Base Models Beat Post-Trained Models on pass@K? What the 'Sharpening Tax' Paper Actually Shows (2610.01509)

"Sharpening Tax in Post-Training" (arXiv 2610.01509, submitted 1 October 2026) reports that across 14 base and post-trained model pairs and three agentic benchmarks, the tax is positive at a budget of 128 rollouts in 36 of 42 cases. In plain terms: post-trained models win on one attempt, but a base model with a light harness often solves more distinct tasks when you let it try many times. The authors are mostly at Meta Superintelligence Labs, with co-authors at UW-Madison, NYU and Stanford, and every number below is their own report.

We read: the full paper (arXiv HTML version, main text and appendices), not just the abstract.

What problem does this paper solve?

It tests whether the "sharpening hypothesis" holds for agents, not just for math and code. The hypothesis says RL post-training amplifies behaviours the base model already has, raising single-shot accuracy at the cost of solution coverage.

Earlier evidence for this came mostly from math and coding. The authors argue those domains are a weak test for two reasons: pre-training exposes models heavily to them, and final-answer checks can credit a lucky rollout with flawed reasoning. Agentic tasks, where multi-turn tool use is rare in pre-training data, are a harder case. If post-training must teach new skills anywhere, it should be here.

The prior work they build on includes Yue et al. (arXiv 2504.13837), who found that RLVR improves sampling efficiency but rarely elicits fundamentally new reasoning patterns, and Zhao et al. (arXiv 2504.07912), who trained models from scratch on controlled data mixes to study what RL amplifies.

How does it work?

The method has three parts: a pass@k protocol on open checkpoint pairs, a scalar metric called Sharpening Tax, and a training-time sampler called PTGS.

Setup. The paper uses 14 public pairs such as google/gemma-4-31B vs gemma-4-31B-it, from Gemma-4, Ministral-3, Qwen2.5 and Qwen3.5, ranging from 3B to 35B parameters. Each task gets up to 128 rollouts. Three benchmarks are used: the multi-turn base category of BFCL v4, WebShop and ACEBench. Success is decided by environment state, not by matching an answer string.

The harness. Base models get a dataset-independent scaffold: a simple system prompt plus relaxed tool-calling and parsing. Base models receive raw text with no chat template. Post-trained models use their native chat template and the dataset-default scaffolding, with thinking mode switched off.

The metric. With pass@1 as accuracy and pass@k as coverage, the paper defines raw scalability and a calibrated version:

A(K) = sum_{k=1..K-1} [ pass@K - pass@k ]
S(K) = A(K) / ((K-1) * (1 - pass@1))
Tax_X(K) = X_Base(K) - X_Post(K),  X in {A, S}

A positive tax means extra rollouts help the base model more than they help the post-trained model. The calibration divides by the single-shot failure rate so the score stays between 0 and 1.

PTGS. Posterior-tempered group sampling tracks each prompt's discounted success and failure counts, draws a difficulty estimate from a Beta posterior (Thompson sampling), and sets the rollout temperature to T_x = tau^h(p_hat). Hard prompts are heated toward tau and easy prompts cooled toward 1/tau. The paper uses tau between 1.2 and 1.5, gamma of 0.95, and raises the target success rate from 0.25 to 0.5 during training. It is dropped at test time.

What are the results?

On pass@1 the post-trained models lead. On pass@K the base models scale more steeply and, for larger models, cross over. The headline example is gemma-4-31B on WebShop: the base model reaches over 85% pass@128 against 56% for the post-trained model.

Source: arXiv 2610.01509.

The mechanism the authors propose is "bimodalization". Post-training empties the middle category of tasks that sometimes succeed, pushing them to always-solved or never-solved. Those middle tasks are exactly the ones extra rollouts convert into wins.

Scale matters. For Gemma-4 on WebShop, the crossover budget falls from more than 128 rollouts at 4B to about 3 at 31B. Averaged over the largest backbone of each family (12 model-benchmark combinations), the base curve overtakes the post-trained curve at around k=22. For the smallest backbones it never does within 128 rollouts. For those small models, the paper says post-training supplies basic skills such as well-formed tool calls.

Cheap to estimate. The tax at 8 rollouts, measured on half the tasks, predicts the tax at 32 rollouts on the held-out half with a Spearman correlation of 0.85. The authors use this to propose routing between base and post-trained models per task.

PTGS results. The sampler was tested by fine-tuning Qwen2.5-7B-Instruct on two small environments, averaged over five runs.

Source: arXiv 2610.01509, table of RL results. The un-tuned Qwen2.5-7B-Instruct starting point scored 20.7 pass@1 and 76.6 pass@128 on Sokoban, and 26.3 and 89.1 on FrozenLake.

Note the Sokoban rows: both RL methods push pass@128 below the starting model's 76.6, and PTGS only partly recovers it.

Does the evidence hold up?

Partly. The pass@K pattern appears across several families, but the comparison is not like for like, and the causal story is an inference.

