Marco Simnacher, Georg Keilbar, Benjamin König +2stat.ML cs.AI cs.LG math.ST stat.ME
Conditional independence tests (CITs) test for conditional dependence between two random objects $X$ and $Y$ given a third random object $Z$. Existing CITs have limited applicability to high-dimensional data, especially multimodal data like text. However, we show that such tests are of interest for large language model (LLM) outputs, where we test whether an output $X$ generated from a source text $Z$ carries information about an attribute $Y$ beyond $Z$ itself. For this purpose, we propose embedded CITs (eCITs), which embed $X$ and $Z$ and apply an existing CIT to the resulting representations and to $Y$. We show that, provided the embedding of $Z$ is sufficient, i.e. retains the information $Z$ carries about either $Y$ or the representation of $X$, the null hypothesis transfers from $X$ and $Z$ to their representations, so that a CIT valid for the embedded hypothesis is valid for the original one. We further give conditions for equivalence of the two hypotheses, and show that sufficiency weakens to mean sufficiency when the embedded test targets conditional mean independence. We propose a semi-synthetic simulation design to assess type I error (T1E) control and power of the eCITs for given embedding maps on a specific dataset and task, and use it to evaluate them on our application. Applying the eCITs to German Parliament speeches, we find for all combinations of embedding maps considered that the summaries of two LLMs contain information about the speaker's faction and gender beyond the speech they were generated from.
Whether a language model has improved itself is increasingly judged not by mean accuracy but by which individual problems it gains and loses. Tracking these transitions means differencing two noisy estimates, leaving them vulnerable to measurement artifacts. Auditing three rounds of rank-$32$ LoRA self-training on Qwen3-8B against a frozen control pushed through the identical pipeline, we identify seven measurement failures, each of which inverts a reported finding when its control is absent. Several are standard practice. A ledger built on a single greedy decode manufactures capability changes on an untrained model, largely an artifact of inference batching; the expansion statistic separating acquisition from sharpening assigns that same model a rate of $0.280$. The natural threshold repair does not survive replication: estimated across the frozen comparisons such a design already contains, its null stays non-zero. We replace it with a per-problem exact test against a pooled baseline under false-discovery-rate control, which detects nothing on any held-out replicate and is unchanged under the multiple-testing rule, error rate and pool size. Applied to a ladder of arms matched in stream, volume and evaluation, the audit finds that external distillation improves problems the base model rarely reaches while three forms of self-training do not; a regression rejects this asymmetry as a by-product of distillation's larger overall gain ($p < 10^{-8}$). On the far smaller set of problems the base model never reaches, the evidence is inconclusive, while self-training corrupts problems solved at baseline at rates well above the measured floor. Transition-level auditing therefore requires a separately measured null for every statistic it reports: nulls that cost no new experiments, built from baseline replicates a multi-arm study already owns, though not from as few as most possess.
Studies of industrial visual inspection commonly report the area under the receiver operating characteristic curve (AUROC) and the overlap between anomaly maps and defect masks. Neither measure specifies the false-alarm rate at a selected threshold, while recurrent defect locations and mask geometry can inflate overlap. We combine a distribution-free upper tolerance threshold with a paired-minus-crossed spatial test. This test compares each detector's score-contributing locations with the matched defect mask and with masks from other images; the difference in rates defines spatial-evidence lift relative to the empirical chance-overlap rate. We evaluate three detectors on 120 point-defect images from three ISP-AD modalities and three fixed data splits. Of 378 alarms, 230 overlap the matched mask. Paired and crossed rates are nevertheless similar in eight of nine detector--modality cells; only DINOv2--ASM has a positive 95\% bootstrap lower bound (lift 0.259, 95\% interval 0.159--0.347). On the independent Magnetic Tile Defect dataset, the same analysis gives lifts of 0.203 (0.169--0.236) for Wide ResNet-50 (WRN50) patch memory and 0.231 (0.202--0.262) for Vision Transformer B/16 (ViT-B/16) patch memory, with one-sided permutation $p=10^{-5}$ for both. When crossed masks are restricted to the same defect class, the lifts remain 0.185 and 0.210. Exact sample planning shows that, with 150 calibration normals, a 95\%-confidence distribution-free claim is supported only for target false-positive rates of 1.98\% or higher; a 1\% target requires at least 299 normals. The results support reporting operating-point performance and chance-corrected spatial evidence alongside AUROC and raw mask overlap.
