How do you know a fine-tuned AI model is actually better?

You measure it. Hold out a portion of the client's real examples so the model never sees them during training, score the plain base model on those held-out questions first, fine-tune, then score again on the identical questions with identical scoring. The difference is the lift. Because the only thing that changed is the fine-tune, the improvement is attributable to it.

Does fine-tuning actually improve accuracy, or is the base model already good enough?

It depends on the task and, critically, on how much data you have. On a public benchmark of 510 lawyer-annotated commercial contracts, a base Qwen3-4B extracted short contract fields at 62.2% accuracy. Fine-tuned on 396 examples it reached 83.5-85.4%, a lift of 21.3 to 23.2 points across three runs. The same model trained on only 48 examples produced a lift inside the noise floor, so the amount of data was the deciding factor rather than the model's ceiling.

How much of our own data do we need to fine-tune a model?

Fewer examples than most people expect, but more than a handful. In our contract-extraction measurements, 48 training examples produced no measurable improvement while roughly 400 produced a 22-point gain. The honest answer for any specific case is that it depends on how varied and how consistent the examples are, which is what a paid readiness assessment measures on the client's own corpus.

Why can't you just use a public AI benchmark score?

Public benchmarks measure general ability on standardised tests, not your work. A model that scores well in the abstract can still be mediocre at reading your contracts or following your policies. Public benchmarks are also increasingly targeted during training, so a high score can reflect test preparation as much as capability. The only benchmark that answers your question is built from your own tasks.

Research record

XOR, Tuned, and It Still Halves the Steps

By Joshua Bolick, Awareness Software Group ~9 min read September 2026

Ongoing research. This is an experimental result from active work, not a settled conclusion. The numbers are what we measured and the method is described so you can judge it, but the programme is still running and later experiments may revise what it means.

A note on the language in these records. This is a working laboratory notebook for research into training AI models more cheaply and efficiently, so you will read that an approach did not work, that a result did not hold up, or that one method was worse than another. That is the research doing its job, not a verdict on the engineering we deliver to clients. Ruling an approach out is how the search narrows, and these are the pages that teach us the most: nearly every technique we now rely on came from understanding why something else fell short. Testing our own ideas at least as hard as anyone else's is the point of publishing them. More about this programme and why we run it.

Part of a bigger question: Is the task we are studying actually hard? – Often it is not. A rule from 1990 with no parameters beats the trained model on the task most of these results were measured on, and what an intervention costs is set by the task's own structure.

In plain English

What we asked. Our easy-start recipe halved the steps on the XOR task, but ordinary training's best learning rate might have been lower than the two we had tried. We tried two lower ones.

What we found. Ordinary training was about equally good across the lower rates, best at 0.002. At that rate the easy start still reached the solution in about half the steps.

Why it matters. Tuning the ordinary recipe moved it by a few hundred steps; the gap was about five thousand. The speed-up now holds against a tuned baseline on four different tasks.

The rest of this page is the technical record: the design, every number, and the limits. It is written for a reviewer, and you do not need it to have understood the result above.

New here? How to read a research record

Start at the verdict. Every record states, before the experiment was run, what result would have made us abandon the idea. That is the "kill test". Then it says whether the test fired. Nothing gets reinterpreted after the fact.
Numbers in square brackets are uncertainty. 23.4 [18.1, 28.7] means our best estimate is 23.4 and the true value is probably somewhere in that range. If a range includes zero, we cannot claim an effect.
Results that rule an idea out are kept. Roughly half of what is published here says an approach did not work, including plenty of our own. Those pages are the output, not a shortfall: knowing which direction is a dead end is what lets the next experiment go somewhere better, and most of what we now rely on came out of understanding why something else fell short. Work that only publishes what worked is not measuring anything.
Read the Limits section. Every record ends with what it does not show. It is the most honest part of any experiment and usually the shortest.
Pro tip: the figures near the top are designed to carry the result on their own. If you read nothing else, read the caption under each one, which says what it shows and what to take from it.

