The Measured
Enterprise 2026

The Delegation Index reads 47.2 for the third quarter of 2026, with a band of 40.8 to 53.2. Its inputs are the lab's own synthetic measurements, the simulations and controlled model runs on generated tasks from five published campaigns, 139,646 units in all. It says nothing about the market or about any single firm. The number summarises how those campaigns came out when enterprise work went to AI agents under oversight and the oversight budget stayed fixed. At a reading of 50 the two balance under the conditions the lab measured.

This first reading sits 2.8 points under balance, and its band contains 50. This quarter's evidence cannot tell balance from imbalance, which is why the number is always quoted with its band.

Each component reads one published number and scores it from 0 to 100. All five weigh the same.

Sprawl holds the index down. With the monitoring budget flat, oversight cost grows as fleet size to the power 1.47, and that leg scores 26.7. Audit detection lifts it, because a reviewer who read the agent's whole record with a per-step checklist found 0.58 of the skipped steps. The other three land within five points of balance, and Chapter 1 walks through the arithmetic step by step.

Error Independence ran one model on two different machines and found that the copies share their mistakes, with an error correlation of +0.447 on the items where the models disagreed. Pairs from different model families averaged −0.102.

Delegation Cliff swept 90,880 simulated organisations. Each added level of delegation depth cost 1.50 on the quality margin, and reviewer capacity bought back the most at +1.46. The quality floor decided whether a cliff showed up at all. It took a floor of 0.99 to turn most of the space fragile; at 0.95 there was none.

SIGIL tested a prediction from the Accountability Rent working paper that review before commitment pays on irreversible decisions. The prediction failed in all 12 registered series. Give the reviewer a ledger of its own past damage and wrongful blocking at the top tier went from 30.1% to 42.7%. The lab published that as a refutation.

AGENESIS-2 measured what a fleet of agents costs as it grows. Under a flat monitoring budget the cost exponent is 1.4665, with a 95% interval of 1.4101 to 1.5230. Give every agent its own check and it falls to 0.9001. Before publication the independent check turned up duplicate runs, which moved one verdict from supported to refuted.

Trial Balance gave the auditor a ledger of what the agent owed. Reading only where that ledger failed to balance found 0.80 of skipped steps at 745 tokens. Log review topped out at 0.58, whatever the budget.

AGENESIS, published in April, simulated first-mover adoption and found a premium of 210%, with the market tipping in 77% of markets.

The year's product is the open decision head, a small service that answers typed questions about a live case with a probability for each answer, on a model the operator runs. Its first version failed to beat a hand-written rule table, with a gap whose interval included zero. A retrained version, tested on 800 fresh cases, scored 0.728 against the rule table's 0.566, a gap of +0.161 with a 95% interval of 0.131 to 0.191. At first it wrongly closed cases more often than the project's bar allowed. The cause sat in the evidence pack the environment built, and Chapter 9 prints both readings.

Chapter 11 lists every correction the pieces report, among them the duplicate runs in AGENESIS-2 and a retracted sentence in Error Independence. Schouw is scheduled for 13 October. The next Delegation Index reading freezes on 5 January 2027.

The Delegation Index is one number a quarter, on a scale from 0 to 100. It sums up what the lab's own published campaigns say about how far enterprise work can go to AI agents under oversight when the oversight spend stays fixed. At 50, the cost of handing work over matches what oversight buys back at no extra spend.

The construction was registered on 5 October 2026, before the Q3 numbers went through it. Only numbers printed in a published piece with a live public link on the freeze date enter. Anything internal stays out, drafts and unposted corrections included.

Version

1, registered 5 October 2026

Freeze

5 October 2026, Chicago time

Campaigns in

5 of 6 published

Recompute

independent, 6 October 2026, every value reproduced to two decimals

Each component reads the lab's best measured design in its campaign with oversight spend held fixed. The rule went on paper in advance so nobody could pick the flattering number afterward.

