Subomi Olagoke
Abstract
An attempt requires two separate efforts, to make a working artifact and to put it in front of anyone, and both draw on one finite budget. The optimal number of simultaneous attempts depends on their sum, while the heuristic most builders use depends on alone. The two used to agree closely because building dominated. Agent-assisted development cut by roughly an order of magnitude and left where it was, so the two prescriptions have come apart.
In simulation, as building gets cheaper the optimal attempt count rises from 4 to 48 across the range studied, shipped output saturates, and the success probability under build-capacity planning falls by more than two orders of magnitude, from 0.163 to 0.0006. The old heuristic does worst at the point where it is most tempting. I derive a closed-form prediction for the size of that error, and the simulation falsifies it; cost heterogeneity softens the error substantially.
I test the mechanism against a single-subject archive of 48 repositories over 21 months, with status notes written at the time, before outcomes were known. Of 17 projects the notes mark as stalled, 100% are stalled at a step that building cannot resolve, and 0% are stalled purely on more code. A strong concurrency effect also turns up, and I decline to claim it because it cannot be identified. I propose that the relevant kind of self-delusion here is a category error about which threshold effort is paying down, and that a probability error does not describe it.
1Introduction
People who build things are routinely given two pieces of advice that contradict each other. One is to be calibrated, since most attempts fail and yours probably will too. The other is to be relentless, since the people who succeed are the ones who kept starting things. Evidence supports both, and the conflict usually gets settled by calling it a matter of temperament.
Temperament has little to do with it. Both pieces of advice are one inequality read on two sides of a threshold, and the threshold has moved.
An attempt is two activities. Getting something to work and getting it in front of a person are separate efforts with separate costs, and one cannot stand in for the other. Call them and . For most of the history of software was much the larger of the two, which had a convenient consequence: you could plan your workload by asking how much you could build, and be approximately right about how much you could ship.
Agent-assisted development broke that. It reduced by something like an order of magnitude and left about where it was, because shipping is mostly made of things that do not compress: a credential another party issues, an app review on someone else's clock, a registration with a human in the loop, a decision only you can make, a customer who answers when they answer. This paper works out what that does to the optimal number of attempts, and to how well the felt sense of progress tracks real progress.
There are three contributions. The first is a two-threshold attempt model in which the optimum depends on the sum of the thresholds and the common heuristic on one of them, so the error between them scales inversely with build cost. The second is a simulation that measures the divergence and, along the way, falsifies the closed form I derive for it. The third is a single-subject empirical study in which the blockers were written down before the outcomes were known. That is unusual in this literature, and it removes the largest source of reconstruction bias.
2Related work
Four literatures border this one. Here is what each already covers.
The first is search-adjusted inference. When many hypotheses are tried and the best is reported, its apparent quality is inflated. The Deflated Sharpe Ratio [1] is the standard treatment in finance, and the garden of forking paths [2] is the general form. My own prior work [3] extends this to hypotheses proposed by language models, where the effective trial count cannot be observed directly. That work asks how much to discount a result given the search. This paper asks how much search to do.
The second is motivated belief. Overconfidence has been modelled as a self-commitment device with real instrumental value, which treats it as a bias that happens to pay. I frame it differently. With belief-dependent effort, the rational credence is a fixed point of an equation that can have several stable solutions. The optimist and the pessimist can each be accurate about the world their own belief produces, so neither can settle the disagreement empirically from where they stand.
The third is non-ergodicity. The argument that time averages and ensemble averages diverge under multiplicative dynamics [4] supplies a boundary condition this paper uses without extending: a high-belief equilibrium is only reachable if the transit is survivable, so it is ruin probability that bounds rational persistence, and expected value does not.
The fourth is entrepreneurial experimentation, where the option-value view of attempts (each one buys information more than it buys an outcome) is well developed. That literature does not yet account for the cost of buying an option having fallen sharply and asymmetrically. The asymmetry by itself changes the optimal policy even with all beliefs held fixed, and this paper sits in that gap.
3The model
3.1 Setup
An agent has a finite budget of non-delegable attention per period and starts attempts. Each attempt carries two costs drawn from independent lognormal distributions: , the effort to reach a working artifact, and , the effort to reach a user. Both consume , and an attempt ships only if both are paid.
Shipping also involves waiting on third parties. I model that as latency, since it consumes no . Latency matters for calendar time and for mortality but not for allocation, and I leave it out on purpose so that the allocation result cannot be produced by a queueing artifact.
