A Sober Look at Progress in Language Model Reasoning: Pitfalls and Paths to Reproducibility

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arXiv:2504.07086v1 [cs.LG] 09 Apr 2025

A Sober Look at Progress in Language Model Reasoning: Pitfalls and Paths to Reproducibility

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Andreas Hochlehnert1  Hardik Bhatnagar1∗  Vishaal Udandarao1,2∘

Samuel AlbanieAmeya Prabhu1†Matthias Bethge1†

1Tübingen AI Center, University of Tübingen  2 University of Cambridge equal contribution, ∘ core contributor, †equal advising

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Abstract

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Reasoning has emerged as the next major frontier for language models (LMs), with rapid advances from both academic and industrial labs. However, this progress often outpaces methodological rigor, with many evaluations relying on benchmarking practices that lack transparency, robustness, or statistical grounding. In this work, we conduct a comprehensive empirical study and find that current mathematical reasoning benchmarks are highly sensitive to subtle implementation choices—including decoding parameters, random seeds, prompt formatting, and even hardware and software-framework configurations. Performance gains reported in recent studies frequently hinge on unclear comparisons or unreported sources of variance. To address these issues, we propose a standardized evaluation framework with clearly defined best practices and reporting standards. Using this framework, we reassess recent methods and find that reinforcement learning (RL) approaches yield only modest improvements—far below prior claims—and are prone to overfitting, especially on small-scale benchmarks like AIME’24. In contrast, supervised finetuning (SFT) methods show consistently stronger generalization. To foster reproducibility, we release all code, prompts, and model outputs, for reasoning benchmarks, establishing more rigorous foundations for future work.

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\faGlobe Leaderboard\faDatabase [Eval Logs](https://huggingface.co/datasets/bethgelab/sober_reasoning/ “”)

Figure 1: The Sombre State of LM Reasoning for Math.(left) when re-evaluating recent 1.5B reasoning-enhanced models on AIME-24 using a standardized framework (see Section 4), we find substantial drops to reported results in the original papers, (right) the observed improvements from recent methods (gray highlighted area) fall entirely within the variance range (orange box plots) of DeepSeek-R1 1.5B model performance. This suggests that these methods do not significantly outperform the base model—underscoring the importance of rigorous, multi-seed evaluation protocols for obtaining reliable performance estimates.Report issue for preceding element

1 Introduction

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“The first principle is that you must not fool yourself, and you are the easiest person to fool.”

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—Richard Feynman

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Reasoning has become central to recent advances in large language models (LLMs), playing a key role in nearly all frontier systems (Jaech et al., 2024; OpenAI, 2025; Meta-AI, 2025). Recent months have seen a surge of research focused on understanding and improving LLM reasoning, accompanied by several open-source tools and training strategies (see Li et al. ( [2025b](https://arxiv.org/html/2504.07086v1#bib.bib55 “”)) for a survey). This momentum has sparked optimism that building capable, competitive reasoning models may soon be within reach.

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However, as evaluation practices shape the direction and perceived progress of the field (Liao et al., 2021; Marie et al., 2021; Prabhu et al., 2020; Colas et al., 2018; Biderman et al., [2024](https://arxiv.org/html/2504.07086v1#bib.bib11 “”)), their persistence—especially in reasoning—calls for renewed scrutiny and higher standards.

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Motivated by a growing number of inconsistent empirical claims across the reasoning landscape, we conduct a rigorous investigation into the current state of reasoning benchmarks, focusing specifically on mathematical reasoning—one of the most widely used testbeds for evaluating algorithmic advances in this space (HuggingFaceH4, 2024).

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Our main finding is that many recent empirical conclusions may be overly optimistic and fail to generalize under careful re-evaluation. We identify a surprising degree of sensitivity in LLM-based reasoning pipelines to seemingly minor design choices—ranging from decoding parameters, prompt formatting, and random seeds to the hardware and software stacks used during evaluation (see Table 1). Particularly concerning is the instability introduced by small benchmark sizes: for example, AIME’24 and AMC’23 each contain only 30–40 examples, making performance metrics highly volatile—where even one question can shift Pass@1 by over 3 percentage points. This leads to substantial variance across seeds, often resulting in double-digit performance swings that challenge the reliability of published results. In Section 3, we systematically analyze the root causes of this instability, including sampling variance, decoding configurations, evaluation frameworks, and hardware heterogeneity. We show that these factors can significantly distort conclusions if not carefully controlled.

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In Section 4, we propose a set of best practices aimed at improving reproducibility and rigor in reasoning benchmarks. We also re-evaluate recent techniques using a standardized and reproducible evaluation stack. Our findings are sobering—reinforcement learning (RL) applied to distillation-based models such as DeepSeek-R1 yields little to no statistically significant gains. Some methods, such as OpenRS, show promising results in original reports, but fail to hold up under repeated evaluation. RL training on base models like Qwen2.5 Math does show stronger performance, but still often underperforms instruction-tuned counterparts.111We note that OpenReasoner-Zero is a consistent exception, achieving competitive performance. Furthermore, RL-trained models exhibit significant performance drops on newer benchmarks such as AIME’25, echoing patterns of test set overfitting or “hill-climbing” observed in prior work (Golchin & Surdeanu, 2023; Dominguez-Olmedo et al., [2024](https://arxiv.org/html/2504.07086v1#bib.bib26 “”)). In contrast, supervised fine-tuning (SFT) continues to deliver stable, generalizable improvements across benchmarks, underscoring its maturity as a training paradigm. These observations point to a critical need for more reliable and standardized evaluation protocols.

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Taken together, in this work, we aim to provide not only a clearer assessment of where current methods stand, but also the tools and practices needed to make reasoning evaluation more transparent, robust, and reproducible. To this end, we open-source all code, prompts, and outputs to facilitate fair and accountable progress in this increasingly important area.

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2 Related Works

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Language Model Reasoning (for Math). The recent releases of OpenAI-O1 (Jaech et al., 2024) (in December 2024) and DeepSeek-R1 (DeepSeek-AI, 2025; Lightman et al., 2023; Team, 2025), REINFORCE++ (Hu, 2025), DPO-VP (Tu et al., 2025), CPPO (Lin et al., 2025a) and GRO (Cai, 2025; Liu et al., 2025b; Shao et al., 2024), curriculums (Wen et al., 2025b) and reward design (Gao et al., 2024a; Ma et al., 2023; Xie et al., 2025; Yu et al., 2024; Sim & Chen, 2024; Yuan et al., 2025). Further, some works also explored scaling up RL-based approaches to modalities beyond just language, including vision (Ma et al., 2025; Huang et al., 2025; Chen et al.,; Liu et al., 2025c; Lin et al., [2025b](https://arxiv.org/html/2504.07086v1#bib.bib60 “”)). In our work, we objectively re-evaluate the claims made by several of these recent works under a standardized lens, and find that many of the reported gains do not hold up strongly when pitted on a level-playing field against well-tuned baselines.

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Sobering Studies on ML Progress. Machine learning is a field of rapid progress. Due to the lightning speed of papers coming out across the various sub-fields of machine learning, practitioners and researchers often fail to rigorously evaluate algorithmic progress (Hutchinson et al., 2022; Machado et al., 2018; Balduzzi et al., 2018; Cawley & Talbot, 2010; Prabhu et al., 2024b; 2020) and test-time adaptation (Press et al., 2023; Gorsane et al., 2022; Jordan et al., 2020). Some works have even gone as far as suggesting that reliable benchmarking of RL-based methods is computationally infeasible (Jordan et al., 2024; Nezhurina et al., 2024), the type of tasks tested (Yan et al., 2025; Dominguez-Olmedo et al., 2024), metrics used (Liu et al., 2024; Kandpal et al., 2023). Given such a volatile landscape, in this work, we aim to level the playing field across recent LM-methods that have been released and provide an objective look on the progress that the reasoning community has made. Our findings, which we discuss in the rest of the paper, are sobering at best.

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3 Exploring the Design Space of Reasoning: What Matters Most?

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Recent reasoning-focused language models are evaluated under highly heterogeneous conditions—including differences in evaluation frameworks and hardware, number of random seeds, temperature, and nucleus sampling parameters (top_p) (see Table 1). While prior work has examined the effect of sampling parameters in multiple-choice (Renze, 2024), the influence of these choices remains underexplored for open-ended reasoning models—particularly those trained with reinforcement learning. In this section, we systematically assess how these evaluation design choices affect reported performance, and highlight the sources of variance that most impact the reliability of results.

