Abstract

If LLM training data is polluted with benchmark test data, then benchmark performance is only a biased estimate of out-of-distribution (OOD) generalization. Typical “decontamination” filters use $n$-gram matching which fail to detect “semantic” duplicates: sentences with equivalent (or near-equivalent) content that are not close in string space. We study this “soft” contamination of training data by semantic duplicates. We embed the Olmo 3 training corpus and find that:

1. contamination remains widespread: we observe semantic duplicates for 76% of the CodeForces test set and 100% of MBPP’s;
2. training on semantic duplicates of benchmark data improves benchmark performance by up to 22pp in controlled experiments and 18–22pp in ecological finetuning, depending on training regime and type; and
3. finetuning on duplicates of benchmark datapoints improves performance by up to 22pp (controlled) and 13–19pp (ecological) on truly-held-out datapoints from the same benchmark.

The generalization we find is “shallow”: it is limited to (2) and (3), and does not typically extend to related benchmarks. We replicate on Olmo 3, Qwen3, and Qwen3.5. We thus argue that recent benchmark gains are confounded: the prevalence of soft contamination means gains reflect both genuine capability improvements and the accumulation of effective test data in growing training corpora.

Full text

Converted from the LaTeX source. The prose is reproduced verbatim, with LaTeX markup removed and citation keys rendered as author–year where named in prose (otherwise dropped). Figures and the related-work comparison table are omitted; cross-references to them are dropped. The appendices are pointed to at the end, not reproduced. Canonical source: the PDF linked above.

1. Introduction

LLM scores on hard reasoning benchmarks have grown rapidly, with many benchmarks nearing saturation even for smaller models. But LLM training corpora have also grown by a factor of at least 10,000x since 2020. Thus, there is reason to expect a proportional increase in benchmark test examples being included in the training corpora of recent LLMs. While AI labs make good-faith efforts to remove syntactic duplicates of benchmark items from their corpora, ‘softer’ forms of contamination (i.e. by ‘semantic duplicate’ examples equivalent to test data but with a high string distance from test data) are hard to detect, and can result from independent reinvention of similar examples, rather than from leaking existing test data into the training corpus. This paper asks: how much does this confound current LLM benchmark scores?¹

which outputs are similarity-weighted combinations of nearby training documents—making soft contamination exactly the regime where benchmark scores should inflate.

We address this question by combining existing contamination detection methods with novel finetuning experiments to diagnose shallow generalization across examples: narrow performance gains from training on datapoints that are qualitatively typical of an existing benchmark. Using the open-data model Olmo 3, we show that modern LLM training corpora include data that are effectively samples from major reasoning benchmark test sets, leading to benchmark scores that (to some extent) demonstrate shallow generalization rather than general reasoning capability. We thus hypothesize that the rapid increase in LLMs’ performance on reasoning benchmarks partly reflects that the rapid growth of LLM corpora has enabled increasing levels of a hidden and internally hard-to-detect kind of contamination. If true, then recent progress on major reasoning benchmarks is weaker evidence for AI progress (conceived as OOD generalization).

Example semantic duplicate of test data, found by our pipeline. Original MBPP sample 297 (Write a function to flatten a given nested list structure.):

def flatten_list(list1):
    result_list = []
    if not list1: return result_list
    stack = [list(list1)]
    while stack:
        c_num = stack.pop()
        next = c_num.pop()
        if c_num: stack.append(c_num)
        if isinstance(next, list):
            if next: stack.append(list(next))
        else: result_list.append(next)
    result_list.reverse()
    return result_list

Semantic duplicate from dolmino:

    :param nested_list: A list that
        may contain other lists
    :return: A flattened list of
        all elements
    """
flattened_list = []
for element in nested_list:
    if isinstance(element, list):
        # Recursively flatten the sublist
        flattened_list.extend(
            flatten_nested_list(element))
    else:
        # Append non-list elements
        flattened_list.append(element)
return flattened_list

Let an exact duplicate of test data be an example in the training corpus which is syntactically identical (up to some $n$-gram) to some item in a relevant test set. A semantic duplicate of test data is an example in the training corpus which has the same meaning (in some sense) as some item in a relevant test set. We call contamination soft when it involves semantic duplicates. We call generalization shallow when it is limited to 1) generalizing within-distribution and 2) generalizing across semantic duplicates.