Write for the ratio of mean costs. Agent assistance is a reduction in . The pre-agent regime is ; the current regime is .
Attempts are built in the order they are started until the budget runs out, and whatever remains is spent shipping, cheapest first. Cheapest-first is a generous assumption. It gives the widening strategy its best chance, so any penalty that strategy suffers is a lower bound. Each shipped attempt succeeds independently with probability , and the objective is the probability of at least one success, , maximised over .
3.2 Two policies
The optimal policy allocates against the total cost of a completed attempt. The intuitive policy, which answers the question "how many of these can I build?", allocates against build cost alone.
The ratio on the last line is the central structural claim, and it explains why the heuristic was ever any good. At , where building cost three times what shipping cost, the two prescriptions differ by 33% and the heuristic is a serviceable approximation. At they differ by a factor of eleven. People did not get worse at reasoning; the quantity the heuristic neglects went from negligible to dominant.
3.3 What the closed form gets wrong
The expression above assumes homogeneous costs. The simulation contradicts it, and the way it fails is informative. The closed form predicts the error ratio grows from 1.33 to 11.00 across the range studied, while the simulated ratio grows only from 1.75 to 4.17.
With heterogeneous costs and cheapest-first shipping, a widened portfolio is not penalised uniformly. Starting more attempts also samples more of the low-cost tail of the shipping distribution, and some of those attempts ship almost for free. Heterogeneity therefore partly hedges against over-widening, and the closed form is better read as an upper bound on the error than as an estimate of it. I keep it because it gets the mechanism right even though it gets the magnitude wrong, and because the bound is what a reader would derive first.
4Simulation results
Parameters: in units of mean shipping cost, sigma 0.45 lognormal on both costs, per shipped attempt, 20,000 Monte Carlo draws per cell, searched over 1 to 90.
| r | M* | shipped at M* | P at M* | M_build | shipped at M_build | P at M_build | error ratio | closed form |
|---|---|---|---|---|---|---|---|---|
| 3.0 | 4 | 3.6 | 0.259 | 7 | 2.23 | 0.1630 | 1.75 | 1.33 |
| 2.0 | 6 | 5.1 | 0.345 | 10 | 1.91 | 0.1406 | 1.67 | 1.50 |
| 1.0 | 10 | 8.4 | 0.500 | 20 | 1.11 | 0.0844 | 2.00 | 2.00 |
| 0.5 | 15 | 12.0 | 0.630 | 40 | 0.50 | 0.0391 | 2.67 | 3.00 |
| 0.3 | 21 | 14.7 | 0.704 | 67 | 0.21 | 0.0163 | 3.19 | 4.33 |
| 0.1 | 48 | 20.7 | 0.821 | 200 | 0.01 | 0.0006 | 4.17 | 11.00 |
Table 1. As building gets cheaper the optimal attempt count rises steeply and success under optimal allocation improves from 0.26 to 0.82. Under build-capacity planning it collapses from 0.163 to 0.0006. The two policies coincide near parity and diverge in both directions from it.
There are three results, listed here in order of how much weight they can bear.
Result 1 is that the optimal attempt count rises, from 4 to 48 as falls from 3.0 to 0.1. It runs against the usual scolding. Cheap building does mean you should start more things, "focus on one thing" is bad advice in this regime, and the relentless camp has the direction right.
Result 2 is that shipped output saturates. It goes from 3.6 to 20.7, sublinear throughout, approaching . The ceiling on how much reaches a person is set entirely by the threshold that did not fall, and adding build capacity does nothing to raise it.
Result 3, the most consequential, is that the penalty for the old heuristic grows as the heuristic becomes more attractive. Success probability under build-capacity planning falls from 0.163 to 0.0006, a factor of 270. The regime that makes it feel possible to start forty things is the regime in which starting forty things does worst.
4.1 Robustness and a real boundary
Sweeping over {10, 20, 40}, over {0.03, 0.08, 0.20} and sigma over {0.25, 0.45, 0.80}, both claims hold jointly in 21 of 27 configurations. All six failures have sigma 0.80 with at most 20, where the optimum is censored at the search ceiling.
These failures mark a boundary condition and are not noise. With high cost heterogeneity and a small budget, choosing the right number of attempts gives way to cost arbitrage: start very many, ship only the cheapest tail, and ignore everything else. Widening is then correct almost without limit, and Result 1 has no interior optimum to find. The regime is real and not a modelling artifact, and it identifies who the paper does not apply to. If your attempt costs vary by more than roughly a factor of ten and your budget is small relative to them, spray. The prescription here holds for moderate heterogeneity, which is the common case.
