Paper · 2026-11-01 · cs.LG, q-bio.QM, stat.ME
Stand-In Effects and Pooling Amplification: Lessons from Biological World Models for Testing Action Effects
Tests whether a world model responds to actions by redrawing future actions from the known randomisation design and scoring observed versus redrawn blocks, giving e-values valid whatever the model. Summing site log-likelihoods collapses when many sites share one action sequence; a mixture over fixed tempering factors avoids this. Author-reported: DIAMOND, pooled 0 of 96 active units, mixture 96.
World modelCausal inferenceConditional randomisation testworld-modelsrandomization-teste-valuesstand-in-effectsmodel-evaluationoptogenetics
AI-compiled by claude-haiku-5-5 on 2026-11-21, not yet reviewed by a human. Every claim cites its source; check it when a detail matters.
In plain words
A world model is meant to predict what happens after an action. A common check on such a model is to break its action input (set the actions to zero, swap in another unit's actions, or retrain without actions) and see whether its predictions get worse. If they do, the check calls the actions effective. This paper shows that the check can fire when the actions do nothing. When the actions were chosen in a correlated way over time, the upcoming actions carry hints about earlier history that the model cannot see. The model learns to lean on those hints, so removing them hurts it even though no real effect exists.
The fix is a randomisation test. If you know the rule that generated the actions, you can draw alternative action sequences from that same rule, score the real sequence and the drawn ones with the model, and compare. Under no effect, the real sequence looks like any drawn one, so the false-alarm rate stays under control whatever the model is. The model only decides how often a real effect is caught.
A second problem appears when many measured points, such as cells or pixels, all share one action sequence. Adding up their per-point scores multiplies any error the model makes in the direction the action pushes, and the evidence collapses even when the effect is real. The paper's repair averages the test over a fixed set of scaling factors chosen before the test. The authors report that every single factor they tried failed somewhere, while the average never did.
TL;DR
The paper builds a conditional randomisation test for world models, written as an e-value, in which the known action-randomisation law supplies the null distribution. Its validity does not depend on the model. Replacement diagnostics (zeroing actions, swapping in other blocks, retraining without actions) can report an effect when none exists. Pooling per-site log-likelihoods breaks the test's power when sites share an action sequence, and single tempering factors, estimated or tuned, failed in some setting. The fixed-grid mixture showed no such failure. All headline numbers are author-reported.
Problem
Replacement diagnostics report an action effect whenever a model's prediction loss rises after the actions are replaced §2.4. When actions are autocorrelated, the future block stands in for omitted history, so these diagnostics can report effects with probability tending to one under the global null §4.4 §5.1. The authors show this on biological designs (ERK, CcaS) and in a pixel world with a logging policy the model cannot see §5.2 §7.1.
A design-based test avoids this, but only if the resampler conditions on the full state that the design used. Resampling each action from its overall frequency, ignoring the recorded state, recreates the false effect §7.2. The validity theory also requires the randomisation law to be known. For approximate or reconstructed laws, the paper gives only a total-variation bound that does not license its real-data tests §4.3.
Pooling sums the site log-likelihoods of a unit. When the model errs along the action contrast and the sites share that error, the sum grows with the number of sites and drives the e-value towards zero §3.3 §6.1. The paper calls this pooling amplification. Shared noise along the contrast causes the same collapse §3.3.
Method
The model is trained and frozen on training data before any test outcome is used. The model affects the test solely through the statistic. The design law sets the error rate, and the model sets the power §3.
Steps:
- Define the units. A unit
i(for example a microscope field, an episode or a robot trajectory) has sitesc(cells or pixels). At origint, the future block is the nexthactions and the target is the outcome att+h. The design lawQ_{i,t}is known §2.1 §2.2. - Score a candidate block with the pooled log-likelihood over the observed sites. The density is Gaussian with variance fixed on training data, and each site's density is floored before the sum §3.1 eq. 1.