To test the hypothesis that soft contamination confounds benchmark results, we gauge the prevalence of semantic duplicates, of items from major reasoning benchmarks, in the training corpus of Olmo 3. We finetune on exact duplicates, semantic duplicates, and (mere) close embedding neighbors to test their capacity to induce shallow generalization.

Our contributions:

• High rates of soft contamination in the wild: We screen 1% of the pretraining data and all of the finetuning data of Olmo 3, around 260 GBs of text, for natural semantic duplicates by using their embedding distance to benchmark data, far more than previous studies. Despite the standard levels of decontamination by the Olmo team, we find more contamination than previous studies;
• Shallow generalization: We finetune Olmo 3 on duplicates of the MuSR, ZebraLogic and MBPP benchmarks and find that benchmark performance also improves on unseen benchmark data. The relative utility of semantic vs. exact duplicates varies by benchmark: on MuSR, both yield comparable gains of approximately 20pp on both seen and unseen items; on MBPP, exact duplicates produce larger gains on seen items (17pp vs. 9pp), but on unseen items semantic duplicates produce larger gains than exact duplicates (7pp vs. 2pp). Finetuning on one benchmark does not tend to improve performance on related benchmarks, suggesting that the generalization in our finetuning experiments is strictly ‘shallow’.
• Natural levels of soft contamination have a substantial effect: To our knowledge, we design the first ecologically valid finetuning study of exposure to semantic duplicates, demonstrating that even truly held-out benchmark items may be significantly inflated by shallow contamination. In the case of MuSR we demonstrate inflation on held-out duplicates by 10–11pp ($p < 0.05$) in Olmo 3, Qwen3 and Qwen3.5. We conclude that the held-out evaluation may be confounded by this effect.
• True hold-out has never been tried: We view this work as a step towards putting LLMs into the original scientific setting of empirical risk minimization: imposing a strict separation between training and test sets, validated on open training data.

2. Related Work

Contamination of LLM training corpora by benchmark test items is a large field of study. (A comparison table in the paper covers key differences between our work and prior studies of semantic duplicates.)

The first wave of contamination studies focused on the prevalence and impact of exact syntactic duplicates (i.e. word-for-word matches in string space), with later work extending the analysis to partial syntactic duplicates. More recently, researchers have begun to study indirect or ‘semantic’ contamination, where data in the training corpora is equivalent to benchmark-items in substantive content without sharing $n$-gram sequences or other syntactical properties. The literature on semantic contamination focuses on performance on a benchmark item and training-exposure to that same item’s near-duplicates as a variant on memorization. Our work instead studies semantic duplicates as a source of shallow generalization, which includes generalization from semantic duplicates to their equivalents in the benchmark, but also – more importantly, and why it still warrants the name ‘generalization’ – generalization to unduplicated examples of the task. Domínguez-Olmedo et al. (2024) study a related phenomenon they call ‘training on the test task’.

Studies of the prevalence of corpora-contamination by exact duplicates of benchmark data typically deploy two kinds of methods: searching for benchmark-item duplicates in open datasets, and memorization testing using ‘membership inference’ style techniques. When studying semantic-duplicates contamination, by contrast, memorization diagnostics are unlikely to capture the right contamination effects. Search in open datasets is therefore preferred in the (small) literature, using a heuristic semantic distance to guide search and human judgment, AI-assistant judgment, or plagiarism-detection software to assign ‘semantic duplicate’ status. Previous work by Yang et al. (2023) and Riddell et al. (2024) has provided high-quality estimates of the prevalence of semantic duplicates of items from major reasoning benchmarks including HumanEval, MMLU, and GSMK8k, in widely-used training corpora such as The Pile, StarCoderData, and RedPajama.

