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

The Learning Rate Was Never Tuned

By Joshua Bolick, Awareness Software Group ~11 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: What actually makes training cheaper? – One thing has worked: stopping part of the training early saved about 7% with no loss of quality. Everything else tested has been matched by a simpler or cheaper method -- and in two cases the clever method was only winning because it was quietly being given more.

In plain English

What we asked. Over three experiments, something that looked like a special feature inside a small model turned out to be a short burst of faster learning at the right moment. The obvious question left was whether the model should simply have been learning faster all along.

What we found. It should. Raising the learning speed by a quarter for the whole of training beat the clever burst, and doubling it made the models learn 38% sooner. The better the setting was chosen, the less the burst added. The setting our experiments had used on these models had never been tuned for how fast they learn.

Why it matters. This is the most ordinary explanation there is, and it took four experiments to reach, because each one checked only the next layer down. The lesson worth copying: before explaining why an intervention speeds training up, check the simplest setting that would do the same. We are now checking which of our other speed-ups share this problem.

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, 64 training runs. The design and kill test were committed (7f6c510) before the run whose output is reported here.

Program v2 Bucket O, item O15. Decisive computation: analysis/whole_run_rate.py. Output: analysis/whole_run_rate.json. Reproduce with python analysis/whole_run_rate.py (about fifteen minutes on a throttled laptop CPU); --reuse re-derives every endpoint from the saved transitions, and was checked to print the identical summary.

Provenance note. A first launch started seconds before its commit, when a lint failure skipped the commit in a chained command; it was stopped, its partial output deleted, the lint fixed (one list expression, no change in behaviour), the pilot committed, and the run restarted from the committed file.

The question

O13 and O14 traced J8's one positive arm down to a learning-rate schedule: 1.5x the learning rate for forty steps opening at step 112 removes 11.6 steps from the transition on J8's eight receivers. J8's rate, 0.002, was never tuned for time-to-transition, and the standing rule says to price every efficiency claim against the cheapest ordinary alternative -- here, a higher rate from the start.

**A slightly higher learning rate from the start beats the clever late boost.** The same eight small models trained at four learning rates, the first being the one our earlier experiments used. In each pair the first bar keeps the rate steady and the second adds the short late boost our last experiment found. Bars are measured against the original rate with no boost. Raising the rate by a quarter for the whole run already beats the boost, and doubling it makes the models learn 38% sooner. The boost matters less the better the rate is chosen. It was making up for a learning rate nobody had tuned.

Every run is J8's own train() on J8's receivers: whole-run rates 0.002 (J8's control, anchored), 0.0025, 0.003 and 0.004, each with and without O14's fixed-step boost.

Kill test, fixed before execution: some unboosted whole-run rate reaches the transition at least as soon as the boosted 0.002 run.

Anchor, in code: the 0.002 controls equal J8's committed transitions exactly. They do.

Result: the kill test fires, at the first rate tried

Change in the transition (steps; negative is sooner), J8's definition (interpolated floor-to-ceiling midpoint, 0.30 gate); no run at any rate was lost to the gate:

Whole-run rate	Plain, against J8's control	With the boost, against J8's control	Plain, against the boosted `0.002` run
`0.002` (J8)	`0`	`-11.84` `[-13.50, -10.18]`	`+11.84` `[+10.18, +13.50]`
`0.0025`	`-22.89` `[-23.84, -21.94]`	`-28.13` `[-30.38, -25.89]`	`-11.05` `[-12.12, -9.98]`
`0.003`	`-38.19` `[-39.82, -36.57]`	`-39.31` `[-41.79, -36.84]`	`-26.36` `[-27.02, -25.69]`
`0.004`	`-57.65` `[-60.38, -54.93]`	`-57.65` `[-60.38, -54.92]`	`-45.82` `[-47.36, -44.28]`

A rate a quarter higher, for the whole run, beats the late boost by 11 steps. Doubling the rate removes 57.7 of about 153 steps -- 38% of the time to the transition -- and the curve had not turned at the largest rate tried.

The boost on top of each rate: -11.84, -5.25, -1.12, -0.00. Its value shrinks as the rate is tuned, and at 0.004 it is zero by construction: the transition (about 95) now comes before the boost's window opens at 112, so the boost acts after the event. The fixed step was set for the 0.002 runs and was not moved.

What this means for the thread, and beyond it

The four-record thread J8 → O3 → O13 → O14 ends at an under-tuned learning rate. A "special direction" (J8) was a lean toward the model's own mean gradient (O13), which was a late learning-rate boost (O14), which is dominated by a slightly higher rate throughout (O15). Each control removed one layer; none of the layers was the mechanism.
Every speed-up measured on J8's substrate at 0.002 is now exposed to the same question: an intervention that makes a model learn sooner may be partly compensating for a rate too low for this task. That is not the same as being explained by it -- an effect can survive at the tuned rate -- but none has been checked. Generates O16 (find the rate optimum and re-run the substrate's two cleanest speed-ups at it) and R18 (an archive audit, no compute, of which published speed-up claims were measured at an untuned rate).

What stands

Kill test fires. O14's late boost is dominated by a whole-run rate of 0.0025 (-11.05 [-12.12, -9.98] against it).
J8's substrate is under-tuned for time-to-transition: 0.004 reaches the transition 38% sooner, with no run lost to the gate.
The late boost's value falls as the rate rises and is zero where the transition precedes it.

Limits

Time to the transition only. This record does not measure final accuracy or stability at the higher rates; a rate that transitions sooner may end worse. O16 must report both.
The rate sweep stops at 0.004; the optimum was not reached.
The boost's window was fixed at step 112 from the 0.002 controls and not re-placed for each rate, so "the boost adds nothing at 0.004" is a statement about that window, not about boosting in general.
J8's substrate only: width-48 GRU, delayed copy, eight receivers.

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.

accuracy: The fraction of answers a model gets right on questions it was not trained on.
gradient: The direction and amount by which each of a model's internal numbers should change to do slightly better. Training is repeatedly following it.
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.
width: How many internal numbers a model uses at each layer. The usual way we vary model size in these experiments.