Active perception treats sensing as an action rather than a fixed input [1], [2]. Learned glimpse policies [11], [12] and attention mechanisms [17] offer possible architectures, but their learning objectives and sensing assumptions differ. In the present design, acquisition and terminal decisions share a budget; the executed proxy study uses committee scores and one-step rules rather than a trained glimpse or attention policy. Bayesian experimental design values an acquisition by integrating posterior information over possible observations [16]. Active learning uses related criteria for label queries [18]. Some acquisition methods are myopic and others plan over budgets; the entire literature cannot be characterized as ignoring future opportunities. The proposed learned policy would address sequential value, while the executed study uses one-step rules.

Industrial defect detection was transformed by the availability of realistic public data, above all the MVTec Anomaly Detection dataset with its fifteen object and texture categories and pixel-precise ground-truth masks [3], later extended in a journal treatment [19] and to logical anomalies [20]. Method families are complementary: GANomaly trains a generative model to reconstruct only nominal appearances and detects deviations in latent space [4]; PaDiM models per-patch distributions of pretrained features [5]; and PatchCore retrieves from a memory of nominal patches, scoring test patches by core-set distance [6]. A unifying review situates these methods against classical shallow baselines and catalogues their assumptions [7]. Backbone capacity matters, with residual and very deep convolutional networks the default feature extractors [21], [22], and robustness of such pipelines to common corruptions is an active concern [23].

Industrial inspection often uses a station-defined acquisition arrangement; the cited anomaly detectors evaluate images after acquisition [3–7]. Corruption studies [23] can assess robustness to input changes, whereas the present decision problem also chooses whether to acquire another view. In Section 5, handwritten-digit images act as proxy parts and deterministic crops or downsamples as distinct information channels. This demonstrates a comparison within that proxy, not transfer to an industrial imaging station.

Sequential acquisition can be formulated through a partially observed process [24]. Reinforcement-learning algorithms [13], [14], [25] and exploration criteria [26–28] motivate possible policies, but none is trained in this study. Wald’s test uses accumulated likelihood ratios under specified sequential sampling assumptions [15]. A discriminative posterior computed from overlapping views is not automatically that likelihood-ratio process. Cost-sensitive learning supplies decision-cost modeling [29]; the executed payoff prices the two error types equally.

Ensembles [8], dropout [9], and calibration methods [10] offer practical evidence models. Member disagreement is a proxy and can be small when every member is wrong. Calibration on nominal examples alone cannot identify a posterior defect probability without information about defective observations and prevalence. The supervised committee used in Section 5 has a different training regime from the proposed nominal-only anomaly scorer.

Table 1 contrasts selected approaches with the proposed AVID architecture. Its proposed row describes design capabilities rather than executed components. These comparisons are not an exhaustive claim that the integration is absent from prior work. The present evidence concerns a digit proxy with preview-assisted policies; learned stopping and asymmetric-cost operating points remain future evaluations.

The design questions address evidence aggregation, planning over remaining budget, and exploration. They organize future tests of the complete architecture. The reported committee experiment evaluates handcrafted selection and stopping, rather than the learned policy or exploration procedure.

RQ1 asks how to aggregate available view evidence and quantify uncertainty under a finite acquisition budget. RQ2 asks whether a learned joint policy improves the quality–cost trade-off at matched scorer capacity and information access.

RQ3 asks whether disagreement and information-based exploration improve learning. That learning comparison is unexecuted here.

H1 predicts a target detection AUC with fewer acquisitions for a learned policy under matched scorer and preview access.

H2 predicts an advantage for planning over myopic selection at small budgets. No reinforcement-learning planner is tested.

H3 predicts useful operating points under asymmetric decision costs. The reported symmetric payoff does not test it.

A part x has a hidden label y∈{nominal,defective}. Acquiring configuration v∈V produces observation Zv, represented by an image Iv=T_v(x) with any specified sensing noise. M ensemble members produce scores and disagreement. The belief bt summarizes acquired evidence. The policy selects an unvisited view or a terminal decision d∈{accept,reject,escalate}, and acquires at most B views. Utility U(d,y) may encode asymmetric decision costs in the design, while the executed experiment uses equal penalties for both error types.