• Delegation price expresses one increment of delegation depth in increments of reviewer capacity, the largest positive lever in the Delegation Cliff space. Both coefficients sit on the same band-standardised scale, so the ratio has no units.
• Oversight yield uses plain review, the better of the two designs SIGIL measured before commitment, under the registered convex cost model.
• For audit detection the rule picks the checklist reader at a full read in Trial Balance, the best diary audit that has a pooled rate and an interval in print.
• Reviewer independence reads the five cross-family pairs in Error Independence, since that was the best pairing measured.
• Sprawl takes the fixed monitoring budget in AGENESIS-2. No other measured arm keeps spend flat while the fleet grows.

Delegation price, P. "Pricing Agent Autonomy" prints a depth coefficient of −1.499 and a reviewer-capacity coefficient of +1.456, on the band-only Sobol fit, n = 4,948. P = 100 × 1.456 ÷ 2.955 = 49.27. One increment of depth costs 1.03 increments of reviewer capacity. The piece prints no interval, so P enters at its point value and adds no width to the band.

Oversight yield, Y. The SIGIL paper prints the value of review against no oversight per tier and per seed. The pooled values run −0.13, −0.17, −0.18, −0.17 and −2.64 from tier 1 to tier 5. Dividing each seed mean by its stake, the square of the tier, and averaging over the five tiers gives m = −0.062, so Y = 46.90. Plain review lost about 6% of the stake per decision. The three seeds give a range of 46.78 to 47.01.

Audit detection, A. Trial Balance prints omission detection at a full read with a per-step checklist of 0.583, 28 of 48, with a 90% cluster-bootstrap interval of 0.479 to 0.667. A = 58.3, with a band of 47.9 to 66.7.

Reviewer independence, R. Error Independence prints the error correlation of each pair on the 47 contested items. The five cross-family pairs read +0.280, +0.013, −0.105, −0.227 and −0.469, with a mean of −0.102. R = 50 × 1.1016 = 55.08. The spread of the five pairs gives a range of 36.00 to 73.45, the widest band in the index.

Sprawl, S. AGENESIS-2 prints an exponent of 1.4665 with a cluster-robust 95% interval of 1.4101 to 1.5230. S = 50 × (2 − 1.4665) = 26.68, with a band of 23.85 to 29.50. A higher exponent gives a lower score, so the band flips.

The index. (49.27 + 46.90 + 58.30 + 55.08 + 26.68) ÷ 5 = 47.25, which rounds to 47.2. The lower ends average 40.76 and the upper ends 53.19.

Five of the lab's six published campaigns enter. Their scale is 139,646 units: 90,880 configurations, 30,000 supervised episodes, 18,360 audits, 150 generated invoices and 256 simulation units. The units behind the five quoted numbers come to 20,154. Those units are different kinds of object, so the total is only a count. The two thinnest legs, 48 checklist audits and 47 contested invoices, carry the two widest bands.

Before Trial Balance entered, the other four components averaged 44.5, with a band of 39.0 to 49.8. Trial Balance went live on 1 October, inside the freeze window, and adding its audit component took the reading to 47.2. So all of that move comes from which campaigns are in.

• Oversight yield under the linear cost model scores 45.66, which moves the index to 47.0.
• Reviewer independence read from the same-weights pair, +0.447, would score 27.7, 1.0 above sprawl at 26.7.
• Audit detection read from the commitment-ledger audit at its lowest published cell, 0.92, would move the index to 54.0. That design has no pooled rate with an interval in print, so the registered rule leaves it out. It is printed here so readers can see it.
• Sprawl under per-agent monitoring, exponent 0.9001, would score 55.0. That arm raises spend with every agent, which breaks the fixed-spend condition.

AGENESIS measures competitive dynamics between firms and prints no oversight quantity, so it stays out. Trial Balance's commitment-ledger audit is the strongest design the lab has measured; once a published piece prints a pooled rate with an interval, it enters through a new version. In SIGIL's after-the-fact audit arm, the paper itself calls the crossings post-hoc and unstable across seeds. The Delegation Cliff quality-floor shares describe the shape of the design space, and the price component already reads that campaign.

