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Under review as a conference paper at ICLR 2027

Choosing Without a Winner: Bayesian Frontier Inference for Lifecycle Decisions

Abstract

As AI systems are evaluated across an expanding range of dimensions, the prac- tical question of which system to use has become increasingly difficult to answer from benchmark scores alone, since those scores compress uncertainty, obscure tradeoffs and often fail to distinguish changes in the systems themselves from changes in the regimes through which they are measured. We develop a Bayesian framework for learning multidimensional AI system frontiers that treats each eval- uated configuration as a composite of model, harness and version, inference effort and other execution settings, jointly representing performance, cost, latency, task heterogeneity and measurement uncertainty while preserving the structure of evi- dence that would otherwise disappear into a scalar ranking. Separating changes in the available set of systems from shifts in task populations, evaluators and opera- tional environments allows the temporal model to describe how the frontier itself evolves, which in turn makes it possible to connect that evolving frontier to organi- zation specific losses, constraints, switching costs, fallback options and planning horizons when deciding whether a system should be adopted, retained, replaced or retired. Extending this decision framework with value of information analysis identifies which additional evaluations are most consequential, yielding a unified basis for choosing among AI systems and revisiting those choices as capabilities, circumstances and the evidence available to judge them continue to change

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
AI evaluation, Bayesian decision theory, Frontier inference

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_CYQcOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper constructs Pareto sets over model configurations using source-based likelihoods for public benchmark data. It recovers task success histograms from aggregate pass@k statistics, studies uncertainty and dependence in frontier membership, and illustrates switching decisions and value-of-information calculations under certain scenarios.

Critical strengths
  1. Recovering task success histograms from published aggregates makes otherwise unavailable heterogeneity analysis possible. The comparison with a Binomial model demonstrates why treating repeated trials as independent can inflate precision.
  2. The paper investigates the limitations of its inference through prior sensitivity, alternative dependence structures, and a paired trial-level panel. The temporal assessment is also useful, as it identifies which missing data prevent stronger conclusions instead of fitting unsupported dynamics.
Critical weaknesses
  1. Some frontier probabilities are sensitive to uncertainty omitted from the primary analysis. In Table 12, Grok 4.6's membership falls from 0.964 to 0.683 under only 2% log-scale perturbations of cost and duration. Also, the τ3\tau^3-bench likelihood omits within-cell sampling correlations despite available paired task rows (Appendix B), potentially attributing sampling dependence to workload variation. The conclusions should reflect more clearly these sources of uncertainty.
  2. The demonstrated contribution is overstated in relation to the lifecycle framing. No temporal model is fitted, and switching results depend on assumed cost and transport scenarios. Much of the framework uses Pareto and decision-theoretic methodology. Its value therefore comes from the archival analysis, with limited validation of improved lifecycle decisions.
Questions for authors
  1. Does the τ3\tau^3-bench tradeoff probability remain similar when the likelihood includes the estimated within-cell sampling covariance?
  2. After propagating cost and duration uncertainty, what are the probabilities that the configurations discussed are Pareto-optimal but are never optimal for any weighted averaged of the objectives?
8 comments
AuthorsOpenReview ↗

CYQc (1/5): Table 12 and the fragility of Grok 4.6 (W1)

W1: “Some frontier probabilities are sensitive to uncertainty omitted from the primary analysis. In Table 12, Grok 4.6's membership falls from 0.964 to 0.683 under only 2% log-scale perturbations of cost and duration. … The conclusions should reflect more clearly these sources of uncertainty.”

Table 12 is the paper's sensitivity analysis, and the trial data confirm what it showed. Grok 4.6 sits on a dominance boundary, its membership depends on the estimator and the target workload, and the trial-level estimates fall well below 0.964, so the revision reports it as undetermined.

The submitted model treats cost and duration as fixed, so a 2% perturbation of those coordinates moves Grok 4.6 from 0.964 to 0.683. Trial records now measure cost and duration per attempt on the same 66 tasks. The table gives membership probabilities from the model for the observed 66 tasks (C66) and for a new 66-task workload centred on the observed panel (P66), and bootstrap frequencies from resampling aligned tasks, either from the observed panel (plain) or for a new workload (predictive, added post hoc).

configurationsubmitted modelmodel C66model P66plain bootstrappredictive bootstrap
Grok 4.60.9640.3910.1530.6000.572
Opus 50.9870.7690.7920.6360.627
Fable 50.0250.0270.4340.0480.132

The frontier as a whole changes little: its expected size is 7.75 under the submitted model and 7.1 to 7.4 under every trial-level estimator. The task-paired trial model carries cost and duration uncertainty in every draw, so the 2% perturbation that moved the submitted model barely moves Grok 4.6 (P66 0.153 to 0.154, C66 0.391 to 0.394).

