Day One Great Research · Working Paper No. 1

The Day One Great Decision Loop

An evidence-informed simulation of research, simulation, independent review and intent checks in human–AI decisions

Claude (AI researcher) with Aaron Chandler · Published October 15, 2026 · Version 3, after three reviews

Reviewed by independent AI agents in three rounds; not externally peer reviewed. See the review and our responses.

Abstract

At base settings, a tiered decision loop cut modeled decision loss by 23.9% against no loop, and kept 98% of the full loop's benefit for 77% of its added time. The loop runs research, simulation, an intent check and a report on every decision, and adds an independent AI reviewer on game-changing ones.

We built a Monte Carlo model in which each step removes one named source of error and can also cause harm. Published studies and 16 catches recorded during our own build inform its parameters; most remain stated assumptions. We ran 200,000 decisions at base settings and 10,000 random parameter settings.

Across those settings the tiered loop's median benefit was 17.0%, its middle 90% ran from −4.8% to 34.9%, and it reduced loss in 90.4% of them. Independent review is the fragile step: with a reviewer from the same model family, it stops reducing loss once a false alarm changes the choice in more than about 16% of reviewed game-changing decisions. Against the light loop, which skips review, the tier wins at base, but its review step helped in only about 58% of settings; the light loop is the safer choice while the reviewer's false-alarm rate is unknown or high.

We recommend keeping the tier on one condition, that wrong review findings change fewer than 1 in 6 reviewed decisions, with the light loop as the fallback; acting on a reviewer's finding only when evidence backs it; using a reviewer from another model family where possible, and replacing the assumptions with 90 days of logged decisions.

1. Introduction

A human–AI founding team makes dozens of decisions a week, and a few of them shape the company. On Oct 15, 2026, Day One Great adopted a written decision loop for every recommendation its AI co-founder makes: research, simulate, bring in an independent reviewer for game-changing calls, check the work against the stated intent, then report.

This paper asks whether that loop is worth its cost. We model each step as a remedy for one named source of error and as a possible source of harm, inform its parameters with published studies and with the first two days of our own build (Oct 14–15), and test it across 10,000 random parameter settings.

Three questions guide the work:

1. How much decision loss does each step remove, and how much time does it cost?
2. Does the tiered policy (all five steps only for game-changing decisions) keep most of the full loop's benefit at a lower cost?
3. Under which assumptions does the loop stop paying off?

The loop matters more for an AI agent than for a person in two specific ways. A language model's knowledge stops at a training cutoff, and models tend to rate their own work too kindly. Each failure has a direct, testable remedy in the loop: research for the first, an independent reviewer for the second.

2. Related work

Each step of the loop answers a documented failure, and the literature also documents where each remedy falls short.

Research against stale knowledge (step 1). Retrieval improves accuracy on knowledge-intensive tasks (Lewis et al., 2020). A model's effective knowledge cutoff often falls earlier than its reported one (Cheng et al., 2024). Retrieval narrows the recency gap but does not close it: with standard retrieval, one model scored 52.8% on 2021 facts and 26.6% on 2025 facts (LiveSearchBench, 2025).

Simulation and mechanical models (step 2). Across a meta-analysis, statistical formulas beat human judgment in 33–47% of studies and lost in 6–16%, about 10% more accurate on average (Grove et al., 2000). That evidence compares clinicians with formulas, so it supports the direction of step 2, not its size. We use Monte Carlo simulation (Metropolis & Ulam, 1949) and global sensitivity analysis (Saltelli et al., 2008).

Self-review is weak (step 4's limit). Without external feedback, models struggle to correct their own reasoning, and performance sometimes falls (Huang et al., 2024). Self-feedback helps where criteria are clear, about 20% absolute on average across tasks (Madaan et al., 2023), and reflection on outside signals helps agents (Shinn et al., 2023). As judges, models favor their own outputs (Zheng et al., 2023; Panickssery et al., 2024).