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3.1 Experimental Setup

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We adopt a consistent experimental setup throughout this section, unless otherwise stated. Our analysis includes nine widely used models grouped into two commonly benchmarked size classes: 1.5B and 7B parameters. For the 1.5B class, we evaluate: DeepSeek-R1-Distill-1.5B (DeepSeek-AI, 2025), II-1.5B-Preview (Intelligent Internet, 2025). Note that DeepScaleR-1.5B, II-1.5B-Preview, and the OpenRS models are all initialized from DeepSeek-R1-Distill-1.5B and subsequently finetuned via reinforcement learning (e.g., GRPO (Shao et al., 2024), and OpenThinker-7B (Team, 2025), trained using supervised learning on reasoning traces derived from DeepSeek-R1. All models are benchmarked on three widely used datasets: AIME’24 ( AI-MO,), and MATH500 (Hendrycks et al., 2021) with the vllm backend (Kwon et al., [2023](https://arxiv.org/html/2504.07086v1#bib.bib52 “”)).

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Table 1: Taxonomy of current open-weight reasoning models. For each model, we report the base model it was post-trained from and the exact type of post-training algorithm applied (RL vs SFT). Further, we note the evaluation framework that the original paper uses for reporting results along with the exact temperature, generation sequence length, and top_p sampling parameters used for AIME-24 evaluation, with the number of generations used for computing Pass@1 (K). It is evident that there is no clear standardization across different models with respect to evaluation frameworks used and the sampling parameters. This motivates the need to closely scrutinize the evaluations of current reasoning models.

Model	Algorithm	Base	Framework	Temp	Top_p	Seq. Len	K
DeepSeek-R1-Distill-1.5B	SFT	Qwen2.5-Math-1.5B	–	0.6	0.95	32,768	64
DeepSeek-R1-Distill-7B	SFT	Qwen2.5-Math-7B	–	0.6	0.95	32,768	64
DeepSeek-R1-Distill-14B	SFT	Qwen2.5-14B	–	0.6	0.95	32,768	64
DeepSeek-R1-Distill-32B	SFT	Qwen2.5-32B	–	0.6	0.95	32,768	64
OpenThinker-32B	SFT	Qwen2.5-32B-Instruct	evalchemy	0.7	0.8	32,768	5
Bespoke-Stratos-32B	SFT	Qwen2.5-32B-Instruct	evalchemy	0.7	0.8	32,768	5
Bespoke-Stratos-7B	SFT	Qwen2.5-7B-Instruct	evalchemy	0.7	0.8	32,768	5
s1.1-7B	SFT	Qwen2.5-7B-Instruct	lm-eval-harness	0	–	32,768	64
s1.1-32B	SFT	Qwen2.5-32B-Instruct	lm-eval-harness	0	–	32,768	64
LIMO	SFT	Qwen2.5-32B-Instruct	math-eval-harness	0	1	32,768	1
MiniMath-R1-1.5B	SFT	DeepSeek-R1-Distill-1.5B	oumi-ai	–	–	–	–
DeepScaleR-1.5B-Preview	RL	DeepSeek-R1-Distill-1.5B	verl	0.6	0.95	32,768	16
Open-RS1	RL	DeepSeek-R1-Distill-1.5B	lighteval	0.6	0.95	32,768	32
Open-RS2	RL	DeepSeek-R1-Distill-1.5B	lighteval	0.6	0.95	32,768	32
Open-RS3	RL	DeepSeek-R1-Distill-1.5B	lighteval	0.6	0.95	32,768	32
II-Thought-1.5B-Preview	RL	DeepSeek-R1-Distill-1.5B	evalscope	0.6	0.95	32,768	64
Oat-Zero-1.5B	RL	Qwen2.5-Math-1.5B	custom	0	1	3,000	1
Oat-Zero-7B	RL	Qwen2.5-Math-7B	custom	0	1	3,000	1
STILL-3-1.5B-preview	RL	DeepSeek-R1-Distill-1.5B	custom	0.6	0.95	32,768	5
FastCurl-1.5B-Preview	RL	DeepSeek-R1-Distill-1.5B	verl	0.6	0.95	32,768	16
LIMR	RL	Qwen2.5-Math-7B	custom	0.4	0.95	3,072	4

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Sampling Parameters: To systematically compare the impact of sampling parameters on accuracy, all experiments in this section were performed with a standardized configuration: temperature=0.8, top_p=0.9, and both max_model_len and max_new_tokens set to 32,768 tokens. This context length matches the limits of models such as OpenThinker-7B and S1.1-7B, although certain models (e.g., DeepSeek) support longer sequences of up to 131,072 tokens. We chose this standardized evaluation length to ensure comparability, with a detailed analysis of the influence of completion length presented in Figure 9. Unless otherwise specified, results in this section are averaged over 10 random seeds for AIME’24 and AMC’23, and 3 seeds for MATH500, following the recommendations from Section 3.2.1.

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3.2 Seed Variance in Evaluation

Report issue for preceding elementFigure 2: Accuracy varies significantly across random seeds. We find significantly high Pass@1 variation across 20 different random seeds for nine models on AIME’24, AMC’23, and MATH500. Variance is particularly high on AIME’24 (upto 15%) and AMC’23 (upto 13%) due to the small number of test samples, highlighting instability of single-seed evaluations.Report issue for preceding element

We begin by analyzing the variance induced purely by the random seed used during evaluation—an aspect often neglected in benchmarking practices. While recent work calls for statistical rigor (e.g., using error bars and multiple runs) (Bowyer et al., 2025; Madaan et al.,.

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Key Insight. Pass@1 values show surprisingly high standard deviation—ranging from 5 to 15 percentage points across seeds. This issue is particularly severe for AIME’24 and AMC’23, which have only 30 and 40 test samples respectively. A change in just one question shifts Pass@1 by 2.5–3.3 percentage points.

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Takeaway 1  Single-seed evaluations on small datasets are highly unstable. Accurate reporting requires averaging over multiple seeds.Report issue for preceding element

Takeaway 2  Small datasets such as AIME24 (30 samples) make model comparisons unreliable, as solving just one extra question already shifts pass@1 by  3%. Variance from sampling parameters or random seeds can easily cause fluctuations of 1–2 correct answers, leading to unstable rankings – especially when models cluster around 30% performance.Report issue for preceding element

3.2.1 Can Bootstrapping Improve Mean Estimates?

Report issue for preceding elementFigure 3: Bootstrapped seed averaging is reliable only beyond a threshold. We plot the variance of Mean Pass@1 scores on AIME’24 when averaging over K=1𝐾1K=1italic_K = 1 to K=10𝐾10K=10italic_K = 10 seed runs, finding that the variance is extremely high for small K𝐾Kitalic_K and significantly reduced by K=10𝐾10K=10italic_K = 10. This suggests that using multi-seed evaluations (K≥10𝐾10K\geq 10italic_K ≥ 10) would yield more stable estimates. For results on AMC23 and MATH500 see Figures 12 and 13 respectively.Report issue for preceding element

To mitigate high variance, recent work has adopted bootstrapping—averaging multiple evaluation runs to stabilize results. For example, DeepSeek reports Pass@1 over 64 runs, while DeepScaleR uses 16. We study the effectiveness of this approach by bootstrapping estimates for AIME’24 using 1 to 10 evaluation runs. Figure 3 shows that while variance is extreme for K=1𝐾1K=1italic_K = 1 and still large for K=2𝐾2K=2italic_K = 2, it reduces sharply for K≥10𝐾10K\geq 10italic_K ≥ 10. Further analysis of variance across additional datasets is presented Figures 12 and 13.

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Takeaway 3  Bootstrapping over 10 runs substantially stabilizes Pass@1 estimates and should be considered a minimal standard for reliable evaluation.Report issue for preceding element

3.2.2 Variance from Sampling Parameters: Temperature and top-p

Report issue for preceding elementFigure 4: Higher temperatures yield better accuracies. We find across all three datasets, higher temperatures produce better peak accuracy but introduce instability, revealing a tradeoff between performance and reproducibility. Results obtained by varying temperature from 0 to 1 in increments of 0.1, while keeping top_p fixed at 0.9.Report issue for preceding elementFigure 5: Higher top_p values improve performance at no cost to stability. Across all datasets, we find that higher top_p values generally improve performance while preserving similar amounts of variance as lower top_p values. Results were obtained by varying top_p from 0 to 1 in increments of 0.1, while holding the temperature constant at 0.8.Report issue for preceding element

Reducing the temperature or increasing the nucleus sampling parameter (top_p) improves the accuracy of performance estimates without incurring additional computational cost. Figure 4 illustrate the impact of temperature and Figure 5 show that of top_p across multiple models and datasets. Notably, a more reproducible estimate is associated with significant drops in measured performance, highlighting a consistent tradeoff between reproducibility and high performance. We recommend optimizing the temperature for performance, and comparing the best parameter per model.

