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 38 of 39

How Many of Our Results Are Close Calls

By Joshua Bolick, Awareness Software Group ~9 min read August 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. More about this programme.

In plain English

What we asked. Every result we publish comes with an error bar, and the verdict comes from whether that bar clears a line we set in advance. One of our recent results was overturned for an uninteresting reason: we simply ran it more times. Its error bar had missed the line by about four hundredths of its own width, and running four times as many repetitions gives an error bar half the size, which was more than enough to move it.

What we found. That made us ask an uncomfortable question about everything else we have published. So we measured, for every result in this project, how far its error bar sits from the line that decides it. Sixteen results across five studies are within one error bar of their own verdict, and the closest one is nearer than the result that already flipped. We are publishing that list, including which of our own headline findings is at the top of it.

Why it matters. Two things to be clear about. Being on this list does not make a result wrong. It means more computer time could move it, and it could move either way: the one we already caught moved toward the effect being real, not away from it. And the tool we built for this was itself wrong the first time, in a way worth admitting: it measured the wrong edge of the error bar, and confidently ranked one of our most solid results as our shakiest. We caught it because the answer disagreed with what we knew about that particular result. A measurement that answers a slightly different question than the one you asked is worse than no measurement, because it looks precise while being wrong.

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.
Negative results are kept. Roughly half of what is published here says an idea did not work, including several of our own. Those pages are not failures, they are the output. 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. Archive-only, no training at all, no GPU, no cost.

Program v2 Bucket J, item J1. Decisive computation: analysis/power_audit.py. Output: analysis/power_audit.json. Reproduce in seconds with python analysis/power_audit.py, reading only committed pilot outputs.

The question

I3 reported two confident readings on six seeds and both were wrong. Its paired interval was +0.0113 [-0.0005, +0.0231]: the deciding bound sat 0.0005 from zero against a half-width of 0.0118, so it missed its boundary by 0.042 half-widths. Eighteen more seeds moved it to +0.0077 [+0.0033, +0.0121] and the verdict reversed.

Sixteen of our published results are decided by a very small margin. Every result here comes with an error bar, and a verdict comes from whether that bar clears a line. One of our results was recently overturned simply by running it more times: its bar had missed the line by about four hundredths of its own width. Running four times as many gives an error bar half the size, which is enough to move a verdict that close. So we measured that distance for every result we have published. The blue band marks where the one we already caught was sitting. Sixteen results across five studies sit within one error bar of the line that decides them, and the closest is nearer than the one that already flipped. That does not make any of them wrong: it means more computer time could move them, in either direction, and the one we caught moved toward its effect being real. We are publishing the list rather than quietly rerunning the convenient half of it. The cheap fix is not cleverer analysis, it is more repetitions of fewer claims.

That is not bad luck, it is arithmetic. A 95% interval's half-width shrinks roughly as 1/sqrt(n), so quadrupling the seeds halves it. Any interval whose deciding bound sits within about one half-width of its line is a candidate to move on nothing but compute.

This programme has 36 committed pilot outputs and most ran 5 to 10 seeds. How many are sitting that close?

Kill test: no published interval sits within one half-width of its decision boundary. Then I3 was isolated and the record's sample sizes are adequate.

Result: sixteen, across five files

File	Fragile intervals	Closest
`relearning_event` (E7)	4	`0.060` half-widths from `0`
`modular_state` (E8)	5	`0.135` from `0.05`
`direction_anatomy` (I3)	3	`0.183` from `0.05`
`unlearnable_control` (I6)	3	`0.204` from `0`
`fitted_combiner` (I4)	1	`0.807` from `0`

The most fragile is E7's frozen-frame paired endpoint, +0.0158 [+0.0009, +0.0307], clearing zero by 0.060 half-widths, against I3's 0.042 before it reversed. That endpoint decides the "real by the intervals" half of E7's letter-versus-intent verdict, so it is the first thing J2 should re-run.

Two readings that are not in danger, and worth saying so explicitly:

I3's own paired difference is now at 0.746 half-widths on 24 seeds: comfortable, which is what adding seeds bought.
E7's materiality verdict is secure. Its low bound sits two full half-widths below the 0.05 floor, so "the expansion recurs but is immaterial" is not at risk. Only the "recurs at all" half is.

The scan's own first version was wrong, and that is the transferable part

The first version scored each interval by whichever bound sat nearer the boundary. It ranked E7's headline as maximally fragile, 0.000 half-widths, because E7's high bound lands on 0.05 exactly.

That is precisely backwards. E7's verdict is decided by its low bound of 0.0143, which is two full half-widths from the floor: one of the most secure nulls in the record, scored as its most precarious.

Every decision rule in this programme is one-sided and of the same form: an effect counts when the interval's low bound clears the line. "Material" is low > 0.05; "clears zero" is low > 0. So the flip distance is always the low bound's distance from the boundary. The corrected metric changes the ranking entirely, and E7 stays at the top for a different and real reason.

A metric that answers a different question than the rule does is worse than no metric, because it is confidently wrong in a way that looks quantitative.

Verdict

The kill test fails. 16 intervals across 5 files sit within one half-width of a decision boundary. I3 was not isolated.
This is a triage list, not a list of errors. Many entries are intermediate values no headline rests on. Reading them is the next step, and J2 does that in flip-risk order.
A fragile interval is not a wrong one. It means the verdict is decided by a margin four times the seeds would erase, in either direction. I3 flipped toward its effect being real.
The cheapest structural fix is not more analysis, it is more seeds on fewer claims. Five to eight seeds is enough to find an effect and not enough to decide a marginal one.

Limits

The scan does not know each record's boundary. It tests the two this programme uses, 0 and the 0.05 materiality floor. An endpoint judged against something else is scored against the wrong line and has to be discarded by eye.
It cannot tell a headline from an intermediate value. Path names are reported so a reader can, but the ranking treats them alike.
Intervals wider than 5.0 are excluded as almost certainly not on a normalised endpoint, which is a crude filter.
The 1/sqrt(n) argument assumes the estimator is well behaved. For a skewed sample like I3's it is a rule of thumb, not a guarantee, and the honest statement is "could move", never "will".
This audits precision, not correctness. An interval can be comfortably clear of its boundary and still be measuring the wrong thing, which is what four of this programme's corrections have actually been.

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.

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.
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.

About this record. This page is the write-up of an experiment we ran ourselves. Every number on it comes from a run we recorded, and the script that produced each one is named in the text above. We publish these results and the data behind them here, including the ones that went against what we expected.

Why we do this. The same care shown above is what we apply to client work. We build custom AI models that you own and run yourself, using our own platform, and the reason we publish research like this is that a model is only worth what its evaluation is worth. If a supplier cannot show you the experiments that went against them, you cannot check the ones that went their way.

All research from this programme →