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Stand-In Effects and Pooling Amplification: Lessons from Biological World Models for Testing Action Effects

Abstract

Whether an action-conditioned world model responds to actions is usually checked by replacing or removing the actions and measuring the loss in accuracy. Taking biological experiments as the guiding case, we show that such diagnostics report action effects where there are none: under autocorrelated designs, future actions stand in for history the model does not see. When the design law is known, a conditional randomization test written as an e-value is valid in finite samples whatever the model. A second failure arises whenever many sites share one action sequence, as in world models: the pooled score turns small model errors along the action contrast into an e-value near zero, so a valid test loses its power although the effect is real. Tempering the score changes the bet, not the validity. The log e-value is concave in the tempering factor and zero at zero, so too small a factor costs little and too large a one can cost everything; every single factor we tried, estimated or tuned, failed in some setting, and mixtures over a fixed grid never did. Our own preregistered analysis of optogenetic ERK experiments failed by pooling; a tempered statistic, registered before the data were obtained, then rejected the null on a never-opened field (E = 1.1e10). In three registered tests on models trained by others, the pooled test rejected in 0 of 96 units of a diffusion model, and reached the power bar in 10 of 26 Atari games under IRIS's token likelihood and 1 of 6 control tasks under TD-MPC2; mixtures fixed in advance reached it in 96 units, 24 games and 6 tasks. On recorded robot video with iVideoGPT the mixture rejected in 155 of 159 trajectories; the pooled test did not collapse there (143). Under exact nulls the statistics made 14 rejections in 26,664 tests.

Introduction

World models that predict how a system will evolve under a sequence of actions are now trained on data from experiments as well as from simulators. In biology the actions are often stimulation programs—light pulses delivered to optogenetically engineered cells, for example—and the hope is that a model trained on such data will answer interventional questions: what would this cell population do under a different program? Before such a model is trusted for that purpose, one wants to know whether its action channel reflects a causal effect of the actions at all. In machine learning this is usually checked with diagnostics that replace the actions by zeros, by another unit’s actions or by a shuffled sequence, or retrain the model without them, and report an effect if predictions get worse. Recent benchmarks for action following in world models instead compare generated rollouts with simulator replays of expert and off-expert actions [9, 10], or score rollouts under perturbed or commanded actions with trajectory estimators, vision-language judges or human annotation [47 b]; Oefinger et al. [35] propose a ladder of checks that a world-model simulator must pass before its verdicts are trusted. None of them reports a test with finite-sample error control. Neither route is available, or reliable, when the data come from a real experiment that cannot be replayed.

The stand-in trap. Replacement diagnostics fail in a simple way. Experimental designs are often autocorrelated: the next stimulus depends on the stimuli before it. A model that sees only a window of recent history can then use the future actions as a stand-in for earlier history that still drives the outcome. Its predictions change when the future actions change, so every replacement diagnostic reports an effect, even when the actions have none; and a model that predicts better learns the stand-in better (Proposition 6). In development simulations the replacement diagnostics reported effects in up to 249/256 replicates of such a null with twelve units, and in 256/256 for every model with 512 units; in a pixel world in which the logging policy depends on state the model cannot see they do so in 64.1% to 100% of test episodes (§7, Figure 4).

A design-based test. When actions were assigned by a randomized program whose law is known, that law supplies exactly what the diagnostics lack. Drawing alternative action blocks from the design law, given everything the design conditioned on, yields blocks that carry the same stand-in information as the observed one; under the null of no effect within the horizon the observed block is exchangeable with them. Scoring the observed and the resampled blocks with the world model gives a conditional randomization test ([7]) in which the model is only a statistic: it determines power, never validity. Written as an e-value, the test can be multiplied over time and across units and averaged across models without any assumption on the model or on shared noise (§ 3, Proposition 1). The conditioning matters: in a post hoc analysis, a resampler that draws each action from its marginal frequency rejected the same pixel-world null in 98.4% to 100% of episodes, while the design-law resampler rejected in none for the two-model average (§ 7.2).