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Additionally, we investigate the impact of the temperature and top_p hyperparameter as prior works often employ different temperature and top_p settings when comparing the same model. To isolate the impact of varying temperature and top_p, we averaged pass@1 across seeds and compute variation of this estimate across temperature and top_p in a boxplot. Figure 6 and 7 show the performance variation. We see that temperature-induced and top_p-induced fluctuations not only affect performance estimates but also introduce substantial variability in performance itself, which can lead to unfair comparisons when evaluating the same model across different temperatures.

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Figure 6: Accuracies vary significantly across temperature values. Across nine different models and three datasets, we observe consistently large variations in performance (upto 15%) induced by changing the temperature. Results were obtained by varying the temperature from 0 to 1 in increments of 0.1, while holding top_p constant at 0.9.Report issue for preceding elementFigure 7: Accuracies vary significantly across top_p values. Across nine different models and three datasets, we observe consistently large variations in performance (upto 8%) induced by changing the top_p value. Results were obtained by varying top_p from 0 to 1 in increments of 0.1, while holding the temperature constant at 0.8.Report issue for preceding element

Takeaway 4  Temperature and top_p can introduce substantial performance variation—especially on small benchmarks—and should be set to each model’s optimal values to ensure fair and stable evaluation.Report issue for preceding element

3.3 Variance from Hardware and Software Factors

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(a) AIME24. Significant differences are observed in model performance across compute clusters.Report issue for preceding element

(b) AMC23. Similar variability is seen across hardware in AMC23 results.Report issue for preceding element

Figure 8: Performance variation across compute clusters. Accuracy differences emerge when the same models are evaluated across compute clusters for both AIME24 and AMC23 datasets—these large differences in performance also persist when evaluating 7B models.Report issue for preceding element

Performance can also vary due to non-obvious factors like hardware and evaluation framework—yet this is rarely acknowledged. Models are often tested on heterogeneous systems and evaluated using different toolchains.For example, S-1.1 (Muennighoff et al., 2025), the OpenRS model suite uses lighteval(Fourrier et al., 2023) for evaluation.

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Hardware Variation. We evaluated the same model across five different compute clusters, each with varying GPU types and memory configurations. As shown in Figure 8, performance varied by up to 8% for OpenRS-1.5B and 6% for DeepSeek-R1-Distill-7B on AIME’24, with similar trends observed on AMC’23. While it is known that inference engines such as vLLM can be sensitive to hardware differences (vLLM Contributors, 2024) may introduce non-determinism—our results demonstrate that these effects can measurably impact benchmark accuracy, even when averaging over multiple seeds.

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Evaluation across different Python frameworks. Evaluation results can vary based on the framework used, due to differences in prompt templates, inference engines (e.g., vLLM (Kwon et al., 2023), evalchemy(Guha et al., 2024) and evalscope( [Alibaba ModelScope Community,](https://arxiv.org/html/2504.07086v1#bib.bib5 “”)).

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To assess this impact, we compare lighteval and evalchemy, keeping all other variables fixed: model, dataset, hardware, decoding parameters, and random seeds (3 per model). For a fair comparison, we evaluated two models, DeepSeek-R1-Distill-1.5B and S1.1-7B, at their default temperature and top_p parameter values on a single GPU. We present results averaged over three seeds for higher robustness. As shown in Table 2, framework-induced differences are generally small (1–2pp) but can still affect model rankings in tightly clustered scenarios.

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Model	lighteval	evalchemy
R1-Distill-1.5B	26.6	26.6
S1.1-7B	22.2	17.7

Table 2: AIME24 across frameworks.Report issue for preceding element

Overall, our findings underscore that significant performance variations can arise solely from differences in hardware and software configurations, emphasizing the need to standardize for reliable evaluations.

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Takeaway 5  Re-running the exact same experimental configurations across compute clusters and evaluation frameworks yields notably different results.Report issue for preceding element

3.4 Effect of Prompt Format and Context Length

Report issue for preceding elementFigure 9: Models are extremely sensitive to output token lengths. We sweep across different max_new_tokens (number of tokens that models are allowed to generate) for DeepScaleR-1.5B and DeepSeek-R1-Distill-1.5B/7B on three datasets and find that they are heavily sensitive to output length limits, with premature truncation degrading the performance.Report issue for preceding element

Maximum Output Tokens. Figure 9 shows that reducing max_new_tokens harms performance—especially on long-form problems. This sensitivity varies by model and dataset. Although reducing this setting lowers cost, it may induce premature stopping, leading to incorrect answers.

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Figure 10: Using no prompt templates yields worse performance. We compare Pass@1 scores across three prompt formats: (1) math-specific prompt with chat template, (2) default chat template only, and (3) no template. Instruction-tuned models perform best with structured prompts and templates; omitting templates leads to consistent performance drops.Report issue for preceding element

Prompt Format. Prompt formatting has a measurable impact on accuracy. As shown in Figure 10, models perform best when using math-specific prompts and their native chat templates. Omitting templates leads to performance drops, particularly for instruction-tuned models. We compare accuracy under three different prompt settings (see Table 5): (1) a math-specific prompt formatted using the model’s chat template, (2) only the model’s chat template with no additional prompt, and (3) no template at all, i.e., the question without any special tokens or instructions. Interestingly, while base models like Qwen2.5-Math may benefit from prompt-free setups (Liu et al., [2025b](https://arxiv.org/html/2504.07086v1#bib.bib65 “”)), instruction-tuned models rely heavily on format alignment. Thus, maintaining consistent and format-aware prompting is essential for maximizing instruction-tuned model performance.

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Takeaway 6  It is critical to use large generation context lengths to avoid output truncation which can degrade performance; further, using correct prompt formats and chat templates is important for extracting best model performance.Report issue for preceding element

4 Way Forward: Standardization in Evaluations

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In this section, we standardize evaluation frameworks, propose best practices, and comprehensively evaluate existing methods.

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4.1 Recommendations: Which practices to adopt?

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We propose a set of best practices informed by our experiments and guided with current research insights:

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• •

Hardware and Software Stack Standardization: To promote reproducibility and facilitate future work, we release all code within a Docker container, along with step-by-step instructions for running experiments on Runpod’s publicly accessible, on-demand GPU instances. This setup allows any researcher to replicate and extend our results under identical conditions.

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• •

Variance Estimates: For small benchmarks (e.g., AIME’24), run evaluations with at least ten random seeds. Report the mean and standard deviation to quantify uncertainty and assess the statistical significance of performance differences.

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• •

Model-Specific Hyperparameter Optimization: Tune hyperparameters (such as temperature and top_p) separately for each model, then fix them across tasks to ensure consistency and fair comparisons.

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• •

Context Length and Prompt Template Selection: Ensure the context length is sufficiently large—especially for models with long reasoning chains—to avoid premature truncation and under-reported accuracy. For instruction-tuned models, always use the appropriate chat template to match the expected input format.

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• •

Robust Answer Matching: We strongly recommend using a resilient answer extraction pipeline that handles parsing issues and evaluates expression equivalence, rather than relying on exact string matching. This reduces the likelihood of spurious gains from formatting artifacts.

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• •

Transparent Evaluation Protocols: We recommend to release code, prompts, and model outputs, and clearly document the evaluation stack. Report uncertainties (e.g., via standard deviations) and include both quantitative and qualitative analyses to enable thorough and reproducible comparisons.

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4.2 Standardization Procedure

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We adopt a largely consistent experimental setup with prior work, with the key difference being our use of publicly accessible cloud instances from Runpod222 https://www.runpod.io/pricing across six benchmarks: AIME’24 ( AI-MO,), AMC’23 (Knovel Engineering, 2025), Minerva (Lewkowycz et al., 2022). All experiments are conducted using the LightEval framework (Fourrier et al., [2023](https://arxiv.org/html/2504.07086v1#bib.bib29 “”)) (0.8.1) with a vLLM backend, repeated across ten random seeds for AIME’24, AIME’25, AMC’23 and three random seeds for the rest. Depending on the base model architecture, we set the maximum number of new tokens (e.g., 4096 for QwenMath-based models), apply optimal hyperparameters, and use the appropriate chat template. LightEval’s LaTeX-based answer extraction and evaluation pipeline ensures reliable and consistent result parsing and correctness matching, similar to math-verify.