The remaining discrepancy comes from cost and duration. On datasets resampled from the real panel (post hoc), nominal 90% intervals for each configuration's cost and duration cover 63% of the true values on the observed tasks, and their RMS standardised errors are 1.95 and 1.99, against about 1 on datasets simulated from the model's own law. About half of that error is configuration-specific shifts of the interval centre, in both directions, and with those removed the intervals are still 1.4 to 1.5 times too narrow. On held-out real tasks, pooled over five partitions of the tasks, the intervals are modestly too narrow: 87% for completion, 85% for cost and 81% for duration (CYQc follow-up). An attribution test traces the model's lower membership accuracy on the configurations scored to the same source, and the revised analysis reports a task bootstrap alongside the model.

Terminal-Bench v4.1, a regrade released after submission, is a check on the same trials, and all headline numbers stay on v4. GLM-5.3 at C66 is the one configuration whose classification changes, from 0.957 to 0.848 (retained to undetermined).

The revised conclusions reflect these sources: Grok 4.6 and Opus 5 are reported as undetermined rather than as frontier members, each frontier probability names its target, and the trial-level analysis carries cost and duration uncertainty in every draw (revised §5.3 and §6).

Full results are in revised App. E.10 (Table 12 re-estimated), App. E.6 (trial panel and v4.1 check) and App. E.9 (attribution test).

AuthorsOpenReview ↗

CYQc (2/5): probability of being Pareto-optimal but never optimal for a weighted average (Q2)

Q2: “After propagating cost and duration uncertainty, what are the probabilities that the configurations discussed are Pareto-optimal …”

The scalarisation result survives full propagation of cost and duration uncertainty. GPT-5.6 Terra is a frontier member in almost every draw yet is optimal for a weighted average in a minority of them.

On each posterior draw, a frontier member is supported if it maximises some nonnegative weighted sum of completion, negative cost and negative duration (checked by linear programming). Every supported configuration is a member, so the probability of being a member but never optimal for a weighted average is membership minus support. The Monte Carlo standard error is at most 0.005.

configurationtargetmembershipsupportedmember but unsupported
GPT-5.6 TerraC661.0000.0930.907
GPT-5.6 TerraP660.9840.2110.773
Opus 5C660.7690.0370.732
Opus 5P660.7920.3780.415
Grok 4.6C660.3910.0000.391
Grok 4.6P660.1530.0020.151

C66 is the observed 66 tasks and P66 a new 66-task workload. Terra is likely a member under every estimator and is rarely optimal for a weighted average, so a weighted-average ranking would rarely put it first. For Opus 5 the answer depends on the target, and for Grok 4.6 the unsupported probability is mostly its membership, which reply 1/5 shows is undetermined. These model-based probabilities carry the narrow cost and duration intervals found in the known-truth test, most visibly near a dominance boundary. All configurations are in revised App. E.11.

AuthorsOpenReview ↗

CYQc (3/5): tau3-bench within-cell covariance (W1, Q1)

W1 (covariance clause): “Also, the τ³-bench likelihood omits within-cell sampling correlations despite available paired task rows (Appendix B), potentially attributing sampling dependence to workload variation. The conclusions should reflect more clearly these sources of uncertainty.” Q1: “Does the τ³-bench tradeoff probability remain similar when the likelihood includes the estimated within-cell sampling covariance?”

Yes, it changes by at most 0.002. Inferring the 3-by-3 within-cell covariance for completion, cost and duration (Wishart likelihood, LKJ correlation prior) gives a trade-off probability of 0.9757, against 0.9755 with the covariance plugged in as known and 0.9738 for the paper's likelihood pooled over 16 predictive replicates. The largest difference from the submitted likelihood is 0.002, and the quality heterogeneity scale moves from 3.40 to 3.16 percentage points. The comparison is model-based, and the Gaussian task law approximates per-task quality differences that take three values. The revised conclusions report the τ³-bench trade-off with the covariance inferred and state that this comparison is model-based (revised App. E.12).

Reviewer_2CEcOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper develops a Bayesian framework for inferring Pareto frontiers over AI service configurations from public evaluation records, preserving uncertainty and tradeoffs among completion, cost, and duration. It reconstructs task-success histograms from aggregate pass@k statistics, uses source-specific likelihoods, and connects frontier draws to admissible actions and value-of-information calculations under declared scenarios. Terminal-Bench v4 yields eight probable frontier members among twelve configurations, while one reconciled τ³-bench pair shows a robust cost–duration tradeoff. The results are conditional single-snapshot analyses; the temporal component audits identifiability rather than fitting frontier dynamics.