Pooling amplification. World models raise a second difficulty that does not arise for a single outcome. In an ERK optogenetics experiment, each microscope field receives one light program and records hundreds of cells; in a pixel world, every pixel of a frame shares the frame’s actions. The natural statistic sums the sites’ log predictive densities and bets on the result. If the model errs along the action contrast in a way the sites share, the sum multiplies that error by the number of sites, and the e-value is driven toward zero however strong the true effect is (§ 3.3). We met this failure in our own registered analysis: on the ERK positive controls, where light is known to drive the reporter, the pooled statistic gave log E=−9576E = -9576 (§ 8.2). In the pixel world, its median log EE fell from −17.3-17.3 to −6832-6832 as frames grew from 64 to 4096 pixels, while the oracle’s rose from 79.0 to 157 (§ 6, Figure 1).

Figure 1. Pooling amplification in a pixel world model. Median log EE over test episodes at the larger effect size as frames grow from 64 to 4096 pixels, without shared noise (A), with a frame-wide additive offset (B) and with a multiplicative gain on the blob (C). The pooled, Kish-tempered and contrast-tempered statistics are averages over the two learned models; the oracles use the true dynamics with independence pooling or with the exact joint likelihood. In A and C the Kish factor is close to one and the Kish-tempered curve coincides with the pooled one; the two oracle curves nearly coincide in every panel. Dotted line: log 20, the rejection threshold. Symmetric-log axis, linear for ∣log⁡E∣≤10|\log E| \le10.

A repair that cannot break validity. Because the design, not the statistic, controls the error rate, the pooled score may be tempered by any factor fixed on training data. We temper by an inverse design effect: the statistic registered for our confirmatory test uses the Kish factor of the residual correlation, and an exploratory variant measures the design effect along the action contrast, which is what governs amplification (§ 3.4). The Kish-tempered statistic, selected on synthetic data, gave log E=349E = 349 on the same ERK test fields in an exploratory reanalysis, and in a confirmatory test registered before the data were obtained it rejected the null on an ERK field that no one involved had opened, with E≈1.1×1010E \approx1.1 \times10^{10} (§ 8.4). In the pixel world, where the Kish factor does not capture the relevant correlation, contrast tempering restored power under every noise condition we simulated, at the larger of the two effect sizes. Estimated factors are fragile, however. The Kish correlation factor and the contrast factor do not change when all per-site precisions are multiplied by one common factor, with predictions, residuals and contrasts held fixed, whereas for unfloored Gaussian scores the tempered log-ee curve shifts along the log-temperature axis (Proposition 9). A mixture over GG fixed tempering factors needs no estimated factor and loses at most log⁡G\log G in log e-value relative to the best member of that grid chosen in hindsight (Proposition 10); in an exploratory comparison on the saved pixel and ERK-like runs it matched contrast tempering in the pixel world and Kish tempering on ERK-like data (§ 6.4). A weighted version that puts most of its weight on the factor chosen on validation data keeps most of validation tuning’s power when that choice transfers, and the mixture’s protection when it does not (§ 3.5, § 6.5, § 8.6). One property explains why single factors fail and mixtures do not: the log e-value of a unit is concave in the tempering factor and equals zero at zero, so a factor below the best one keeps a proportional share of the evidence, while a factor above it can lose everything (Proposition 13, § 12).

Published world models. If pooling amplification is a property of pooled scores and not of our models, it should appear on world models trained by others. We registered three confirmatory tests on released checkpoints that we neither trained nor modified. On DIAMOND, a diffusion world model for Atari games (Alonso et al., [1]), with the mixture as the primary statistic, the pooled score rejected in 0 of 96 units of Boxing, Pong and Breakout in which random actions moved the player, paddle or ball, Kish tempering in 0 and contrast tempering in 1; the mixture rejected in 96 (§ 9). The second test covered IRIS, a token-based Transformer world model for 26 Atari games (Micheli et al., [32]), and TD-MPC2, a latent world model for continuous control (Hansen et al., [19]), with a validation-weighted mixture fixed before the data as the primary statistic. Under IRIS’s own token likelihood the pooled score reached the registered power bar, 24 of 32 units, in only 10 of the 26 games; under TD-MPC2’s latent score it did so in 1 of 6 tasks. The weighted mixture reached it in 24 of 26 games and in all 6 tasks (§ 10). The third test used recorded video of a real robot, which cannot be replayed: BAIR robot pushing ([12]), scored by iVideoGPT ([46]). Its null arm is exact by construction; its arm with the recorded commands measures power and is conditional on a design law reconstructed from the command records. The weighted mixture rejected in 155 of 159 trajectories. The pooled score did not collapse there: it rejected in 143, and failed badly only in a few trajectories, where the mixture’s loss stayed bounded (§ 11). Under exact nulls the statistics of the three tests made 14 rejections in 26,664 tests.