- Compute the e-value at each origin. The exact form uses the full design law
eq. 2. The Monte Carlo form draws
Bblocks from the design law and puts the observed score into its own denominator eq. 3. The MC form is capped atB + 1. Repeated candidate blocks can be counted once with a multiplicity weight §3.1. - Multiply origins within each residue class
r = t mod h, then average thehclass products eq. 4 §3.2. For models, average the per-model e-values §3.2. Reject whenE >= 1/alpha; formprespecified hypotheses, useE >= m/alpha§3.2. - Tempering: replace the pooled score
SbyT = lambda * S, with0 < lambda <= 1fixed on training data and the site count eq. 6 §3.4. Settinglambda = 1recovers the pooled test. - Estimated factors. Kish:
lambda = 1 / (1 + (n - 1) * rho), withrhothe median over training fields of the median pairwise Pearson residual correlation, clipped to[0, 1]eq. 7 §3.4. Contrast tempering eq. 8 is exploratory; the authors do not recommend it §6.3 §9.3. - Factor-free statistics. The mixture averages the whole-unit e-values over the
grid
lambda_g = 2^-geq. 9 §3.5. The validation-weighted mixture puts weightwon the grid factor chosen on validation data and spreads1 - wevenly over the rest eq. 10 §3.5. The authors' primary choice isw = 3/4. Other exploratory statistics are validation tuning, a site-count-adaptive factor, online follow-the-leader rules, and rank e-values §3.5 §3.7. - Betting reading. The exact e-value is a likelihood ratio between a design-based alternative that favours blocks the model rates highly and the design law itself. Tempering moves that alternative along the exponential family §3.6.
# Pooled log score of one candidate block [§3.1] [eq. 1]
# Input: block (h actions); targets (n); histories (n); model; floor
# Output: scalar log score
def pooled_score(block, targets, histories, model, floor):
# Predictive mean and variance per site, fixed on training data [§3.1]
means, variances = model.predict(histories, block) # (n,), (n,)
# Gaussian density of each observed target [§3.1]
densities = gaussian_pdf(targets, means, variances) # (n,)
# Floor each site's density before taking the log [§3.1] [eq. 1]
floored = maximum(densities, floor) # (n,)
# Sum over sites: independence log-likelihood [§3.1]
return sum(log(floored))# Monte Carlo e-value at one origin [§3.1] [eq. 3]
# Input: observed block; targets; histories; model; design law; B
# Output: e-value in [1, B + 1]
def mc_e_value(observed, targets, histories, model, design, floor, B):
# Score the observed future actions [§3.1]
observed_score = pooled_score(
observed, targets, histories, model, floor)
# Draw B blocks from the known design law at this origin [§3.1]
redraws = [design.sample(histories) for _ in range(B)]
# Score each redraw against the same targets and histories [§3.1]
draw_scores = [
pooled_score(a, targets, histories, model, floor)
for a in redraws
]
# Same value as eq. 3, computed in log space [eq. 3]
log_total = logsumexp([observed_score] + draw_scores)
return exp(log(B + 1) + observed_score - log_total)# Combine origins and units into one e-value [§3.2] [eq. 4]
# Input: e[unit][t] for origins t; horizon h; units; origins
# Output: E, a single e-value
def combine(e, h, units, origins):
class_products = []
# Residue classes r = t mod h [§3.2]
for r in range(h):
product = 1.0
for unit in units:
for t in origins:
# Multiply only origins in this residue class [§3.2]
if t % h == r:
product *= e[unit][t]
class_products.append(product)
# Average the h class products; do not multiply them [eq. 4]
return sum(class_products) / h# Tempering mixture over a fixed grid [§3.5] [eq. 9]
# Input: decision unit; grid size G
# Output: E^M, mean of the G whole-unit e-values
def mixture_e_value(unit, G):
# Fixed grid lambda_g = 2^-g, chosen before any test [§3.5]
factors = [2.0 ** -g for g in range(G)]