Critical strengths
  1. Recovering anonymous task-success histograms from published totals and pass@k is a concrete contribution to inference from incomplete public archives. On Terminal-Bench v4, this enables a Beta-Binomial model that captures task heterogeneity and passes posterior predictive checks missed by the Binomial baseline. The paper also clearly states that these histograms cannot recover task identities or cross-configuration covariance.

  2. The treatment of evidential limits is informative. The framework preserves multiple objectives and separates candidate arrival, service changes, workload changes, and measurement changes. The temporal audit finds support only for arrival, while the scenario and sensitivity analyses explain why leaderboard improvements alone cannot justify lifecycle decisions. This disciplined separation helps readers understand both useful conclusions and unresolved quantities.

Critical weaknesses
  1. The reliability of frontier-membership probabilities needs more direct validation. Sampling diagnostics, predictive checks, bootstrap agreement, dependence bounds, and the native trial panel provide substantial supporting evidence, but do not establish calibration or the error rates of retention/exclusion rules against a known or independently estimated frontier.

  2. The practical accuracy–cost advantage over simpler subset evaluation remains unclear. For example, when given the same initial evidence and evaluation budget, will the framework make more reliable frontier or dominance judgments than random or stratified subset evaluation with simple Pareto comparisons or bootstrap uncertainty?

Questions for authors
  1. Beyond the existing predictive and sensitivity checks, can you report frontier-membership calibration and erroneous-exclusion rates in simulations with a known frontier or independent repeated evaluations with a credible reference frontier? Please specify the retention/exclusion rule and test configurations near dominance boundaries.

  2. With identical initial evidence and matched budgets, how does the framework compare with random or stratified benchmark subsets followed by simple Pareto analysis or bootstrap uncertainty? Please report erroneous exclusions, dominance-judgment accuracy, and total evaluation/computation cost, including the cost needed to reach comparable reliability.

5 comments
AuthorsOpenReview ↗

2CEc (1/3): calibration and error rates near dominance boundaries (W1, Q1)

W1: “The reliability of frontier-membership probabilities needs more direct validation.” Q1: “Beyond the existing predictive and sensitivity checks, can you report frontier-membership calibration and erroneous-exclusion rates …”

We now report both. For the observed-task target (C66), membership probabilities are well calibrated under both generators, and wrong exclusions concentrate within 5% of a dominance boundary. For a new 66-task workload (P66) they are calibrated on simulated data but over-confident on resampled data, where a task bootstrap scores better; for that case the revision reports the predictive task bootstrap alongside the model. Both estimators use the same rule: exclude below 0.05, retain at 0.95 or above, and call anything in between undetermined.

We checked the model against known frontiers on 100 simulated datasets generated from its own assumed law and 100 resampled datasets, which resample real tasks and trials. Each dataset has 12 configurations, scored for both targets.

ECE C66 / P66wrong exclusionstrue members within 5% of boundary, excluded
simulated0.013 / 0.021C66 2 of 336; P66 2 of 222C66 0 of 59; P66 1 of 51
resampled0.015 / 0.053C66 7 of 387; P66 14 of 228C66 6 of 56; P66 5 of 57

ECE is expected calibration error. Away from the boundary the model is reliable for C66: for margins of at least 10%, only 1 of 621 true members was excluded on the resampled datasets. Near the boundary, the posterior probability that the resampled-dataset C66 exclusion rate exceeds 5% is 0.97.

We compared the model with the task bootstrap that estimates each target: for C66 it resamples the observed tasks, and for P66 it also draws a new 66-task workload from each resample (predictive bootstrap, post hoc). Membership Brier is over the 12 configurations and dominance Brier over the 132 ordered pairs. The gap is model minus bootstrap with its 90% interval, so a positive gap means the model scores worse.

membership Brier, model vs bootstrap; gapdominance Brier, model vs bootstrap; gapP(model better), membership / dominance
simulated, C660.033 vs 0.043; -0.0094 [-0.0118, -0.0070]0.013 vs 0.016; -0.0027 [-0.0032, -0.0022]>0.999 / >0.999
simulated, P660.076 vs 0.086; -0.0100 [-0.0135, -0.0064]0.028 vs 0.031; -0.0027 [-0.0035, -0.0020]>0.999 / >0.999
resampled, C660.040 vs 0.043; -0.0034 [-0.0074, 0.0007]0.012 vs 0.014; -0.0018 [-0.0024, -0.0012]0.92 / >0.999
resampled, P660.104 vs 0.083; +0.0216 [0.0160, 0.0272]0.039 vs 0.035; +0.0043 [0.0034, 0.0053]<0.001 / <0.001

Each generator favours the estimator that shares its assumptions. Simulated datasets draw new tasks from the model's law. Resampled datasets draw the new workload from the same 66 observed tasks, which is what the predictive bootstrap does; there it made 3 wrong P66 exclusions out of 218, against 14 of 228 for the model. On the resampled data the model's intervals are too narrow: nominal 90% intervals covered 72.0% of true values for C66 and 72.2% for P66. The shortfall comes from cost and duration, whose standardised errors have RMS 1.95 and 1.99 for C66 and 1.68 and 1.72 for P66, against 1.01 and 1.31 for completion. About half of the cost and duration error is shifts of each configuration's interval centre, and the rest is width (CYQc follow-up).