Contributions.

  1. We describe the stand-in trap for action diagnostics of learned world models, give a construction in which replacement diagnostics detect a nonexistent effect with probability tending to one (Proposition 6), and show that a design-based test avoids it only if its resampler conditions on the full state the design used; validity also extends to feedback designs under a conditional product law (Assumption 2), for which fixed policies that read observed history with a lag of at least the horizon, use independent randomization and do not read other units’ actions inside the block are a sufficient construction (Proposition 12).

  1. We identify pooling amplification, a failure of pooled scores when many sites share an action sequence. It is driven by errors that the sites share along the action contrast—chiefly model misspecification, but also shared noise that lies along the contrast—grows with the number of sites, and is invisible to the usual validation, which ours missed (§ 5.3).

  1. We show that within the randomization test, tempering is merely a choice of statistic, fixed on training data and incapable of affecting validity, and we propose measuring the design effect along the action contrast; when the contrast is shared across sites this reduces to a weighted Kish factor (Proposition 7). We show that the Kish and contrast factors are invariant under a common rescaling of the per-site precisions that moves the tempered log-e curve, and that a mixture over a fixed grid of factors loses at most the logarithm of the grid size in log e-value relative to the best of them (Propositions 8–10); a version that puts most of its weight on the factor chosen on validation data loses at most log(4/3) relative to that factor (§ 3.5).

  1. We give design-only bounds on what any statistic can achieve, computable from the command records before any outcome is opened (Proposition 4); they are elementary, but they tell an analyst in advance whether an experiment can yield evidence at all.

  1. We confirm, in three registered tests on four published world-model families—a diffusion model, a token-based Transformer, a decoder-free latent model and a video-token model, on 26 Atari games, 6 control tasks and recorded robot video—that pooling amplification occurs on models we did not build; that tempering by estimated factors did not prevent it; and that mixtures fixed in advance restored or kept power while every statistic kept its error rate under exact nulls (§ 9–§ 11). On the robot video and in three Atari games the pooled score of a model’s own token likelihood did not collapse, and we say where it does and does not (§ 13).

  1. We show that the log e-value of a unit is concave in the tempering factor and zero at zero (Proposition 13). Hence every negative tempered log e-value is an over-bet, a factor below the best keeps a proportional share of the evidence, and a mixture over a dyadic grid keeps at least half of the best log e-value of any factor in its range, minus the logarithm of the grid size. In 4512 saved units, every observed collapse was an over-bet (§ 12).

  1. We report a complete, preregistered validation pipeline for world-model action tests on real experiments, including its failures, with every reported number generated from committed, hashed result files.

Related work. Randomization tests for experiments in which treatments act over time are established: exact tests of the sharp null of no temporal causal effect, with lag-pp causal estimands, for time-series experiments ([4]); conditional randomization tests of partially sharp nulls indexed by a lag in stepped-wedge trials, and by a distance for spillover ([50]); and tests of the carryover horizon and of non-anticipation in switchback experiments ([26]). The use of machine-learning predictions as randomization-test statistics is also established ([40, 18, 17]); we use both and claim neither. E-values and testing by betting ([38, 44, 37, 15]) give the aggregation we rely on; model-X conditional-independence tests with e-values ([16]) and sequential Monte Carlo tests ([13]) are close relatives. Tempering likelihoods under misspecification is established in generalized and safe Bayesian inference ([14]), and learning or weighting a grid of learning rates in online learning ([23, 42]); we make no priority claim for tempering, for mixtures or for rank calibrators. The tempering formulas are standard; §3.4 and §3.6 give their sources, and the contrast factor resembles the score-based rescalings used in composite likelihood. Criticism of permutation-based feature importance for forcing extrapolation ([21, 5]) and work on causal confusion, copycat behaviour and policy confounding in imitation and reinforcement learning identify related shortcuts; those works ask whether a policy has learned the wrong cue and repair it with targeted interventions ([11]), adversarial removal of the nuisance information ([45]), or a broader distribution of trajectories ([39]), whereas we ask whether a world model’s action channel reflects an effect and use only the known design, with finite-sample error control. Design-respecting world models ([49]) and advantage-style action channels that contrast a world model’s predictions across actions ([25]) are conceptually adjacent. In biology, randomized optogenetic stimulation has been used for causal inference ([27]); we analyze two published optogenetics datasets ([34, 29]), released as Nałęcz-Jawecki et al. [33] and Lugagne et al. [28].