We use a method convergent with that of Yang et al. (2023) to estimate the prevalence of semantic duplicates in Dolma, Olmo’s custom training corpus. While our search covers a much larger dataset and finds many more semantic duplicates per benchmark item, our results are consistent with their findings of the rate of semantic duplicates in corpora.

Xu et al. (2025) study fake-news detection with a domain-specific concept of ‘entity-exposure’. Two central methods in the literature are 1) finetuning on contaminated data to simulate training-exposure (assuming or verifying that the model had no or limited prior exposure), as applied by Yang et al. (2023) to semantic duplicates, and 2) using duplicate-prevalence data to test for correlations between a benchmark-item’s rate of duplication in a model’s training corpus and the model’s performance on the item, which Riddell et al. (2024) apply to semantic duplicates. Our work uses a finetuning approach, but tests not only gains on a benchmark item from finetuning on its own semantic duplicates, but also gains on benchmark items from finetuning on semantic and exact duplicates of other items in the benchmark. Inspired by Koçyiğit et al.’s study of the memorization-effects caused by injecting realistic dosages of exact duplicates into a clean finetuning corpus, we also design (to our knowledge) the first ecologically valid finetuning study of the effect of exposure to semantic duplicates.

3. Methodology

Our full pipeline is described in the paper’s pipeline figure. To know what the model has seen (and so conduct a controlled analysis of OOD), our experiments use Olmo-3-7b, an open-data model. (Some closed models also allow finetuning, but with their closed corpora we cannot rule out prior training, which would confound our effect estimates.) The appendix describes the four benchmarks we used to measure the effect of finetuning: MBPP, CodeForces, MuSR, and ZebraLogic. All code available on GitHub.

3.1. Finding semantic duplicates in the wild

Olmo 3 corpus. We embed 1% of the Olmo 3 Base training data (Dolma3 and Dolmino) and all of the Olmo 3 Instruct finetuning data (Dolci SFT, Dolci Instruct DPO and Dolci Instruct RL). To sample from the base training data, we employ a stratified reservoir sampling strategy that preserves the corpus’s hierarchical structure. See the appendix for more dataset details.

Embeddings. We used llama-embed-nemotron-8b to embed the above datasets. At time of writing this model is #2 on the Massive Text Embedding Benchmark (MTEB) leaderboard. All embeddings were done in FP16 precision. Embeddings were performed on around 260GB of raw text and saved to an AWS storage system. Embeddings were performed over the course of approximately 2 days using a cluster of 8 H100 gpus.

Cosine similarity. To find candidate duplicates, we embed both Olmo 3 corpus data and benchmark data and calculate the cosine similarity between benchmark data points (MBPP and CodeForces) and our 1% sample of the whole corpus. The appendix covers this process in detail.

Semantic and exact duplicates among high cosine similarity matches. For MuSR, the highest cosine similarity matches are around $0.4$, and upon manual inspection it appears there are no duplicates, or MuSR-like problems in the training corpora. We conclude that the Olmo 3 datasets have no semantic duplicates of MuSR. For ZebraLogic we found many exact duplicates and a few semantic duplicates, which we take as a demonstration of the sensitivity of our cosine similarity pipeline. Besides these semantic duplicates, most other high cosine similarity matches were easy ‘Zebra puzzles’ not comparable in complexity to the ZebraLogic examples. After manual inspection of the top matches for MBPP and CodeForces we decide to sample and annotate using an LLM.

Exact duplicates: sampling and annotating ZebraLogic. We observed several ZebraLogic tasks in the training corpora verbatim. We obtain the rate of exact duplicates as in the appendix.