EXPLORATORY. Not a preregistered study. Local CPU, 32 new training runs of 24000 steps plus 48 re-used from A63. The design and the kill test were committed (2c551a8) before any run.

Program v2 Bucket A, item A67. Decisive computation: analysis/xor_lower_rates.py. Output: analysis/xor_lower_rates.json.

The question

A63 found the easy-XOR warm-up ahead of plain training by -5466.2 [-8759.0, -2173.5] steps, but plain's better peak (0.003) was the lower edge of a two-point grid, so plain's optimum was not found. Does plain XOR at a lower rate close the gap?

**Tuned to its best rate, ordinary training still takes twice as long on XOR.** Ordinary training on the XOR task was tried at four learning rates. It is about equally good from 0.0015 to 0.003, best at 0.002, and fails at 0.005. The flat line is the easy-start recipe at a single rate. *At ordinary training's best rate, the easy start still reaches the solution in about half the steps. Tuning the baseline moved it by a few hundred steps against a gap of about five thousand.*

Design: plain with a 500-step learning-rate warm-up at peaks 0.002 and 0.0015, A63's sixteen seeds, 24000 steps. The best of all four plain peaks is compared with A63's mixed runs, paired. Kill test, fixed before execution: mixed minus the best plain peak includes zero or lies above it; a best peak at 0.0015 is reported as not found. Anchor, in code: re-running A63's plain 0.003 cell on its first seed reproduces it -- held.

Results

Plain XOR, peak rate (sixteen seeds)	Mean steps to `0.9`	Median	Solved by `24000`
`0.0015` (new)	`12724`	`10470`	`14`
`0.002` (new)	`11336`	`9220`	`15`
`0.003` (A63)	`11652`	`9775`	`14`
`0.005` (A63)	`22708`	`24000`	`2`
easy XORs first (A63)	`6186`	`4475`	`15`

Best plain peak: 0.002, inside the grid. Plain XOR is flat from 0.0015 to 0.003 (means within 1400 steps) and fails at 0.005.
Mixed minus the best plain peak: -5150.6 [-8982.3, -1319.0] steps; ratio of mean steps 0.546.

The kill test does not fire. Plain XOR's optimum is found, and the easy warm-up still reaches the solution in about half the steps, with both arms solving 15 of 16.

What it says

A63's caveat is closed: tuning plain XOR's rate moved its mean by 316 steps, against a gap of about 5000. The easy-start speed-up now holds against a tuned baseline for four hard two-input tasks on the GRU -- modular sum, difference, XOR, and a maximum that is hard for plain training -- with ratios from 0.48 to 0.74, and on the LSTM for the sum.

The best plain cell is picked from four on the same seeds the comparison uses, which favours plain, so this selection works against the finding.

What stands

A67: kill test does not fire. Best plain XOR peak 0.002 (interior); mixed minus it -5150.6 [-8982.3, -1319.0] steps; ratio 0.546.

Limits

One task at one difficulty; width 48; sixteen seeds. The mixed arm ran at 0.003 only and was not itself tuned, which if anything understates it.

Terms on this page

Every piece of vocabulary this record uses, in plain language. Generated from the text above, so it cannot drift out of step with it.

baseline: The thing you compare against. A result without one is not a result.
GRU: Gated Recurrent Unit. A compact design for processing sequences one item at a time, with internal switches controlling what it keeps in memory.
kill test: A condition written down before running the experiment that says what result would make us abandon the idea. Fixing it in advance is what stops a disappointing result being reinterpreted as an encouraging one.
learning rate: How big a step training takes each time it updates the model. Too small and nothing happens; too big and it never settles.
LSTM: Long Short-Term Memory. An older and larger relative of the GRU, also gated, also for sequences.
seed: The number that fixes all the randomness in a training run. Same seed, same run. Running several seeds is how you tell a real effect from a lucky one.
width: How many internal numbers a model uses at each layer. The usual way we vary model size in these experiments.