Organization. Section 2 sets up units, sites, designs and nulls; §3 gives the test and the tempered statistics; §4 states the theory. Sections 5–7 report synthetic validation, pooling amplification and its repair, and the stand-in trap; §8 reports the real-data evidence, and §9–§11 the registered tests on published world models, the last on recorded robot video; §12 gives one account of every collapse; §13 compares all settings and discusses limitations. The appendices give proofs, design laws, all tables and disclosures, the registrations and hashes, the baseline study, the full records of the three published-model tests, and the exploratory studies run after the second version of this paper.

Problem setup

Units, sites and actions

We observe assignment units i=1,…,Ni=1,\ldots,N at discrete times tt. At each time unit ii receives an action Ai,t∈AA_{i,t} \in\mathcal{A}, and outcomes Yi,c,tY_{i,c,t} are recorded at each of its measurement sites c∈Cic \in C_i. All sites of a unit share the unit’s action sequence: actions are assigned to units, not to sites. This distinction matters throughout the paper. In the CcaS/CcaR optogenetic experiment a unit is one cell lineage with a single site; in the ERK experiment a unit is a microscope field, and its sites are the hundreds of cells that receive the same light program; in a pixel world model a unit is an episode and its sites are pixels.

Write a=(aj,s)a=(a_{j,s}) for a complete assignment of actions to all units and times, and Yi,c,s(a)Y_{i,c,s}(a) for the corresponding potential outcome. We assume no anticipation: Yi,c,s(a)Y_{i,c,s}(a) depends on aa only through (aj,r)r≤s(a_{j,r})_{r\leq s}. Observed outcomes are Yi,c,s=Yi,c,s(A)Y_{i,c,s}=Y_{i,c,s}(A). For an original tt and a horizon h≥1h\geq1, the future block of unit ii is Ai,tF=(Ai,t+1,…,Ai,t+h)A^F_{i,t}=(A_{i,t+1},\ldots,A_{i,t+h}) and the targets are Yi,c,t+hY_{i,c,t+h}. Let Ft\mathcal{F}_t denote the observed joint history up to tt: all units’ outcomes and actions up to tt, the clock, and any further covariates that are functions of the past.

Randomized open-loop design

Assumption 1 (Design). For every origin tt, conditionally on Ft\mathcal{F}_t and on all potential outcomes,

A⋅,tF∼∏iQi,t,A^{F}_{\cdot,t} \sim\prod_i Q_{i,t},

where Qi,tQ_{i,t} is a known law over future blocks that depends only on unit ii’s own past actions Ai,≤tA_{i,\leq t} and on a design stratum fixed in advance.

Assumption 1 states that actions were generated by an open-loop randomized program that did not look at outcomes. We call Qi,tQ_{i,t} the design law. In the experiments we analyze it is reconstructed from the published protocol and acquisition code (Appendix § 17); every validity statement is conditional on that reconstruction, which we call a working law, and approximate laws are treated in § 4. Two features of the design law matter below. First, Qi,tQ_{i,t} may depend on the unit’s entire action history, typically far more of it than a predictive model conditions on. Second, a unit whose design is deterministic at tt (a zero-entropy law) carries no randomization information, and contributes an e-value of exactly one.

Designs that read past outcomes. Assumption 1 describes open-loop programs. Some experiments, including the trap experiment of § 7, use a logging policy that reads earlier outcomes or states. The validity results extend to such designs under the following assumption.

Assumption 2 (Design with delayed feedback). For every origin tt, conditionally on Ft\mathcal{F}_t, on all potential outcomes and on the frozen training and design information,

A⋅,tF∼∏iQi,t,A^{F}_{\cdot,t} \sim\prod_i Q_{i,t},

where each Qi,tQ_{i,t} is known and Ft\mathcal{F}_t-measurable. For the own-channel null of § 2.3 with a tested independent set II, the same product form holds for the blocks of the units in II conditionally also on the future blocks of all units outside II.

Assumption 1 is the special case in which Qi,tQ_{i,t} depends only on the unit’s own past actions and its stratum. The product form is essential: a known marginal law for each unit does not justify multiplying unit-wise factors when one unit’s policy can react to another unit’s actions inside the block. Proposition 12 shows that the validity results hold under Assumption 2, and gives a sufficient condition: each unit’s policy reads observed history only with a lag of at least hh, never another unit’s actions inside the block, and uses fresh randomization independent of everything else.

