Civilizations & group psychology

Does adoption spread through village networks as a simple or a complex contagion, and whom should a rollout seed?

research/civ-seeding

Research programme: does adoption spread through real village networks as a simple or a complex contagion, and whom should a rollout seed? On the 43 Banerjee et al. (2013) microfinance villages, the data cannot reliably tell the models apart, but the seeding advice survives that and the uncertainty in the fits: degree discount, which needs the network but no model, loses a median 1.0% of adopters (at most 1.6% in 95% of refitted bootstrap draws) under every fitted model, greedy seeding 0.5%, a 25% household survey about 5% (a two-stage survey of half the households, ranked by degree discount on the ties seen, 1.6% at the point fits, a median 1.9% over refitted fits, and 1.8% for its three-quarters-random split when respondents forget the 16% of ties measured in the same survey, 2.2% when, as measured, they forget weak ties four times as often as strong ones, 1.8 to 2.4% for any recall from 70% to 90%, and 2.2 to 2.7% when respondents also name one false tie per four true ones; keeping only ties both ends name helps a census, not a half survey, and stops helping once about half of false ties are named by both ends), the lender's leaders 6 to 10%, and clustering seeds together does not help; complex centrality, the measure built for complex contagions, loses up to 3.7% (a median 3.3% over refitted fits; it helps more the higher the fitted threshold, but never matches degree discount), and seeding whole neighbourhoods 10 to 13%.

66 tests

What it found

Research programme on the 43 Karnataka village networks of Banerjee, Chandrasekhar, Duflo and Jackson (2013; CC0 replication data, 9,126 households, 44,367 ties): can cross-sectional adoption data tell a simple contagion from a complex one, and which seeding rule stays near the best under every model the data cannot reject?

Milestone 1 ports the authors’ estimation code (information model, five moments, identity weights, their 31 × 39 grid, Bayesian bootstrap). It reproduces the data (non-leader take-up 18.7% vs 18.5% published, leaders 24.7% vs 24.8%), qP > qN (98.4% of 1,000 bootstrap draws) and the counterfactual (take-up falls by 0.337 with non-adopters silent; paper 0.32), but not the published point: the minimum is qN = 0.05, qP = 0.30 for three seeds against 0.10, 0.50, which scores 11 times our minimum; qP is weakly identified (95% interval 0.15–1.0) and moves to 0.15–0.25 with two-step weights or quarterly periods.

Milestone 2 fits two complex-contagion models on the same information spread, a reinforcement model (logit gains γ per adopting neighbour) and a fractional threshold, and compares them leaving one village out. Both fit better in sample (reinforcement γ = 0.10, positive in 99.5% of 1,000 bootstrap draws, criterion 41% lower; this fine-grid, free-intercept fit is post hoc, the pre-registered coarse grid gave γ = 0) yet predict held-out villages worse than the simple model (better in 13 and 19 of 43; in 12% and 24% of paired bootstrap draws). Take-up by adopting neighbours, 8.3% with none to 35.0% with four or more, is more convex than the simple model's 8.1% to 27.2%, a shape reinforcement, homophily or degree could each leave.

Milestone 3 simulates 200 datasets from each fitted model on the real networks and refits all three: in sample the criterion picks the reinforcement model for 85% of datasets the simple model made; leaving one village out recovers the true model 58.5%, 82% and 55.5% of the time (simple, threshold, reinforcement), so milestone 2’s verdict is weak evidence. The moment map’s weakest direction trades the base adoption rate against word of mouth and reinforcement (condition number 79). A post-hoc check finds the real villages’ held-out errors two to four times larger than any model produces in its own synthetic data: every model is too homogeneous across villages.

Show the rest of the summary (18 more paragraphs, 1,499 words)

Milestone 3b adds a village random effect on the base adoption rate, identified by the squared village take-up rate: it is not needed (σ-hat = 0 in every family; the information model’s own word-of-mouth randomness already matches how much take-up varies between villages) and it does not close the gap (no synthetic dataset from the information or reinforcement model reaches the real held-out error). A threshold model with a free intercept does reach it (19% of its synthetic datasets) and now predicts held-out villages best (loss 0.169 against 0.181 and 0.210).

The misfit is in where adopters sit, not how many: 57% of the real error is one moment, own adoption times second-neighbour adopters (a quirk of the original code), which a cascade model reproduces and a per-household-chance model cannot.

Milestone 4 scores ten seeding rules at the leaders’ budget under all three fitted models: the advice barely depends on which model is right. Greedy seeding under the threshold model loses at most 0.5% of adopters against the best rule under every model (minimax-regret in 94% of bootstrap draws), the structural rules rank almost identically (Kendall τ 0.81–1.0), top degree loses 2–4%, the lender’s leaders 6–10%. Clustered seeds do not help even under the threshold model: one clustered patch is about as bad as random, and the best seeds have moderate degree and are rarely neighbours. Point fits, a fixed budget and no homophily; a model’s counterfactual, not a field result.

Milestone 5 asks what a rollout without a fitted model or a full census gives up: degree discount (Chen, Wang and Yang 2009) loses at most 1.4% under every fitted model and beats top degree in every bootstrap draw, while forbidding adjacent seeds alone loses 3.4% because it drops seed degree to 13; surveying a random 25% of households and seeding top estimated degree loses at most 4.5% (90% interval 1.7–9.7%), 10% loses 6.7%, and friend nomination (no network data) loses 6.2% against 12.1% for random seeds.