The index reads one lab's synthetic measurements under the lab's own conditions. The Delegation Cliff coefficients inside it are descriptive slopes. SIGIL and Trial Balance each ran one model in the measured seat, so the reading holds for those models. The balance point at 50 marks where the lab's measured conditions cancel. Outside this index it means nothing.

1. Only numbers from live public pieces on the freeze date enter.
2. The first paragraph of every release says the index reads the lab's own synthetic measurements.
3. The headline never appears without its band and the count of campaigns and units behind it.
4. Components with no band are named, and the release says the printed band is too narrow by their width.
5. When the band contains 50, the release says the reading cannot tell balance from imbalance.
6. The construction changes only through a new dated version, and the first release under it restates every earlier reading.
7. Someone who did not build the reading recomputes it from the construction page and the cited pieces before release.
8. A refuted result enters on the same terms as a supported one. SIGIL's refutation sits in oversight yield at full weight.
9. The builder had read every input before fixing the balance points, because the inputs were public. The registration binds every reading after the first, which was made with the inputs already known.

The lab studies how organisations hand work to AI agents and how they oversee it. Every campaign follows the same eight steps. If the lab tried to steer a result toward the answer it hoped for, the steps would leave a dated trace of the attempt.

During 2026 the verification pass on AGENESIS-2 found 95 duplicate pairs of simulations and moved a verdict from supported to refuted before the paper went out. Trial Balance's first attempt halted at its calibration gate with zero production units, and the gate rule was rewritten the same evening. SIGIL's registered prediction failed in every series, and it went out as a refutation. Chapter 11 lists every correction the pieces report.

The campaign chapters that follow share one layout. The question comes first, then what was registered before any unit ran, then what was measured and at what scale. The finding carries its number and, where the piece prints one, its interval. A chart rebuilt from the published numbers follows. Each chapter closes with what the campaign does not claim and with where the numbers were checked.

What happens to an industry when one company adopts AI agents before its competitors do? AGENESIS was the lab's first published campaign, and it asked that question of a simulated market.

The site records no pre-registration for AGENESIS and no verification status. The findings are in the piece. This chapter reports them with no registration line, since none exists on the record.

AGENESIS is an agent-based simulation of enterprise AI adoption. The published article reports 100 independent simulation runs across 4 industry verticals, under 5 adoption configurations and 3 macroeconomic conditions.

The firm that adopted first earned a premium of 210% over its competitors, and the market tipped toward one firm in 77% of the simulated markets. The lab's later campaign on sprawl cost reused the same simulator and added an agent lifecycle to it.

AGENESIS has no agent lifecycle. Agents are created once and never retired, and the AI cost a firm pays has nothing to do with how many agents it runs. A firm with fifteen agents and a firm with a hundred and fifty pay the same at the same level of adoption. The sprawl-cost campaign in Chapter 7 was built to fill that gap. AGENESIS prints no interval and no oversight quantity, so the Delegation Index leaves it out.

The site records no verification status for this piece, and the two numbers above are quoted from the published article.

A common resilience design runs the same model a second time, on different accelerators or in a second region, and treats the second answer as a check on the first. Civil aviation learned long ago that two identical computers fail the same way at the same moment. Flight control systems run on processors from different makers, with software written by teams kept apart, and the industry calls that dissimilar redundancy. This study asked whether a second copy of a model, on different hardware, makes different mistakes.

Ground truth is generated with each item, so the correct answer is known before any model sees it. No model grades another, and so there is no judge inside the measurement. The site records no pre-registration beyond that design. For each pair of models the study computed the phi coefficient on error indicators. Phi sits near zero when two models go wrong on different items and near one when they go wrong together.

Four model configurations scored the same 150 invoice-extraction items. The key comparison ran model A twice, in two builds with identical weights. The builds differed in quantisation and in the silicon and serving stack beneath them. Models B and C came from other families.

103 of the 150 items were unanimous. On 54 of them all four models were right. All four missed the other 49. Those items measure how hard an item is, so the headline uses the 47 items where the models disagreed.

