Adaptive Experimentation Can Hide Model Error:Detection Limits and Falsification Budget

Ramnarayan Choudhary

stat.MENov 5, 2026

Adaptive Experimentation Can Hide Model Error:Detection Limits and Falsification Budget

Authors: Ramnarayan Choudhary

Organizations: MBZUAI

Abstract

An experiment can be informative about the parameters of a working model and uninformative about whether that model is wrong. Adaptive design can reinforce this mismatch by repeatedly selecting settings where an incorrect model fits. We bound the power of any valid adequacy test in terms of the experimenter's own sampling distribution, then distinguish information absent from the selected data from information lost by the detector. A computable diagnostic measures unresolved error relative to a declared expansion of the working model. It motivates a training-free rule that reserves part of the design budget for falsification. The empirical record is mixed: the independently specified primary study fails detection eligibility, and a later numerator diagnostic fails its improvement criteria. After the frozen rule fails on fresh continuous-null panels, a disclosed secondary horizon-calibrated revision detects 35.8% of misspecified campaigns versus 31.7% for a class-separation control at T = 240, but has no resolved advantage at T = 480. In a corrected 289-unit measured replay it improves on random design and trails class-discrimination EIG. A conditional futility bound explains why remaining time matters without proving the gate constant or its power. These results support separating parameter learning, model checking and detector performance; they do not establish a universally superior design policy or prospective scientific discovery.

Figures & tables

Figure 1: Detection recovery varies across settings and comparators. Panels (a–e) use the frozen

.1

gate at

T=30

; (f–h) use the revised

\log(20)/T

gate (asterisk in legend). Descriptive 95% intervals use 5,000 world/curve resamples in (a–g), seed 0; (h) resamples 20 cell lines with unit weighting, seed 20261026. Campaigns per world/unit: 50 in (g,h), 200 otherwise. Counts label worlds/curves; (h) shows 127 low-

p

units of 289. Dose/soybean and location use earlier random-detectable pools; both measured replays use full-data fit labels. Class EIG exceeds the rule in (h). These heterogeneous evaluations are neither pooled nor eight confirmations of one unchanged rule. The technical record retains separation, all-world results and registered failures.

Panel	Frozen 0.1	Revised	Class EIG	Sep.
Fresh continuous null, $T=240$	2.78	35.78	28.44	31.67
Drug transfer, $T=60$	59.31	76.79	70.17	69.77
Fresh continuous null, $T=480$	10.22	52.00	46.89	51.44

Table 1: The revision helps, but does not erase frozen failures. Detection percentages; fresh continuous-null panels each have 18 non-null worlds and 50 campaigns/world/arm. Drug transfer reuses 24 earlier worlds, 200 campaigns per world. Sep. is the partial class-separation adaptation.

Appendix figures & tables16 assets

Supplementary material from the paper’s appendix.

Appendix

Figure 2: Several tested estimation-oriented experimenters retain little detection power. (a) Rate at which a valid adequacy test detects a planted model error within 30 experiments, and (b) entropy of the experimenter’s design distribution, on 16 misspecified worlds in four families (15 for GPT-6 Astra). Open Qwen3.5 models (blue) keep detection power by scanning or repeating settings; several frontier reasoning models (red, two providers) concentrate their designs like the information-maximizing optimizer (greedy EIG). The association between concentration and detection in these selected worlds is not a causal capability comparison. Whiskers are

\pm 1

s.e. across worlds; open models use 4 campaigns per world, frontier models 1–2 (pilot), random design and greedy EIG 200. The dashed lines mark random design’s detection rate and the entropy of a uniform design.

Figure 3: Greedy EIG yields low detection in the generic families; its accuracy cost changes sign. (a) Rate at which the valid adequacy test ( 1 ) fires within 60 experiments, mean over 12 misspecified worlds per family (200 seeds each); whiskers are

\pm 1

s.e. across worlds. (b) Change in protected risk of greedy EIG relative to random design, fixed working model, one dot per misspecified world (32 per family, 200 seeds each); bars are medians.

Figure 4: A targeted falsification budget buys most of randomization’s detection at a fraction of its cost. Horizontal axis: mean relative increase in protected risk over greedy EIG on the 28 well-specified controls. Vertical axis: detection rate on the 21 detectable misspecified worlds. Whiskers are

\pm 1

s.e. across worlds; 200 seeds per world and policy; the working model is expanded on detection. Lines connect the measured budget settings and are guides only; pure discrimination is the targeted budget at

\gamma=1

. Separate markers show two baselines: an Atkinson-style compound criterion and greedy EIG under a tempered (generalized-Bayes) posterior.