Milestone 6 scores the rules over a village bootstrap that refits all three models in every draw (205 distinct fitted processes; the information model’s fit moves off its point estimate in 93% of draws): degree discount’s median worst-case regret is 1.0% (5–95%: 0.3–1.6%), it beats top degree in all 500 draws, and its one rate parameter barely matters (0.9–1.2% for any p from 0.01 to 0.15). Parameter uncertainty widens the model-specific greedy rules’ tails (greedy under the threshold model 0.1–2.4%, under the information model up to 7.3%) but not degree discount’s. Scoring randomised rules on independent runs moves milestone 5’s 25% survey result from 4.5% to 5.0–5.1%, at its 5% bar.

Milestone 7 adds complex centrality (Guilbeault and Centola 2021), the measure built for complex contagions: its best version (absolute threshold 2) loses at most 3.7% of adopters (top degree 4.1%, degree discount 1.4%, which beats it in every bootstrap draw); at a fractional threshold of one half it is mostly degree; and seeding whole neighbourhoods, as the measure presumes, loses 10–13%, about as much as random seeds.

Milestone 8 rescores the complex-centrality rules over milestone 6’s 500 refitted bootstrap draws: degree discount still beats every one of them in every draw; the absolute-2 version (median worst case 3.3%, 5–95%: 2.4–5.3%) beats top degree in 74% of draws, and under the threshold model its loss falls as the refitted threshold rises (4.9% at θ = 0.4, 2.7% at 0.6), the direction its theory predicts, yet never down to degree discount’s.

Milestone 9 asks whether a partial network survey can stand in for a census: surveying half the households at random, then the households they named most, and ranking by degree discount on the ties seen loses 1.6% under the worst fitted model (census degree discount 1.4%; the same ranking on a random half 3.3%); the adaptive second stage does not help top-estimated-degree ranking (5.9% against 5.2% on a quarter), and the best quarter-sample rule (4.5%) stays just above census top degree (4.1%).

Milestone 10 rescores those survey rules over the 500 refitted bootstrap draws: the half survey loses a median 1.9% (5–95%: 1.0–3.3%) against 1.1% for census degree discount and beats census top degree in 97% of draws; spending three quarters of it at random and a quarter on the most-named households lowers that to 1.5%, and the adaptive stage beats a plain random sample in 89–93% of draws.

Milestone 11 measures how many ties a respondent names, by capture–recapture on the survey’s converse questions (borrow from / lend to, visit / invite): about 84% for three questions together (68–83% for one). At that recall the three-quarters-random half survey loses a median 1.8% (census degree discount with the same forgetting 1.4%, census top degree 4.1%), and with half of all ties forgotten degree discount on a census still beats top degree on a perfect census in 99% of draws.

Milestone 12 asks whether respondents forget weak ties more: stratified by how many other survey questions name the same pair, recall is 61% for ties no other question names, 81% for one and 94% for two or more, so the pooled 84% was only a little high (stratified 81%). Under that uneven forgetting the half survey loses a median 2.2% (beating census top degree in 98% of draws) and census degree discount within a point of a perfect census.

Milestone 13 gives every randomised rule its own scoring stream and re-draws four rules five times: the apparent census gain from uneven forgetting (0.9% against 1.8%) is Monte Carlo noise (mean gap −0.07 point over five copies), and a randomised rule’s joint median moves by up to 0.47 point (sd) between copies, so sub-point differences between randomised rules in milestones 10 to 12 are within noise; the survey advice (about 2%) is unchanged.

Milestone 14 re-draws 16 randomised rules five times and pools the copies (500 survey draws per village), putting a Monte Carlo standard error of 0.03–0.24 point on each: forgetting half the ties now costs more than forgetting a quarter (milestone 11’s non-monotone recall was noise), the three ways of splitting a half survey are within 0.4 point and not ranked (three quarters random 1.79%, one quarter 1.81%, half 2.17%), the half survey at the measured recall loses a median 2.2% and beats census top degree in 97% of draws, and a single copy biases every worst-case regret up by about 0.15 point.

Milestone 15 fills in the recall range a field team works in (0.7 to 0.9) with ten Monte Carlo copies of three rules (se 0.10–0.16 point): no rule scores worse with more recall in any adjacent pair beyond 2 se, milestone 14’s apparent dip for census degree discount at 0.85 was noise (+0.12 point, se 0.15; the first five copies ran high), census rules are flat across the range (top degree 4.2–4.3%, degree discount 1.4–1.6%), and the half survey improves by 0.21 point per 0.1 of recall (se 0.07), from 2.39% at 0.7 to 1.81% at 0.9, beating census top degree in at least 97% of draws at every level.

Milestone 16 adds false ties, swept because the archive cannot measure them: at 85% recall plus up to one false tie per four true ones, census degree discount loses 1.6–1.9% and the half survey 2.2–2.7%, both beating a perfect census ranked by top degree in 95–99% of draws; false ties placed at random cost nothing measurable, while false ties that close triangles cost every rule more (top degree 0.8 point at one per four, z 3.5; census degree discount 2.8% and the half survey 2.9% at one per two).

Milestone 17 tests the field fix, keeping only ties both ends name: on a census it removes the triangle-closing cost (census degree discount 2.8% to 2.2% at one false tie per two, z 2.6; top degree 5.1% to 4.6%, z 2.4) and leaves both rules flat in the false-tie rate, for about 0.2 point of lost recall when there are no false ties; on the half survey, where most ties cannot be checked, it saves nothing and costs 0.2–0.5 point under random false ties, so a census should be filtered and a partial survey should not.