# Whole-unit e-value at each constant factor (T = lambda * S) [§3.5]
unit_values = [
tempered_unit_e_value(unit, lam) for lam in factors
]
# Averages are taken per decision unit [eq. 9]
return sum(unit_values) / G# Validation-weighted mixture W(w) [§3.5] [eq. 10]
# Input: unit_values[g] for g in 0..G-1; gv = index of the factor with
# the largest median validation log E (ties go to the larger
# factor); w fixed in advance (primary 3/4)
# Output: E^W(w)
def weighted_mixture(unit_values, gv, w):
G = len(unit_values)
# Weight w on the validation-chosen factor [eq. 10]
chosen = w * unit_values[gv]
# Spread 1 - w evenly over the other G - 1 factors [eq. 10]
others = sum(unit_values[g] for g in range(G) if g != gv)
return chosen + (1 - w) / (G - 1) * others# Kish tempering factor [§3.4] [eq. 7]
# Input: n (sites of this unit at this origin); residual series from
# training fields only, one per site
# Output: lambda in (0, 1]
def kish_factor(n, residuals_by_field):
field_medians = []
# Pairwise Pearson correlations within each training field [§3.4]
for field in residuals_by_field:
# Skip pairs with fewer than 3 finite, non-constant matches [§3.4]
pair_rhos = pearson_pairs(field)
field_medians.append(median(pair_rhos))
# Median over fields, then clip to [0, 1] [§3.4]
rho = clip(median(field_medians), 0.0, 1.0)
# Inverse design effect of n sites with intraclass rho [eq. 7]
return 1.0 / (1.0 + (n - 1) * rho)Hyperparameters
| Name | Value | Where | Notes |
|---|---|---|---|
Monte Carlo draws B | 127 (bag of 128 with the observed block) | §3.1 §9.1 §11.1 | Pixel world, DIAMOND, IRIS, TD-MPC2 and robot use the same bag size. |
| Rejection threshold, single hypothesis | E >= 20 (alpha = 0.05) | §3.2 §9.1 §8.4 | Used for every published-model test and the M5 test. |
| Rejection threshold, five prespecified hypotheses | E >= 100 | §8.2 | e-Bonferroni rule m / alpha with m = 5. |
Grid of tempering factors lambda_g | 2^-g, g = 0..G-1; G = 15 (or 13 in the pixel world) | §3.5 §6.4 | G = 15 reaches 1/n for 12,288 sites. |
Validation weight w | 3/4 primary; 1/4 and 1/2 secondary | §3.5 §10.1 | Chosen before any test data existed. |
Fractional Kelly kappa | 1/2 per origin | §3.6 §6.3 | Reference arm, simulation only. |
| Online grid O57 | 2^(-j/4), j = 0..56 | §3.5 | Follow-the-leader rule on earlier origins. |
Rank calibrator kappa | 1/ln(B+1) (R); 1/2 (R_1/2) | §3.5 | Averaged over tied positions. |
| Density floor (log scale) | log(1e-12) for token log-likelihoods | app. L app. B | Floor applied per site, before summing. |
| Variance floor, Gaussian pixel score | (1/255)^2 (one intensity step) | §9.1 | Score-rule study also tried (8/255)^2 and (32/255)^2 §9.4. |
| Kish estimate | median of medians, clipped to [0, 1], per model and horizon | §3.4 | Training-field validation residuals only. |
| Contrast factor clip | [1/n, 1] | §3.4 | Exploratory. |
| DIAMOND test units | 16 validation units; test set of 32 active-condition and 64 null-condition units, per game | §9.1 | Segments of up to 500 agent steps. Models: released checkpoints, not retrained. |
| DIAMOND sampler | 3 denoising steps; one noise image per origin, shared by all candidate actions | §9.1 | Score sites: 64 x 64 x 3 = 12,288. |
| IRIS and TD-MPC2 units | 16 validation and 32 test units per game or task; 64 under null | §10.1 | IRIS scores 16 tokens per frame; TD-MPC2 scores 512 latent coordinates. |
| Robot test set | 80 validation and 159 test trajectories; 14 origins each | §11.1 | Candidate pool of 14,294 recorded commands. Model size: not stated. |
| Reference models (ERK, CcaS) | Four additive models: a linear-Gaussian one, a GRU, a small Transformer, gradient boosting; averaged | §8.1 | Trained on training-unit outcomes only. Parameter counts: not stated. |
Results
All numbers are author-reported. The statistic is named as in the paper.