Semantic duplicates: sampling and annotating MBPP and CodeForces. We investigate matches between MBPP and CodeForces across the five training datasets. For each dataset and benchmark, we select candidates in the top 0.1% of cosine similarity. From this subset, we either take the top 100 or randomly sample 100 points, and prompt gemini-3-flash-preview to classify them. The model outputs a boolean label for semantic duplication, a categorical relationship type (exact, equivalent, subset, superset, or unrelated) which serves as a guiding heuristic, the reasoning for its choice, and a confidence score.

To validate this automated pipeline, we manually annotated a stratified sample of 190 items across CodeForces and MBPP (available in our GitHub repository). Our human annotations demonstrated general consistency and correctness with the LLM judge, though we noted occasional LLM misclassifications regarding whether CodeForces superset problems constituted true semantic duplicates, and can miss related problems as being not semantic duplicates when they are. To be conservative against false positives, we ran a secondary verification pass using gemini-3-pro on the potential duplicates initially flagged by the preview model, ensuring there was sufficient algorithmic uplift from the corpus text to the test problem. Examples of semantic duplicates found by our pipeline are provided in the appendix, and further details on the annotation process can be found in the appendix.

Generating synthetic semantic duplicates. The appendix gives a detailed description of our generation of synthetic semantic duplicates for each benchmark.

3.2. Finetuning on Duplicates

Our experiments distinguish between different kinds of ‘shallow generalization’ gains: 1) gains on one benchmark item from training on semantic duplicates; 2) gains on one benchmark item from training on exact duplicates of other items in the benchmark; and 3) gains on a benchmark item from training on semantic duplicates of other items in the benchmark.

We finetune Olmo 3 Instruct on duplicates of the following benchmark datasets: MuSR, ZebraLogic, and MBPP. We use either exact duplicates or semantic duplicates generated as in Section 3.1. To finetune Olmo 3 Instruct (a non-reasoning model) on these datapoints we first get a teacher model to generate Chain-of-Thought (CoT) reasoning traces. We use Opus 4.5 as teacher model, and for MuSR we also experiment with using GPT 4.1-mini.

We take the formatted questions and corresponding CoT answers and use LoRA to finetune Olmo 3 Instruct. The appendix explains our choice of finetuning approach. To get propensities, we use a temperature of 0.7 and do 8 parallel generations (for each of the unfinetuned model, the CoT generations of the teacher model, and for the finetuned model).

We split a finetuning dataset of duplicates in two and only finetune on half of it, while evaluating the finetuned model on both seen and unseen duplicates. To assess whether performance goes up on related benchmarks we use TrueDetective as a mirror for MuSR, Arc Challenge as a mirror for ZebraLogic, and HumanEval as a mirror for MBPP. We also evaluate performance on Arc Easy, BoolQ, HellaSwag, PIQA and Winogrande.

4. Results

4.1. Exact duplicates in training corpora

Surprisingly, we found that the Olmo Instruct RL dataset contains exact duplicates of 70% of one of their reported benchmarks’ (ZebraLogic) test data. The appendix describes this issue.

4.2. Natural semantic duplicates in training corpora

Relationship of cosine similarity to semantic duplicate status. We plot cosine similarity against semantic duplicate status. For both MBPP and CodeForces we find that even within the top 0.1% highest cosine similarity matches, semantic duplicates are far more common among the highest cosine similarity matches.

Benchmark examples with at least one semantic duplicate. 100% of MBPP problems have at least one semantic duplicate in the top-100 training data points by cosine similarity. We also find $\geq 1$ semantic duplicate per benchmark datapoint when we randomly sample 100 matches out of the top 0.1% cosine similarity matches. For CodeForces we find that 75.9% of problems have at least one semantic duplicate in the top 100 cosine similarity matches. Based on these findings we conclude contamination by semantic duplicates is widespread. (The above numbers are a lower bound: if we checked all the data and not just the top 100, we would very likely find more semantic duplicates for CodeForces.) We also consider the likelihood of a test point having a single semantic duplicate based on its elo, and find that easier problems (lower elo score) are statistically more likely to have semantic duplicates. See the appendix for more details.