Independent review helps, but same-family reviewers share errors (step 3). Combining independent forecasts improves accuracy (Clemen, 1989), and in a formal model diverse solvers can beat the most able ones (Hong & Page, 2004). Multi-agent debate improves factuality and reasoning (Du et al., 2024). But on one benchmark, when two models both erred they gave the same wrong answer 60% of the time (E. Kim et al., 2025). In a 2026 workshop study, verifiers from another model family correlated less with the generator than same-family verifiers, 0.54 against 0.77 as reported (Mueller et al., 2026). Errors a model repeats consistently evade self-checks, while a separate verifier catches more (Tan et al., 2025).

Software engineering shows the same pattern. Inspections of one 1975 program found 82% of its errors before machine testing (Fagan, 1976), while modern code review finds fewer defects than developers expect (Bacchelli & Bird, 2013).

Intent checks and prospective hindsight (step 4). Imagining that a plan has already failed raises correct identification of reasons by 30%, in Klein's account of Mitchell, Russo and Pennington (Klein, 2007). Structured judgment reduces unwanted variation between decisions (Kahneman et al., 2021). Training and teaming improved forecasting accuracy (Mellers et al., 2014), though a 2025 reanalysis found those effects shrank or reversed under controls (Hauenstein et al., 2025).

Reporting to the person (step 5). In a study of 308 people, explanations raised agreement with wrong AI answers from 78.2% to 82.8%, while showing sources lowered it to 68.2% (S. S. Y. Kim et al., 2025). A report helps the person catch errors only when it shows sources and assumptions, not just reasons. Our model lets this step help or hurt.

3. The decision loop

Every recommendation runs research, simulation, an intent check and a report; only game-changing decisions add an independent review by a fresh agent.

Aaron Chandler set the gate's definition; the agent applies it and states which tier it used. Each step has one output: cited sources, compared outcomes, review findings, a yes or a revision against the stated intent, and a report with sources and assumptions.

4. Model

Each decision is a choice among K = 4 options; the agent picks the option it estimates best, and loss is the value given up plus the cost of any defect that ships. Every loop step changes one term of the estimate, and every step can also do harm.

Options and stakes. A decision is game-changing with probability g. Routine decisions have stakes s = 1; game-changing stakes are lognormal with mean S. True option values are scaled standard normals:

The agent's estimate. The agent sees each option through noise, a blind spot it shares with its own self-checks, and possibly an outdated fact that overrates one option j:

Here T is the objective the agent optimizes, ε is noise with standard deviation σ, β is a blind spot with standard deviation σ_b, and H collects harms from the steps themselves.

Step 1, research, removes the stale fact with probability d_R. With probability p_bad it imports a misleading source, which overrates a random option by Δ.

Step 2, simulation, removes a share φ of the noise variance. With probability p_m its model is wrong, which overrates a random option by Δ_m while still feeling precise:

Step 3, independent review, averages the agent's view with a reviewer whose blind spot correlates with the agent's at ρ:

This treats the reviewer as forming a full second estimate of every option, which favors review; a reviewer who only critiques the chosen option would add less. With probability p_fa the reviewer raises a false alarm that moves the choice to the agent's second-best option.

Step 4, the intent check, catches a misread objective with probability q_I. It can also do harm: with probability p_oc it "corrects" a correct reading into a wrong one, which the person catches at rate h_m.

Misread objectives. With probability p_mis the agent optimizes the wrong objective, T = 0.3V + √0.91·sZ with Z standard normal, unless someone catches it. Step 4 catches it with probability q_I, the reviewer with q_IR(1 − ρ/2), and the person with h_m, which rises when step 5 is used.

Hidden defects. With probability p_d the chosen plan carries a defect costing c·s·u, with u uniform on 0.5–1.5. A caught defect costs a tenth of that to rework. A share κ of defects is subtle enough to defeat every AI check at once, so the AI checks' detections are correlated; only the person can catch those:

Here q_S is the self-check rate (step 4), q_R the reviewer's rate (step 3), and h the person's rate: h_loop with a step-5 report, h_base without one. Because explanations can raise over-reliance, Section 8 lets h_loop fall below h_base.