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4.3 A Sober Look: Results

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Model	AIME’24	AIME’25	AMC’23	MATH500	Minerva	Olympiad
Based on: Deepseek R1 Distill Qwen 1.5B (RL)
R1-Distill (DeepSeek-AI, [2025](https://arxiv.org/html/2504.07086v1#bib.bib23 “”))	28.7±plus-or-minus\pm±4.8	22.3±plus-or-minus\pm±5.2	71.5±plus-or-minus\pm±3.9	84.9±plus-or-minus\pm±0.3	30.5±plus-or-minus\pm±1.0	52.4±plus-or-minus\pm±0.4
L1-Exact (Aggarwal & Welleck, [2025](https://arxiv.org/html/2504.07086v1#bib.bib2 “”))	24.4±plus-or-minus\pm±3.3	22.3±plus-or-minus\pm±4.2	70.5±plus-or-minus\pm±3.7	86.6±plus-or-minus\pm±0.8	31.5±plus-or-minus\pm±1.7	52.5±plus-or-minus\pm±1.3
L1-Max (Aggarwal & Welleck, [2025](https://arxiv.org/html/2504.07086v1#bib.bib2 “”))	27.7±plus-or-minus\pm±4.2	21.0±plus-or-minus\pm±5.0	73.2±plus-or-minus\pm±6.0	84.7±plus-or-minus\pm±0.1	33.3±plus-or-minus\pm±0.9	52.3±plus-or-minus\pm±0.6
Open-RS1 (Dang & Ngo, [2025](https://arxiv.org/html/2504.07086v1#bib.bib20 “”))	28.9±plus-or-minus\pm±6.0	21.3±plus-or-minus\pm±4.2	75.0±plus-or-minus\pm±3.3	85.1±plus-or-minus\pm±0.8	30.4±plus-or-minus\pm±0.2	53.2±plus-or-minus\pm±1.9
Open-RS2 (Dang & Ngo, [2025](https://arxiv.org/html/2504.07086v1#bib.bib20 “”))	31.3±plus-or-minus\pm±7.7	22.7±plus-or-minus\pm±5.6	73.0±plus-or-minus\pm±5.7	84.1±plus-or-minus\pm±0.2	29.2±plus-or-minus\pm±1.1	53.7±plus-or-minus\pm±0.6
Open-RS3 (Dang & Ngo, [2025](https://arxiv.org/html/2504.07086v1#bib.bib20 “”))	29.7±plus-or-minus\pm±4.6	24.7±plus-or-minus\pm±6.5	69.2±plus-or-minus\pm±5.5	84.2±plus-or-minus\pm±1.1	28.6±plus-or-minus\pm±2.3	51.8±plus-or-minus\pm±0.8
STILL-3 (Min et al., [2024](https://arxiv.org/html/2504.07086v1#bib.bib76 “”))	34.7±plus-or-minus\pm±5.5	24.0±plus-or-minus\pm±6.4	72.5±plus-or-minus\pm±5.4	86.6±plus-or-minus\pm±1.9	30.0±plus-or-minus\pm±0.6	53.9±plus-or-minus\pm±1.5
II-Thought (Intelligent Internet, [2025](https://arxiv.org/html/2504.07086v1#bib.bib44 “”))	32.0±plus-or-minus\pm±5.9	24.0±plus-or-minus\pm±4.1	79.5±plus-or-minus\pm±5.1	86.6±plus-or-minus\pm±0.6	31.7±plus-or-minus\pm±0.6	54.9±plus-or-minus\pm±0.4
FastCuRL (Song et al., [2025](https://arxiv.org/html/2504.07086v1#bib.bib99 “”))	36.3±plus-or-minus\pm±4.3	27.0±plus-or-minus\pm±3.7	78.8±plus-or-minus\pm±4.1	87.9±plus-or-minus\pm±1.2	30.8±plus-or-minus\pm±1.4	56.5±plus-or-minus\pm±0.6
DeepScaleR (Luo et al., [2025](https://arxiv.org/html/2504.07086v1#bib.bib67 “”))	37.0±plus-or-minus\pm±6.6	30.3±plus-or-minus\pm±4.3	76.2±plus-or-minus\pm±4.6	87.8±plus-or-minus\pm±1.0	31.0±plus-or-minus\pm±1.5	55.5±plus-or-minus\pm±1.1
Based on: Deepseek R1 Distill Qwen 7B (RL)
R1-Distill (DeepSeek-AI, [2025](https://arxiv.org/html/2504.07086v1#bib.bib23 “”))	52.3±plus-or-minus\pm±6.3	39.0±plus-or-minus\pm±5.9	91.5±plus-or-minus\pm±2.7	94.1±plus-or-minus\pm±0.3	40.1±plus-or-minus\pm±0.4	67.3±plus-or-minus\pm±0.1
Light-R1 (Wen et al., [2025a](https://arxiv.org/html/2504.07086v1#bib.bib109 “”))	53.0±plus-or-minus\pm±4.8	41.0±plus-or-minus\pm±3.5	90.0±plus-or-minus\pm±3.1	93.5±plus-or-minus\pm±0.5	41.3±plus-or-minus\pm±1.3	68.0±plus-or-minus\pm±1.2
Based on: Qwen2.5 Math 1.5B (RL)
Math (Base) (Yang et al., [2024b](https://arxiv.org/html/2504.07086v1#bib.bib115 “”))	11.3±plus-or-minus\pm±3.6	5.7±plus-or-minus\pm±2.7	44.0±plus-or-minus\pm±4.9	51.7±plus-or-minus\pm±5.5	11.3±plus-or-minus\pm±2.2	26.0±plus-or-minus\pm±0.6
Oat-Zero (Liu et al., [2025a](https://arxiv.org/html/2504.07086v1#bib.bib64 “”))	16.0±plus-or-minus\pm±3.2	6.7±plus-or-minus\pm±3.4	52.5±plus-or-minus\pm±2.9	73.5±plus-or-minus\pm±1.7	26.3±plus-or-minus\pm±0.8	37.2±plus-or-minus\pm±1.3
Math (Instruct) (Yang et al., [2024b](https://arxiv.org/html/2504.07086v1#bib.bib115 “”))	12.0±plus-or-minus\pm±1.7	11.7±plus-or-minus\pm±5.7	54.8±plus-or-minus\pm±5.3	74.7±plus-or-minus\pm±0.5	26.7±plus-or-minus\pm±1.8	37.9±plus-or-minus\pm±0.2
Based on: Qwen2.5 Math 7B (RL)
Math (Base) (Yang et al., [2024b](https://arxiv.org/html/2504.07086v1#bib.bib115 “”))	20.7±plus-or-minus\pm±3.8	8.7±plus-or-minus\pm±3.9	56.2±plus-or-minus\pm±5.7	64.3±plus-or-minus\pm±0.5	17.3±plus-or-minus\pm±1.9	29.0±plus-or-minus\pm±0.5
SimpleRL-Zoo (Zeng et al., [2025b](https://arxiv.org/html/2504.07086v1#bib.bib121 “”))	22.7±plus-or-minus\pm±5.2	10.7±plus-or-minus\pm±3.4	62.2±plus-or-minus\pm±3.6	76.9±plus-or-minus\pm±1.8	30.1±plus-or-minus\pm±2.8	39.3±plus-or-minus\pm±0.6
LIMR (Li et al., [2025a](https://arxiv.org/html/2504.07086v1#bib.bib54 “”))	30.7±plus-or-minus\pm±3.2	7.8±plus-or-minus\pm±3.3	62.2±plus-or-minus\pm±3.4	76.5±plus-or-minus\pm±0.4	34.9±plus-or-minus\pm±1.3	39.3±plus-or-minus\pm±0.9
Oat-Zero (Liu et al., [2025a](https://arxiv.org/html/2504.07086v1#bib.bib64 “”))	28.0±plus-or-minus\pm±3.1	8.8±plus-or-minus\pm±2.5	66.2±plus-or-minus\pm±3.6	79.4±plus-or-minus\pm±0.3	34.4±plus-or-minus\pm±1.4	43.8±plus-or-minus\pm±1.1
Math (Instruct) (Yang et al., [2024b](https://arxiv.org/html/2504.07086v1#bib.bib115 “”))	15.7±plus-or-minus\pm±3.9	10.7±plus-or-minus\pm±3.8	67.0±plus-or-minus\pm±3.9	82.9±plus-or-minus\pm±0.1	35.0±plus-or-minus\pm±0.6	41.3±plus-or-minus\pm±0.9
Based on: Qwen2.5 1.5B (RL)
Qwen (Base) (Yang et al., [2024a](https://arxiv.org/html/2504.07086v1#bib.bib114 “”))	0.0±plus-or-minus\pm±0.0	0.0±plus-or-minus\pm±0.0	2.5±plus-or-minus\pm±2.5	3.3±plus-or-minus\pm±1.5	1.8±plus-or-minus\pm±0.4	1.5±plus-or-minus\pm±0.5
SimpleRL-Zoo (Zeng et al., [2025b](https://arxiv.org/html/2504.07086v1#bib.bib121 “”))	0.3±plus-or-minus\pm±1.1	0.3±plus-or-minus\pm±1.1	13.2±plus-or-minus\pm±4.7	12.0±plus-or-minus\pm±6.5	4.0±plus-or-minus\pm±2.4	4.2±plus-or-minus\pm±2.0
Qwen (Instruct) (Yang et al., [2024a](https://arxiv.org/html/2504.07086v1#bib.bib114 “”))	1.3±plus-or-minus\pm±1.7	0.7±plus-or-minus\pm±1.4	26.2±plus-or-minus\pm±4.8	57.5±plus-or-minus\pm±1.1	19.4±plus-or-minus\pm±1.3	20.3±plus-or-minus\pm±1.1
Based on: Qwen2.5 7B (RL)
Qwen (Base) (Yang et al., [2024a](https://arxiv.org/html/2504.07086v1#bib.bib114 “”))	3.3±plus-or-minus\pm±3.3	0.0±plus-or-minus\pm±0.0	30.0±plus-or-minus\pm±9.0	64.6±plus-or-minus\pm±1.0	25.7±plus-or-minus\pm±0.9	30.1±plus-or-minus\pm±1.2
SimpleRL-Zoo (Zeng et al., [2025b](https://arxiv.org/html/2504.07086v1#bib.bib121 “”))	14.0±plus-or-minus\pm±2.1	4.3±plus-or-minus\pm±2.7	58.0±plus-or-minus\pm±1.6	77.9±plus-or-minus\pm±0.8	33.0±plus-or-minus\pm±0.2	39.0±plus-or-minus\pm±0.1
Open Reasoner Zero (Hu et al., [2025](https://arxiv.org/html/2504.07086v1#bib.bib40 “”))	19.7±plus-or-minus\pm±2.9	15.7±plus-or-minus\pm±2.7	59.5±plus-or-minus\pm±4.5	83.9±plus-or-minus\pm±1.1	31.6±plus-or-minus\pm±1.3	47.6±plus-or-minus\pm±1.7
Qwen (Instruct)	12.3±plus-or-minus\pm±3.2	7.3±plus-or-minus\pm±3.4	52.8±plus-or-minus\pm±4.8	77.1±plus-or-minus\pm±1.2	34.9±plus-or-minus\pm±1.0	38.7±plus-or-minus\pm±1.0
Based on: Qwen2.5 7B (SFT)
Qwen (Instruct) (Yang et al., [2024a](https://arxiv.org/html/2504.07086v1#bib.bib114 “”))	12.3±plus-or-minus\pm±3.2	7.3±plus-or-minus\pm±3.4	52.8±plus-or-minus\pm±4.8	77.1±plus-or-minus\pm±1.2	34.9±plus-or-minus\pm±1.0	38.7±plus-or-minus\pm±1.0
Eurus2 Prime (Cui et al., [2025](https://arxiv.org/html/2504.07086v1#bib.bib19 “”))	17.8±plus-or-minus\pm±2.2	14.0±plus-or-minus\pm±1.7	63.0±plus-or-minus\pm±3.9	80.1±plus-or-minus\pm±0.1	37.5±plus-or-minus\pm±1.0	43.9±plus-or-minus\pm±0.3
s1.1 (Muennighoff et al., [2025](https://arxiv.org/html/2504.07086v1#bib.bib78 “”))	19.0±plus-or-minus\pm±3.2	21.0±plus-or-minus\pm±5.5	59.5±plus-or-minus\pm±3.7	80.8±plus-or-minus\pm±0.6	37.5±plus-or-minus\pm±1.1	48.2±plus-or-minus\pm±1.4
Bespoke Stratos (Bespoke Labs, [2024](https://arxiv.org/html/2504.07086v1#bib.bib10 “”))	20.3±plus-or-minus\pm±4.3	18.0±plus-or-minus\pm±4.8	60.2±plus-or-minus\pm±4.9	84.7±plus-or-minus\pm±0.5	39.1±plus-or-minus\pm±1.3	51.9±plus-or-minus\pm±1.1
OpenThinker (Team, [2025](https://arxiv.org/html/2504.07086v1#bib.bib102 “”))	30.5±plus-or-minus\pm±6.2	26.0±plus-or-minus\pm±4.4	71.4±plus-or-minus\pm±3.9	88.3±plus-or-minus\pm±1.4	37.9±plus-or-minus\pm±3.8	55.6±plus-or-minus\pm±1.4
OpenR1 (Face, [2025](https://arxiv.org/html/2504.07086v1#bib.bib27 “”))	48.3±plus-or-minus\pm±8.9	35.5±plus-or-minus\pm±4.2	86.0±plus-or-minus\pm±4.5	–	–	–
OpenThinker2 (Team, [2025](https://arxiv.org/html/2504.07086v1#bib.bib102 “”))	53.0±plus-or-minus\pm±4.6	41.0±plus-or-minus\pm±5.0	87.0±plus-or-minus\pm±3.5	81.6±plus-or-minus\pm±0.7	33.9±plus-or-minus\pm±0.2	46.9±plus-or-minus\pm±1.3