Milestone 18 drops that milestone’s best-case assumption, that each end invents a false tie on its own: when a share κ of false ties is named by both ends (and so survives the filter), the filter’s gain for census degree discount shrinks from 0.60 point at κ = 0 to 0.39 at 0.25, turns into a cost by κ ≈ 0.4–0.5, and costs 0.5–0.6 point at κ = 1 (z 3.0 to 7.9), five times its recall cost with no false ties; census top degree never pays for it measurably.

So the filter helps a census only if false ties are mostly one-sided, which reciprocity itself cannot reveal. Recall is independent across the two ends of a tie within a strength stratum, the strength measure is a proxy, and the false-tie rate and its proportionality to degree are assumed and swept, not measured.

Research log

Ongoing: each run adds a batch and an entry, newest first. Source: LOG.md.

2026-11-19 · Plan: does the reciprocity filter still pay when both ends invent the same false tie? (milestone 18, plan written before the full run; a smoke run at toy sizes checked the code only; outcome below)

Show 19 earlier entries

2026-11-19 · Plan: does keeping only reciprocated ties undo the cost of false ties? (milestone 17, plan written before the full run; a smoke run at toy sizes checked the code only; outcome below. Disclosed: one aside in the committed plan said the BCDJ archive separates reciprocated from one-sided reports; its household matrices are symmetrised (milestone 11), so that aside was wrong and was cut during the run; no hypothesis changed)

  • Why: milestone 16 found that false ties placed among friends of friends (triadic closure) cost every rule more than random ones, up to +0.96 point for census degree discount at φ = 0.5, and named the field's standard fix as the next step: keep a census tie only if both ends name it. It is a common choice in network surveys, but it trades one error for another. At recall ρ = 0.85 per tie end, the unfiltered census sees a true tie with probability 1 − 0.15<sup>2</sup> = 0.98; the filtered one only with 0.85<sup>2</sup> = 0.72, while a false tie survives only if both ends independently invent the same tie, which is rare. Whether that trade is worth making for seeding is the question a survey designer would ask next.
  • Model (seeding.survey_recall(..., recip=True)): a tie between two surveyed households is kept only if both report it; a tie with one surveyed end cannot be checked and is kept on its one report; stage-1 counts (which pick stage 2 and estimate unsurveyed households' degrees) are unfiltered, since the other end has not been surveyed yet. Surveyed households' degree is their filtered seen degree. The filter uses no random draws. tests/test_seeding.py checks that it is a no-op at perfect recall with no false ties, keeps a true tie with probability ρ<sup>2</sup> in a census, keeps fewer than a tenth of false ties at φ = 0.5, and leaves one-sided ties and stage-1 estimates alone in the half survey.
  • Run (experiments/m17_reciprocity/run.py): milestone 16's harness unchanged (own stream per rule keyed by name, B = 500, S = 100, 100 draws per randomised rule, milestone 12's primary rules, milestone 15's 47-rule reference never swapped, a key rule capped at its own adopters), at ρ = 0.85. Three rules (census top degree, census degree discount, adaptive-dd-0.5-s0.75) × five cells (φ = 0; φ = 0.25, 0.5 × uniform, closure placement) × with and without the filter: 30 rules, five copies each. φ = 0.1 is dropped (milestone 16 found it indistinguishable from 0).
  • Sanity: the 15 unfiltered rules carry milestone 16's names (milestone 11's at φ = 0), so their five copies reproduce milestone 16's to 1e-4.
  • H46 (the filter undoes closure errors): census dd at φ = 0.5, closure, filtered scores better than unfiltered by more than 2 Monte Carlo se (paired copies). Refuted otherwise.
  • H47 (the filter is cheap without false ties): census dd at φ = 0, filtered minus unfiltered, at most +0.5 point. Reasoning: milestone 14 found census dd at ρ = 0.5 (seen-tie probability 0.75, close to the filter's 0.72) at 1.74%, against 1.25–1.75% at higher recall. Refuted otherwise.
  • H48 (the filter makes census dd flat in φ): filtered census dd at φ = 0.5 minus filtered at φ = 0 within 2 Monte Carlo se, both placements.
  • H49 (the filter helps the half survey): adaptive-dd-0.5-s0.75 at φ = 0.5, closure, filtered better than unfiltered by more than 2 Monte Carlo se. Expected to be the hardest to hold: only ties with both ends surveyed (about a quarter of them) can be checked, and stage-1 counts are not filtered at all.