Semantic duplicate occurrence stratified by training dataset. We investigate the relationship between where in the training scheme a training dataset is used, and the extent of semantic duplicate contamination. All training datasets have semantic duplicates for MBPP. For CodeForces we observe that again, semantic duplicates of problems exist in each dataset, particularly in Dolma, Dolci SFT and Dolci DPO.

Semantic duplicates are sparse and investigating more data leads to more matches. Previous work has found that $n$-grams typically miss many semantic duplicates; we instead work with cosine similarity. See the appendix for details. In the appendix we also show the proportion of benchmark problems that have at least one semantic duplicate in the training data scaling with the number of datapoints we sample. For CodeForces, this statistic drops to 28.4% when sampling only the top-1 cosine similarity match. We suggest that the reason we found more semantic duplicates than previous work is that we investigated far more data.

4.3. Finetuning on Semantic Duplicates

MuSR. We experimented with three levels of synthetic semantic duplication, with increasing dissimilarity, generated as detailed in the appendix. The table below shows that when we finetune on duplicates of half of the benchmark $(n = 125)$, performance goes up equally on the unseen half of the benchmark. Finetuning on exact duplicates of MuSR benchmark data leads to similar gains as finetuning on a variety of semantic duplicates: in both cases performance goes up by c. 20%. When instead of finetuning on duplicates (exact or semantic), we finetune on datapoints that have been selected for high cosine similarity to benchmark datapoints, the performance hardly goes up from baseline. We also check the performance change on a different benchmark from the same domain, TrueDetective, and find that performance remains stable. The appendix also shows that using a better teacher model to generate CoT reasoning traces results in further gains for finetuning.

ZebraLogic. The table below shows that, when finetuning on exact duplicates of half of the benchmark data $(n = 500)$, performance also goes up on the other half. Finetuning on exact duplicates leads to a much larger jump in performance (for both seen and unseen benchmark items) than semantic duplicates, in contrast to our finding for MuSR. In fact, we find that finetuning on semantic duplicates hardly increases performance, and in one case (combining shuffling, substituting and paraphrasing), that the performance on ZebraLogic substantially degrades, even though performance on the control same-domain benchmark (Arc Challenge) remains stable. We tentatively attribute this to compounding distribution shift in both the puzzles and their CoT traces: ZebraLogic’s substitution operates on domains (e.g., color→shape) in a way MuSR’s tree-based regeneration does not, so the teacher’s reasoning traces shift accordingly, and stacking all three transformations likely pushes training too far from the test distribution to support transfer.

MBPP. The table below shows that, when finetuning on exact duplicates of half of the benchmark data (n=210), we see a substantial jump on that half of the data, while performance on the unseen half hardly changes. Finetuning on semantic duplicates has a moderate effect, but it affects both seen and unseen performance. Again, finetuning on nonduplicate but cosine-similar data does not improve performance substantially. We also evaluate the finetune on a related benchmark, HumanEval, and find a surprising jump after tuning on semantic duplicates. We hypothesize that this jump happened because our semantic duplicate dataset is fairly rich, and so demands some generalization.

Key results from our experiments finetuning Olmo 3 on semantic duplicates. We see large gains from training on semantic duplicates, in MuSR’s case statistically equivalent to training on exact duplicates. The ‘Control’ column denotes a second similar-domain benchmark: for MuSR this is ‘True Detective’; for ZebraLogic this is the ARC Challenge and for MBPP this is HumanEval. We see no significant improvement to the control scores when finetuning on any setting of MuSR or ZebraLogic duplicates; we do see a surprising leap in HumanEval (MBPP’s control) for semantic duplicates. Accuracy (%) ± stderr. Abbreviations: P=Paraphrase, SH=Shuffle, SU=Substitution, cos similarity=high cosine similarity corpus matches. Experiments were performed on 8 A100 GPUs, each experiment taking around 2-3 hours.