Before conditioning, every pair looked correlated, from 0.556 to 0.827. On that reading you would give up on a second reviewer altogether.

On the contested items, the pair with identical weights stayed at +0.447, the highest in the matrix. The five pairs from different model families averaged −0.102, and model A's first build against model B sat at −0.469. Changes of machine and serving setup left the correlation standing. Only a change of model family moved it through zero.

• The same-family reading comes from one pair, the only two systems in the set with identical weights. One pair counts as an observation, and it would take more pairs before anyone quotes it as a rate.
• The five cross-family pairs run from −0.469 to +0.280. A mean of −0.102 sits inside a spread that wide and describes it poorly. Two families can still fail together; the reading covers these families on this task.
• The study ran one task, chosen because its ground truth cannot be argued with. Open-ended work is untested.
• The article also reported a model-free checker as a floor for independence. A later note retracted that sentence. Chapter 11 gives the details.

Model scoring ran through a separate verification path, and every model-pair correlation survived the later review that retracted the checker sentence.

Any organisation deploying AI agents is betting that pushing work further from human review costs less than keeping it close, and few of them put a price on that bet. This campaign tried to. Where does delegation stop paying, and which design choices buy the margin back?

Four predictions went on the record before the sweep.

• H1. The design space has a cliff, a sharp boundary between robust and fragile configurations.
• H2. Better observability outranks raw reviewer capacity.
• H3. Agent self-check is the dominant lever.
• H4. An audit death spiral forms, where eroding trust raises audit load until capacity saturates and quality falls.

The campaign simulated an agent organisation with twelve design dimensions, and this chapter turns on two of them, delegation depth and reviewer capacity. The sweep scored 90,880 configurations on the margin between the quality each organisation produces and the floor it must hold. It finished with zero error units. A revalidation certificate reran 200 random configurations from scratch: the median difference was 0.002 and the 95th percentile 0.0117, against a tolerance of 0.05.

Delegation depth carries the largest weight in the space, with a negative sign: each increment costs 1.50 on the margin. Reviewer capacity buys back the most at +1.46. Model capability at +0.95 and self-check calibration at +0.92 follow, close enough to read as tied. Task coupling is the second-largest cost, at −0.96.

The quality floor decides the failure geometry. At a 0.95 floor, 60% of the space is a broad transition band with no cliff. Raise the floor to 0.99 and the cliff appears, with 79% of the space fragile.

refutedH1 at the 0.95 floor. H2, H3 and H4 not supported.

The observability prediction failed. Capacity sits at +1.46, verification coverage at +0.31 and detection lag at −0.26. Interaction terms between observability and capacity came out real and positive, which makes observability a complement to reviewer capacity, and the hypothesis fails all the same. As for the spiral, mean margin rises across trust-response quintiles, even inside the high-stress stratum where depth and coupling are both high, so it never formed.

• The coefficients are descriptive slopes on the Sobol sample inside the transition band, n = 4,948. They describe how the margin moves where a boundary exists, and they carry no causal weight over the whole space.
• The 0.99 result rests on one 256-unit calibration sweep. The 0.95 result is replicated on the 8,192-unit Sobol set. The article gives the two legs different weight for that reason.
• Reviewer capacity is a parameter in this design. Reviewers here never tire.
• Capability and self-check differ by 0.034. The article reads them as tied.

Every result file carries a finite margin and a null error code, which is how the zero-error count was checked. The 200-pair revalidation certificate passed. The published coefficients come from the corrected band-only fit; Chapter 11 describes the correction that produced them.

Once a reviewer holds the power to stop an AI worker, the usual next step is to make it accountable for what it lets through. This campaign asked whether an AI supervisor authorises differently when it carries a running record of the damage its own past approvals caused. It also asked how the value of its review changes as decisions get harder to undo.

The hypothesis came from the Accountability Rent working paper. It predicted that review before commitment loses value on reversible decisions, turns positive past some level of irreversibility, and climbs steeply from there. A flat response falsifies it, as does a concave one or the absence of any crossing.