  • H50 (the filter helps census top degree): census top degree at φ = 0.25, closure (milestone 16's +0.77-point cost), filtered better than unfiltered by more than 2 Monte Carlo se.
  • Predictions (not tests): the filter's gain grows with φ and is larger under closure than uniform placement for every rule; under uniform placement at φ = 0.25 (where milestone 16 found no cost) the filter is a net loss for the census rules; the filtered half survey stays at or below 3% in every cell.
  • Caveats fixed now: false reports are drawn independently per respondent, so two friends of friends who each invent the tie to the other do so by chance; real false ties may be correlated (a shared event both remember as a tie), which would let more survive the filter, so this is a best case for it. Recall is uniform and independent per tie end; five copies give an se of about 0.1–0.25 point that is itself rough.
  • Outcome (experiments/m17_reciprocity/run.py, verdicts.txt, verdicts.json, results.txt, reciprocity.svg; 3,340 s on 4 cores). Sanity held: the 15 unfiltered rules match milestone 16's copies 0–4 to 5e-6. A key rule beats the 47-rule reference in 0.8–1.3% of cells per copy (0.05% pooled). Pooled joint median worst-case regret (MC se), unfiltered → filtered: census top degree at φ = 0 4.33 → 4.55%; φ = 0.25 uniform 4.30 → 4.34, closure 5.09 → 4.62; φ = 0.5 uniform 4.41 → 4.57, closure 5.12 → 4.63%. Census degree discount at φ = 0 1.82 → 1.93%; 0.25 uniform 1.81 → 1.61, closure 1.92 → 2.20; 0.5 uniform 2.16 → 1.75, closure 2.78 → 2.18%. Half survey at φ = 0 2.32 → 2.52%; 0.25 uniform 2.42 → 2.90, closure 2.70 → 2.56; 0.5 uniform 2.60 → 2.81, closure 2.89 → 2.88%. Same-reference rows: perfect census dd 1.18%, perfect census top degree 4.02%.
  • H46 held. Census dd at φ = 0.5, closure: the filter saves 0.60 point (se 0.24, z 2.6), 2.78% to 2.18%.
  • H47 held, weakly. Census dd at φ = 0: the filter costs +0.11 point, but with se 0.36 (the filtered rule's copies run 0.96–2.63%, the noisiest key rule here, se 0.31), so a cost up to about 0.8 point is not excluded. Census top degree, the steadier rule, pays a clear +0.23 (se 0.10) for the lost recall.
  • H48 held, weakly. Filtered census dd at φ = 0.5 minus φ = 0: uniform −0.17 (se 0.36), closure +0.25 (se 0.48). The bar was 2 se, and these se are the largest in the run, so "flat" here means "no detectable slope", not a tight bound. Filtered census top degree, with smaller se, is flat too: +0.01 and +0.08 at φ = 0.5 (se 0.16–0.20), against +0.09 and +0.79 unfiltered.
  • H49 refuted. The half survey at φ = 0.5, closure: filtered minus unfiltered −0.01 (se 0.16). Worse, under uniform placement the filter hurts the survey: +0.48 (se 0.13, z 3.7) at φ = 0.25 and +0.21 (se 0.06, z 3.9) at 0.5. In the half survey only ties between two surveyed households can be checked, so the filter removes some false ties and many true ones among surveyed households while leaving the one-sided and stage-1 errors untouched.
  • H50 held. Census top degree at φ = 0.25, closure: −0.47 (se 0.20, z 2.4); at 0.5, −0.48 (se 0.19, z 2.6).
  • Predictions: the gain growing with φ and larger under closure than uniform held for census top degree only (census dd at 0.25 closure moves the wrong way, +0.28, se 0.28; the survey's gain is larger under closure at both rates but never negative by more than 1 se); the filter as a net loss for the census rules under uniform placement at 0.25 missed (top degree +0.04, dd −0.20, both within 1 se); the filtered half survey at or below 3% held (2.52–2.90%).
  • Reading: for a census, the filter is a cheap insurance policy. With no false ties it costs census top degree about 0.2 point and census degree discount an amount the run cannot resolve (+0.1, se 0.4); with triangle-closing false ties at one per two true ones it saves both about half a point, and after filtering neither rule's score depends on the false-tie rate or placement within noise. For the half survey it does not pay: most of its ties cannot be checked, and filtering the ones that can costs more true ties than false ones under random errors. So the advice splits by design: filter a census; do not filter a partial survey. Under the strongest case for the filter (independent false reports), its gain on the census rules is about half a point, smaller than the 2-point gap between degree discount and top degree; choosing the ranking still matters more than cleaning the ties.
  • Next: correlated false reports (both ends of a false pair invent it together, the case where the filter fails); the paper's tables with pooled medians and MC se (milestones 10 to 17); tie strength in the contagion; the paper draft.