Table 3: A Standardized and Sober Compilation of LM-Reasoning Results. We report Pass@1 accuracy (mean ±plus-or-minus\pm± std) of all models across six math reasoning benchmarks under a standardized evaluation setup—results are averaged over ten seeds for AIME and AMC, and three seeds for the rest, using the LightEval framework with best hyperparameters tuned per method, 32,768 context lengths for all except 4,096 for Math models, and appropriate prompt templates. RL- and SFT-based variants are evaluated relative to their respective base or instruction-tuned models. Main takeaways—(1) RL-trained methods do not yield meaningful performance gains, (2) SFT on reasoning traces yields significant generalization.Report issue for preceding element

We present experimental results in Table 3, and analyze different aspects of the results.

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RL-training on R1-Distill We evaluated several reinforcement learning (RL) approaches (e.g., GRPO) using the DeepSeek R1-Distill-1.5B model. We first observe that none of the L1 models (Aggarwal & Welleck, 2025) reported strong gains (10–15%) on AIME, AMC, and OlympiadBench. However, our replication showed no statistically significant improvements over the R1 - Distill baseline. Same case held for Still-3 and Light-R1 model, which showed no significant improvement over the R1-Distill baseline. II-Thought and FastCurl yield modest improvements across benchmarks, especially over AIME’24 but the observed gains did not carry over significantly to AIME’25 indicating overfitting to existing benchmarks. Only DeepscaleR demonstrated robust, significant improvements across benchmarks.

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Takeaway 1  Most RL-trained variants of the DeepSeek R1-Distill model do not yield meaningful performance improvements (except DeepscaleR), suggesting that a reliable and scalable RL training recipes are still lacking.Report issue for preceding element

RL Training on Qwen2.5 Math and Base Models: We next analyze RL training applied to the Qwen2.5 Base and Qwen2.5 Math Base models, a trend trying to replicate gains by Deepseek-R1 Zero. Unlike the R1-Distill results, RL training with Oat-Zero, LIMR, and SimpleRL-Zoo consistently produced statistically significant gains over the base model, especially across Math500, Minerva and OlympiadBench benchmarks. This indicates that RL-based approaches can indeed offer substantial improvements given a base model instead of a distilled R1 model. However, these gains remained smaller than those achieved via instruction tuning in the original Qwen papers, suggesting that instruction tuning alone may be sufficient to far surpass current gains from RL methods in this setting. We also observed that the improvements on AIME’24 were also significant, but did not carry over to AIME’25 indicating a troubling overfitting trend. Notably, Open Reasoner-Zero-7B was the only RL-trained model to consistently outperform the instruct-tuned baseline by large margins across all benchmarks.

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Takeaway 2  While RL-trained methods can often substantially improve base model performance, instruction tuning remains superior (except Open Reasoner Zero), suggesting again that a reliable and scalable RL training recipes are still lacking.Report issue for preceding element

Effectiveness of Supervised Finetuning. We assessed supervised finetuning methods like s1.1, Eurus2 Prime, Bespoke Stratos, OpenR1 and OpenThinker models, which further refine instruction-tuned models using reasoning traces. Supervised methods consistently outperformed the instruct-tuned baseline across all benchmarks (even Minerva) and generalized comparatively well to AIME’25. The performance improvements from OpenThinker were especially notable. These results underscore the maturity and effectiveness of SFT when training recipes are scaled to large datasets.

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Takeaway 3  Supervised finetuning on reasoning traces from larger models yields significant, generalizable gains across benchmarks with progress over time successfully replicated — highlighting its robustness and maturity as a training paradigm.Report issue for preceding element

Overfitting and Generalization We now examine the overfitting by comparing performance on AIME’24 versus the more challenging AIME’25. RL-trained models showed a pronounced performance drop between the two, indicating overfitting to the training distribution. In contrast, supervised fine-tuning (SFT) models maintained consistent improvements, suggesting better generalization. Openthinker2 showed significant degradation compared to Openthinker across benchmarks not provided in their blogpost, indicating overfitting via data-curation. This highlights a gap in current evaluation protocols, and a need to assess out-of-distribution generalization for reasoning models.