The output contract was frozen on 30 August 2026, before any harness code existed. It fixed the scoring and a gate that required the unsupervised worker to err between 10% and 35% on a pilot. It also made a rerun under a second, linear cost model mandatory. One amendment, recorded before the second pilot, changed only the task generator and harness capacity and pre-committed a stopping rule against retuning more than once.

An AI worker approved or rejected synthetic firm decisions across five tiers, from invoice approvals that reverse next cycle to public statements that cannot be taken back. The same base model sat in a second seat and reviewed it under four designs:

• no oversight;
• an after-the-fact audit of a 20% sample;
• review with the power to block before commitment;
• the same blocking review carrying a liability ledger of the harm its own past approvals caused.

Worker and reviewer share one model on purpose, so any difference comes from the incentive design. Every decision was scored against programmatic ground truth. The campaign ran 30,000 episodes on local hardware, in two full campaigns, one per cost model, with three seeds per cell.

refutedThe registered prediction failed in all 12 series, under both cost models.

Review never crossed zero, in any of the 12 registered series. Its value collapsed at the most irreversible tier, where the theory wanted it to rise, to −2.64 per decision against no oversight. The liability ledger made it worse, at −3.81.

At that tier plain review wrongly blocked 30.1% of decisions, and the ledger pushed the share to 42.7%, since refusing was the one action it never charged for.

A reviewer that can only block can fix one kind of mistake, a wrongful approval. The share of worker errors that were wrongful approvals fell from 93% at tier 1 to 1.4% at tier 5, one false approval against 68 false rejections.

• This is a controlled simulation with one open-weight model family in both seats, scored against constructed ground truth.
• The liability ledger is a thin, simulated form of accountability.
• A follow-up registered to test stronger models stopped before it ran an oversight trial. Four other models got between 97.3% and 100% of cases right unsupervised, which left a reviewer nothing to catch, so the result holds for this setting only.
• The after-the-fact audit arm shows positive cells in some series. Its seeds disagree on where and whether it crosses zero, and the paper reports those cells so nobody has to dig for them.
• The contract-clause tier produced no worker errors across both campaigns, so its value figures are pure oversight cost.

A separate verifier recomputed every table from the raw episode ledgers and found zero mismatches on 14,950 convex and 14,952 linear scored units, 29,902 in all. It also confirmed that the grid was complete and that no review unit carried ledger state. That pass surfaced one documentation defect in the tail pre-registration, recorded as erratum E1 and listed in Chapter 11.

The governance literature says an agent portfolio you cannot retire from fast enough costs more than proportionally as it grows, though nobody had put a number on it. This campaign asked how fast the cost of a simulated agent fleet grows with its size, and whether the answer depends on how the monitoring budget is set.

Seven hypotheses with frozen thresholds went on the record before the two seeds that count had ever run. The kill condition came from the review that commissioned the work: if cost turned out linear in agent count, the design was falsified and the project would retire.

H3, an ordering of the four factors, was registered as descriptive only.

In the simulation, agents ramp up and then drift silently out of spec, doing damage while nobody notices. A flagged agent queues for review and gets retired. Cost is the harm from degraded agents still running plus staff time spent reviewing. No cost term depends on how many agents exist, so any growth beyond linear has to come through the review queue and the detection lag, or through overlap between agents. 256 runs covered eight portfolio sizes from 57 to 787 agents, over an 18-month horizon in weekly ticks.

Under a flat monitoring budget, cost grows as fleet size to the power 1.4665, with a cluster-robust 95% interval of 1.4101 to 1.5230. Doubling the fleet multiplies cost by about 2.76. Where every agent carries its own check and review grows with the fleet, the exponent is 0.9001, with an interval of 0.8664 to 0.9337, about 1.87 per doubling.

You can see the mechanism in the detection lag. With a fixed inspection budget, the time from an agent going bad to someone noticing runs from 2.78 weeks at 57 agents to 22.49 weeks at 787. Under the flat budget, changing review capacity produced a bit-identical simulation in 55 of 64 matched cases, because the review queue never formed, which puts detection upstream of review.

refutedH4, the regime ceiling, after the duplicate correction. H6 refuted as well.