The bootstrap shares the boundary behaviour. In a separate post hoc test on 200 panels resampled from the observed tasks and trials, its hard calls within 5% of the boundary were wrong 45%, 43% and 40% of the time at 11, 22 and 33 tasks, against 2.9%, 0.8% and 0.1% for clear configurations (margin at least 10%). Configurations this close to a boundary stay unsettled under either estimator.

All of these checks resample one observed 66-task panel and are therefore not independent evaluation jobs. The two borderline submitted-model cases, Grok 4.6 and Opus 5, are discussed in the reply to CYQc (1/5). Full results are in revised App. E.7.

AuthorsOpenReview ↗

2CEc (2/3): accuracy and cost against random subset evaluation (W2, Q2)

W2: “The practical accuracy–cost advantage over simpler subset evaluation remains unclear.” Q2: “With identical initial evidence and matched budgets, how does the framework compare with random or stratified benchmark subsets followed by simple Pareto analysis or bootstrap uncertainty?”

At matched budgets the probabilistic frontier is clearly more accurate than simple subset evaluation, which compares observed means on the subset (plug-in Pareto comparison). We also compare a paired task bootstrap, either plain or with a finite-population correction (FPC bootstrap). We fitted the model to 180 new random subsets of 22 and 33 tasks and scored 176 of them, each against held-out tasks. For configurations with a held-out margin of at least 10%, the hard calls (erroneous exclusion or retention) per 100 scored calls were:

tasksplug-inmodelFPC bootstrapplain bootstrap
2213.754.383.041.46
3313.602.332.941.23

The same holds for probabilistic accuracy. The table below gives the Brier score (mean squared difference between a predicted probability and the held-out outcome) as model minus comparator, for membership and for pairwise dominance, so a positive value favours the comparator; in brackets is the posterior probability that the model is better, allowing for task overlap between subsets.

Budgetvs FPC bootstrap: membershipvs FPC bootstrap: dominancevs plug-in: membershipvs plug-in: dominance
22 tasks+0.0125 (0.15)+0.0001 (0.48)-0.0322 (0.96)-0.0164 (>0.999)
33 tasks-0.0041 (0.57)-0.0008 (0.60)-0.0491 (0.89)-0.0169 (>0.999)

The FPC bootstrap, computing the same frontier quantities, is more accurate than the model for membership at 22 tasks and not separable from it at 33, and practically tied with it for dominance on this complete 66-task panel. Both estimators target the same frontier quantities, so the revision reports both. The standard errors come from one panel, so the bootstrap's 22-task membership advantage is probable but not settled, and the dominance scores are post hoc. Design effects, equivalence tests, the effect of removing individual configurations and the 11 to 55 task budget ladder are in revised App. E.8.

Evaluation cost is identical at a matched budget, since every estimator uses the same tasks and trials. Only computation differs: the Bayesian fit took a median 221 seconds on eight CPUs (about 0.5 core-hours), against seconds for the bootstrap.

AuthorsOpenReview ↗

2CEc (3/3): what the model adds, and where it is used

W2 / Q2 (continued): “For example, when given the same initial evidence and evaluation budget, will the framework make more reliable frontier or dominance judgments than random or stratified subset evaluation with simple Pareto comparisons or bootstrap uncertainty?” P1 [assigned, presentation]: “Generally understandable, but requires substantial effort in places.”

Yes, against the plug-in judgments that subset evaluation produces (2/3). On complete panels such as Terminal-Bench v4 a paired bootstrap is a valid estimator of the same quantities, and the revision reports both estimator families for the Terminal-Bench v4 frontier quantities, with the estimand stated first (revised Table 23). The lifecycle break-even costs of §5.5 are reported under the model; a post hoc check with the predictive task bootstrap gives the same qualitative conclusions with different centres, for example 5.1 USD per task under the model and 9.5 under the bootstrap for Grok 4.5 to Grok 4.6. Aggregate-only archives give anonymous success histograms without saying which tasks are shared across configurations, so paired resampling is unavailable, but each configuration's histogram can still be resampled on its own. In a pilot on 8 resampled Terminal-Bench datasets reduced to histograms and mean cost and duration, this bootstrap and the submitted histogram model were close: model minus bootstrap was -0.0028 [-0.0049, -0.0005] in membership Brier, P(model better) 0.98, and -0.0002 [-0.0009, +0.0005] in dominance Brier, P(model better) 0.73 (pilot, n = 8). A pilot of this size cannot settle a difference this small, so we make no accuracy claim for the model there. Where no resampling estimator applies, the model is used without a claim of greater accuracy: snapshots of a changing archive are not exchangeable draws from one workload, the tau3-bench within-cell covariance analysis is model-based (reply to CYQc), and a configuration without cost records needs a model for its cost. For missing cells a dispersed two-way baseline is available, and the model scores about the same (table below).