2026-11-18 · Plan: does the seeding advice survive respondents who name ties that do not exist? (milestone 16, plan written before the full run; a smoke run at toy sizes checked the code only; outcome below)

  • Why: milestones 11 to 15 modelled one kind of survey error, forgetting a tie. The other kind is naming one that is not there: a respondent who reports a neighbour's friend as their own, or answers "who do you borrow from" with someone they have only thought of asking. Lincoln–Petersen (milestone 11) assumes no false positives, and the BCDJ archive cannot separate a one-sided report from a forgotten tie, so the false-positive rate is not measured here: it is swept. A false tie can do more damage than a forgotten one, because degree discount uses the seen ties to discount neighbours of chosen seeds, and a census sees every false report.
  • Model (seeding.false_reports, survey_recall(..., fp, fp_mode); fp = 0 draws nothing extra, so milestones 11 to 15 reproduce, tests/test_seeding.py checks it): on top of recall ρ = 0.85 (the measured three-question recall rounded, milestone 11), each household names m<sub>i</sub> ~ Poisson(φ × its true degree) households it has no tie to, drawn without replacement from a pool. Two placements: uniform (any non-neighbour in the village) and closure (non-neighbours who share a neighbour with i, the triadic-closure error). False reports enter the stage-1 counts, the seen ties and the degree estimate exactly as true ones. The contagion still runs on the true network. Proportional-to-degree rates are an assumption (a respondent with more ties has more chances to misattribute one); disclosed, not tested.
  • Run (experiments/m16_false_ties/run.py): milestone 15's harness unchanged (own stream per rule keyed by name, B = 500, S = 100, 100 draws per randomised rule, milestone 12's primary rules, milestone 15's 47-rule reference never swapped, a key rule capped at its own adopters). Rules: census top degree, census degree discount and adaptive-dd-0.5-s0.75 at φ = 0.1, 0.25, 0.5 × two placements (18 new, kept out of the reference), plus the same three at φ = 0 (milestone 11's names); five copies each (21 rules × 5). Pooled medians and Monte Carlo se as milestone 15.
  • Sanity: the three φ = 0 rules reproduce milestone 15's copies 0–4 to 1e-4 (same names, streams and reference).
  • H42 (the advice survives modest false ties): the half survey at φ ≤ 0.25, both placements, has pooled joint median at most 3% and beats perfect-census top degree in at least 90% of draws. Refuted if any of the four cells fails.
  • H43 (census degree discount is robust): census dd at φ = 0.25 scores at most 0.5 point worse (pooled) than at φ = 0, for both placements. Refuted otherwise.
  • H44 (placement matters for a degree ranking): census top degree at φ = 0.25 scores worse under uniform than under closure placement by more than 2 Monte Carlo se. Reasoning: uniform false reports land evenly and flatten the census degree ranking; closure reports land on friends of friends, who are disproportionately the hubs the ranking already favours. Refuted otherwise.
  • H45 (stress): census dd at φ = 0.5 still beats perfect-census top degree in at least 90% of draws, both placements.
  • Predictions (not tests): every rule's pooled median rises with φ under both placements; the half survey loses less than census dd per unit of φ, because only half the households report; closure hurts degree discount more than uniform (a false tie between two friends of friends discounts a candidate who is near the seed anyway, but it also hides real distance).
  • Caveats fixed now: five copies give an se about 0.1–0.2 point that is itself rough; false reports are independent of everything but degree; no false report is ever corrected by the other end (the field practice of keeping only reciprocated ties is not modelled, and is the obvious next step if false ties hurt).
  • Outcome (experiments/m16_false_ties/run.py, verdicts.txt, verdicts.json, results.txt, false_ties.svg; 2,280 s on 4 cores). Sanity held: the three φ = 0 rules match milestone 15's copies 0–4 to 5e-6. A key rule beats the 47-rule reference in 0.7–2.2% of cells per copy (0.08% pooled). Pooled joint median worst-case regret (MC se), φ = 0, then 0.1 / 0.25 / 0.5: census top degree 4.33 (0.09) at φ = 0, then uniform 4.61 (0.07) / 4.30 (0.29) / 4.41% (0.20), closure 4.78 (0.20) / 5.09 (0.09) / 5.12% (0.26); census degree discount 1.82 (0.19), uniform 1.70 / 1.81 / 2.16%, closure 1.64 / 1.92 / 2.78% (0.22); half survey s0.75 2.32 (0.24), uniform 2.21 / 2.42 / 2.60%, closure 2.24 / 2.70 / 2.89% (0.10). Same-reference rows: perfect census dd 1.18%, perfect census top degree 4.02%. (The φ = 0 pooled values are five-copy pools, so they differ from milestone 15's ten-copy ones by up to 0.25 point; the copies themselves are identical.)
  • H42 held. Half survey at φ = 0.1 / 0.25: uniform 2.21% / 2.42%, closure 2.24% / 2.70%; beats perfect-census top degree in 97.6, 97.4, 97.8 and 94.8% of draws.
  • H43 held. Census dd at φ = 0.25 minus φ = 0: uniform −0.01 point (se 0.28), closure +0.10 (se 0.24).
  • H44 refuted, the other way round. Census top degree at φ = 0.25, uniform minus closure: −0.80 point (se 0.22, z −3.5): closure-placed false ties hurt top degree, uniform ones do not (uniform costs +0.28, −0.03, +0.09 point at φ = 0.1, 0.25, 0.5; closure +0.45, +0.77, +0.79). The placement gap has the same sign for every rule at φ ≥ 0.25 (census dd at 0.5 −0.62, z −3.1; the survey −0.29 at 0.25 and 0.5, z −2.0).
  • H45 held. Census dd at φ = 0.5 beats perfect-census top degree in 99.0% (uniform) and 95.4% (closure) of draws.
  • Predictions: regret rising with φ for every rule and placement held only for closure (uniform is flat within noise for top degree and, up to 0.25, for both dd rules); the survey losing less than census dd per unit of φ held in sign at 0.5 (closure +0.57 against +0.96; uniform +0.28 against +0.34), not tested; closure hurting dd more than uniform held at 0.5 only.
  • Exploratory, after the run (diagnose.py, diagnose.txt; not a test): H44's reasoning was that uniform false reports scramble the degree ranking. They do not scramble it more than closure ones: at φ = 0.25 a noisy census's top b keeps 83.8% (uniform) and 83.9% (closure) of the true top b, Kendall τ 0.856 and 0.884, and the chosen seeds' mean true degree is 98.1 and 98.2% of the true top b's. What differs, slightly, is clustering: the chosen seeds have 3.09 (uniform) and 3.15 (closure) true ties among themselves per seed, against 3.22 with no false ties. Uniform errors swap in households from elsewhere in the village, which disperses top degree's famously clustered picks a little; closure errors swap in friends of friends, which keeps them together. That is consistent with the scores but small, and the mechanism is not established.
  • Reading: a survey whose respondents name false ties at up to a quarter of their true ones changes nothing a rollout team would do: census degree discount stays at 1.6–1.9%, the half survey at 2.2–2.7%, and both beat a perfect census ranked by top degree in 95–99% of draws. At one false tie per two true ones placed among friends of friends, census degree discount (2.8%) and the half survey (2.9%) are no longer distinguishable, and both still beat top degree. The kind of error matters more than its rate: errors that close triangles cost every rule more than errors placed at random, so a survey's false-positive check should look for triadic closure, not just count unreciprocated names.
  • Next: a reciprocity filter (keep a census tie only if both ends name it) against these false-tie settings, since it trades false positives for recall; tie strength in the contagion; the paper's tables with pooled medians and MC se; the paper draft.