We observe a pattern of shallow generalization. We repeatedly find that performance also improves on benchmark data that was unseen during finetuning: i.e. the delta between seen and unseen performance is small (apart from two cases of finetuning on exact duplicates). This suggests within-benchmark-distribution generalization. We tested benchmark improvement on different, but same domain benchmarks, and typically did not find substantial improvement, confirming shallow generalization. We also find that improvement or finetuning on high cosine similar datapoints does not by itself improve benchmark performance.

4.4. Ecologically Valid Finetuning

Realistic Contamination Dosage. We simulate SFT-stage exposure using our observed contamination rates. For MBPP, 40% of the top 0.1% cosine-similarity matches were true semantic duplicates. This establishes that roughly 4 in 10,000 training datapoints act as a semantic duplicate for any given test item—a conservative lower bound given our sampling density and false negative rate.

Finetuning contaminated and clean models. We finetune Olmo-3-7b-base, Qwen3-8b-base and Qwen3.5-9b-base, on Olmo-SFT data interspersed with MuSR semantic duplicates, for which our annotation experiments verify that no duplicates exist in the model’s training data. We then split the MuSR data into two halves of 125 datapoints each, and generate 4 semantic duplicates for them, two duplicates of level 2 and two of level 3, so 500 duplicates in total. We perform three finetuning runs with 1) a clean dataset of 10,000 SFT datapoints verified to be decontaminated, 2) a contaminated version of the same dataset where 5% of clean samples are swapped with 500 semantic duplicates corresponding to the ‘seen’ subset, and 3) an exact contamination version of the same dataset where 5% of clean samples are swapped with 500 exact duplicates corresponding to the seen subset. We evaluate each finetuned model at each epoch by prompting each model 20 times per question on all three finetuned models. See the appendix for details. We plot the accuracy curves during finetuning, and a table of the mean values and p-values.

Results on Olmo-3-7b. Despite a very low contamination rate, the contaminated model scores 16.9pp higher than the clean model on the seen subset ($p = 0.001$) and 11.4pp higher on the unseen subset ($p = 0.037$). Notably, on the unseen subset semantic contamination produces larger gains than exact contamination: training on exact duplicates yields essentially no held-out gain (51.2 vs. 51.0 clean baseline), suggesting that paraphrased duplicates leak to held-out items more effectively than verbatim ones. To verify that these performance gains reflect ‘shallow’ generalization rather than robust capability gains, we evaluate on TrueDetective, a benchmark in the same domain as MuSR. We find that performance on TrueDetective remains stable across finetuning conditions.

Results on Qwen3-8b and Qwen3.5-9B. We replicate the identical experiment on Qwen3-8B-base and find that contamination significantly inflates benchmark performance, comparable in magnitude to Olmo 3. The contaminated model scores 13.2pp higher than the clean model on the seen subset ($p$ < 0.001) and 9.9pp higher on the unseen subset ($p <$ 0.001). As with Olmo 3, semantic contamination is at least as effective as exact contamination on held-out items (68.9 vs. 65.6 for exact). Unlike with Olmo 3, however, the clean model itself shows substantial benchmark gains from finetuning relative to baseline (+5.0pp seen, +7.8pp unseen), concentrated on the random benchmark-subset we use as the ‘unseen’ subset for the contaminated model. We observe modest improvement on the control benchmark TrueDetective for the finetuned contaminated model. We further replicate the experiment on Qwen3.5-9B-base, finding the largest contamination effect of the three models. The contaminated model scores 15.3pp higher than the clean model on the seen subset ($p < 0.001$) and 11.4pp higher on the unseen subset ($p = 0.009$). As with Olmo 3 and Qwen3, semantic contamination is statistically indistinguishable from exact contamination on held-out items (74.7 vs. 75.0 exact, $p = 0.754$). As with Qwen3, the clean model also shows gains relative to baseline (+6.8pp seen, +8.2pp unseen), concentrated on the random unseen subset.