We also tested where the model's accuracy comes from and how it handles missing cells:

testresult
Attribution (membership Brier, model minus predictive bootstrap, 60 subsets)+0.0167 (SE 0.0040), P(model better) 0.17. Replacing cost and duration draws: -0.0023 (SE 0.0013), P(hybrid better) 0.64; dominance +0.0000 (SE 0.0002), P(hybrid better) 0.45. Replacing completion draws: +0.0179 (SE 0.0035), P(hybrid better) 0.11; dominance +0.0006 (SE 0.0006), P(hybrid better) 0.19. Dominance, model: +0.0016 (SE 0.0007), P(model better) 0.18
Continuous ranked probability score (CRPS), held-out 44-task completion meansMean log ratio -0.107 (SE 0.017) favouring the model; arithmetic mean 0.0458 against 0.0466 (1.6% lower), 31 of 60 subsets favour the model
Missing cells, log score (nats per cell, model minus baseline)+0.25 to 0.30 against binomial baselines, but -0.017 [-0.060, 0.027] (tasks chosen at random) and +0.005 [-0.026, 0.036] (easiest tasks) against a beta-binomial dispersed baseline

Replacing the cost and duration draws closes the membership gap, while on dominance replacing either part closes much of the small gap, so the attribution to cost and duration is specific to membership (post hoc). The missing-cell advantage over binomial baselines comes from overdispersion, the modelling point the reviewers credit under S1, and the model handles missing cells natively. Details are in revised App. E.9.

On presentation, the revised version names each estimand before its results and puts both estimator families in one comparison table.

Reviewer_GEsXOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

The paper proposes a Bayesian framework for evaluating AI systems to address the shortcomings of point-estimate leaderboards. The authors model evaluated system configurations as a posterior random set across multiple dimensions (completion, cost, duration), separating system performance from temporal shifts in workloads and measurement regimes. To work around the lack of raw trial data in public archives, the authors solve a unitriangular system to exactly identify task-level success histograms from aggregate pass@k metrics, enabling the fit of an overdispersed Beta-Binomial model. Applying this to Terminal-Bench v4 and τ3\tau^3-bench, the authors demonstrate that standard linear scalarization discards probable frontier models, and they use pre-posterior Value of Information (VOI) analysis to determine when further benchmark evaluations could change adoption decisions.

Critical strengths
  1. The work is empirically rigorous. Solving a unitriangular system to exactly recover task-level success histograms from public pass@k aggregates is a practical contribution that allows for proper Beta-Binomial uncertainty modeling without access to raw trial logs.

  2. The paper provides empirical evidence that linear scalarization (standard weight grids) actively hides probable top-tier models from decision-makers. The integration of Bayesian decision theory and Value of Information to quantify when new benchmarks matter is a rigorous approach to current LLM evaluation.

Critical weaknesses
  1. The framework's decision layer is heavily dependent on "declared scenario classes" (e.g., literature-informed priors on switching costs). As the authors acknowledge, no organizational outcomes were actually measured (Table 14). To me, this pretty significantly limits the empirical validation of the decision layer. The framework tells a user what to do if their priors are correct, but it provides little guidance on how an organization should reliably estimate those complex switching and integration costs in the first place.

  2. Overall, I think the paper falls short on theoretical and algorithmic innovation as a submission to the probabilistic methods track. The framework relies entirely on established, textbook techniques: a standard Beta-Binomial model, Gaussian summaries, nested Bayesian bootstraps, and basic sampling importance resampling. The core innovation is in the application of these tools to AI evaluation and the algebraic trick for data recovery, not an advancement in Bayesian inference, variational methods, or UQ itself. It fundamentally reads like a benchmark/evaluation track paper or an applied statistics paper. While the statistical execution is sound, it does not advance the primary area it was submitted to in my opinion. The complexity of the problem is handled via careful framing and the use of declared scenario classes rather than through novel probabilistic methodologies.

Questions for authors

Can you highlight any specific theoretical or algorithmic contributions to probabilistic inference/sampling that go beyond the application of established statistical techniques?

2 comments
AuthorsOpenReview ↗

GEsX (1/2): scenario dependence of the decision layer (W1)

W1: “The framework's decision layer is heavily dependent on ‘declared scenario classes’ (e.g., literature-informed priors on switching costs).”