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Takeaway 4  Current RL-based approaches are very susceptible to overfitting, emphasizing the need for more rigorous out-of-distribution benchmarks. By comparison, SFT models exhibit stronger generalization and resilience.Report issue for preceding element

4.4 Do Discovered Phenomena Replicate? A Detailed Analysis.

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We further investigate two recently noted phenomena to see if they replicate in our experiments: (1) how response length correlates with performance, and (2) the decline in response diversity following reasoning-focused training.

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4.4.1 Are Incorrect Responses Longer?

Report issue for preceding elementFigure 11: Response Length vs. Accuracy. Histogram of correct vs. incorrect responses by response length, averaged over random seeds across AIME24, AIME25, AMC23, MATH500, Minerva and OlympiadBench benchmarks. Longer outputs tend to be more error-prone, even in complete responses not close to the maximum sequence length.Report issue for preceding element

Recent research (Wang et al., [2025](https://arxiv.org/html/2504.07086v1#bib.bib108 “”)) suggests that incorrect answers often have disproportionately long reasoning chains. We first verify whether this finding holds in our setting, and then we explore possible explanations behind the observed variations.

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Do longer responses indicate a higher likelihood of an incorrect answer? We compare the distribution of response lengths for correct and incorrect answers across 6 datasets (AIME24, AIME25, AMC23, MATH500, Minerva and OlympiadBench) averaged across random seeds for each model. Figure 11 shows histograms of the average number of responses per seed, binned by response length. A clear trend emerges: shorter responses are significantly more likely to be correct, while longer responses become progressively more error-prone. This pattern is consistent across all seeds and is especially pronounced for responses exceeding 10,000 tokens. We now address two questions:

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Q1. Does this pattern hold for both RL- and SFT-trained models?

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Yes. We find the trend is consistent across both RL- and SFT-trained models (additional figures provided in Appendix figures 17 and  18 ). We consistently observe that the effect is more pronounced in RL-trained models (displayed on the left) than in SFT-trained models (displayed on the right). As detailed in the Appendix, both the Qwen 2.5 Math base exhibit a slight shift in length, though this shift is notably more evident in R1-distill and subsequent RL-trained models.

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Q2. Is this primarily because of truncated or incomplete responses?

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Although responses nearing the 32,000-token limit are almost always incorrect (due to limited context-length), this trend persists even for complete responses which are shorter– Longer responses are associated with a higher likelihood of being incorrect.

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Takeaway 5  Longer responses correlate with a greater chance of error, response length is a practical heuristic for consensus@k, identifying low-confidence or failed generations.Report issue for preceding element

4.4.2 Is There Diversity Collapse in Reasoning Training?

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		AIME’24	AIME’25	AMC’23
Model	Baseline	δ⁢@⁢1𝛿@1\delta@1italic_δ @ 1	δ⁢@⁢5𝛿@5\delta@5italic_δ @ 5	δ⁢@⁢10𝛿@10\delta@10italic_δ @ 10	δ⁢@⁢1𝛿@1\delta@1italic_δ @ 1	δ⁢@⁢5𝛿@5\delta@5italic_δ @ 5	δ⁢@⁢10𝛿@10\delta@10italic_δ @ 10	δ⁢@⁢1𝛿@1\delta@1italic_δ @ 1	δ⁢@⁢5𝛿@5\delta@5italic_δ @ 5	δ⁢@⁢10𝛿@10\delta@10italic_δ @ 10
Open-RS3	R1-Distill	+1.51.5{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+1.5}+ 1.5	-0.6	+1.5	-1.0	+0.4	+1.4	-0.9	-0.2	+0.4
DeepScaleR	R1-Distill	+9.09.0{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+9.0}+ 9.0	+0.6	+0.2	+4.44.4{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+4.4}+ 4.4	+3.6	+2.2	+6.16.1{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+6.1}+ 6.1	-1.8	-1.7
S1.1-7B	Qwen-Instruct	+5.75.7{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+5.7}+ 5.7	+10.9	+13.5	+11.911.9{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+11.9}+ 11.9	+10.5	+10.4	+5.85.8{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+5.8}+ 5.8	+9.6	+9.7
II-Thought	R1-Distill	+2.52.5{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+2.5}+ 2.5	-3.5	-3.6	+0.80.8{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+0.8}+ 0.8	+0.5	+1.2	+6.36.3{\color[rgb]{0,0.5,0}\definecolor[named]{pgfstrokecolor}{rgb}{0,0.5,0}+6.3}+ 6.3	+0.7	+0.2

Table 4: RL-trained models do not show a diversity collapse ( [Dang et al.,](https://arxiv.org/html/2504.07086v1#bib.bib21 “”)). We report the delta between Pass@k of RL-trained models and their corresponding baselines. Unlike reported in prior work, we observe no significant phenomenon of diversity collapse: δ⁢@⁢5𝛿@5\delta@5italic_δ @ 5 and δ⁢@⁢10𝛿@10\delta@10italic_δ @ 10 are largely positive, and are negative at similar rates as δ⁢@⁢1𝛿@1\delta@1italic_δ @ 1.Report issue for preceding element

[Dang et al.](https://arxiv.org/html/2504.07086v1#bib.bib21 “”) has reported a counterintuitive phenomenon in reasoning models: improvements in Pass@1 achieved through supervised fine-tuning or RL can reduce Pass@k performance due to diminished output diversity—a phenomenon termed diversity collapse. Theoretical analyses attribute this collapse to the model concentrating too much probability mass on a single reasoning path, while current decoding strategies fail to recover the lost diversity.

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To examine these claims, we compare the Pass@k performance (for k∈1,5,10𝑘1510k\in{1,5,10}italic_k ∈ 1 , 5 , 10) of RL-trained models against their corresponding base models (e.g., DeepSeek-R1-Distill-Qwen-1.5B) across all datasets. Table 4 shows the delta in Pass@k relative to each method’s base model.

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Findings. We do not observe a consistent diversity collapse. Gains in Pass@1 generally come with improvements in Pass@k, though the magnitude of these gains varies. When Pass@k performance does drop, it does so alongside (rather than independently of) occasional declines in Pass@1, providing no support for the diversity collapse hypothesis.

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Takeaway 6  Standard decoding strategies appear sufficient to capture the model’s full distribution over valid reasoning paths, counter to the diversity collapse hypothesis.Report issue for preceding element

5 Conclusion

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Our study shows that much of the perceived progress in LLM-based reasoning, particularly in mathematical benchmarks, rests on unstable and often non-reproducible foundations. We find that minor differences in sampling parameters, prompt formatting, hardware, and software configurations can lead to major shifts in reported performance—casting doubt on many recent empirical claims. Reinforcement learning methods, while promising in theory, offer at best modest gains in practice and are prone to overfitting, especially on small benchmarks like AIME’24. In contrast, supervised finetuning continues to deliver consistent, generalizable improvements across a wide range of benchmarks and model sizes.

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To address these challenges, we advocate for standardized, transparent evaluation protocols. Our open-sourced framework, complete with Dockerized environments, seed-averaged metrics, and robust answer matching, provides reproducible foundations for future research. We hope this work shifts the focus from leaderboard chasing to methodological rigor—ensuring that future claims of progress in reasoning are both meaningful and measurable.

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Author Contributions

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Andreas, Vishaal and Ameya conceived the project. Andreas and Hardik co-led the experiments, with Vishaal and Ameya advising the experimental design. The manuscript was written by Andreas, Hardik, Vishaal and Ameya. Matthias and Samuel provided helpful feedback and advice throughout the project.

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Acknowledgments

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The authors would like to thank (in alphabetical order): Matteo Farina, Shyamgopal Karthik, Nikhil Parthasarathy, Shiven Sinha, Joschka Strüber, Thaddäus Wiedemer for helpful feedback on the draft. AH acknowledges funding by the Federal Ministry of Education and Research (BMBF), FKZ: 01IS24079A. HB has received funding from the Digital Europe Programme under grant agreement No 101195233 (OpenEuroLLM). AH, HB and VU thank the International Max Planck Research School for Intelligent Systems (IMPRS-IS) for support. VU also thanks the European Laboratory for Learning and Intelligent Systems (ELLIS) PhD program for support. VU was supported by a Google PhD Fellowship in Machine Intelligence. AP and MB acknowledge financial support by the Federal Ministry of Education and Research (BMBF), FKZ: 011524085B and Open Philanthropy Foundation funded by the Good Ventures Foundation. This work was supported by the Digital Europe Programme under grant agreement No 101195233 (OpenEuroLLM).