Eq. (1) defines the unshaped net-utility objective. Eq. (2) specifies an aggregation interface rather than a proven Bayesian update. Eq. (3) defines genuine expected information gain by averaging over the predictive distribution of a prospective observation Zv. It requires an observation model. Arbitrary entropy bonuses are not generally policy-invariant shaping; a decaying bonus alone does not guarantee convergence to an optimum of Eq. (1). The experiment uses a preview entropy score instead of evaluating Eq. (3).

max [U(dT, y) − ∑ cacq (vt)] , T ≤ B. (1)

bt+1 = Ψ(bt, vt+1, st+1, ut+1), sv = ∑ hm (Iv), uv = SDmhm(Iv). (2)

EIG(v ∣ bt) = Zv∼p(⋅∣bt,v)[DKL(p(y ∣ bt, Zv, v)‖p(y ∣ bt))]. (3)

The finite budget and utility can price both errors and escalation. An ensemble score does not automatically constitute a calibrated belief; its interpretation must be validated. Formal expected information gain averages over observations before acquisition, whereas the tested rule evaluates actual candidate features in advance. Evaluation separates ordered-view AUC from deployed accuracy, acquisition count, and utility.

The proposed design has an acquisition model, ensemble scorer, evidence aggregator, and learned policy over acquisition and terminal actions. Nominal-only anomaly scoring and PPO policy training are possible implementations, not the implemented committee experiment. Any ratio-based fallback requires a justified likelihood model for Wald error bounds; otherwise it is an interpretable heuristic.

The acquisition set is finite and known costs are specified per configuration.

Physical validity of transformed views requires measurements; two-dimensional resampling does not reproduce new viewpoints or relighting in general.

A nominal-only anomaly score requires additional calibration evidence before it is read as defect probability. The tested committee is supervised.

Prevalence and sample dependence must be specified. Drift may require recalibration but is not automatically corrected by it.

The acquisition budget B and terminal costs are externally specified.

The proposed acquisition model would apply geometric and photometric transformations, potentially using differentiable resampling [30]. Two-dimensional crops and resampling do not reproduce a new physical viewpoint or illumination geometry. The executed study uses only the six deterministic digit transforms of Section 5.1.

Each acquired view supplies member scores, their mean, and disagreement. The full architecture would use independently trained scorers [8]. Temperature scaling calibrates supervised probabilities under an appropriate validation design [10]; nominal-only calibration cannot determine defect odds by itself. Disagreement may indicate sensitivity among fitted members but need not increase for every informative or hazardous observation.

The belief encoder consumes the set of evidence records together with their acquisition parameters. Each record is embedded and annotated with a positional code of its configuration, and an attention block with masking over unvisited configurations aggregates the records into a recurrent belief token [17]. The policy head outputs a categorical distribution over unvisited acquisitions and the three terminal actions, with visited views masked so that repeated acquisition is structurally impossible. A value head supports proximal policy optimization. The architecture is deliberately set-based: order invariance over acquisitions removes spurious sequence effects, and the mask makes budget accounting explicit, since the action space shrinks deterministically as the episode proceeds.

Two design choices deserve justification. First, acquisition parameters are embedded alongside evidence because the value of a view depends not only on what was seen but on what was looked at; two identical scores from orthogonal view geometries carry different implications. Second, the terminal actions are part of the same policy rather than a separate classifier, because the option value of continuing, one more acquisition versus deciding now, is exactly the quantity the value head must learn, and separating the decisions would force a hand-crafted arbitration between them.

A future PPO policy could optimize terminal utility minus acquisition costs [14]. Information and disagreement bonuses would define additional training objectives; their effects and decay schedule require empirical evaluation, without a policy-invariance guarantee. The ratio fallback can use target-error thresholds as design parameters, but formal sequential error bounds require verified likelihood assumptions and dependence treatment. Neither this training procedure nor escalation is executed by the committee study. Algorithm 1. AVID decision loop for one part.