| Setting | Statistic | Result | Source |
|---|---|---|---|
| ERK positive control, 10 min (registered M4) | Pooled | log E = -9,576; not rejected | §8.2 |
| ERK positive control, 30 min (M4) | Pooled | log E = -2,974.53; not rejected | §8.2 |
| CcaS, 1 step, four-model average | Pooled | log E = -1.68; not rejected | §8.2 |
| CcaS, 6 steps, four-model average | Pooled | log E = 3,466.13; rejected | §8.2 |
| CcaS, 12 steps, published model | Pooled | log E = 17,572.64; rejected | §8.2 |
| ERK exploratory check X, 9 test fields, 10 min | Kish | four-model log E = 349, against -9,576 pooled on the same fields | §8.3 |
| ERK, one unopened field, 10 min (registered M5) | Kish | log E = 23.1 (E about 1.1e10); rejected at E >= 20; 30 min descriptive only | §8.4 |
| DIAMOND (Boxing, Pong, Breakout), 96 active units | Pooled / Kish / contrast / mixture M | 0 / 0 / 1 / 96 rejections; nulls 0 | §9.2 |
| IRIS token likelihood, 26 games, full execution | Pooled / W(3/4) | pooled 24 of 32 units in 10 games; W(3/4) in 24 of 26 games | §10.2 |
| TD-MPC2 latent score, 6 tasks | Pooled / W(3/4) | 1 of 6 tasks / all 6 tasks | §10.2 |
| iVideoGPT on BAIR robot video, 159 test units | Pooled / W(3/4) | 143 / 155 rejections; median log E 13.9 vs 15.3 | §11.2 |
| Exact nulls across the three published-model tests | All statistics | 14 rejections in 26,664 tests | abstract; §9.2 §10.2 §11.2 |
Simulation and pixel results, in words: the pooled score's median log E fell as pixels grew from 64 to 4096, while the oracle's rose §6.3. Replacement diagnostics reported effects in most episodes in the stand-in construction, while the design-law resampler never rejected §7.1.
Paper vs code
No official code.
The arXiv abstract and the TeX source (main file, sections and appendices)
contain no code link. Links in the source are to OSF (the project w37um and
the preregistrations) app. E. The paper says the frozen analysis code is
archived as CODE_ARCHIVE.zip attached to the OSF registration zxar3
app. E. That archive is not a public repository, so it is not used here.
Searches made: the OSF project page (the fetch returned an empty page, so its contents are unverified); and six GitHub repository searches (stand-in effects world model; pooling amplification; tempered e-value world model; conditional randomization action effects; optogenetic ERK world model; biological world model replacement diagnostics). None returned a repository that clearly belongs to the authors.
Pitfalls
- Replacement diagnostics are not a test of action effects. The zero-block, other-unit-block and retraining checks can fire with probability tending to one when no effect exists §4.4. Do not use them as the test, and do not treat their rejections as evidence of an effect §13.
- The resampler must condition on the full design state. Use the design law given the complete recorded history. A marginal resampler breaks validity and reproduces the false effect §7.2. The paper's negative control had no power for this reason §7.2.
- Validity depends on the design law. The law is reconstructed from records, not documented, in most datasets. For ERK it is the working law V3, not verified for the M5 field. For CcaS, the results depend on a delayed copy of the generator; the one-step shift came to light only once the initial design checks had failed §8.1 §13 app. C. The robot data's law is reconstructed from command records §11.1.
- The observation mask must not depend on future actions under the null. This is an assumption, not something the theory checks §2.3.