Partial sharp nulls

Definition 1 (Global sharp-in-future null). H0G(h)H_0^{G}(h): for every unit ii, site cc and origin tt, Yi,c,t+h(a)=Yi,c,t+h(a′)Y_{i,c,t+h}(a) = Y_{i,c,t+h}(a') whenever aa and a′a' differ only in the future blocks a⋅,tFa^{F}_{\cdot,t} of any units.

Definition 2 (Own-channel null). Given a spillover graph N\mathcal{N} on units, H0own(h;N)H_0^{\mathrm{own}}(h;\mathcal{N}): for every unit ii, site cc and origin tt, Yi,c,t+h(a)Y_{i,c,t+h}(a) is unchanged when ai,tFa^{F}_{i,t} alone is changed. Future actions of N\mathcal{N}-neighbours may affect Yi,c,t+hY_{i,c,t+h}; units that are not neighbours have no effect.

Both nulls are sharp: they constrain every unit’s potential outcomes, not an average effect. A rejection therefore means that some site responds to some future action, not that the response is large or typical. Both are partial: they concern only the effect of the next hh actions on the outcome at t+ht+h. Actions before the window may have arbitrary effects—this is the dependence that makes action-conditioned prediction possible. At the same target times, the null for horizon hh therefore implies the null for every shorter horizon, but not for a longer one, whose window includes earlier actions. Shared noise of any form, across sites or across units, is allowed. Rejecting H0GH_0^{G} means only that global future-action invariance fails; attributing an effect to a unit’s own actions requires H0ownH_0^{\mathrm{own}} and its layout assumptions. Conditional randomization tests of partially sharp nulls are not new: Zhang and Zhao [50] test nulls indexed by a time lag for lagged treatment effects in stepped-wedge trials, assuming no interference and no anticipation, and nulls indexed by a distance threshold for the range of spillover effects; our contribution is not the null, but the analysis of what goes wrong when it is tested with learned models (§ 2.4 and § 3.3).

Admissible statistics. A statistic for unit ii at origin tt may use any Ft\mathcal{F}_t-measurable covariate, unit ii’s own targets Yi,c,t+hY_{i,c,t+h}, and unit ii’s candidate future block, and nothing else. In particular, no statistic may use other units’ future actions, and under H0GH_0^G none may use other units’ targets, which can respond to unit ii’s future actions through spillover. This is a requirement to be verified for each dataset, not an assumption: in the CcaS release, for example, the neighbour-exposure covariate is aligned one step ahead of the neighbours’ commands and must be replaced by its lag (Appendix § 17). Which sites contribute at an origin is determined by an observation mask (finite own history and target). That this mask does not respond to future actions under the null is a stated assumption about the measurement process; formally, the measurement process, including any randomness in it, is part of the potential outcomes on which Assumption 1 conditions.

Stand-in effects

An action-conditioned world model predicts Yi,c,t+hY_{i,c,t+h} from a finite window of the past together with the future block. Under an autocorrelated design the future block is correlated with actions that precede the window, and those earlier actions may affect the target through the system’s memory. The future block then carries information about the target that the window lacks, even when H0GH_0^G holds: future actions act as a stand-in for omitted history. A model trained to predict will use this information, and its predictions will change when the future block is changed.

Common action diagnostics read this change as an action effect. They compare predictions under the observed block with predictions under inputs that break the stand-in dependence—all-zero block, a block taken from another unit or another time, or a model retrained without actions—and report an effect when the prediction loss rises. We call all of them replacement diagnostics (the pixel protocol of § 7 and Appendix § 21 calls them common diagnostics). Nothing in these comparisons controls how often they do so when no effect exists, and a model that predicts better learns the stand-in better. Proposition 6 gives a construction in which the zero-block, other-unit and retraining diagnostics report an “effect” with probability tending to one under H0GH_0^G; blocks taken from another time of the same unit are not covered by it.

The design law removes the problem. Blocks drawn from the full history-measurable design law Qi,tQ_{i,t} retain the dependence on the recorded design state that the observed block has, so they carry the same stand-in information; under Assumption 1 this state reduces to the unit’s past actions and its stratum. Under H0GH_0^G and Assumption 1 or 22, the observed block is exchangeable with such draws given Ft\mathcal{F}_t and the targets, and no statistic can separate them except by chance. The conditioning is essential: resampling from a law that ignores part of the state the design used—for example, the marginal frequency of each action—breaks the stand-in dependence again and reproduces the false effect (§ 7).