The harness is applied to one side only. The paper's own ablation shows the harness helps base models a lot on some benchmarks. Averaged over eight base models, BFCL pass@32 goes from 15.19 to 49.13 with the harness, and WebShop pass@32 from 39.48 to 49.15. On ACEBench the harness does nothing useful (89.25 to 87.69). The authors also observed the same harness hurts post-trained models. That is a fair design choice for asking what each model can do at its best, but it means "base beats post-trained" really means "base with a tuned scaffold beats post-trained with its default scaffold".

Thinking mode is off. Post-trained models were run without explicit reasoning so rollout counts, not tokens, set the budget. The authors ran an ablation with thinking on for gemma-4-31B and Qwen3.5-35B-A3B on BFCL, and report the same overall trend, though it improves the post-trained models.

Consistency tells the other half. The base model's pass^k (the chance that all k rollouts succeed) falls toward zero as k grows, while the post-trained model's stays much higher. If you need a result that works every time, the post-trained model is the better choice.

Benchmark choices. BFCL uses a single category (multi_turn_base) rather than the full suite, because the authors say the base vs post-trained comparison can flip between categories. WebShop uses the first 500 goal instructions. ACEBench uses a 770-task subset and excludes tasks that need an LLM user simulator. Only three text-agent benchmarks are covered, so the "pervasive" claim is bounded by that.

Uncertainty is reported, partly. The tax curves carry 95% paired bootstrap intervals from 1,000 task resamples. The authors note the last point of each curve (K equal to the number of rollouts) is noisier. The PTGS table reports means over five runs; the main table does not show a spread, so small gaps such as FrozenLake GRPO tax (0.029 vs 0.028) should be read as no difference.

Observational, not causal. The open checkpoints do not disclose their training data or recipes. The "-it" and "-Instruct" models may mix SFT, preference optimisation and RL in unknown proportions, so the authors use "RL post-trained" as shorthand. They state that the analysis remains observational rather than interventional.

Contamination. The authors chose ACEBench partly because it is more recent and less commonly reported, so less likely to have been optimised for in post-training. That is a reasoned argument, not a test.

Reproducibility. The arXiv paper and project page link a code repository, and the evaluated checkpoints are public. The serving stack is stated (vLLM 0.19.0, with gemma-4-12B on 0.23).

How does it compare with related work?

It extends a line of pass@k studies from math and code to agents, and it adds a scalar metric and a mitigation.

One point of difference stands out. Zhao et al. control the pretraining data, an interventional design, while the Sharpening Tax paper says its own analysis remains observational. The paper also lists data-dependent and training-dependent views, such as Zhang et al. (arXiv 2512.07783), as positions between advocacy and skepticism. For background on how RL changed LLM training, see our explainers on DeepSeek-R1 and InstructGPT and RLHF.

What does a working researcher take from this?

Report coverage next to accuracy, and report the budget. A pass@1 table hides what extra sampling would buy.

Practical points that follow from the paper:

1. Check the crossover before choosing a model. If you run a large model with a big rollout budget and a verifier, the base model may solve more tasks. The authors say this suits cases where diversity and creativity matter, such as scientific discovery.
2. Do not assume it for small models. At 3B to 4B the post-trained model won across the budget range tested.
3. Estimate the tax cheaply. Eight rollouts on half the tasks were enough to predict the 32-rollout tax in the authors' data.
4. Fix the harness before comparing. A scaffold changed base pass@32 on BFCL by more than 30 points. Any base vs instruct comparison needs the scaffold stated.
5. Try per-prompt temperature in RL. PTGS changes only rollout sampling and, per the authors, adds no computational overhead. It needs replication beyond two small environments.

The scale-versus-coverage pattern also echoes the scaling-law literature the paper cites for model capacity. For that background, see Scaling Laws Explained.

What's still unclear?

Several things remain open, and some are the paper's own admissions.

• Which post-training stage causes the loss? The authors did not compare SFT, RL and on-policy distillation. With undisclosed recipes, the tax cannot be pinned on RL.
• Does it hold with the best scaffold for each side? A tuned harness for post-trained models, or the thinking mode on by default, could shrink the gap. The paper shows only that the trend survives the thinking-on ablation on two models.
• Does it generalise beyond binary, text-only agents? The metric needs a binary success signal. Multimodal models and vision-language-action models are listed as open questions.
• Does PTGS scale? Evidence is a 7B model, two small environments, 200 training steps and five runs. The authors' broader claim that tax is not unavoidable rests on that.
• Is heavier RL different? The authors say whether heavier RL moves beyond elicitation remains open, and that a lighter-recipe view may fit open checkpoints better than frontier RL.
• Framing. The topic is sometimes summarised as "Meta shows base models beat post-trained models". The affiliations are mixed, and the result is conditional on harness, scale and budget.

Weakest point of the argument: the headline comparison pairs a scaffold built for base models with default scaffolding for the others, on three benchmarks, using checkpoints whose training is unknown.