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What does “better” mean for your coding model?
There is no universal coding score that proves one model is better. A fine-tune might improve short function completion but fail to help with navigating an unfamiliar repository, fixing regressions, or producing code a team can review. Start by defining the work the model is supposed to do and what a successful result looks like.
- Work type: Specify whether the model writes standalone functions, repairs repository issues, generates tests, reasons from execution output, or supports another task.
- Operating context: Record the languages and repository types, prompt style, context limits, and whether the model runs alone, in an editor, or inside an agent loop.
- Success criteria: Choose a primary measure—such as passing task tests or an accepted patch—and define any unacceptable regressions in advance. If readability, maintainability, or reviewability matter, state how you will assess them.
This definition determines which tasks belong in the evaluation. A repository-repair fine-tune should not be declared better solely because it scores higher on short function-synthesis problems.
How do you make a fair base-versus-fine-tune comparison?
Run the exact base checkpoint used to create the fine-tune, if it is available, alongside the fine-tuned checkpoint. Change the model checkpoint—not the surrounding experiment. Otherwise, a score difference could come from the prompt, agent, runtime, or generation budget rather than fine-tuning.
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- Use the same evaluation harness, prompt templates, task versions, dependencies, and test setup.
- Match decoding parameters, samples per task, context limits, tool access, and timeouts.
- Keep hardware and runtime conditions comparable, and record relevant versions and checkpoint hashes.
- If you are evaluating a model-plus-agent product, hold the agent scaffold fixed. If you also want to compare scaffolds, report that as a separate experiment.
For repository tasks, setup itself can affect whether a patch is judged successful. SWE-bench describes testing both whether a patch fixes the issue and whether it passes regression tests; its benchmark introduction helps explain why patch application and test configuration are part of the evaluation, not incidental details.
Which coding tasks should you include?
Use multiple task types that reflect the intended workflow. A useful mix can reveal whether a fine-tune improves a narrow capability while leaving other important work unchanged or worse.
| Task type | What it can reveal | What it does not establish by itself |
|---|---|---|
| Short, standalone code synthesis | Whether generated code meets the specified behavior on compact problems. | Whether the model can understand an existing codebase, produce a repository patch, or avoid regressions. |
| Repository issue repair | Whether the model can work within an existing project and produce a patch that addresses an issue while passing relevant tests. | Whether it is better at unrelated tasks such as standalone synthesis, or whether a benchmark task and its tests accurately represent your workflow. |
| Newly published contest tasks | Performance on recently collected programming problems. LiveCodeBench describes an approach that collects new contest tasks over time and covers capabilities beyond code generation. | Performance on your private repositories or customer workflow. |
Use stable public benchmarks as reference points, but keep a private held-out set for the decision that matters. If you sample tasks from real code or customer work, remove sensitive information and keep development data separate from the final evaluation set. Do not tune prompts or hyperparameters on the final holdout.
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Public tasks can be exposed through training data, source repositories, published solutions, or release notes. Prefer tasks created after the model’s known training cutoff or private tasks where practical. Record what is known about the cutoff and benchmark exposure; investigate outputs that reproduce distinctive known solutions.
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A test suite is only useful if it checks the behavior the task actually asks for. Review task statements and tests for hidden requirements, incidental implementation constraints, weak tests that allow incomplete fixes, misleading prompts, broken dependencies, and failures caused by the environment rather than the generated code.
Recent audits show why this review matters, while also requiring careful limits on what the figures mean. OpenAI reported that 59.4% of 138 audited SWE-bench Verified tasks had material issues in their tests or problem descriptions. These were tasks that o3 did not consistently solve over 64 independent runs; the finding is not a random estimate for all tasks in that benchmark or for coding benchmarks generally.
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In a separate 2026 audit, OpenAI’s SWE-Bench Pro analysis flagged 27.4% of tasks as likely broken in its datapoint pipeline and 34.1% in its human annotation campaign. Those percentages refer to the respective audited sets, not every task in SWE-Bench Pro. OpenAI also reported that frontier-model pass rates on its 731-task public SWE-Bench Pro split changed from 23.3% to 80.3% over eight months. That is not a controlled comparison of one model and does not by itself establish that the benchmark remained valid.
For a consequential decision, manually inspect a sample of wins, losses, and apparent ties. Confirm whether each outcome reflects the requested behavior, rather than an invalid test or setup failure. An automated judge can help prioritize this review, but its verdict alone does not establish that the benchmark is sound.
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Generation budget changes results, so state the sampling policy rather than reporting a score without context. A pass@1 result, a result based on many attempts, and a result that selects the best of many outputs answer different questions. Use the same number of samples and the same selection rule for both checkpoints.
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The Codex paper reported 28.8% of HumanEval problems solved at one reported setting and 70.2% with 100 samples per problem. Those are results from the paper’s 2021 setting—not current model rankings—but they illustrate how strongly repeated sampling can change a reported score. See Evaluating Large Language Models Trained on Code for the paper.
Report enough detail for someone to understand what was measured and how stable the difference is:
- Task set identity and version, number of tasks, and task-level outcomes.
- Checkpoint identifiers or hashes, prompt and harness versions, decoding settings, and sample count and selection rule.
- Aggregate results alongside the kinds of tasks that improved, worsened, or tied.
- Uncertainty estimates suited to the comparison; for stochastic generation, use multiple runs or samples where appropriate.
- Representative successful and failed outputs, including manually reviewed examples when the decision is important.
Do not treat a small aggregate gap as decisive without examining uncertainty and paired task outcomes. HumanEval.org documents bootstrap confidence intervals for its blind preference leaderboard; that is a useful example of making uncertainty visible, although its specific rating procedure belongs to that leaderboard, not every coding evaluation. If code quality beyond test passing matters, add blinded human comparisons using a written rubric, randomized output order, hidden model identity, and an option to call ties. Keep those judgments alongside functional tests rather than substituting for them. See HumanEval.org’s methodology.
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Does a benchmark gain matter in the real workflow?
Before adopting the fine-tune, run a small pilot on work that resembles its intended use. Benchmark performance is evidence about performance on that evaluation set; it does not automatically predict the result in your team’s workflow. Choose the pilot measures before looking at results, and adapt them to the way your organization uses code.
- Whether tasks are completed and patches are accepted.
- Whether accepted changes introduce regressions.
- How much human review or correction is needed.
- Time and compute per successful or accepted task, when those costs affect the decision.
Compare the complete model-and-tool workflow if that is what you plan to deploy, while keeping those results distinct from model-only benchmark scores. A fine-tune may be useful despite a modest benchmark change if it improves an important workflow outcome; conversely, a public benchmark gain may not justify adoption if the pilot shows more review work, regressions, or cost.
What is enough evidence to call the fine-tune better?
Call it better only in the scope you tested: on a representative, held-out task mix, under matched conditions, with credible task tests and a generation budget stated clearly. The comparison should show where results changed, how uncertain the difference is, and whether the gain carried into the intended workflow without unacceptable regressions or review burden. OpenAI’s 2026 evaluation audit argues that useful evaluations should be difficult to game, trustworthy, and reflective of the capability being assessed; that is a sound standard for judging the evidence, not a substitute for testing your own use case.
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