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Your Benchmark Is an Empirical Measure Over Difficulty

Yifan Sun, Naicheng Yu, Jiawen Gong, Jingyan Shen, Huan Zhang

arXiv:2610.29927v1cs.LGcs.AIcs.CL

TL;DR

Benchmark scores depend on how questions are distributed across difficulty, which can affect model comparisons and progress monitoring. The paper models benchmarks as empirical difficulty measures and proposes diagnostics for mismatch and coverage gaps. Across 25 benchmarks in 7 domains, both issues are prevalent, and BENCHFILL reduces the sum of the top three difficulty gaps with three inserted items.

  • Problem

    Benchmark evaluations can yield different model comparisons or miss localized training progress when question difficulty distributions differ from the intended evaluation or leave regions uncovered.

    Source: §1 · p. 1

  • Method

    The paper models each benchmark as an empirical measure over difficulty and uses Wasserstein distance and the maximum adjacent difficulty gap as diagnostics, with theoretical guarantees.

    Source: §1 · p. 2

  • Results

    Across 25 benchmarks spanning 7 domains, both mismatch and large coverage gaps are prevalent; BENCHFILL reduces Top-3 Sum by 21.09%–38.88% with three inserted items per benchmark.

    Source: §1 · p. 2

  • Takeaways & Limitations

    Difficulty-targeted gap filling can improve coverage of under-covered regions and strengthen a benchmark’s ability to monitor localized training progress.

    Source: §4.2 · p. 9

    When prior information is unavailable, the default-target analysis assumes a fixed average performance difference whose location along difficulty is otherwise unrestricted.

    Source: §2.1 · p. 4

Abstract

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A benchmark is not merely a collection of test questions; it naturally induces an empirical measure over difficulty. In this work, we develop this measure-based view of benchmark evaluation. This perspective allows us to identify and formalize two central failure modes: measure mismatch, where the benchmark difficulty distribution differs from the intended difficulty distribution, and coverage gaps, where uncovered regions along the difficulty axis prevent benchmarks from detecting meaningful localized training progress. We propose two diagnostic metrics that capture these two failure modes and provide rigorous theoretical guarantees. Empirically, we analyze 25 popular benchmarks spanning 7 domains using carefully estimated item difficulties. Our results show that many benchmarks implicitly overweight certain difficulty regions, so their leaderboard conclusions should be interpreted with caution; others leave substantial portions of the difficulty axis uncovered, limiting their ability to monitor the model improvement process. Finally, we turn diagnosis into action by introducing BenchFill, a simple difficulty-targeted item rewriting algorithm that effectively reduces local coverage gaps.

1 Introduction

Benchmark conclusions depend not only on model performance but also on how questions are distributed across difficulty. The paper treats benchmarks as empirical measures over difficulty to formalize measure mismatch and coverage gaps, develop diagnostics, and assess their prevalence.

1 Introduction

  • A benchmark’s empirical measure assigns equal evaluation mass to each question at its difficulty level.Source: §1 · p. 2
  • Measure mismatch occurs when benchmark and target distributions weight difficulty differently, while coverage gaps leave intervals with little or no benchmark mass.These gaps can obscure substantial model gains concentrated in the uncovered intervals.Source: §1 · p. 2
  • Both difficulty-distribution mismatch and large coverage gaps are prevalent across 25 benchmarks spanning 7 domains.The study estimates question difficulty using Item Response Theory and computes the proposed diagnostic metrics.Source: §1 · p. 2
  • The proposed diagnostics are Wasserstein distance to a target difficulty distribution and the maximum gap between adjacent benchmark difficulty points.The paper reports theoretical results characterizing distributional mismatch and detectability of localized improvements.Source: §1 · p. 2
  • BENCHFILL reduces the sum of the top three difficulty gaps by 21.09%–38.88% with only three inserted items per benchmark.Source: §1 · p. 2

2 Formalization and Theory

The theory represents a benchmark as an empirical measure over item difficulty, making explicit how its difficulty distribution shapes evaluation. It formalizes distribution mismatch and difficulty coverage as limits on leaderboard comparisons and progress monitoring.