Method

A predictor ff is trained and frozen, on units whose data do not depend on the test units’ tested actions, before any test outcome is used, and it enters the test only through a statistic. The design law, not the model, controls the error rate; the model determines power.

Scores and per-origin e-values

For unit ii and origin tt, let Ci,t⊆CiC_{i,t} \subseteq C_i be the sites whose own history and target are observed, and let ni,t=∣Ci,t∣n_{i,t} = |C_{i,t}|. For a candidate block aa, define the site log score and the pooled unit score

ℓi,c,t(a)=log⁡max⁡{ε, pf(Yi,c,t+h∣Hi,c,t,a)},Si,t(a)=∑c∈Ci,tℓi,c,t(a),(1)\ell_{i,c,t}(a) = \log\max\left\{\varepsilon,\ p_f\left(Y_{i,c,t+h} \mid H_{i,c,t},a\right)\right\}, \qquad S_{i,t}(a) = \sum_{c \in C_{i,t}} \ell_{i,c,t}(a), \tag*{(1)}

where Hi,c,tH_{i,c,t} is the site’s admissible history and pfp_f is the model’s predictive density. All our reference models use a Gaussian density whose variance, like the floor ε\varepsilon, is fixed on training data; the floor is applied per site before summing. The pooled score is the independence log-likelihood of the unit’s sites ([8]). It treats sites as independent, but validity does not rest on that.

For any admissible statistic Ti,t(a)T_{i,t}(a)—the pooled score, or the tempered scores of § 3.4—the exact and Monte Carlo (MC) e-values at (i,t)(i,t) are

ei,tex=exp⁡Ti,t(Ai,tF)∑aQi,t(a)exp⁡Ti,t(a),(2)e^{\mathrm{ex}}_{i,t}=\frac{\exp T_{i,t}(A^F_{i,t})}{\sum_a Q_{i,t}(a)\exp T_{i,t}(a)}, \tag*{(2)}
ei,tmc=(B+1)exp⁡Ti,t(Ai,tF)exp⁡Ti,t(Ai,tF)+∑b=1Bexp⁡Ti,t(Ai,t(b)),Ai,t(1),…,Ai,t(B)∼iidQi,t.(3)e^{\mathrm{mc}}_{i,t}=\frac{(B+1)\exp T_{i,t}(A^F_{i,t})}{\exp T_{i,t}(A^F_{i,t})+\sum_{b=1}^{B}\exp T_{i,t}(A^{(b)}_{i,t})},\qquad A^{(1)}_{i,t},\ldots,A^{(B)}_{i,t}\overset{\mathrm{iid}}{\sim}Q_{i,t}. \tag*{(3)}

The numerator scores the observed future actions; the denominator averages the score over the design. This is the conditional randomization test [7], with the design law in the role of the known conditional law, written as an e-value. Under H0GH_0^G and Assumption 1, the observed block is distributed as Qi,tQ_{i,t} given Ft\mathcal{F}_t and the targets (under H0ownH_0^{\mathrm{own}}: given Ft\mathcal{F}_t, the future blocks of units outside the independent set, and the targets of the units in it), and the statistic is a fixed function of the candidate block given these. Both e-values therefore have conditional mean one (Proposition 1). The MC form is valid because it includes the observed score in its denominator, which also caps it at B+1B+1. Identical candidate blocks may be merged with their multiplicities, and a zero-entropy design gives e≡1e\equiv1, as does an origin at which no site is eligible, since the pooled and tempered scores are then identically zero (the tempered score is read as zero there even where its factor would be undefined); statements about the field mean and the site average concern nonempty site sets. We use the exact form when the block space can be enumerated and the MC form otherwise.

Aggregation

Origins are grouped into residue classes r∈{0,…,h−1}r\in\{0,\ldots,h-1\} by t≡r(modh)t\equiv r\pmod h. Within a class, consecutive origins are hh apart, so their future blocks do not overlap and each factor is determined by the history at the next origin of the class and the Monte Carlo draws used at its own origin; the factors therefore multiply into an e-value along the class (Proposition 1). Under H0GH_0^G the joint design also allows multiplication across units:

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