Loss, cost and efficiency. For a policy π we estimate expected loss and hours per decision, then the loss avoided per added hour:

Definitions. Loss is measured in units of one standard deviation of a routine decision's option values. Loss reduction is the mean, over replications, of 1 − L_π / L₀. A severe failure is a game-changing decision whose loss exceeds its stakes. Hours per decision include the 0.5 hours a decision takes without the loop.

Runs and intervals. Policies share the same random draws (common random numbers), so differences between policies are not sampling noise. The main run uses 40 replications of 5,000 decisions at base parameters. Its 95% intervals are normal intervals across those replications: they measure simulation noise only, not uncertainty about the parameters, which Section 8 addresses.

5. Parameters and evidence

No parameter is measured directly. Published studies guide the direction and rough size of eight, our build guides four, and the rest are stated assumptions; Section 8 varies every one across its full range.

Four more parameters complete the model: the size of a stale belief (Δ = 1.5, range 0.75–2.5), the size of a simulation error (Δ_m = 1.0, range 0.5–2.0), the defect cost (c = 0.8 of stakes, range 0.4–1.5, times a uniform 0.5–1.5 draw), and the person's chance of catching a misread objective (h_m = 0.30 bare, range 0.2–0.4; 0.45 with a report, range 0.25–0.55). The code and stored results are in the repository, in research/code/wp1.

6. Results

At base parameters the tiered loop cut modeled loss by 23.9%, close to the full loop's 24.4%, at 1.86 rather than 2.26 hours per decision. The light loop, which skips review, cut it by 19.6% at 1.66 hours. Simulation noise on these figures is about ±0.9 points; the bars below show the much wider spread across parameter settings.

Across 10,000 random settings, the median benefit was 17.0% for the tiered loop, 16.1% for the full loop and 15.3% for the light loop. In the middle 90% of settings the light loop never did worse than no loop; the tiered and full loops sometimes did, through review false alarms (Section 8).

At base, severe failures on game-changing decisions fell from 27.9% to 19.2%, and defects reaching the final result fell from 22.2% to 15.2% of decisions.

At the margin, review on game-changing decisions avoided 0.30 units of loss per added hour; extending review to routine decisions avoided 0.017, about one eighteenth as much. In 61% of the 10,000 settings, review was worth more per hour on game-changing decisions than on routine ones.

At base, four steps each add 4 to 5 points: the report (4.7), the intent check (4.6), review on game-changing decisions (4.2) and research (4.0). Simulation adds 1.7, because a wrong simulation model sometimes misleads with false precision.

7. Case evidence from the Day One Great build

Of 16 recorded catches during the Oct 14–15 build, independent review found the most serious by the author's own classification: a privacy failure after release, and 20 code issues across two changes. The loop was written down on Oct 15, so earlier rows show its steps in informal use; rows naming the person or live monitoring fall outside the loop, and the author classified every row after the fact.

Counting every step a row names (some name two): research appears in 4 rows, simulation in 3, independent review in 3 (holding 20 code issues and the privacy failure), the intent check in 6, live checks in 2, and the person in 1. The two live-check rows were found only after release; no step before release replaces watching the running system.

8. Sensitivity

Within the stated ranges, the tiered loop reduced loss in 90.4% of 10,000 random settings, with a median of 17.0% and a middle 90% from −4.8% to 34.9%. Severe failures on game-changing decisions fell in 85.7% of settings. These shares describe the ranges we chose, not probabilities about the world.

The reviewer's false-alarm rate matters most. With a same-family reviewer, review on game-changing decisions stops reducing loss once a false alarm changes the choice in more than about 16% of reviewed decisions; on routine decisions the line is about 12%. This is a rate per reviewed decision, not the share of a reviewer's findings that are wrong. Counting the time review takes, both lines sit lower still.

In the first 3,000 of those settings, adding review to routine decisions made results worse in 61% of them, and review on game-changing decisions did so in 42%, mostly where false alarms were frequent. We test false-alarm rates up to 40% on purpose: the rate is not yet measured.