Natural contamination leads to benchmark gains. Our results show that the presence of semantic duplicates in training corpora, even at low rates, can lead to substantial gains in evaluation results. When finetuning on semantic duplicates instead of finetuning on clean data, we find a statistically significant increase on truly-held-out benchmark test data performance, that is, we observe within-benchmark generalization when finetuning on semantic duplicates.

5. Conclusion

We found widespread soft contamination of Olmo 3 training data with semantic duplicates, despite strong efforts from the Olmo team to filter out duplicates (Section 4.2); we also found that finetuning models with an ecologically valid amount of semantic benchmark duplicates leads to a statistically significant increase in benchmark performance (Section 4.4). We conclude that benchmark performance is indeed confounded by soft contamination. Shallow generalization is observed when the controlled finetuning on test data semantic duplicates improves performance by up to 22 percentage points while same-domain benchmark performance remains unchanged (Section 4.3).

5.1. Limitations

We likely underestimate the prevalence of semantic duplicates in frontier training corpora, because for cost reasons our detection methods did not embed the full pretraining corpus. Another downward bias is the relative absence of rephrasings in Dolma: synthetic data pipelines now often involve intentionally creating semantic duplicates at scale, and so our estimates of their prevalence are likely lower than the true rate in closed corpora using such methods. Similarly, we do not cover SOTA synthetic data provided via RL environments. Our experiment design is limited to models with an open-source training corpus - a small and potentially unrepresentative set of systems. While our comparative claims remain robust, absolute performance effects might differ under full finetuning. Furthermore, contamination dynamics during our SFT-stage simulation may differ from massive pretraining. The training corpora used in frontier models are much larger than Dolma – see e.g. the 30T tokens used in some Llama 4 runs. These larger corpora will have more semantic duplicates, but also a different rate of natural semantic duplicates than Dolma.

A fundamental objection to our project is that out-of-distribution (OOD) generalization is no longer the (only) goal of AI development: an alternative is to instead bring all common tasks in-distribution (Chollet 2024, Patel 2025, Leech 2024 §5.3.2). Perhaps the real-world utility of LLMs shows that our concerns about OOD generalization are not practically important, even if generalization is largely shallow. This is valid, but 1) then the deviation from the assumptions of empirical risk minimization should be explicitly noted, and secondly 2) (even perfect) hidden interpolation may not be practically equivalent to OOD generalization, and so being explicit about which is being instantiated is crucial.

Impact Statement

We aim to advance understanding of what LLM benchmark scores say about general capabilities on new inputs. Our findings have implications for how the AI research community, policymakers, and the public interpret reported progress on reasoning benchmarks.

More-accurately measuring AI capabilities helps to calibrate decisions about AI deployment, regulation, and research. If benchmark gains partly reflect interpolation from a growing corpus rather than more general capability improvements, then recognizing this could help prevent overconfidence in model generalization to novel tasks.

We do not believe this work poses significant risks. While our methods could inform more sophisticated benchmark gaming, the contamination we study is likely accidental rather than adversarial, and our detection methods are likely more useful for auditing than for evasion.

Our finding of contamination in Olmo 3 is only possible because of the unusual level of transparency of its model development process. It would be unfair for readers to thereby assume that the degree of contamination in Olmo is unusual, and worse, a perverse incentive against transparency.

Our work could easily be misread as ‘debunking’ LLM capabilities and so spur complacency about near-term AI impacts. Our results suggest that benchmark gains are confounded (and so partially shallow), not that they are illusory.

Appendices

The paper continues with appendices (detailed methodology, synthetic data generation, annotation schemes, and further results, including degradation analysis and the ecological-finetuning tables). These are not reproduced here; see the PDF.