Input: part x; scorer ensemble h_1,…,h_M; evidence aggregator Ψ; policy πθ; acquisition budget B; terminal decision costs; ratio thresholds A_L, A_U and a justified evidence model 1: E ← empty evidence set; visited ← empty set 2: for t = 1,…,B do 3: b_t ← Ψ(E, visited) 4: choose a_t from πθ given b_t and B−|visited| 5: if a_t is a terminal decision d then 6: compute a sequential evidence ratio under the specified model if the policy and ratio rule disagree, set d ← escalate 7: emit d and the acquisition record; stop 8: else 9: I_v <- acquire(x, a_t); (s_v, u_v) <- ensemble evidence 10: E ← E ∪ {(a_t,s_v,u_v)}; visited ← visited ∪ {a_t} 11: end if 12: end for 13: if no decision was emitted, apply the configured ratio rule; set d ← escalate if inconclusive; otherwise choose accept/reject, then emit d Output: decision d in {accept, reject, escalate} and audit record

Per-view cost includes transformation, M scorer evaluations, evidence aggregation, and any sensor movement. Preview policies also score unvisited candidates. Such work is not covered by counting acquired views alone. Caching may reduce simulation work but does not remove a physical information-acquisition cost; runtime must be measured at the intended station.

Several failure conditions can be identified in advance. They are stated here so that negative results can be localized, and each is paired with its planned mitigation.

I. Transform-reality gap: two-dimensional transforms cannot capture parallax, true perspective, and surface-relief shading; conclusions must be re-validated on physical stations before transfer claims are made. II. Ensemble degeneration: correlated members understate disagreement, starving both exploration and stopping; mitigated by member decorrelation and monitored by calibration metrics.

III. Cost misspecification: wrong penalties shift operating points silently; mitigated by sweeping the penalty ratio and reporting the full operating curve rather than a single point.

IV. Degenerate policies: always-reject or always-accept attractors under asymmetric costs; mitigated by curriculum design and by anchoring evaluation against the sequential-ratio baseline.

V. Prevalence drift: a shifted defect rate miscalibrates the posterior; mitigated by periodic recalibration and by reporting sensitivity to prevalence misspecification.

The reported study uses the 1,797 8×8 grayscale images distributed by scikit-learn’s load_digits interface [31], derived from the UCI optical-recognition data [32] It defines proxy defects by digit classes ({3,8,9} in the main composition; prevalence 0.299), not industrial damage. Six transforms expose four quadrant crops and two global 2×2 block-mean downsamples, one preceded by Gaussian smoothing with σ=0.8. Training-split standardization is described per 16-feature block. Acquired blocks fill a 96-feature vector, and unacquired blocks are zero. MVTec evaluation [3] is future work, and a dated preregistration is not established.

The belief model is a supervised bagged committee of ten logistic regressions [33]. Bootstrap fitting includes random view masks, retaining each view with probability 0.5 and at least one view. The committee mean is used as a defect score, without an automatic calibration guarantee. The five policies are random order, fixed order, maximum preview disagreement, a posterior-odds threshold rule labeled SPRT, and AVID preview selection with one-step stopping. AVID scores a candidate by current binary entropy minus the mean member entropy after inserting its actual features; this can be negative and is not the expected information gain of Eq. (3). Its stopping score is six times the predicted reduction in min(p,1−p), compared with cost 0.15. The ratio baseline uses posterior odds divided by prior odds between thresholds 0.05 and 20. Overlapping deterministic views do not justify treating this discriminative ratio as a product of independent likelihood ratios, so Wald guarantees are not assigned. Confidence baselines use threshold 0.90. These settings are reported without a timestamped prespecification record.

AVID and disagreement-greedy selection evaluate actual candidate features before their acquisition is charged. This is an oracle preview in the proxy experiment, not a measured coarse physical preview. Non-preview baselines have unequal information access. Net utility is correct=+1, wrong=−5, minus 0.15 per acquired view; its expectation is 1−6e−0.15v, where e is the error rate and v the mean count. Changing a wrong decision into a correct one gains six, not four. The protocol uses stratified 60/20/20 splits, twenty seeds for each of three compositions, and separate no-stopping AUC curves and deployed stopping metrics. The stated 126 s runtime and software configuration require original logs; view counts omit preview scoring and possible physical preview costs.