- Pooling amplification is a fact of the pooled score, not of the data. Summing many correlated site scores drives log E down as sites are added, and stronger effects can make it worse §3.3 §6.1. Partial execution makes the model misspecified along the contrast and triggers the collapse §9.4 §10.2.
- The model's own token likelihood can avoid the collapse at full execution, but not under partial execution. At execution probability 0.5 it collapsed in all three of Boxing, Pong and Breakout §10.2. Do not assume a proper likelihood is safe.
- Estimated factors are fragile. In the median unit on DIAMOND, the Kish and contrast estimates were roughly 11 to 82 times the best grid factor §12. Validation tuning of one factor collapsed on ERK because the training fields' cell counts differ from the test fields' §8.6. Making the factor depend on cell count stopped the collapse, but for one of the models it still discarded most of the evidence §8.7.
- Kish estimates are not independent validation. On ERK the contrast is shared across cells, so agreement with Kish is partly structural §8.5.
- Mixture bounds. The mixture can lose up to
log Grelative to the best grid member (log 15is about 2.71). Averages are taken per decision unit, not per origin §3.5 §4.5. Log e-value curves are concave in the factor and pass through zero at zero: an oversized factor can erase all the evidence, while an undersized one keeps a proportional share §12. - Degenerate cases. A zero-entropy design, or an origin with no eligible
site, gives e = 1 exactly §3.1 §5.4. The MC e-value cannot exceed
B + 1. AtB = 127this caps a single origin at 128. - Rank e-values depend on ties. They averaged over tied positions and failed on ERK-like data §6.4. Use them only as secondary statistics, as the paper does.
- Magnitudes are not effect sizes. A rejection shows that at least one site is affected by a future action inside the horizon. The size and the mechanism remain open §13. The M5 log E of 23.1 is a rejection, not an estimate.
- Post hoc and non-blind parts. M4 re-analysed data already analysed in an earlier study. X and the validation-tuning checks were exploratory. Only M5 is confirmatory for the repair, on one field at one horizon §13. The repair was selected on synthetic data, and one tie-break detail was implemented only after the evaluation §6.2.
- Notation.
lambdais the tempering factor in this paper. The registrations uselambdafor a Gaussian precision §3.7. - Horizon. The published-model and robot tests use a horizon of one step. The DIAMOND, IRIS and TD-MPC2 tests use random actions in simulators; robot data use recorded commands whose law is reconstructed §9.3 §10.3 §11.3.
- Not covered. Pinning an effect on one unit's own actions requires the own-channel null plus layout assumptions §2.3. Those analyses carry an eligibility bound that says nothing, so they are descriptive §8.2.
Lineage
- Builds on: the conditional randomisation test of Candès et al. 2018 (
candes2018panning), e-values of Vovk and Wang 2021 (vovk2021evalues), and Kish's design effect of 1965 (kish1965survey). The independence log-likelihood follows Chandler and Bate 2007 (chandler2007inference). The lagged-null variant follows Zhang et al. 2025 (zhang2025randomization). - Compared against: replacement diagnostics (zero block, other-unit block, retraining without actions, shuffled windows) §7.1; Kish and contrast tempering; validation tuning; rank e-values.
- Models tested: DIAMOND (Alonso et al. 2024), IRIS (Micheli et al. 2023), TD-MPC2 (Hansen et al. 2024), iVideoGPT (Wu et al. 2024) on BAIR robot pushing (Ebert et al. 2017). The ERK and CcaS reference models are the authors' own.
- Superseded by: not known.
Source and license
Adapted from “Stand-In Effects and Pooling Amplification: Lessons from Biological World Models for Testing Action Effects” by Bowen Xu, Boyu Chen, Jiaying Li (arXiv:2611.01666), used under CC BY 4.0. Changes: condensed and restructured for implementation, with tables, equations and algorithms taken from the paper and its code, each cited to its source. Not affiliated with or endorsed by the authors.