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 Halves the Steps Too

By Joshua Bolick, Awareness Software Group ~10 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.

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 helped a small network learn to add and subtract two remembered symbols. We tried a different operation: bitwise XOR, which combines the two symbols bit by bit with no carrying.

What we found. It helped just as much. Starting on easier versions reached the solution in about half the steps of ordinary training at its better learning rate, and solved it on 15 runs of 16.

Why it matters. So the speed-up is not about one kind of arithmetic. One thing is still open: ordinary training's best rate may be lower than the two we tried, and that is the next test.

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, 48 training runs of 24000 steps on sixteen fresh seeds. The design, a disclosed throwaway and the kill test were committed (bbc8873) before any run.

Program v2 Bucket A, item A63. Decisive computation: analysis/xor_mixture.py. Output: analysis/xor_mixture.json.

The question

The easy warm-up roughly halves the steps a recurrent network needs for a hard two-read task when the task is modular addition or subtraction (A44, A57) -- one group, Z32 -- and it helps on a maximum that is hard for plain training while slowing an easy one (A62). Does it hold for XOR -- a group operation of a different group (Z2^5, bitwise on each symbol's five bits), with no carries?

**For a different operation, XOR, the easy start halves the steps too.** The hard task is to output the bitwise XOR of the symbols 2 and 7 steps back. Ordinary training was run at two learning rates; the easy-start recipe first trains on XORs of nearer symbols. *The easy start gets most runs to the solution in about half the steps of ordinary training at its better rate. A lower rate for ordinary training has not been tried yet; that is the next test.*

Design: GRU, width 48, 24000 steps, sixteen fresh seeds 28001-28016. Hard target x[t-2] XOR x[t-7]; easy warm-up of XORs on (2,3)/(2,4)/(2,5) for 2000 steps at rate 0.003 (A57's loop with the target swapped). Plain with a 500-step learning-rate warm-up at peaks 0.003 and 0.005, the better compared. A one-seed throwaway, disclosed before running, had plain unsolved at 16000 steps and the warm-up at 3540. Endpoint: steps to 0.9 (never = 24000), paired. Kill test, fixed before execution: mixed minus the better plain peak includes zero or lies above it. Anchor, in code: the loop reproduces A57's first mixed run -- held.

Results

Arm (sixteen fresh seeds, hard XOR)	Mean steps to `0.9`	Median	Solved by `24000`
easy XORs first (`0.003`)	`6186`	`4475`	`15`
plain, peak `0.003`	`11652`	`9775`	`14`
plain, peak `0.005`	`22708`	`24000`	`2`

Better plain peak: 0.003. Mixed minus it: -5466.2 [-8759.0, -2173.5] steps; ratio of mean steps 0.531.

The kill test does not fire. With XOR as the hard task, the easy warm-up reaches the solution in about half the steps of plain training at its better rate, with an interval wholly below zero.

The better plain rate is at the grid's lower edge. The script's edge check only looked at the top of the grid and printed False; 0.003 is the bottom of a two-point grid, so a lower plain rate is not tested, and the plain optimum is not found. The sum's tuned rate was also near 0.003 (A31, A36), and at 0.005 plain XOR mostly fails, so a lower rate would have to help plain by more than 5000 steps to close the gap -- possible, not shown. A67 tests it.

What it says

The speed-up is not specific to Z32. XOR has no carries and a different group structure, and the easy start gives about the same ratio (0.531) as for the sum and difference (0.48-0.58). With A62, the pattern so far is that the easy start helps whenever the hard two-input task is hard for plain training, whatever the operation -- and A66 (a random table, running) asks whether it needs any structure at all.

What stands

A63: kill test does not fire. XOR: mixed minus the better plain peak -5466.2 [-8759.0, -2173.5] steps; ratio 0.531; solved 15 against 14. The better plain peak (0.003) is at the lower edge of the grid.

Limits

Plain's optimum is not found (lower edge of a two-point grid); A67 runs plain at 0.002 and 0.0015.
One task at one difficulty; width 48; sixteen seeds.

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.

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.
recurrent: A design that reads a sequence one item at a time, carrying memory forward. The main alternative is attention, which looks at everything at once.
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.