2026-11-18 · Plan: is the seeding advice monotone in tie recall between 0.7 and 0.9? (milestone 15, plan written before the full run; a smoke run at toy sizes checked the code only; outcome below. Disclosed after the run: the per-rule table's header named a column, "pooled from copies 0-4 only", that the code never printed; the label was removed from run.py and verdicts.txt)

  • Why: milestone 14 settled the recall ordering from 0.75 to 0.5 but left the range the field actually sits in unresolved: census degree discount scored 0.49 point worse at ρ = 0.85 than at 0.75 (about 2 se on five copies), and 0.33 worse than at the matched uniform 0.82. The measured three-question recall is 0.81–0.84 (milestones 11 and 12), so whether the advice gets better or worse as a field team's recall improves from 0.7 to 0.9 is the question a survey designer would ask. Five copies were too few to say; this step uses ten and a finer grid.
  • Run (experiments/m15_grid/run.py): milestone 14's harness unchanged (own stream per rule keyed by name, B = 500, S = 100, 100 draws per randomised rule, milestone 12's 53 primary rules), plus census top degree, census degree discount and adaptive-dd-0.5-s0.75 at ρ = 0.7, 0.8 and 0.9 (new, kept out of the reference), and nine replicates of all three at ρ = 0.7, 0.75, 0.8, 0.85, 0.9: 15 rules, ten copies each (1,000 survey and scoring draws per village pooled).
  • Change from milestone 14, fixed now: the reference best is the 53 primary rules minus the 15 key rules, never swapped, and a key rule's regret is 1 − adopters / max(reference best, its own adopters). So every copy and every recall level is scored against the same yardstick; milestone 14 swapped its 16 rules into the reference together. The run reports how often a key rule beats the reference (expected near zero, so the change should not matter).
  • Sanity: copy 0 of the six rules shared with milestone 14 (the three bases at 0.75 and 0.85) reproduces milestone 14's copy 0 within 0.05 point (exact unless a key rule was the best in some draw); copies 1–4 reproduce its copies within the same bound, since streams are keyed by name.
  • H38 (monotone): for each of the three rules and each adjacent pair of grid points, the pooled median at the higher recall is no more than 2 Monte Carlo se above the lower one. Refuted for any of the 12 pairs (with 12 one-sided 2-se tests about one false refutation in four runs is expected under monotonicity; a refutation is reported with its z).
  • H39 (milestone 14's bump was noise): census degree discount at ρ = 0.85 minus 0.75, pooled over ten copies, is at most 2 se. Refuted otherwise.
  • H40 (ten copies are enough): every one of the 15 pooled medians has a Monte Carlo se of at most 0.20 point (milestone 14's largest was 0.24 on five copies; √2 fewer gives about 0.17).
  • H41 (the advice holds across the field range): the half survey at every ρ in 0.7–0.9 has pooled joint median at most 3% and beats perfect-census top degree in at least 90% of draws.
  • Predictions (not tests): the least-squares slope of each rule's pooled median on ρ is negative (more recall, less regret); census degree discount stays within 1.0–1.8% across the grid; pooled medians again sit below the mean of the copies.
  • Caveats fixed now: as milestone 14, replicates re-draw surveys and scoring runs only, so this is Monte Carlo error, not parameter uncertainty; recall is uniform and independent per tie end (milestone 12 found uniform and measured stratified recall indistinguishable at a matched level); ten copies give an se that is itself uncertain by about a quarter.
  • Outcome (experiments/m15_grid/run.py, verdicts.txt, verdicts.json, results.txt, grid.svg; about 49 minutes on 4 cores). Pooled joint median worst-case regret (MC se) at ρ = 0.7 / 0.75 / 0.8 / 0.85 / 0.9: census top degree 4.30 (0.14) / 4.29 (0.13) / 4.31 (0.11) / 4.23 (0.11) / 4.20% (0.10); census degree discount 1.64 (0.16) / 1.45 (0.10) / 1.56 (0.12) / 1.57 (0.12) / 1.37% (0.10); half survey s0.75 2.39 (0.11) / 2.01 (0.10) / 1.96 (0.10) / 2.13 (0.14) / 1.81% (0.12). Same-reference rows: perfect census degree discount 1.18%, perfect census top degree 4.02%.
  • Sanity, half met. Copy 0 of the six shared rules matches milestone 14's copy 0 to 0.046 point (bar 0.05). Copies 1–4 differ by up to 0.135 point, over the bar. The cause is the reference change fixed in the plan: a key rule beats the 47-rule reference best in 1.7–5.0% of (draw, family, rule) cells in a single copy (0.3% pooled), not "near zero" as expected, so where milestone 14 counted those cells as zero regret against itself, this run caps them the same way but against a reference that no longer includes the other swapped rules. The per-rule values move by at most 0.14 point; no verdict is near that margin except H39, read below.
  • H38 held. None of the 12 adjacent pairs has the higher recall scoring worse by more than 2 se; the largest positive step is the survey from 0.8 to 0.85, +0.17 (se 0.16, z +1.1). Two steps improve by over 2 se: the survey from 0.7 to 0.75 (−0.38, z −2.4) and from 0.85 to 0.9 (−0.32, z −2.1), and census degree discount from 0.85 to 0.9 (−0.20, se 0.06, z −3.3).
  • H39 held. Census degree discount at 0.85 minus 0.75: +0.12 point (se 0.15; 2 se 0.29). Per copy: +0.33, +0.75, +0.56, +0.51, +0.23 in copies 0–4 (which reproduce milestone 14's), −0.34, +0.18, −0.03, −0.23, −0.74 in copies 5–9. Milestone 14's 0.49-point bump came from five copies that all happened to run high at 0.85; the five new ones do not. Reading the five-copy se (0.09) as precise was the error: an se from five copies is itself rough, as that plan's caveat said.
  • H40 held. Largest pooled MC se 0.16 point (census dd at 0.7); every rule 0.10–0.16.
  • H41 held. Half survey: 2.39% at 0.7, 2.01, 1.96, 2.13, 1.81% at 0.9; beats perfect-census top degree in 97.0, 99.0, 98.6, 98.0 and 99.2% of draws.
  • Predictions: slopes negative for all three (held in sign; census top degree −0.05 point per 0.1 of recall, se 0.06, and census dd −0.08, se 0.09, are flat within noise; the survey −0.21, se 0.07, 2.9 se); census dd within 1.0–1.8% (held, 1.37–1.64%); pooled medians below the copy mean (held for all 15, by 0.01–0.11 point, mean 0.06, smaller than milestone 14's 0.15, likely because capping at the rule's own adopters removes part of the max-over-rules bias).
  • Reading: across the range a field team's name generator reaches (milestones 11 and 12 measured 0.81–0.84), recall barely matters to a census-based rule: top degree loses about 4.2–4.3% and degree discount 1.4–1.6% whether respondents name 70% or 90% of their ties. It matters a little to the half survey, which relies on named ties twice (to pick the second stage and to rank): each extra tenth of recall saves about 0.2 point of adopters, 2.4% at 0.7 to 1.8% at 0.9. No recall level in the range overturns the advice. Milestone 14's non-monotonicity at 0.75–0.85 was Monte Carlo noise.
  • Next: put pooled medians with MC se into the paper's tables (milestones 10 to 15); why stratified recall steadies scores (milestone 14's exploratory); false-positive ties; tie strength in the contagion; the paper draft.