The independent check found 95 duplicate pairs among the 256 rows, 161 distinct simulations in all. Correcting for them left every point estimate in place and widened the intervals. That flipped H4 from supported to refuted: fitted on the four smallest sizes the exponent is 1.4949, on the four largest 1.3238, and the corrected intervals overlap by 0.0145. H6 failed too. Retirement policy moved the exponent by 0.0622 and overlap by 0.0892, both under the frozen 0.10, so the follow-on study will carry two factors.

• This is a calibration on one simulated industry, one company size, one degradation rate and one 18-month window. It was registered as a calibration that cannot confirm anything on its own.
• The value 1.47 awaits a confirmatory study, and until then the lab leans on the shape of the curve.
• The flattening at large sizes is an observed direction with a failed test.

An independent agent re-derived every number from the raw ledger without reading the analysis code. It found that only 161 of the 256 result signatures were distinct. The campaign's own guard had checked replicate distinctness inside each cell, and every duplicate pair sat across two cells. The paper prints the registered and corrected numbers together, and Chapter 11 sets out the correction.

An agent's log records what it did. It has no line for a step it skipped, so a reviewer finds the gap only by knowing the procedure and checking each step against it. Bookkeepers solved a version of this with the second entry. This campaign asked whether the same idea works for agents. If the layer that hands out the work writes down what the agent owes, and the harness writes down what the agent ran, can an auditor find skipped steps for a fraction of the reading cost by looking only where the two books fail to balance?

The registration predicted that imbalance-first audit would reach 0.80 omission detection at a third of log review's reading cost or less, at 8, 12 and 16 requisitions. A balanced book, it said, would hide a wrong amount carried on both sides. And a reader of the log would miss a skipped step far more often when the agent wrote a line claiming the step was done.

The first attempt halted at its calibration gate on 11 September with zero production units. Its gate had required a reading to move that the campaign existed to measure, so a strong true result would have failed it. The lab rewrote its gate rule that evening. The second attempt was registered and frozen before its first unit, with one added arm, a log reader told to tick off every step the procedure requires before it gives a verdict.

A procurement workflow with seven steps ran at seven lengths, from one requisition to sixteen. Five conditions were injected into each diary: no fault, a skipped step, a skipped step with a line claiming it was done, a wrong amount, and a wrong amount carried on both sides of the book. Four auditors read each diary under reading budgets from 200 to 12,800 tokens, seven for most arms. Log review reads the diary top down. The imbalance-first auditor opens the trial-balance report and goes on to read only the requisition that failed to balance. A random sample of the same size controls for the effect of reading less. The checklist reader gets the log reviewer's diary plus an instruction to mark every owed step present or absent.

The auditor was one open model under a fixed reply schema, on local hardware. It ran 18,360 audits, including 3,240 on diaries written by a different model running the workflow for real.

Imbalance-first reached 0.80 omission detection at the smallest budget, 745 prompt tokens at eight requisitions, and sat between 0.92 and 1.00 in every cell. Log review stayed under 0.80 at every budget and length, peaking at 0.58. Per thousand tokens read, imbalance-first produced about 21 times as many correct omission findings as log review at its best budget, 1.34 against 0.063.

The balance check has an exact blind spot. A wrong amount that enters before the work is assigned sits in both books, so the trial balance is clean, and the check found 0 of 1,044 of them. A full read of the diary finds those almost every time, because the vendor's quote still shows the true amount.

The cheapest result in the campaign came from the checklist instruction. With the whole diary in front of it, plain log review found skipped steps at 0.25, with a 90% interval of 0.19 to 0.31. The same auditor told to tick off each owed step found 0.58, with an interval of 0.48 to 0.67, and accused no clean diary at a full read on the primary seeds.