With everything else at base, the false-alarm rate alone moves the benefit from 29.8% to 4.5%. In the global analysis it also has the strongest rank correlation with the benefit (−0.53), ahead of the defect cost (0.25), the person's catch rate with a report (0.22) and the share of defects no AI check can catch (−0.21). The base value here, 23.7% from 200,000 decisions, sits inside the main run's simulation interval.

9. Limitations and threats to validity

The results show what follows from a stated model, not what the loop has been proven to do; five limits matter most.

1. Structure drives the result. Each step is modeled as a remedy with one matching harm. Review is modeled as a full second estimate of every option, which favors it; a critique of the chosen option alone would add less.
2. Most parameters are assumptions. Section 8 varies all of them, but the ranges are themselves judgment calls, and the shares of settings it reports depend on them. Loss is in model units, not dollars or days.
3. The case series is small and self-assessed. It covers 16 catches by one team over two days, with no control group. The agent whose process is under study classified the rows, and Section 2 shows models judge their own work too kindly.
4. The reviewer is the same model family. We set ρ = 0.77 from one workshop study. A reviewer from another family is untested here.
5. Hours understate cost. The model counts working hours, not delay or attention spent reading reports, and the break-even false-alarm rates ignore time altogether.

Some sources need care. The 30% premortem figure is Klein's account of an earlier study we could not open. The 0.77 correlation comes from a 2026 workshop paper whose page does not define the measure. The 60% shared-error figure comes from one benchmark. The 82% inspection figure comes from one 1975 program. The forecasting-training effects are contested by a 2025 reanalysis.

Conflict of interest. Claude designed the loop, built the model, and wrote this paper. An independent AI agent reviewed it (see Review and responses); it has not been externally peer reviewed.

10. Conclusion and recommendations

The tiered loop cut modeled loss by 23.9% at base, beat no loop in 90% of tested settings, and beat the light loop at base. Across settings, though, its review step helped in only about 58%, and the light loop never fell below no loop in the middle 90%. So we keep the tier on one condition, with the light loop as the fallback, and act on five points, most of them aimed at its one fragile step.

1. Keep the tier. Review on routine decisions earns about one eighteenth as much per hour and made results worse in most tested settings.
2. Act on a reviewer's finding only with evidence. Each finding needs a failing test, a cited source or a reproducible check before it changes the plan; that is how the false-alarm rate stays under the 16% line.
3. Measure how often a wrong review finding changes a decision. If that happens in more than 1 in 6 reviewed game-changing decisions, switch to the light loop, with review advisory only, until the rate falls. This is the condition the tier depends on.
4. Use a reviewer from another model family for the highest-stakes calls when one is available, to lower shared errors.
5. Keep the intent check and the report with sources. Each adds about as much as review, for about two-thirds of its average time.

The model's assumptions should give way to measurements. We will log every decision's tier, what each step caught, each review finding accepted or rejected and whether it proved right, and the hours spent. Ninety days of logs, starting Oct 15, 2026, can replace most of the assumed parameters in Section 5.

Review and responses

An independent AI referee, who had not seen the work, reviewed the first draft on Oct 15, 2026, and recommended major revision. It reran all four scripts, which reproduced byte for byte, and checked eight citations against their sources. This version answers every point.

The revisions lowered the base benefit from 31.2% to 23.9%, the game-changing review break-even from 23% to 16% false alarms, and the share of settings where the loop helps from 99.4% to 90.4%. The recommendation to keep the tier stands; the recommendations on review became stricter.

In a second round the same referee reran every script into a fresh copy (results again byte-identical), confirmed the published code matches the files, and rated the six major points resolved or mostly resolved. It recommended minor revision. Its five remaining points are fixed here: the title no longer says "calibrated", the conclusion compares the tier with the light loop, an unsupported chance baseline is gone, and a chart caption and title are corrected.

A third independent review, of the version prepared for the website, found one more error: the false-alarm threshold had been described as a share of the reviewer's findings, but the model measures the share of reviewed decisions that a false alarm changes. The wording is corrected throughout, including the operating rule in Section 10. It also found that the review-harm figures came from the first 3,000 of the 10,000 settings, not from new ones. Separately, drawing the web figures from the stored results exposed one step value rounded wrongly (4.3 instead of 4.2). Both are corrected.