Figure 5: Expansion-relative diagnostics correlate with realized error in the tested worlds. (a) The blindness certificate

B_{T}

of Proposition 9 , computed by the agent from its own models and data, against the realized protected error of its working model, for every (world, policy) cell; the dashed line is equality. (b) The ignorance part

U_{T}

under greedy EIG against random design, one point per world; the dashed line is equality. 96 worlds in five environments (76 misspecified, 20 well-specified), 200 campaigns each,

T=60

Method	Attempts ( $60/120$ )	$H=60$	$H=120$
Expected discrepancy (candidate)	12/24	0.35 (0.35)	4.51 (1.15)
Random overrides	12/24	0.00 (0.00)	0.69 (0.47)
Balanced coverage	12/24	0.00 (0.00)	0.00 (0.00)
Class MI	12/24	1.39 (0.68)	4.86 (1.24)
Alternative-parameter EIG	12/24	0.69 (0.47)	4.86 (1.21)
Combined latent EIG	12/24	0.00 (0.00)	4.86 (1.18)

Appendix

Table 2: No registered horizon meets the baseline detectability requirement. Detection percentages over 18 equally weighted non-null worlds, with 16 response-history replicates per world and method. Parentheses give within-world Monte Carlo standard errors on this fixed panel, not population confidence intervals; a zero estimated error does not establish zero uncertainty. All physical observations continue to the horizon. References are ineligible for capped-baseline selection. Run 2095b9fe , scientific registration 22c10ec2 , completed source 15cd075 .

Figure 6: The adaptive gain shrinks against stronger controls. All 49 previously unused fitted worlds at

T=30

, with 200 campaigns per world; whiskers are descriptive 95% world-bootstrap intervals, not separate campaign uncertainty or population guarantees. Probing budgets differ, and the third contrast changes both acquisition and detector expansion. The registered selected-world and zero-alarm failures remain failures.

Figure 7: Preventing permanent cessation has a probing cost. Four fixed policies on the two-model construction at

T=200

; the horizontal axis uses the correct-model law and is logarithmic, while the vertical axis uses the misspecified law. Deterministic numerical enclosures are smaller than the markers; no sampled campaigns, swept frontier or interpolation is shown. Counts stop at rejection. The ignorance-gate point follows analytically.

Figure 8: A correct trigger cannot repair a blind target score. Two known positive-departure witnesses at

T=30

: scores coincide in (a), whereas predictive cancellation in (b) survives forced targeting. Bars show deterministic probability enclosures, smaller than the plotted marks, not confidence intervals; no sampled seeds. Mirrored departures, nulls, fixed-slot controls and effort endpoints remain in the complete record.

$T$	Greedy	Random	Disc 0.2	Floor	$M_{1}$ EIG	Class EIG
30	2.40	71.83	58.19	94.25	92.58	94.65
60	6.42	92.23	86.35	97.85	97.94	98.23

Appendix

Table 3: Source-location detection (percent), averaging all 24 two-source worlds equally. These are saved campaign means from run fd0610ac , source 7a4ecca ; no random-detectability selection is applied in this table.

Design policy	Detection rate	Design entropy (bits)	Protected risk
Random design	0.583	4.64	0.407
Greedy EIG	0.001	1.40	0.421
Qwen3.5-0.8B, plain prompt	0.328	2.96	0.436
Qwen3.5-2B, plain prompt	0.453	3.92	0.423
Qwen3.5-4B, plain prompt	0.609	4.47	0.409
Qwen3.5-9B, plain prompt	0.625	4.10	0.410

Appendix

Table 4: Open language models keep detection power; frontier reasoning models from two providers lose it, and the blindness monitor restores it. Pooled over the misspecified worlds in four families,

T=30

. Detection uses the valid adequacy test; design entropy is that of the pooled design distribution (uniform over 25 settings is 4.64 bits). Baselines use 200 campaigns per world; open models 4 campaigns per world and prompt. ∗ Frontier pilot: 2 campaigns per world; random design detects 0.713 on the 13 worlds Astra completed. † Second provider: 1–2 campaigns per world (spend caps truncated second campaigns), all 16 worlds in both arms.