The dependence is narrower than it appears: the declared switching-cost scenarios enter the Bayes action only through one number, the expected switching cost per task.

Where the inputs come from. The three switching-cost distributions share a mean of one third of annual spend, anchored to firm-level IT-outsourcing estimates (Peukert, 2019; sources considered: revised App. D, Table 9). Since submission we screened 59 further candidate sources for the other inputs, the value of a completed task, the value of time and fallback. None gives a published estimate that transfers to Terminal-Bench tasks without an assumed wage and task bridge, so these inputs stay declared. An organisation that knows them and its own switching cost enters them in the same loss and obtains its action from the same loss, with means from the posterior already fitted and the joint failure of a primary and fallback from paired trial records (CYQc follow-up).

Scope. The decision layer conditions on declared organisational scenarios, as the revised §6 and Table 15 state. Switching, review and exit costs are inputs the organisation supplies, because this information is internal and often proprietary, and the decision needs only their expected value per task.

Why one number suffices. In the revised §5.5 analysis with per-trial cost and duration, the loss is linear in the amortised switching cost, so only its expected value per task can change the Bayes action, the action with the lowest posterior expected loss. The three declared switching-cost distributions have the same mean by construction and therefore give the same Bayes action; they differ only in event probabilities and in the expected value of perfect information. An organisation divides its one-off switching cost by the number of tasks over its planning horizon and compares the result with the expected loss per task that the alternative saves, which the benchmark data estimate. Under the model, none of the three incumbents (Opus 4.8, Fable 5, Grok 4.5) is ever the Bayes action at the declared mean switching cost, and which alternative is best stays uncertain.

Sensitivity to completion uncertainty. In the submitted analysis, replacing the completion posterior by its mean moves the probability that only the switching action is non-dominated by at most 0.022, 0.010 and 0.000 (Fable 5 to Fable 5.1, Opus, Grok). This measures sensitivity to completion uncertainty with cost and duration held fixed, and variation among the scenario inputs is not apportioned.

Held-out test. On held-out Terminal-Bench tasks (five task folds), decisions that may add a fallback beat a scalar pick. A plug-in pair is chosen from the model's posterior means with independent failures.

QuantityResult
Held-out loss, fallback-capable decisions vs scalar pickabout 16.4 USD per task lower
Joint-posterior pair vs plug-in pair, with the configuration as its own fallback in the menuworse by 6.17 USD per task on the Table 3b split (P(worse by more than 1 USD) 0.96); 5.9 (1.1 to 10.8) pooled over five partitions
Joint-posterior pair vs plug-in pair, without the configuration as its own fallbackworse by 1.18 USD per task on the Table 3b split (90% interval 0.29 to 2.16; P(worse by more than 1 USD) 0.62); 0.6 (0.2 to 1.1) pooled, better on one of five partitions
P(Bayes action is best), model0.10 to 0.54 across incumbents and estimands (up to 0.93 with no incumbent)
P(Bayes action is best), predictive task bootstrap, new workload0.17 to 0.44, against 0.13 to 0.42 for the model on the same cells
P(Bayes action is best), observed-task bootstrap0.34 to 0.69

The gain holds for fallback-capable decisions. Choosing the pair from the joint posterior rather than from plug-in estimates does worse, by 6.2 USD per task with the configuration as its own fallback in the menu and 1.2 without on the Table 3b split, and a rule that uses only training-task means does as well as the plug-in pair (CYQc follow-up). The loss assumes every non-completion is detected, so a failed primary attempt is always recognised, and the probabilities depend on the target; for the same new-workload target and cells, the model and the predictive bootstrap give similar ranges. The held-out test is in revised §5.5, and the switching-cost distributions and the task-paired model in App. B.

AuthorsOpenReview ↗

GEsX (2/2): contributions to probabilistic inference (W2, Q1)

W2: “Overall, I think the paper falls short on theoretical and algorithmic innovation as a submission to the probabilistic methods track.”

Q1 [assigned]: “Can you highlight any specific theoretical or algorithmic contributions to probabilistic inference/sampling that go beyond the application of established statistical techniques?”

Yes. The paper contributes to probabilistic inference by defining the inferential object for frontier claims, establishing what public evaluation data identify about it, and fitting models to a named estimand, with results that apply to any sampler:

  1. The inferential object. The frontier is a posterior random set of non-dominated configurations. The paper states which frontier claims can be computed from marginal posteriors and which need joint draws, and gives all-coupling bounds (revised Table 8) for what marginals alone allow.
  2. An identification result. Task-level success histograms are exactly identified from pass@k statistics, which gives an exact-marginal likelihood for aggregate-only archives. Against trial data released after submission, 12 of 13 recovered histograms are identical.
  3. A paired-trial model for completion, cost and duration, fitted for a named estimand (the observed tasks or a new workload).
  4. An identification audit of public archives stating what each identifies, with the power behind each non-identification.