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References

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• Agarwal et al. (2021)↑ Rishabh Agarwal, Max Schwarzer, Pablo Samuel Castro, Aaron C Courville, and Marc Bellemare.

Deep reinforcement learning at the edge of the statistical precipice.

Advances in neural information processing systems, 34:29304–29320, 2021.

• Aggarwal & Welleck (2025)↑ Pranjal Aggarwal and Sean Welleck.

L1: Controlling how long a reasoning model thinks with reinforcement learning.

arXiv preprint arXiv:2503.04697, 2025.

• (3)↑ AI-MO.

AIMO Validation AIME Dataset.

• AI-MO (2024)↑ AI-MO.

AIMO Validation AMC Dataset.

[https://huggingface.co/datasets/AI-MO/aimo-validation-amc](https://huggingface.co/datasets/AI-MO/aimo-validation-amc “”), 2024.

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• (5)↑ Alibaba ModelScope Community.

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• Andrychowicz et al. (2020)↑ Marcin Andrychowicz, Anton Raichuk, Piotr Stańczyk, Manu Orsini, Sertan Girgin, Raphael Marinier, Léonard Hussenot, Matthieu Geist, Olivier Pietquin, Marcin Michalski, et al.

What matters in on-policy reinforcement learning? a large-scale empirical study.

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• Anthropic (2025)↑ Anthropic.

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• Balduzzi et al. (2018)↑ David Balduzzi, Karl Tuyls, Julien Perolat, and Thore Graepel.

Re-evaluating evaluation.

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• Bespoke Labs (2024)↑ Bespoke Labs.

Bespoke-stratos-7b.

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Lessons from the trenches on reproducible evaluation of language models.

arXiv preprint arXiv:2405.14782, 2024.

• Bowyer et al. (2025)↑ Sam Bowyer, Laurence Aitchison, and Desi R Ivanova.

Position: Don’t use the CLT in LLM evals with fewer than a few hundred datapoints.

arXiv preprint arXiv:2503.01747, 2025.

• Cai (2025)↑ Xin Cai.

One framework to rule them all: Unifying rl-based and rl-free methods in rlhf.

arXiv preprint arXiv:2503.19523, 2025.

• Cawley (2011)↑ Gavin C Cawley.

Baseline methods for active learning.

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• Cawley & Talbot (2010)↑ Gavin C Cawley and Nicola LC Talbot.

On over-fitting in model selection and subsequent selection bias in performance evaluation.

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• Chan et al. (2019)↑ Stephanie CY Chan, Samuel Fishman, John Canny, Anoop Korattikara, and Sergio Guadarrama.

Measuring the reliability of reinforcement learning algorithms.

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• Colas et al. (2018)↑ Cédric Colas, Olivier Sigaud, and Pierre-Yves Oudeyer.

How many random seeds? statistical power analysis in deep reinforcement learning experiments.

arXiv preprint arXiv:1806.08295, 2018.

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• Dang & Ngo (2025)↑ Quy-Anh Dang and Chris Ngo.

Reinforcement learning for reasoning in small llms: What works and what doesn’t, 2025.

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• (21)↑ Xingyu Dang, Christina Baek, J Zico Kolter, and Aditi Raghunathan.

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• DeepMind (2025)↑ Google DeepMind.

Gemini 2.5: Our most intelligent ai model, 2025.

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• DeepSeek-AI (2025)↑ DeepSeek-AI.

DeepSeek-R1: Incentivizing Reasoning Capability in LLMs via Reinforcement Learning, 2025.

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• Dominguez-Olmedo et al. (2024)↑ Ricardo Dominguez-Olmedo, Florian E Dorner, and Moritz Hardt.

Training on the test task confounds evaluation and emergence.

arXiv preprint arXiv:2407.07890, 2024.

• Face (2025)↑ Hugging Face.

Open r1: A fully open reproduction of deepseek-r1, January 2025.

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• Feng et al. (2025)↑ Kaituo Feng, Kaixiong Gong, Bohao Li, Zonghao Guo, Yibing Wang, Tianshuo Peng, Benyou Wang, and Xiangyu Yue.

Video-r1: Reinforcing video reasoning in mllms.

arXiv preprint arXiv:2503.21776, 2025.

• Fourrier et al. (2023)↑ Clémentine Fourrier, Nathan Habib, Hynek Kydlíček, Thomas Wolf, and Lewis Tunstall.

LightEval: A lightweight framework for LLM evaluation, 2023.

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• Gao et al. (2024a)↑ Jiaxuan Gao, Shusheng Xu, Wenjie Ye, Weilin Liu, Chuyi He, Wei Fu, Zhiyu Mei, Guangju Wang, and Yi Wu.

On designing effective rl reward at training time for llm reasoning.

arXiv preprint arXiv:2410.15115, 2024a.

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• Ghosh et al. (2024)↑ Adhiraj Ghosh, Sebastian Dziadzio, Ameya Prabhu, Vishaal Udandarao, Samuel Albanie, and Matthias Bethge.

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arXiv preprint arXiv:2412.06745, 2024.

• Golchin & Surdeanu (2023)↑ Shahriar Golchin and Mihai Surdeanu.

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• He et al. (2024)↑ Chaoqun He, Renjie Luo, Yuzhuo Bai, Shengding Hu, Zhen Leng Thai, Junhao Shen, Jinyi Hu, Xu Han, Yujie Huang, Yuxiang Zhang, Jie Liu, Lei Qi, Zhiyuan Liu, and Maosong Sun.

Olympiadbench: A challenging benchmark for promoting agi with olympiad-level bilingual multimodal scientific problems, 2024.

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• Hu (2025)↑ Jian Hu.

Reinforce++: A simple and efficient approach for aligning large language models.

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• Hu et al. (2025)↑ Jingcheng Hu, Yinmin Zhang, Qi Han, Daxin Jiang, and Heung-Yeung Shum Xiangyu Zhang.

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arXiv preprint arXiv:2503.06749, 2025.

• HuggingFaceH4 (2024)↑ HuggingFaceH4.

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• Intelligent Internet (2025)↑ Intelligent Internet.

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• Jaech et al. (2024)↑ Aaron Jaech, Adam Kalai, Adam Lerer, Adam Richardson, Ahmed El-Kishky, Aiden Low, Alec Helyar, Aleksander Madry, Alex Beutel, Alex Carney, et al.

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arXiv preprint arXiv:2412.16720, 2024.

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• Jordan et al. (2020)↑ Scott Jordan, Yash Chandak, Daniel Cohen, Mengxue Zhang, and Philip Thomas.

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• Jordan et al. (2024)↑ Scott M Jordan, Adam White, Bruno Castro Da Silva, Martha White, and Philip S Thomas.

Position: Benchmarking is limited in reinforcement learning research.

arXiv preprint arXiv:2406.16241, 2024.

• Kandpal et al. (2023)↑ Nikhil Kandpal, Haikang Deng, Adam Roberts, Eric Wallace, and Colin Raffel.

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Vineppo: Unlocking rl potential for llm reasoning through refined credit assignment.

arXiv preprint arXiv:2410.01679, 2024.

• Knovel Engineering (2025)↑ Knovel Engineering.

Amc-23 dataset, 2025.

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Efficient memory management for large language model serving with pagedattention.

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Solving quantitative reasoning problems with language models.

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Are we learning yet? A meta review of evaluation failures across machine learning.

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• Lin (2025)↑ Yen-Ting Lin.

Aime 2025 dataset, 2025.

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Mind with eyes: from language reasoning to multimodal reasoning.

arXiv preprint arXiv:2503.18071, 2025b.

• Lipton & Steinhardt (2019)↑ Zachary C Lipton and Jacob Steinhardt.

Troubling trends in machine learning scholarship: Some ml papers suffer from flaws that could mislead the public and stymie future research.

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• Liu & Zhang (2025)↑ Jiawei Liu and Lingming Zhang.

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Visual-rft: Visual reinforcement fine-tuning.

arXiv preprint arXiv:2503.01785, 2025c.

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DeepScaleR: Surpassing O1-Preview with a 1.5B Model by Scaling RL, 2025.

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Rethinking rl scaling for vision language models: A transparent, from-scratch framework and comprehensive evaluation scheme.

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Eureka: Human-level reward design via coding large language models.

arXiv preprint arXiv:2310.12931, 2023.

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Revisiting the arcade learning environment: Evaluation protocols and open problems for general agents.

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• (72)↑ Lovish Madaan, Aaditya K Singh, Rylan Schaeffer, Andrew Poulton, Sanmi Koyejo, Pontus Stenetorp, Sharan Narang, and Dieuwke Hupkes.