• One auditor model ran. The second registered family was excluded before its calibration gate, and the lab claims nothing about it.
• Log review never reached the bar, so the registered cost ratio is unbounded and the 21-times figure is the finite comparison to quote. The campaign cannot split the checklist's gain between the list and its definition of evidence.
• One workflow, one fault per diary, and real diaries only up to three requisitions. Nobody priced the cost of building a commissioning layer that writes obligations in ledger form.

An independent rescoring from the raw ledgers matched every point estimate, with 90% cluster-bootstrap bounds differing only by bootstrap noise.

Most decisions inside a governed business process are questions with consequences. Does this case have the evidence it needs? Should someone ask the supplier for a document, or think harder about the one on file? A decision head answers questions of that shape. You hand it the state of a case and a list of typed questions, yes or no or pick one of these, and it returns a probability for each answer, a number a workflow can threshold and audit.

Jev, a hosted service from TypeSafe AI, showed the shape. The lab built an open version that applies the same request and response pattern on an open-weights model running on hardware the operator owns. The project asked two things. Can a controller tell "this case needs a document nobody has" from "this case needs someone to interpret a document already on file"? And does an open, self-hosted head asked the same typed questions get there?

The head renders the state of a case once, as a shared prefix. Each question then goes in its own call, appended to that prefix, so no question's prompt contains another question's text. Each call asks for exactly one token at temperature zero and reads the model's token probabilities over the answers the question accepts. If none of the accepted answers appear, the head returns a flagged uniform distribution, so it never invents a number. Every decision writes an audit row with the question and its probabilities, raw and calibrated. The row also carries the latency and a hash of the exact request.

Five hypotheses with numeric predictions went on the record before any evaluation data existed. The first, discrimination, predicted the head's decision-class accuracy between 0.64 and 0.76 and required it to beat the rule table and the typed-sample arm with a case-clustered bootstrap interval excluding zero. Three adversarial reviews cleared the design, and the first two returned "must not run". A later registration set 0.04 as the wrong-claim rate that would trigger a redesign of the claim guard, and 0.02 as the bar a shipped head must meet.

The controller sits inside a synthetic supplier-onboarding workflow and picks the next of six approved actions: continue, retrieve a document, request one, consult an expert model, hand the case to a person, or claim the case complete. Every case is generated from templates with no model involved, so ground truth is correct by construction and no client data appears anywhere. The first round used 800 evaluation cases and a 200-case challenge set with contradictory evidence. A second registration retrained the head and tested it on 800 fresh cases. A third moved everything to a second process, accounts-payable exception routing, on 400 and 200 cases. All of it ran on local hardware.

refutedH1, discrimination, on the first registered split. The zero-shot head did not beat the rule table.

On 800 evaluation cases the zero-shot head scored 0.545 against the rule table's 0.575. The gap of −0.029 has a 95% interval of −0.060 to +0.001, and H1 was rejected. Completion at cost was rejected as well: the head completed fewer cases correctly and called the expert model about a hundred times as often as the rule table, 0.376 calls per case against 0.004. Its decision-class calibration error came in at 0.5247, more than six times the registered ceiling of 0.08.

The retrained head scored 0.728 on the 800 fresh cases, against 0.566 for the rule table, a gap of +0.161 with a 95% interval of 0.131 to 0.191. On the challenge set it scored 0.739 against 0.565, a gap of +0.171 with an interval of 0.115 to 0.224. A separately fine-tuned learned head scored 0.701 on the fresh cases. Its gap to the retrained head, −0.027 with an interval of −0.056 to +0.002, fails the project's own acceptance rule, so the learned head ships as experimental and the retrained head stays the default.

On the fresh cases, the retrained head wrongly claimed a case complete at a rate of 0.0466, above the 0.04 trigger. A taxonomy of its 37 wrong claims, checked independently, found the cause in the environment. In 31 of them the pack builder had padded the evidence pack with extra supporting documents. Of the 101 extra documents, 91 fail the harness's own validity check for entity and currency. The fix was registered before it was computed: the pack builder now checks every supporting document with the same predicate the ledger already used.