Table 3 reports one-view AUC 0.9522 for preview-based AVID, versus 0.8636 for random, 0.8556 for fixed, and 0.7541 for preview-disagreement selection. At two views the AVID value is 0.9667, and all policies reach 0.9806 at six. This comparison mixes selection with access to unacquired features. The lower disagreement-greedy result is an observation, not proof that disagreement always selects the least informative view.

AVID stops after 1.65 views on average versus 3.90 for the ratio baseline, a reduction of about 58%. Its reported accuracy is 0.8650 and utility −0.058, versus 0.9368 and +0.036 for the ratio baseline. Fixed and random confidence stopping have utilities +0.198 and +0.190. The source primary utility contrast reports W=11, p≈1.0e−4. Thus lower counted acquisition volume does not imply better utility under the stated payoff. Inference remains exploratory across overlapping repeated splits.

The AVID and disagreement policies use actual unacquired candidate features as previews (Fig. 1).

Table 4 shows the accuracy–cost trade-off. Always acquiring six views gives accuracy 0.9392 and utility −0.265, compared with 0.8650 and −0.058 for AVID stopping. The utility gain ≈0.207 combines cost saving 0.15×(6−1.65)=0.6525 with loss in decision payoff 6×(0.9392−0.8650)=0.4452. Accuracy is therefore materially lower, not almost unchanged. Replacing preview selection with random next views gives 3.48 views, accuracy 0.9065, and utility −0.083. These contrasts concern combined selection/stopping behavior and preview access.

Under the thin-stroke composition, AVID reports 1.32 views and utility −0.243; under the alternative dense composition its utility is approximately zero. Composition changes task labels, prevalence, and view informativeness together. These patterns do not isolate a causal effect of semantic evidence sparsity or validate reinforcement-learning exploration.

Table 6 retains the source Wilcoxon [34], Holm [35], and Friedman [36], [37] summaries. The reported Friedman statistic is χ²(4)=69.72, p=2.60e−14. Utility mean ordering is fixed, random, ratio, AVID, then disagreement. A nonsignificant AVID-versus-disagreement test is not equivalence. The twenty repeated splits reuse the same corpus with overlapping examples, so the test assumptions and dependence require inspection. Wilcoxon assesses signed-rank differences, not arithmetic mean direction or acquisition-cost efficiency.

The preview selector has the highest displayed one-view AUC, but it uses privileged candidate content. The reported 78% of 48.6 wrong decisions per seed that would become correct with all six views is a retrospective overlap count requiring prediction records. It identifies potentially recoverable exits, not their unique cause. Complementary-view value is a possible explanation for myopic stopping, but confidence errors, preview modeling, and split variability are alternatives. Full-view accuracy 0.9392 does not imply that every individual additional view is valuable.

The committee realization has lower AVID utility than the ratio and confidence-stopping baselines, despite fewer counted views. The proxy uses deterministic 8×8 images and supervised linear models. Reinforcement learning, attention aggregation, escalation, and asymmetric error costs are not executed, so H1–H3 about the complete design are not resolved by this campaign.

The reported proof-of-concept outcomes require the exact split indices, view transforms, committee predictions, policy traces, and executable implementation for independent verification.

The digit proxy does not measure industrial damage, real viewpoint costs, or sensing noise. Its results cannot establish either absolute or relative performance at a physical station. Nominal-only scoring is a proposed component, while the tested committee uses defect labels. Unpriced oracle preview is a central information-access limitation. Repeated splits, probability calibration, joint-view dependence, and prevalence changes further bound inference. Station scheduling and asymmetric economics remain untested.

Acquiring all views may be rational when error costs dominate acquisition costs. Here it improves accuracy while lowering utility under one chosen payoff. Greedy and confidence rules are useful comparators, but this experiment contains no learned planner. A ratio rule is auditable without being a formally valid Wald test. Physical previews and escalation need explicit observation and cost models.