2 Formalization and Theory

  • The benchmark score averages performance across item difficulties, equivalently integrating a model’s difficulty-conditioned performance against the benchmark’s empirical difficulty measure.Each item contributes equal evaluation mass at its difficulty level.Source: §2 · pp. 2–3

2.1 Measure Mismatch

  • A target distribution represents the intended evaluation mix; mismatch between it and the benchmark’s difficulty measure can distort model gaps and even reverse their ordering.The target may encode the desired application mix.Source: §2.1 · p. 3
  • The 1-Wasserstein distance measures benchmark–target difficulty mismatch and, for L-Lipschitz performance differences, bounds score-difference distortion and supports rank stability.When the target score difference exceeds L times the mismatch distance in magnitude, the benchmark-induced ordering agrees with the target ordering.Source: §2.1 · pp. 3–4
  • With no prior information about where performance differences occur, the uniform target is the unique maximin choice, but is not claimed to be universally optimal.It serves as a neutral default that does not privilege difficulty regions a priori.Source: §2.1 · p. 4

2.2 Coverage Gaps

  • Because the benchmark measure assigns zero mass to intervals without items, localized training gains in those regions may not affect its score.The maximum gap is the largest interval on the difficulty axis containing no benchmark point.Source: §2.2 · p. 4
  • The diagnostic pipeline estimates item difficulties from empirical success rates across multiple LLMs, checks the response matrix and fitted IRT model, then computes metrics over normalized difficulty.The overview describes a 1PL IRT fit followed by post-fit diagnostics.Source: Figure 2 · p. 5
  • The maximum gap G(B) is the exact asymptotic minimax detection boundary for a benchmark’s ability to detect localized improvements.Its threshold separates undetectable intervals from improvements that become detectable with enough repeated samples.Source: §2.2 · p. 5
  • If a localized improvement’s width is no greater than the maximum adjacent difficulty gap, no level-α test has nontrivial worst-case power, regardless of repeated evaluations.For a wider improvement, repeated evaluations can eventually make it detectable.Source: §2.2 · p. 5

3 Empirical Diagnosis of Current Benchmarks

The section evaluates benchmarks as difficulty distributions, estimating item difficulty with IRT and measuring both distribution mismatch and local coverage gaps. Across the examined benchmarks, both issues are common and can limit leaderboard interpretation and training-progress monitoring.

3 Empirical Diagnosis of Current Benchmarks

  • The study analyzes 25 benchmarks across seven domains and measures mismatch with 1-Wasserstein distance and coverage with the maximum adjacent difficulty gap.The empirical benchmark view motivates diagnostics for both mismatch and localized coverage.Source: §3 · p. 5, §3.1 · p. 6

3.1 Difficulty Estimation and Metrics Calculation

  • IRT estimates item difficulty relative to model ability, while the 1PL model assigns each item a difficulty parameter that reflects the ability required for correct solutions.The analysis uses a diverse set of models and fitting diagnostics; all benchmarks pass the seven reported checks.Source: §3.1 · pp. 5–6

3.2 Results and Analysis

  • 10 of 25 benchmarks have DDM ≥0.10, indicating substantial deviation from the same-size uniform difficulty reference.Non-uniform difficulty weighting is not inherently problematic when it matches the intended evaluation objective; without a specified objective, high-DDM results are not difficulty-neutral comparisons.Source: §3.2 · pp. 6–7, Table 1 · p. 7
  • 8 of 25 benchmarks have Max Gap ≥0.10, and 9 of 25 have Top-5 Sum ≥0.30, leaving difficulty regions where localized training progress may go undetected.AIME24 and AIME25 have Top-5 gap sums close to 0.5; even benchmarks with hundreds of items, including HumanEval and BBH-5 objects, show substantial gap metrics.Source: §3.2 · p. 7, Figure 3 · p. 7

4 BENCHFILL: Difficulty-Targeted Gap Filling

BENCHFILL targets uncovered difficulty intervals by iteratively rewriting benchmark items toward a chosen difficulty and annotating the resulting variants. In experiments, it reduces coverage gaps, and curated math-benchmark variants show more comprehensive difficulty coverage.