5Empirical study
5.1 Data
The data are a single subject's complete project archive: 51 repositories, of which one has no readable history and two are clones of others, leaving n = 48 spanning November 2024 to August 2026. For each, the full commit history gives first and last activity, commit count, distinct active days, and lines changed. Alongside the archive is a set of 74 status notes written during the work, before outcomes were known.
Those notes are why the archive is worth studying despite n=48 and a single subject. Work on motivated belief usually has to reconstruct prior beliefs after the outcomes are known, which contaminates the very variable of interest. Here the blockers were written down at the time.
One measurement problem has to be reported first. Commit-derived effort measures are not valid for this subject's recent work. First commits show entire subsystems arriving at once: one project's initial commit is 137 files and 12,916 insertions, and another's complete history is a single commit of 76 files made on the day the work finished. When a project is mostly agent-built in one session, the repository is often initialised at or after completion, so first-commit date is not a start date and commit counts understate effort severely. A study of this kind that uses commit volume as an effort proxy without checking for this will conclude that recent projects were barely worked on. Several were built intensively in hours.
5.2 Primary result: what stalled projects are stalled on
The study's main finding comes from coding the notes by blocker type. Initial automated coding returned 18 stalled projects. An audit against the full notes found one false positive, where a regular expression matched PARKED inside the string UN-PARKED and read a negation as a confirmation. Corrected, n = 17. I re-coded three ambiguous cases by hand with written reasons.
| Blocker category | n | share | Examples from the notes |
|---|---|---|---|
| Third-party external | 14 | 82% | An API key, a testnet faucet, agent registration, marketplace approval, an APNs auth key, server provisioning, a domain |
| External and build | 2 | 12% | A missing frontend plus an undeployed backend; a conversion pending plus a go-ahead |
| Own non-delegable step | 1 | 6% | A one-week validation test only the subject can run. No third party, no code |
| Purely more code | 0 | 0% | None |
| Involves a non-automatable step | 17 | 100% | Every stalled project without exception |
Table 2. Blocker classification of 17 stalled projects from contemporaneous notes. The finding got stronger after an audit that corrected an error against the hypothesis.
Only 13 of 48 projects, 27%, ever received sustained iteration after their initial build. All 17 that the notes mark as stalled are stalled at a step that no amount of building resolves, and none is waiting on code.
5.3 A strong result I decline to claim
Projects begun while many others were active were far less likely to get sustained attention. Restricting to a 90-day minimum observation window to handle right-censoring, the Spearman correlation between concurrency and post-burst active days is −0.60, and 82% of projects in the low-concurrency half were sustained against 25% in the high half.
I do not claim it, and splitting by era shows why.
| Era | n | concurrency range | sustained | mean days after burst |
|---|---|---|---|---|
| before 2026-03 | 8 | 1 to 8 | 7 / 8 | 30.8 |
| 2026-03 to 2026-04 | 12 | 9 to 25 | 6 / 12 | 7.8 |
| 2026-05 | 7 | 23 to 26 | 0 / 7 | 0.4 |
Table 3. Concurrency does not vary meaningfully within eras, because the subject accumulated projects monotonically. Concurrency and calendar time are the same variable in this dataset and cannot be separated.
There is no low-concurrency 2026-05 project to compare against. The Spearman correlation between concurrency and start date is +0.35, so any apparent effect is partly a time trend. Given the measurement problem above there is also a credible rival explanation: a project with no activity after its burst may have been finished in one session, and need not have been starved of attention. A correlation of −0.60 that cannot be decomposed is not evidence, and reporting it as evidence would repeat the error this paper is about.
5.4 Calibration, and what is not identified
Two observations cannot identify three parameters. Normalising in units of shipping cost and fixing , the value of that reproduces 13 shipped is 0.111 at = 14, 0.148 at 16, 0.223 at 20, and 0.336 at 26. For this subject, then, shipping costs between three and nine times what building costs. The point estimate is not identified, but the order of magnitude is. The observed = 48 sits between and , at neither extreme, so the heuristic has captured the subject partly but not fully.
6Discussion
6.1 Delusion as a category error
I began by treating self-delusion as a probability error, a credence higher than the evidence licenses. The data do not support that as the failure at work here, and a more specific account fits better.