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Mm-eureka: Exploring visual aha moment with rule-based large-scale reinforcement learning.

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• Meta-AI (2025)↑ Meta-AI.

The llama 4 herd: The beginning of a new era of natively multimodal ai innovation, 2025.

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Imitate, explore, and self-improve: A reproduction report on slow-thinking reasoning systems, 2024.

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• Mirzadeh et al. (2024)↑ Iman Mirzadeh, Keivan Alizadeh, Hooman Shahrokhi, Oncel Tuzel, Samy Bengio, and Mehrdad Farajtabar.

Gsm-symbolic: Understanding the limitations of mathematical reasoning in large language models.

arXiv preprint arXiv:2410.05229, 2024.

• Muennighoff et al. (2025)↑ Niklas Muennighoff, Zitong Yang, Weijia Shi, Xiang Lisa Li, Li Fei-Fei, Hannaneh Hajishirzi, Luke Zettlemoyer, Percy Liang, Emmanuel Candès, and Tatsunori Hashimoto.

s1: Simple test-time scaling, 2025.

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• Musgrave et al. (2020)↑ Kevin Musgrave, Serge Belongie, and Ser-Nam Lim.

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• Nezhurina et al. (2024)↑ Marianna Nezhurina, Lucia Cipolina-Kun, Mehdi Cherti, and Jenia Jitsev.

Alice in wonderland: Simple tasks showing complete reasoning breakdown in state-of-the-art large language models.

arXiv preprint arXiv:2406.02061, 2024.

• OpenAI (2025)↑ OpenAI.

OpenAI o3-mini System Card, January 2025.

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Empirical design in reinforcement learning.

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• Peng et al. (2025)↑ Yingzhe Peng, Gongrui Zhang, Miaosen Zhang, Zhiyuan You, Jie Liu, Qipeng Zhu, Kai Yang, Xingzhong Xu, Xin Geng, and Xu Yang.

Lmm-r1: Empowering 3b lmms with strong reasoning abilities through two-stage rule-based rl.

arXiv preprint arXiv:2503.07536, 2025.

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Proof or bluff? evaluating llms on 2025 usa math olympiad.

arXiv preprint arXiv:2503.21934, 2025.

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Gdumb: A simple approach that questions our progress in continual learning.

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• Prabhu et al. (2024a)↑ Ameya Prabhu, Shiven Sinha, Ponnurangam Kumaraguru, Philip HS Torr, Ozan Sener, and Puneet K Dokania.

Randumb: A simple approach that questions the efficacy of continual representation learning.

arXiv e-prints, pp.  arXiv–2402, 2024a.

• Prabhu et al. (2024b)↑ Ameya Prabhu, Vishaal Udandarao, Philip Torr, Matthias Bethge, Adel Bibi, and Samuel Albanie.

Efficient lifelong model evaluation in an era of rapid progress.

arXiv preprint arXiv:2402.19472, 2024b.

• Press et al. (2023)↑ Ori Press, Steffen Schneider, Matthias Kümmerer, and Matthias Bethge.

Rdumb: A simple approach that questions our progress in continual test-time adaptation.

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• PyTorch Contributors (2024)↑ PyTorch Contributors.

Reproducibility — pytorch documentation.

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• Renze (2024)↑ Matthew Renze.

The effect of sampling temperature on problem solving in large language models.

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• Reuel et al. (2024)↑ Anka Reuel, Amelia Hardy, Chandler Smith, Max Lamparth, Malcolm Hardy, and Mykel J Kochenderfer.

BetterBench: Assessing AI Benchmarks, Uncovering Issues, and Establishing Best Practices.

arXiv preprint arXiv:2411.12990, 2024.

• Roberts et al. (2025)↑ Jonathan Roberts, Mohammad Reza Taesiri, Ansh Sharma, Akash Gupta, Samuel Roberts, Ioana Croitoru, Simion-Vlad Bogolin, Jialu Tang, Florian Langer, Vyas Raina, et al.

Zerobench: An impossible visual benchmark for contemporary large multimodal models.

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Appendix A Appendix

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A.1 Bootstrapping Results on Additional Datasets

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To complement our analysis in 3, we present bootstrapped variance results on two additional datasets: AMC’23 and MATH500. As shown in Figures 12 and 13, high variance in Pass@1 persists even when averaging over multiple seeds (K=5𝐾5K=5italic_K = 5), mirroring the trends observed on AIME’24. These results reinforce our conclusion that small benchmark sizes yield unstable estimates and that robust performance reporting requires multiple seed runs.

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Figure 12: Variance of mean Pass@1 on AMC’23. Bootstrapped estimates show substantial variance even with K=5𝐾5K=5italic_K = 5 evaluation runs, highlighting the instability of single-seed evaluations.Report issue for preceding elementFigure 13: Variance of mean Pass@1 on MATH500. Similar to AIME’24 and AMC’23, the estimates remain volatile across seeds. Even K=5𝐾5K=5italic_K = 5 runs do not eliminate variance, underscoring the need for larger K𝐾Kitalic_K.Report issue for preceding element

A.2 Hardware & Software Variations

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In Figure 14, we show that the model performance variation due to hardware configuration is not limited to AIME’24 and AMC’23. Similar discrepancies are observed on MATH500, where different compute clusters yield different accuracy scores—even when model, seeds, and decoding parameters are held constant. This further emphasizes the need for hardware and software standardization when reporting benchmark results.

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Figure 14: Performance variation across compute clusters on MATH500. Differences in GPU type and environment lead to non-trivial shifts in performance, reinforcing the importance of hardware standardization.Report issue for preceding element

A.3 Prompt Variants and Template Settings

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We provide the exact templates used for our three prompt settings in Table 5: Math, Default, and No Template. These formats are based on the DeepSeek tokenizer but adapted for each model’s specific chat template. Our results (in 3.4) indicate that instruction-tuned models are highly sensitive to prompt formatting, with performance degrading significantly when prompts deviate from their training-time structure.

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Prompt	Example
Math	<|begin_of_sentence|><|User|>Solve the following math problem efficiently and clearly. The last line of your response should be of the following format: ’Therefore, the final answer is: $\boxed{ANSWER}$. I hope it is correct’ (without quotes) where ANSWER is just the final number or expression that solves the problem. Think step by step before answering.\n <|Assistant|>\\n{Question}
Default	<|begin_of_sentence|><|User|>{Question} <|Assistant|>\\n
No Template	{Question}

Table 5: Prompt templates used in our evaluation. The inclusion or exclusion of structured prompt tokens significantly impacts performance for instruction-tuned models.Report issue for preceding element

A.4 Effect of Output Length Limits

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We further explore how varying max_new_tokens impacts model accuracy. Figures below compare OpenRS-series models (with 131,072-token context windows) and OpenThinker/S1.1 models (with 32,768-token limits).

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Figure 15 shows that OpenRS models are highly sensitive to this parameter—shortening outputs results in clear accuracy drops. Similarly, Figure 16 reveals the same pattern for OpenThinker-7B and S1.1-7B, despite their smaller context lengths. In both cases, premature truncation leads to incomplete reasoning chains and incorrect answers, confirming the importance of setting appropriate generation limits.

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Figure 15: Impact of max_new_tokens on OpenRS models. Models with long context support (131,072 tokens) experience degraded performance when max_new_tokens is set too low.Report issue for preceding elementFigure 16: Impact of max_new_tokens on OpenThinker and S1.1 models. Despite shorter context limits (32,768 tokens), performance still degrades noticeably when output length is constrained.Report issue for preceding element

A.5 Response Length vs. Accuracy — Per-Model Breakdown

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To supplement the aggregated results shown in Figure 11, we include detailed histograms for each individual model in the appendix. These plots show the distribution of correct and incorrect responses across response lengths, averaged over random seeds. Due to the number of models analyzed, we split the results into two figures for clarity.

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Figures 17 and 18 reveal that the overall trend observed in the main paper holds consistently across nearly all models: incorrect responses tend to be longer than correct ones.

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These results reinforce the idea that excessively long outputs often indicate failure modes such as hallucinated reasoning, verbose overthinking, or degenerate loops. Importantly, this correlation persists well below the maximum sequence length, ruling out truncation as the sole cause.

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Figure 17: Response Length vs. Correctness — Models (1/2). Average number of correct and incorrect responses across response length bins for a subset of models. Longer responses consistently correlate with incorrect predictions.Report issue for preceding elementFigure 18: Response Length vs. Correctness — Models (2/2). Continuation of model-wise response length analysis. The same trend holds across the remaining models, with incorrect answers being disproportionately long.Report issue for preceding element

Across all models, longer responses are a consistent marker of incorrect outputs, making response length a useful signal for detecting low-confidence or erroneous reasoning chains.

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