Figure 9: Prompt gains are clearer than setting-specific gains in this pilot. Differences across 16 selected worlds at

T=30

; whiskers are descriptive 95% world-bootstrap intervals. The original ablation uses historical reference arms; Argon retains one or two campaigns per world after failures and earlier spend caps. The score-only prompt also supplies framing and reference guidance.

Family	Designs	Working model $\mathcal{M}_{0}$ (grid)	Outcomes	$A$
Dose–response	$x\in[-4,8]$	$\mathrm{logit}\,p=b(x-a)$ ( $31\times 20$ )	Bernoulli	3.0
Linear	$x\in[-1,1]$	$\mu=\alpha+\beta x$ ( $25\times 25$ )	Gaussian, $\sigma=0.5$	1.0
Michaelis–Menten	$S\in[0.1,100]$ , log	$\mu=V_{\max}S/(K_{m}+S)$ ( $25\times 25$ )	Gaussian, $\sigma=0.1$	0.3
PK decay	$t\in[0.25,12]$	$\mu=C_{0}e^{-kt}$ ( $25\times 25$ )	Gaussian, $\sigma=0.08$	0.25
Poisson rate	$x\in[0,1]$	$\log\lambda=\alpha+\beta x$ ( $25\times 25$ )	Poisson, 0–15+	0.8
Discounting (2-D)	delay $\times$ ratio, $5\times 5$	$\mathrm{logit}\,p=(R/(1+kD)-1)/\tau$ ( $25\times 25$ )	Bernoulli	2.0

Appendix

Table 5: The seven design families. Each has 25 designs and a grid-exact working model

\mathcal{M}_{0}

. “Deviation scale”

A

sets the amplitude of planted deviations and of the expansion

\mathcal{M}_{1}

, in link units (logit, mean, or log rate).

Panel/bump	Nearest mean KL	$TD^{*}$	$\log\pi_{.005}$	Oracle	$\mathcal{M}_{1}$	Beta	Hedge
240/1	.000732	4.3	$-7.99$	.71	.03	.05	.04
240/5	.000951	3.9	$-7.78$	.55	.01	.01	.01
480/3	.000160	2.9	$-6.47$	.41	.02	.03	.03
480/2	.000764	5.8	$-7.15$	.86	.07	.11	.11

Appendix

Table 6: Difficult-bump diagnostics.

TD^{*}

is rounded numerical separation, not achievable power. Detection is out of 100 fixed-design campaigns; the neighborhood mass uses uniform weights over 38,185 library members.

Arm	Low- $p$ detection	High- $p$ alarm	High- $p$ risk premium
Greedy	.040	.0011	$0.00\%$
Random	.078	.0000	$-1.65\%$
Class EIG	.273	.0206	$-.89\%$
Separation	.264	.0196	$-.57\%$
Revised rule	.247	.0006	$-.21\%$

Appendix

Table 7: Historical large-replay summaries from flawed normalization; withheld as supporting evidence. There are 50 campaigns/unit/arm. Detection averages the 168 low-

p

units; alarms and relative prediction-risk premiums average the 108 high-

p

units. Values retain the run log’s rounding.

Arm	Detection (%)	High- $p$ alarm (%)	Risk premium (%)	Simulated-null alarms
Greedy	2.38	.094	0	0
Random	3.42	.212	$-.787$	0
Class EIG	17.37	1.153	$+.105$	1
Separation	16.02	.353	$+.028$	0
Revised rule	14.16	.494	$+.017$	0

Appendix

Table 8: Corrected replay. Detection among 127 low-

p

units (6,350 campaigns/arm); high-

p

alarms and relative risk premium among 85 high-

p

units (4,250/arm). The last column is a separate known-grid-null simulation (5,780/arm), not an empirical adequacy label. Means weight units equally.

Comparator	Unit point and IID interval	Unit-weighted cell interval	Equal-cell point and cell interval
Random	$10.74\ [7.09,14.83]$	$[6.46,16.24]$	$16.01\ [8.01,25.73]$
Class EIG	$-3.21\ [-5.39,-1.34]$	$[-5.70,-.68]$	$-1.67\ [-4.24,.93]$
Separation	$-1.86\ [-4.61,.85]$	$[-5.07,1.12]$	$.85\ [-2.65,5.23]$

Appendix

Table 9: Revised-rule minus comparator, percentage points. Registered paired bootstrap sensitivity uses 5,000 draws; cell resampling retains all units in each drawn cell line. All intervals are descriptive and conditional on fitted labels.

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