References

Every source below was opened and checked on Oct 15, 2026; notes mark the six that need care.

1. Bacchelli, A., & Bird, C. (2013). Expectations, outcomes, and challenges of modern code review. ICSE 2013.
2. Cheng, J., Marone, M., Weller, O., et al. (2024). Dated data: Tracing knowledge cutoffs in large language models. COLM 2024.
3. Clemen, R. T. (1989). Combining forecasts: A review and annotated bibliography. International Journal of Forecasting, 5(4), 559–583.
4. Du, Y., Li, S., Torralba, A., et al. (2024). Improving factuality and reasoning in language models through multiagent debate. ICML 2024, PMLR 235, 11733–11763.
5. Fagan, M. E. (1976). Design and code inspections to reduce errors in program development. IBM Systems Journal, 15(3), 182–211. The 82% figure is inspection efficiency on one program.
6. Grove, W. M., Zald, D. H., Lebow, B. S., et al. (2000). Clinical versus mechanical prediction: A meta-analysis. Psychological Assessment, 12(1), 19–30.
7. Hauenstein, Thomas, Illingworth, et al. (2025). Rethinking the role of teams and training in geopolitical forecasting. Psychological Science, 36(1). Title shortened as listed on the publisher's page.
8. Hong, L., & Page, S. E. (2004). Groups of diverse problem solvers can outperform groups of high-ability problem solvers. PNAS, 101(46), 16385–16389.
9. Huang, J., Chen, X., Mishra, S., et al. (2024). Large language models cannot self-correct reasoning yet. ICLR 2024.
10. Kahneman, D., Sibony, O., & Sunstein, C. R. (2021). Noise: A flaw in human judgment. Little, Brown Spark.
11. Kim, E., Garg, A., Peng, K., & Garg, N. (2025). Correlated errors in large language models. ICML 2025, PMLR 267, 30038–30066. The 60% figure comes from one benchmark.
12. Kim, S. S. Y., Vaughan, J. W., Liao, Q. V., et al. (2025). Fostering appropriate reliance on large language models: The role of explanations, sources, and inconsistencies. CHI 2025.
13. Klein, G. (2007). Performing a project premortem. Harvard Business Review, September, 18–19. Read in a third-party reproduction; its 30% figure cites Mitchell, Russo and Pennington (1989), which we could not open.
14. Lewis, P., Perez, E., Piktus, A., et al. (2020). Retrieval-augmented generation for knowledge-intensive NLP tasks. NeurIPS 2020, 33, 9459–9474.
15. LiveSearchBench (2025). arXiv:2511.01409. Authors not shown on the page we opened.
16. Madaan, A., Tandon, N., Gupta, P., et al. (2023). Self-Refine: Iterative refinement with self-feedback. NeurIPS 2023, 36.
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20. Panickssery, A., Bowman, S. R., & Feng, S. (2024). LLM evaluators recognize and favor their own generations. NeurIPS 2024, 37.
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23. Tan, Sun, Liu, et al. (2025). Too consistent to detect: A study of self-consistent errors in LLMs. EMNLP 2025.
24. Zheng, L., Chiang, W.-L., Sheng, Y., et al. (2023). Judging LLM-as-a-judge with MT-Bench and Chatbot Arena. NeurIPS 2023, Datasets and Benchmarks.

How to cite

Claude, & Chandler, A. (2026). The Day One Great Decision Loop: An Evidence-Informed Simulation of Research, Simulation, Independent Review and Intent Checks in Human–AI Decisions (Day One Great Working Paper No. 1). Day One Great, ChiefOS, Inc. https://dayonegreat.com/research/decision-loop

The text and figures are © 2026 ChiefOS, Inc. Quote short passages with a link back. The model code in research/code/wp1 is MIT-licensed; run it to reproduce every number here. Claude is an AI model made by Anthropic; Anthropic has not reviewed or endorsed this paper.