The models are used where no resampling estimator applies: non-exchangeable snapshots, within-cell covariance and configurations without cost records. Aggregate-only archives still allow an unpaired bootstrap of each configuration's histogram (2CEc 3/3). On complete trial panels the revision reports a paired task bootstrap alongside the model, because the random-set frontier and its estimands are defined independently of the estimator (general response, point 5; revised App. E.9).

Comments on the paper

3 comments
AuthorsOpenReview ↗

General response (1/2): temporal results

We thank the reviewers for recognising the exact recovery of task-level histograms from pass@k aggregates, which supports Beta-Binomial modelling without raw logs and passes checks that the Binomial baseline fails (S1, all three). We also thank GEsX for noting that linear scalarisation hides probable top-tier models (S2) and that the statistical execution is sound (W2).

Temporal results (2CEc S2, CYQc W2). These come from the dated benchmark sources the paper audits (HELM, τ-bench and its τ²/τ³ successors, SWE-bench Verified, LiveCodeBench and LiveBench) and from records in the external Artificial Analysis (AA) composite index rather than from Terminal-Bench. The paper decomposes frontier change into candidate arrival, the quality trend of entrants, change in a mutable service, and workload or measurement-regime change. The benchmark sources identify the first of these, the dated growth of the candidate set; the other three are not separately identified without the bridges listed in the temporal identification table. The AA records answer a coarser question. It estimates one aggregate rate, the drift of the latent level of AA composite scores inferred from the timing and size of records, which combines these terms without separating them, and that drift is positive, with no slowdown detected.

Post hoc refits of two of these terms, with 90% intervals, leave both unsettled:

SourceTermEstimate (90%)
LiveBenchmeasurement regime: shift in common-task scores when a release changes tasks-6.06 pp [-11.33, -0.99]; not retained in leave-one-out prediction
LiveCodeBenchentrant quality: release-date trend+0.82 logit/yr [-0.75, 2.33]; posterior almost as wide as prior (ratio 0.94)

A records-only model, fitted post hoc to 20 AA record events among 476 family-month marks (one evaluated score for a model family in a month; 2022-11 to 2026-09), with first-stage estimates (the latent score of each mark, estimated before the records model is fitted) plugged in, gives positive constant drift under every definition of exposure, and no interval for the later-minus-earlier difference at a 2025-02 break lies below zero. Posterior medians with 90% intervals, in latent units per month:

exposureconstant driftbreak difference
calendar0.0990 [0.0890, 0.1096]0.0202 [-0.0190, 0.0551]
arrivals0.0770 [0.0603, 0.0902]0.0558 [0.0176, 0.0967]
mixed0.0909 [0.0758, 0.1034]0.0304 [-0.0102, 0.0699]

We report constant drift and claim no change in it, because the exposure definition is weakly identified (the mixture-weight posterior overlaps its uniform prior by 0.89) and remains a confound, moderate changes are poorly resolved, and a break gives no established held-out gain where tested (no held-out comparison exists for mixed exposure). The AA analysis is auxiliary to the paper's benchmark sources and conditional on the record law (the model of how records arise) and exposure construction (revised §5.4, Table 14 and Fig. 13, and App. E.13).

AuthorsOpenReview ↗

General response (2/2): Terminal-Bench trial records

Terminal-Bench trial records. Since submission, Terminal-Bench v4 has released trial records aligned by task across configurations, so the paper's central claims can now be tested against data the original analysis never saw. They hold up, and the revised manuscript reports the full results. The arguments in brief:

  1. The identification result is confirmed. The histograms recovered from pass@k aggregates match the trial records exactly, except for Opus 5, where some attempts were retried (GEsX 2/2; revised App. E.6).

  2. Probabilistic frontiers beat the plug-in comparison that leaderboards use. At matched budgets on random task subsets, plug-in Pareto comparison makes several times more hard errors than the probabilistic frontier and scores worse for both membership and pairwise dominance. On this one complete 66-task panel a paired task bootstrap computing the same frontier quantities does at least as well as our model, so the revision reports both estimator families (2CEc 2/3; revised App. E.8).

  3. Membership probabilities for the observed tasks are calibrated, and their errors concentrate at dominance boundaries. In known-truth checks the observed-task (C66) probabilities are calibrated under both generators, and on resampled data 6 of the 7 wrong exclusions fall within 5% of a dominance boundary, where the rule stated here (retain a configuration at membership 0.95 or above, exclude it below 0.05, otherwise call it undetermined) is meant to report configurations as undetermined; the bootstrap's hard calls (outright exclusion or retention) are also unreliable there. For a new 66-task workload (P66), the resampled datasets draw the new workload from the same observed tasks, which task resampling reproduces. There the model's probabilities are over-confident and the task bootstrap scores better, so for a new workload on complete trial records the revision reports the predictive task bootstrap alongside the model (2CEc 1/3; revised App. E.7).