2026-11-18 · Plan: do milestones 10 and 11's sub-point findings survive pooled Monte Carlo copies? (milestone 14, plan written before the run; outcome below)

  • Why: milestone 13 found that one randomised rule's joint median moves by up to 0.47 point (sd) between Monte Carlo copies, and the bootstrap intervals since milestone 6 do not carry that error. Two findings in the README rest on gaps of that size: milestone 10's split lean (three-quarters-random half survey 1.5% against the half split's 1.9%, 0.41 point, H21) and milestone 11's non-monotone recall (ρ = 0.75 scored worse than ρ = 0.5 for three of four rules). The fix the log named: pool copies and report Monte Carlo error beside the bootstrap interval.
  • Run (experiments/m14_pooled/run.py): milestone 13's harness unchanged (own stream per rule, B = 500, S = 100, 100 draws per randomised rule, milestone 12's 53 primary rules), with four replicates (#r1 to #r4) of 15 rules: milestone 13's four key rules (same names, so their replicates must reproduce milestone 13's copies), adaptive-dd-0.5, adaptive-dd-0.5-s0.25, adaptive-dd-0.5-s0.75, and census-degree, census-dd and adaptive-dd-0.5-s0.75 at ρ = 0.85, 0.75 and 0.5. Two readings per rule: per copy (as milestone 13, replicate c swapped in for every one of the 15 rules) and pooled (each village's mean adopters averaged over the five copies, i.e. 500 draws per village, swapped in for all 15; regret against the best of the primary set with the pooled columns). Monte Carlo standard error of a pooled joint median: sd of the five copy medians / √5; of a pooled difference between two rules: sd of the five per-copy differences / √5.
  • Sanity: rebuilding milestone 13's five copies (only its four rules swapped) from this run reproduces its per-copy medians to its 1e-5 rounding, since the streams are keyed by name.
  • H34 (pooling is enough): every one of the 15 rules has a pooled-median Monte Carlo se of at most 0.15 point. Refuted if any exceeds it.
  • H35 (milestone 10's split lean is real): at f = 0.5 and perfect recall, pooled adaptive-dd-0.5-s0.75 minus adaptive-dd-0.5 is at most −0.25 point and more than 2 Monte Carlo se below zero. Refuted otherwise.
  • H36 (forgetting is monotone): for census-degree, census-dd and adaptive-dd-0.5-s0.75, the pooled median at ρ = 0.75 exceeds the one at ρ = 0.5 by no more than 2 Monte Carlo se. Refuted for a rule whose 0.75 row is more than 2 se above its 0.5 row (milestone 11's non-monotonicity then real for that rule).
  • H37 (the headline stands): pooled adaptive-dd-0.5-s0.75-r0.85 has joint median at most 2.5% and beats perfect-census top degree in at least 90% of draws.
  • Predictions (not tests): pooled medians within 0.5 point of copy 0 for every rule; the split lean shrinks but keeps its sign; the ρ = 0.75 bump is noise for the census rules.
  • Exploratory (not a test): milestone 13's unexplained gap (matched rules vary five to six times more between copies than measured ones); report each rule's copy sd beside the share of draws in which it is the minimax rule, to see whether rules that sit at the top vary more.
  • Caveats fixed now: replicates re-draw the randomised rules' surveys and scoring runs only; the bootstrap draws, refits, deterministic rules and greedy searches are shared, so this is Monte Carlo error, not parameter uncertainty; five copies give a rough se.
  • Disclosed after the run: the plan said 15 rules; the list it gives is 16 (four + three + nine). The run used the 16 listed; only the count in labels was wrong and was corrected in run.py and verdicts.txt.
  • Outcome (experiments/m14_pooled/run.py, verdicts.txt, verdicts.json, results.txt, copies.svg; 1,560 s on 4 cores). Sanity held: milestone 13's five copies, rebuilt from this run, match its per-copy medians to 5e-6 (its 1e-5 rounding). Pooled joint medians [bootstrap 5–95%] (MC se): census dd measured 1.34% [0.56, 2.38] (0.03), matched 1.42% (0.22); half survey s0.75 measured 2.09% (0.03), matched 2.05% (0.11); at perfect recall s0.25 1.81% (0.24), half split 2.17% (0.22), s0.75 1.79% [0.96, 2.87] (0.12); census top degree at ρ = 0.85 / 0.75 / 0.5: 4.28 / 4.20 / 4.58%; census dd 1.75 / 1.25 / 1.74%; half survey s0.75 2.23 / 1.99 / 3.05%. Reference rows (pooled reading): perfect census dd 1.08%, census top degree 3.98%.