4.1 Problem Setting and Method

  • BENCHFILL iteratively selects nearby parent items, rewrites them into child variants at a target difficulty, annotates valid children, and updates memory to guide later rounds.It selects the valid child closest to the target for human review before insertion.Source: §4.1 · p. 8

4.2 Experimental Setup and Results

  • Experiments target the three largest gaps in eight representative benchmarks, using a budget-matched best-of-N uniform-parent rewriting baseline.The search runs for at most eight rounds, retrieving four parents and generating four children per parent in each round.Source: §4.2 · p. 9
  • With three inserted items per benchmark, BENCHFILL reduces Top-3 Sum by 21.09%–38.88%; its average reduction is 32.67%, versus 35.06% for the oracle and 17.52% for the uniform-parent baseline.On AIME24, AIME25, and AIME26, BENCHFILL reaches the oracle reduction; Target Dev. is consistently below 0.01.Source: §4.2 · p. 9, Table 2 · p. 9

4.3 Curated Gap-Filled Benchmarks

  • Four curated math benchmarks expand from 30–40 items to 50–80 items, with generated items manually reviewed and low-quality or incorrect items discarded.The resulting AMC23-BenchFill, AIME24-BenchFill, AIME25-BenchFill, and AIME26-BenchFill variants substantially reduce the largest original gaps and bring distributions closer to uniform.Source: §4.3 · pp. 9–10, Figure 5 · p. 10

5 Related Work

Related work examines benchmark reliability through several lenses, including contamination, sensitivity to evaluation choices, and benchmark quality. The paper complements these lines by analyzing benchmark-induced difficulty distributions; it also builds on IRT-based difficulty estimation in NLP evaluation.

Science of benchmarking

  • Prior work studies benchmark reliability through contamination, sensitivity to decoding, prompting, or implementation, evaluation signal and noise, and broader benchmark-quality criteria.The paper positions its difficulty-measure perspective as complementary to these approaches.Source: §5 · p. 10

Related Work

  • This work adds a measure-based analysis of benchmark difficulty to prior studies of benchmark reliability and IRT-based evaluation.It formalizes measure mismatch and coverage gaps.Source: §5 · p. 10

IRT and its applications

  • IRT originated in psychometrics and has been adopted in NLP evaluation and leaderboard analysis, including work assigning continuous item difficulties and assessing benchmark measurement quality.Easy2Hard-Bench reports that its IRT difficulty labels align with human pairwise judgments better than GPT-4-based difficulty annotations.Source: §5 · p. 10

6 Conclusion

The conclusion frames benchmarks as empirical measures over difficulty, a perspective used to formalize mismatch and coverage gaps and derive diagnostics. The authors aim for more reliable and transparent benchmark evaluation; they report no foreseen direct negative societal impacts because the work focuses on benchmark analysis.

6 Conclusion

  • The paper views each benchmark as an empirical measure over difficulty and uses this perspective to formalize mismatch and coverage gaps, with theoretical results and practical diagnostics.The authors describe this perspective as having potential to open new ways to study and rethink benchmark evaluation.Source: §6 · p. 10

A.1 Broader Impacts

  • The authors state that diagnosing mismatch and coverage gaps can help researchers assess when benchmark scores provide faithful evidence for model comparison and training-progress monitoring.They frame more transparent comparison and more informed benchmark design as possible benefits.Source: §A.1 · p. 16
  • The authors do not foresee direct negative societal impacts, noting that the work focuses on benchmark analysis rather than model deployment or data collection.Source: §A.1 · p. 16

A.2 Limitations and Future Work

The paper develops a measure-based view to analyze measure mismatch and coverage gaps, while noting that it addresses only two consequences of that view. Its related-work discussion describes IRT as a common foundation for difficulty-aware evaluation because it models item difficulty and model ability from response data.

A.2 Limitations and Future Work

  • The authors characterize two issues—measure mismatch and coverage gaps—rather than exhausting the consequences of the measure-based perspective.They propose that further benchmark failures and design objectives could be formulated through the induced difficulty measure.Source: §A.2 · p. 16
  • The framework is primarily post-hoc: it diagnoses existing benchmarks and reduces pronounced coverage gaps through targeted item insertion.The authors identify designing the difficulty structure during benchmark construction as a next step.Source: §A.2 · p. 16

A.3 Extended Related Work

  • IRT is a common foundation for difficulty-aware evaluation because it jointly models item difficulty and model ability from response data.Prior approaches described include human ratings, LLM-based difficulty judgments, and intrinsic problem-complexity estimates.Source: §A.3 · p. 16

B.1 Measure Mismatch

This section establishes theoretical guarantees for diagnosing measure mismatch and coverage gaps, then describes the benchmark selection and IRT diagnostics used to compare normalized item difficulties with a uniform reference and assess the largest uncovered gap.