Building feels like progress toward shipping. For most of the history of the craft that feeling was a decent estimator, because the two thresholds moved together and building was the larger. When collapsed and did not, the felt sense of progress came loose from actual progress. A belief calibrated to the old ratio became systematically wrong without ever feeling wrong, since the sensation it tracks is now produced faster than before.
The delusion is not about probability. It is a category error about which threshold effort is paying down.
Unlike a story about miscalibrated probability, this account can be tested. It predicts that stalled work clusters at the non-automatable step, which Table 2 finds at 100%, and that the felt-progress signal correlates with build activity and not with distance to a user.
6.2 Predictions
- Aggregate inventory: public repository counts per developer should have risen sharply since agent assistance became common, while shipped-artifact counts stay roughly flat, because by Result 2 the ceiling did not move.
- Blocker composition: the share of abandoned projects blocked on non-code steps should rise over time within individual histories, and not only across them.
- Domain gradient: the effect should be strongest where is most rigid. Regulated software, app stores, hardware and enterprise sales should show the largest gap, and a personal script published to a package registry the smallest.
- Intervention: capping concurrent attempts at the shipping-constrained optimum, in place of the build-constrained one, should raise shipped output without raising effort. This can be tested prospectively and is the obvious next study.
6.3 Limitations
Several of these are severe. The study has n = 48, one subject and no control, so nothing here establishes generality; the archive supports a mechanism, not a population estimate. Blocker coding is partly manual and was done by a party to the analysis. The audited reasons are published so the coding can be contested, but it is not blind. The concurrency channel is unidentified and is reported only to record that it was looked for. Success probability is assumed independent across attempts, which understates the value of concentration, since real attempts share learning. Effort is treated as a single fungible budget, when in practice building and shipping draw on partly different capacities. And the closed form in section 3.2 is falsified by my own simulation and kept only as a bound.
The strongest claim the evidence supports is the composition result in Table 2. Everything about magnitudes is model output, and the model is a first draft.
7Conclusion
Being calibrated and being relentless are not opposing temperaments. They are the same inequality evaluated on two sides of , and the advice feels contradictory because most people compute it with one term missing.
Cheap building does mean you should start more things. That part of the optimistic instinct is correct, and the simulation supports it strongly: the optimal attempt count rises more than tenfold across the range studied. It does not mean you should start as many as you can build. In the simulation that number is 2.7 to 4.2 times too large in the agent-assisted regime (r from 0.5 down to 0.1; 1.75 to 4.17 across the full range studied), and the gap widens as building gets cheaper.
What the archive supports is less comfortable. Forty-eight repositories is not evidence of a lack of discipline; it is close to a rational response to a real collapse in the cost of an attempt. The error is subtler than a character flaw and easier to correct. It is having re-optimised against the threshold that moved, while the one that binds stayed where it was.
References
- D. H. Bailey and M. López de Prado. The Deflated Sharpe Ratio: correcting for selection bias, backtest overfitting and non-normality. Journal of Portfolio Management 40(5):94–107, 2014. doi:10.2139/ssrn.2460551
- A. Gelman and E. Loken. The garden of forking paths: why multiple comparisons can be a problem, even when there is no “fishing expedition” or “p-hacking” and the research hypothesis was posited ahead of time. Unpublished manuscript, Department of Statistics, Columbia University, 2013. sites.stat.columbia.edu/gelman/research/unpublished/forking.pdf
- S. Olagoke. How many strategies did you really try? Effective trial counts for LLM-proposed backtests. System report, 2026. subomi.net/papers/ayo-effective-trials-llm-search
- O. Peters. The ergodicity problem in economics. Nature Physics 15:1216–1221, 2019. doi:10.1038/s41567-019-0732-0
Appendix. Reproduction
All simulation figures come from sim/fast.py at a fixed seed. A slower, independently written reference implementation lives in sim/model.py. Agreement between the two is the only check performed on the simulation code, and a third implementation would be worth having.
data/projects_raw.json 51 repos, raw git statistics
data/projects.json 48 after dedupe, concurrency + sustained
data/labels.json initial automated blocker coding
data/labels_audited.json corrected, audit_reason on every change
data/stalled_audit.json the 17, with full note text
AUDIT.md 1,902 lines of evidence behind each call
scripts/extract.py git history extraction
scripts/analyze.py concurrency and sustained-iteration measures
scripts/fixed.py censoring and confound checks
scripts/label.py blocker coding rules
sim/model.py reference implementation, readable
sim/fast.py vectorised, used for all reported figures
sim/calibrate.py Table 1, calibration fit, robustness sweep