Benchmark contamination is diagnosed with n-gram overlap, likelihood-based membership inference, or canary strings, and each needs something usually unavailable: the training corpus, a well-chosen test statistic, or foresight at release. A recent alternative reads it off a linear probe on internal activations. We show the natural way to do this does not work, specify one that survives measurement, then find that the correction making it work carries more variance than the null it is tested against. The protocol reports a zero-sum contrast on the depth profile of probe accuracy, recentred on a level-matched placebo baseline, tested against a label-permutation null, with the reference set twice the size of the suspect set. Each choice replaces a simpler alternative we rejected on measurement. Reporting the level of excess separability rather than its shape makes the false positive rate track the size of the analyst's own control set, 0.03 to 0.99 under a true null. Contrasting against a flat depth profile rejects a true null 0.72 of the time when surface decodability rises with depth, and loses all power when it falls. On real transformers the protocol fails a test the simulations did not pose. The recentring subtracts an estimate, and the permutation null holds it fixed. Re-estimated across split seeds on four audits of contaminated checkpoints, its standard deviation is 1.30 to 1.56 times the null's own in every arm: what is subtracted to remove a bias is more variable than what it corrects. The one nominally significant result, p = 0.0075, becomes 0.0745 once that variance is propagated, and no verdict is issued. The simulations missed this because their surface key is the covariate driving item variation; on real text it is a proxy, and degrading key quality in simulation reproduces it. We add a companion measurement and a widened null. No arm shows contamination.
The dominant practice in language model evaluation is to report a single accuracy number per model and declare the higher one better, without testing whether the gap could plausibly be sampling noise. On benchmarks of a few thousand items, and under temperature sampling where a model can differ from itself run to run by more than the reported gap between models, this practice routinely overstates confidence in headline claims. The statistical machinery to fix this -- confidence intervals, paired significance tests, power analysis, clustered standard errors, multiple-comparison correction -- is well established, but no standard, pip-installable tool packages it in the shape an evaluation actually takes: a per-item results table. We present evalci, a pure-Python library (numpy/scipy/pandas only) that turns a per-item results table into a publication-ready claim -- e.g., "Model A beats Model B, $Δ=3.1$ pts, 95% CI [1.2, 5.0], paired permutation $p=0.002$, $n=1{,}319$" -- in one function call, with adapters for lm-evaluation-harness and HELM output. Every routine is validated against an independent reference (statsmodels, or brute-force exact enumeration) rather than only against itself. As a case study, we re-analyze a public comparison of nine language models' MMLU accuracy and find that 3 of the 8 adjacent leaderboard-rank gaps are not statistically significant after correcting for the 36 pairwise comparisons the ranking implies. evalci is available at https://pypi.org/project/evalci/ (source: https://github.com/Shreyaskc/evalci, DOI: https://doi.org/10.5281/zenodo.21201815)
When many people highlight the same document, is the crowd a single consensus, or is it internally structured into reader sub-groups that mark different things -- and is that structure a stable property of a reader or of the document? Building on prior work showing an individual's within-document highlighting signal is a whisper while individuality lives in selection, we ask the group-level question on a co-readership platform using a margin-preserving curveball null. Experiment 1: within a document, readers form strong sub-groups -- pairs agree far beyond what shared salience, mark density, and sentence popularity predict (nearest-neighbour agreement z=+6.3, significant in 88% of documents). Under an eight-block region-preserving null, shared engagement with the same coarse regions of the document accounts for about 40% of this excess; the majority survives as finer reader-specific agreement (z=+3.6, 77% significant). So the within-document crowd is, in a descriptive sense, factional. Experiment 2: is that grouping a stable reader trait? Here we are honest about power. The cross-document split-half reproducibility of a pair's agreement is near zero pooled (+0.078 and 0.000 in two separately drawn samples), and a power calibration shows the test is informative only for pairs that co-read many documents. In the only informative high-overlap subset (k>=4), point estimates are positive but small-sample, imprecise across the separately drawn samples, never significant, and attenuate under the region-preserving null. We therefore leave cross-document stability unresolved: the data is consistent with anything from situational grouping to a weak-to-moderate stable reader trait. The crowd is factional within a document; whether its factions follow the reader across documents is, honestly, beyond our reach.
We adapted the Reliable Change Index (RCI; Jacobson and Truax, 1991) from clinical psychology to item-level LLM version comparison on 2,000 MMLU-Pro items (K=10 samples at T=0.7). Two within-family pairs were tested: Llama 3 to 3.1 (+1.6 points) and Qwen 2.5 to 3 (+2.8 points). On the full benchmark, most items showed no reliable change (79% and 72%). However, over half the items were floor/ceiling. Among analysable items, change was bidirectional with large effect sizes: 34% improved and 28% deteriorated for Llama; 47% improved and 39% deteriorated for Qwen (median |delta p| = 0.50 and 0.90). Churn was asymmetric by difficulty: low-accuracy items improved, high-accuracy items deteriorated. Domain-level decomposition revealed family-specific reversals: Llama lost physics while Qwen lost law. Greedy single-shot evaluation missed 42% of reliably changed items and falsely flagged 25% of unchanged items. The aggregate accuracy gain is the net residual of opposing item-level movements. We recommend reporting churn rate alongside aggregate accuracy.