B.1 Measure Mismatch

  • Under an L-Lipschitz performance difference, distribution mismatch controls score distortion and ensures benchmark and target rankings agree; repeated-sample estimates also yield ordering stability under the stated independence and bounded-score assumptions.The finite-sample theorem gives a high-probability distortion bound and rules out an observed rank flip when the bound is smaller than the target performance difference.Source: §B.1 · pp. 16–18
  • With no prior knowledge of where performance differences occur along difficulty, the uniform target is the unique maximin choice that preserves the full average difference in the worst case.The result considers signed performance differences with a fixed average level and otherwise unrestricted location.Source: §B.1 · pp. 18, 20

B.2 Coverage Gaps

  • The maximum gap G(B) is the exact asymptotic minimax detection boundary for interval-localized performance differences under benchmark B.When an improvement region is wider than the maximum gap, benchmark points cannot all miss it.Source: §B.2 · p. 21

C.1 Benchmark Details

  • The benchmark summary reports domains, example counts, and evaluation rollouts per item.Table 3 summarizes the benchmarks used in the analysis.Source: §C.1 · p. 23, Table 3 · p. 23

C.2 Model Selection Details

  • Non-agentic evaluation uses 12 models sampled across ten equal-width Text Arena score tiers plus leaderboard extremes, while agentic evaluation uses models from HAL, including Claude Sonnet 4.5, Claude Opus 4.1, GPT-5, and Gemini 2.0 Flash.The Text Arena overall score is used as a proxy for broad capability across domains.Source: §C.2 · pp. 23–24

C.3 IRT Fitting and Diagnostics

  • IRT diagnostics assess response-matrix information and ordering consistency, with thresholds of at least 0.3 for information and at most 0.3 for inversion rates; fitting uses Bayesian 1PL-IRT with a guessing parameter for multiple-choice items.Information is higher when aggregate success rates are near 0.5, while lower inversion rates indicate better agreement with the latent ordering.Source: §C.3 · p. 24
  • All benchmarks pass the reported response-matrix and MCMC diagnostic thresholds.The diagnostics assess convergence and sampling quality, including chain agreement, effective sample size, and divergent transitions.Source: §C.3 · p. 25
  • Average leave-one-out Pearson and Spearman correlations are at least 0.9723 and 0.9704, while minimum correlations are 0.9137 and 0.9089, respectively.These results indicate difficulty estimates remain stable when any one of the 12 selected models is excluded.Source: §C.3 · p. 26

C.4 Metric Calculation Details

  • The DDM is the 1-Wasserstein distance between normalized benchmark difficulties and a same-size empirical uniform reference, while the gap metric uses the maximum spacing across the difficulty axis.Difficulties are min-max normalized to [0, 1] before comparison.Source: §C.4 · p. 26

C.5 Model Comparison for Different Difficulty Estimation Models

Model comparisons support using 1PL-IRT for the study’s difficulty estimates: BIC favors it on most benchmarks, while favored alternatives show reliability or fitting problems. Leave-one-out refits also show consistently high difficulty correlations.

C.5 Model Comparison for Different Difficulty Estimation Models

  • BIC selects 1PL over 2PL for 21 of 25 benchmarks, often by large margins.The authors report that adding item-specific discrimination parameters is unsupported for most benchmarks after accounting for model complexity.Source: §C.5 · pp. 26–27
  • Leave-one-out refits show consistently high difficulty correlations, supporting the selected 12 models as sufficient for stable item difficulty estimation.The reported correlations are Pearson and Spearman correlations across refits that each remove one model.Source: Table 7 · p. 27
  • For the four benchmarks where BIC favors 2PL, problematic sampling diagnostics make those fits unreliable alternative difficulty estimates.The corresponding 1PL fits remain well-behaved.Source: §C.5 · p. 27
  • MIRT-2 and MIRT-3 do not provide stable posterior estimates on smaller benchmarks, and larger-benchmark fits did not complete reliably within the fitting budget.The authors conclude that the analyzed response matrices do not support stable multidimensional difficulty estimates.Source: §C.5 · p. 27

C.6 Posterior Uncertainty Analysis

Posterior uncertainty leaves the main DDM and coverage-gap conclusions intact, while multidimensional IRT fits show poor mixing. Benchmark calibration uses greedy quantile matching to select items closer to a target difficulty distribution.