After the fix the wrong-claim rate falls to 0.0113 for the retrained head, 0.0088 for the rule table and 0.0163 for the learned head. Every case that changed moved from wrong to verified, and no other case moved. Both heads meet the 0.02 bar on the validated pack and miss it on the original pack. Nobody found the fix until the trigger had fired and its cause was traced.

Three guards were tried against wrong claims, and all three were retired. Voting across several readings of the pack separated wrong claims from right ones at an AUC of 0.56, below its registered gate. The deterministic evidence guard first reported 79 of 79 caught, until a review found its checks reused the functions that define a wrong claim; the lab withdrew the number as circular. Opening the cited document, a reading layer reached an AUC of 0.52 on its own and added nothing on top of the deterministic check. The validity check now lives inside the pack builder and calls no model.

On accounts-payable routing the head scored 0.650 and the rule table 0.648. The gap of +0.002, with an interval of −0.029 to +0.034, missed the registered bar, and the head's lead from the first process was gone. A learned head trained on onboarding scored 0.522 when pointed at the new process with no retraining. Retrained on 100 labelled cases from the new process, 271 decisions, it scored 0.663 and came level with the head. A version with every input from the judging head removed scored 0.660, which closed the question of whether the learned head was leaning on the head's own answers.

In the first round the open head changed its answer on 4.95% of repeated decisions, while a second campaign shared its endpoint. Re-measured with nothing else attached and one call in flight, it changed on 0.05% of repeats on both processes. At four calls in flight the figure rose to 3.40% and 1.95%, with the disagreements clustered on one worker thread, the mark of calls batched together. The shipped service now defaults to one call in flight, which costs throughput and leaves accuracy where it was. At the item level, the retrained head's probabilities were already calibrated: expected calibration error 0.0178 before any refit and 0.0143 after one.

Two open encoders released in September, encoder A and encoder B, ran on the same benchmark. Fine-tuned on 1,567 labelled onboarding decisions, encoder A scored 0.815 on the challenge set, above the retrained head. With only 201 decisions from the second process to learn from, it fell below the rule table there.

The open head competes on accuracy and on who owns the data and the tuning. A live case stays on the operator's network. Because the calibration fit runs on the operator's own labelled cases, it produces a reliability table an auditor can inspect, and each decision leaves an audit row behind it. To change behaviour, the operator relabels data. On speed, the hosted service answers a question in 0.35 seconds; the open head's fast mode took a median of 3.1 seconds under load on local hardware. A workflow gate fires about 3.4 times per case, inside steps that take minutes to days, so for most gates accuracy decides it. The code is public under Apache-2.0 at https://github.com/dtinholt/decision-head.

• Every case is synthetic, from one generator family, and the training labels and the scorer share one oracle. Real supplier files are messier.
• The second process shares the first one's blocker mix by construction. A process built differently is registered as future work.
• The retrained head clears its wrong-claim bar only on the validated pack, and the fix came after the trigger fired.
• The expert-consultation phase and its blind adjudication sample have not run.
• The head and the worker ran on one quantised base model, and nothing here measures another.

Every phase was rescored from the raw case files by a party that did not build the scorer, importing the scorer's own metric functions. The consistency and abstention re-measurements matched on 28 of 28 cells within a tolerance of 0.0005. The encoder runs were recomputed cell by cell within the same tolerance and audited for leakage and training overlap before anyone read a hypothesis.

Schouw is scheduled for 13 October. Its numbers stay out of this report until the piece is live, and it enters the Delegation Index at the first freeze after that date if it reads one of the five registered quantities.

The next Delegation Index reading freezes on 5 January 2027. Campaigns published by then enter under the rules in Chapter 1. A campaign that reads a quantity none of the five components covers enters only through a new dated version, and the release that first uses it restates the Q3 2026 reading beside the original.

The decision-head code is public under Apache-2.0 at https://github.com/dtinholt/decision-head (release v0.1.0, 7 October 2026). A transfer test on a process with a different blocker mix and obligation structure is registered, along with the expert-consultation phase that has not yet run.

The lab publishes its corrections, and the original number stays visible beside each one. Every entry below is reported in the piece it corrects or in a note attached to it.