlled comparisons that isolate the target-aware score.Added controlled comparisons of target-aware acquisition and count balancing.
aubWOutcome sufficiency: The causal interpretation is conditional on Assumption 3.2. Sender identity or dose can be included in the exposure definition; Theorem 5.7 addresses bounded departures from sufficiency.Clarified the outcome-sufficiency condition and its sensitivity analysis.

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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