C.6 Posterior Uncertainty Analysis

  • DDM posterior standard deviation is typically 0.011 (range 0.006–0.020), about 8%–12% in typical cases, so reported values are not artifacts of difficulty-estimation noise.Source: §C.6 · pp. 27–28
  • BIC favors 1PL on 21 of 25 benchmarks, while the four 2PL-favored fits have worse sampling diagnostics and corresponding 1PL fits remain well-behaved.Source: Table 8 · p. 28, Table 9 · p. 28, §C.6 · p. 28
  • The observed Max Gap exceeds a same-size uniform baseline with median posterior probability 0.999, and the observed-to-baseline ratio has median 3.85×.Max Gap posterior standard deviation ranges from 0.017 to 0.041; the ratio reaches 18.8× on ScienceQA, 11.3× on MedQA, and 5.9× on ZebraLogic.Source: §C.6 · p. 28

C.7 Additional Experimental Details and Results

  • Multidimensional IRT fits generally mix poorly, with high maximum R-hat and very small minimum bulk ESS, so they do not provide stable alternative difficulty estimates.Source: Table 10 · p. 29

D Benchmark Calibration

  • Greedy quantile matching selects unused items nearest to target difficulty locations, producing a pruned benchmark intended to better approximate the target distribution.Source: D Benchmark Calibration · p. 29

D.1 Experimental Setup

The calibration experiment tests whether pruning a source benchmark toward a target difficulty distribution improves agreement with rankings from other math benchmarks. Uniform is used as a neutral target, not as an assumption about the reference distribution.

D.1 Experimental Setup

  • The experiment calibrates each of eight math benchmarks in turn and compares its model ranking with a leave-one-out ranking aggregated from the other benchmarks.Source: §D.1 · p. 30
  • Without an application-specific target, calibration uses the uniform distribution as neutral debiasing, not as a claim that the leave-one-out reference distribution is uniform.Source: §D.1 · p. 30
  • The study compares source and reference rankings before and after calibration using Spearman and Kendall correlations; W1(ν, Unif) tracks distance from the uniform target.Source: §D.1 · p. 31, Table 11 · p. 31

D.2 Results

Calibration improves agreement between rankings from a source benchmark and a leave-one-out reference, outperforming same-size random pruning. The accompanying BenchFill procedure retrieves nearby parent items and references, rewrites candidates toward a target gap, and selects the valid child closest to the target.

D.2 Results

  • Calibration raises average Spearman correlation from 0.890 to 0.930 and Kendall correlation from 0.802 to 0.848 against the leave-one-out reference ranking.On Minerva-Math, Spearman rises from 0.601 to 0.790 and Kendall from 0.455 to 0.667; high initial agreement on other benchmarks is preserved using the pruned benchmark.Source: §D.2 · p. 31
  • Random pruning scores 0.895 average Spearman and 0.801 Kendall, while calibration lowers average W1(ν, Unif) from 0.096 to 0.028; random pruning yields 0.109.The comparison uses the same pruning size and averages random-pruning results over 30 trials.Source: §D.2 · p. 31

E Additional Details and Experimental Results of BENCHFILL

  • BenchFill retrieves parents nearest the target gap, supplies nearby item–difficulty references, iteratively rewrites and annotates valid children, then selects the child closest to target for expert review.Source: E Additional Details and Experimental… · p. 32

E.1 Implementation Details

  • The implementation targets each benchmark’s three largest gaps, uses difficulty-aware iterative search, and compares against a budget-matched uniform-parent rewriting baseline.The baseline matches BenchFill’s total rewrite budget and final selection rule but omits difficulty-aware retrieval, nearby references, and iterative memory updates.Source: §E.1 · pp. 32–33

E.2 Additional Experimental Results

BenchFill detects localized post-SFT gains in three tested cases, whereas the original and baseline benchmarks detect none. Additional analyses find that the rewriter responds to target difficulty before feedback and that iterative search generally improves alignment.

E.2 Additional Experimental Results

  • All 24 final selected items passed GPT-5.4 validity checks and human review without modification or replacement; one failed initial candidate was regenerated.Source: §E.2 · p. 33
  • Before iterative feedback, higher specified target difficulties produce higher mean annotated difficulties within most benchmarks, with separated targets usually yielding distinct child-difficulty distributions.Source: §E.2 · p. 34, Figure 7 · p. 37
  • BenchFill detects a positive post-SFT gain in all three cases (3/3), while Original and Original + Baseline detect none (0/3 each).The figure analyses report that mean target deviation generally decreases across rounds and generated children often concentrate more closely around the target.Source: §E.2 · p. 34, Table 12 · p. 34, Figure 8 · p. 37
  • Representative examples pair each selected item with its original ancestor and show ancestor, target, and annotated difficulty values.Source: §E.2 · p. 34, Table 13 · p. 35
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