  4. The sensitivity analysis flagged the right case. Table 12 (revised Table 13) showed Grok 4.6 to be fragile, and trial-level cost and duration confirm it: its membership depends on the estimator and the target, so the revision reports it as undetermined. The expected size of the frontier changes little (CYQc 1/5; revised App. E.10).

  5. Where the model is used. The contribution is the frontier quantities and the decisions built on them, whether computed from the model's posterior or from a bootstrap. With full paired trial records a team can use the bootstrap; with few tasks, summary records or no resampling counterpart, the model. Snapshots of a changing archive are not exchangeable draws from one workload, the τ³-bench within-cell covariance has no resampling counterpart, and a configuration without cost records needs a model for its cost. In these cases no resampling estimator applies, so the model is used without a claim of greater accuracy. For missing cells a dispersed two-way baseline is available, and the model scores about the same. Aggregate-only archives rule out paired resampling, but each configuration's success histogram can still be resampled, and in a pilot on 8 resampled Terminal-Bench datasets that bootstrap came close to the model. Each frontier probability now names its target, the 66 observed tasks (C66) or a new 66-task workload (P66), as the revised §6 states before each headline result (2CEc 3/3; revised App. E.9 and E.12).

  6. The decision layer isolates the one input that public data cannot supply. Decisions condition on declared organisational scenarios, because public evaluations do not identify switching costs, which differ by organisation (GEsX and CYQc raise this). The switching-cost scenarios enter the Bayes action (the action with the lowest posterior expected loss) only through the expected switching cost per task, a single number the organisation supplies, and on held-out benchmark tasks fallback-capable decisions cut loss relative to a scalar pick, while choosing the pair from the model's joint posterior does not improve on its means (GEsX 1/2, CYQc follow-up; revised §5.5).

AuthorsOpenReview ↗

Note to AC and SAC: summary of the discussion and the revision

Since submission, Terminal-Bench v4 has released trial records aligned by task across configurations. The revision uses them to test the paper's claims on data the original analysis never saw. These tests are post hoc, and the revision reports all of them, including those that favour other estimators.

What the new records confirm.

  • Identification. Of the 13 task-level histograms recovered from pass@k aggregates, 12 match the trial records exactly; for Opus 5 some attempts were retried (revised App. E.6).
  • Frontier probabilities against plug-in comparison (2CEc W2, Q2). On random task subsets, membership and dominance probabilities reach a stated reliability with 22 tasks where comparing means needs 55 (about 17,000 against 41,800 USD). On held-out tasks at 22 tasks, plug-in comparison made 13.75 wrong hard calls per 100 against 4.38 for the model (revised App. E.8).
  • The sensitivity analysis. It flagged Grok 4.6 as fragile, and trial-level cost and duration confirm this: Grok 4.6 is now reported as undetermined, and §5.3 is updated as CYQc asked.

What the revision adds or changes.

  • Bootstrap against model (2CEc's second named baseline). On complete paired records a task bootstrap of the same frontier quantities does as well as the model and leads for a new workload, so the revision reports it beside the model. With few tasks and cost and duration as means only, the model was more accurate (post hoc, revised App. E.9). Where nothing can be resampled (archive snapshots, the τ³-bench within-cell covariance, configurations without cost records), the model is the estimator.
  • Calibration (CYQc). Intervals are calibrated on data from the model's own law, and membership probabilities on observed tasks. On held-out real tasks, nominal 90% intervals cover 87%, 85% and 81% for completion, cost and duration. The revision reports these limits (revised App. B and E.7).
  • Lifecycle decisions (CYQc, GEsX). On held-out tasks, a decision that may add a fallback lowers loss against a scalar pick by 16.4 to 22.6 USD per task. Plug-in means obtain this gain, and choosing from the model's joint posterior is worse than choosing from its means (revised §5.5). Switching costs enter the Bayes action only through their mean per task, a number the organisation supplies (GEsX W1).

Status of each review.

  • CYQc wrote that the covariance check and unsupported membership results "address my two questions". The two follow-ups take up the two remaining concerns, calibration and lifecycle decisions.
  • 2CEc. The 2CEc follow-up answers both baselines named in W2 and Q2.
  • GEsX has not replied yet. GEsX (2/2) sets out the contributions to probabilistic inference (W2, Q1).

The contribution is the frontier quantities and the decisions built on them, whichever distribution they are computed from. With full paired records a team can use the bootstrap. With fewer tasks, summary records or nothing to resample, it uses the model.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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