  • H34 refuted. Largest pooled-median MC se 0.24 point (adaptive-dd-0.5-s0.25; bar 0.15); 8 of 16 rules exceed 0.15.
  • H35 refuted. Pooled s0.75 minus half split −0.38 point (per copy −1.05, −0.41, −0.50, −0.14, +0.35; se 0.23, so 1.7 se, under the 2 se bar); s0.75 lower in 83% of pooled draws. The one-quarter-random split is as far below the half split (−0.36, se 0.25), and s0.75 against s0.25 is −0.02. Reading: at f = 0.5 the three splits are within about 0.4 point of each other and the data do not rank them; milestone 10's "three quarters random is best" is not supported beyond "the split matters little".
  • H36 held. ρ = 0.75 minus ρ = 0.5, pooled: census top degree −0.38 (se 0.29), census dd −0.48 (0.17), half survey −1.06 (0.22): every rule now scores worse at 0.5 than at 0.75 (by over 2 se for census dd and the survey, 1.3 se for top degree), so milestone 11's non-monotonicity was Monte Carlo noise.
  • H37 held. Pooled half survey (s0.75) at ρ = 0.85: 2.23% [1.47, 3.45], beats perfect-census top degree in 97.2% of draws.
  • Milestone 12's H28 on pooled scores: census dd measured minus matched −0.07 (se 0.25), survey +0.04 (se 0.10), as milestone 13 read it.
  • Prediction (pooled within 0.5 point of copy 0): missed, max shift 0.86 point (adaptive-dd-0.5, whose copy 0 at 3.03% is its worst copy).
  • Not planned: (1) pooled medians sit below the mean of the five copy medians for all 16 rules, by 0.11 to 0.21 point (mean 0.15): worst-case regret takes a maximum over three families and a best over rules, so Monte Carlo noise in a single copy biases its regret upward, and every row since milestone 10 carries that small upward bias. (2) Census dd at ρ = 0.85 scores 0.49 point above ρ = 0.75 (paired se 0.08, but 0.22 from the two rules' own copy sds; the paired se from five copies is itself rough), and the survey 0.25 above (se 0.26); and census dd at the matched uniform 0.82 scores 1.42% against 1.75% at 0.85. So the 0.75–0.85 range is not resolved, with differences between neighbouring recall levels of 0.3–0.5 point surviving pooling. Not tested.
  • Exploratory: rank correlation of copy sd with pooled minimax share over the 16 rules −0.04, so "rules near the top vary more" does not explain milestone 13's puzzle. The 16 rules' copy sds put the puzzle the other way round: the two rules under measured, stratified recall are the stable ones (0.08 and 0.06 point), while every other rule runs 0.17 to 0.54; why the per-stratum recall matrix steadies a rule's score was not tested.
  • Reading: five pooled copies bring a randomised rule's Monte Carlo error to about 0.1–0.25 point, which settles the recall ordering from 0.75 to 0.5 (monotone) and the advice's headline (about 2% for the half survey at the measured recall, 1.1–1.8% for census degree discount at every recall level tried, about 4% for census top degree), and leaves the split share unranked. Finer claims need more draws, and the next step should size them from these sds (to reach 0.1 point se, about 30 copies for the noisiest rules).
  • Next: report pooled medians with MC se in the paper's tables; a finer ρ grid (0.7 to 0.9) with 10 copies to settle the 0.75–0.85 range; why stratified recall steadies scores; false-positive ties; tie strength in the contagion; the paper draft.

2026-11-17 · Plan: is milestone 12's census gain from uneven forgetting real, or the harness's re-draw noise? (milestone 13, plan written before the run; outcome below)

  • Why: milestone 12 refuted H28 in an unexpected direction (census degree discount 0.9% under measured, uneven recall against 1.8% under the matched uniform level), but its own sanity check found that adding rules re-draws the others by up to 0.53 point, because every extra randomised rule shared one scoring stream. A gap under twice that noise cannot carry a claim in the paper. Two fixes: give each rule its own stream, and measure the Monte Carlo noise directly instead of inferring it from re-draws.
  • Harness change (experiments/m6_uncertainty/run.py, off by default so milestones 6 to 12 reproduce): PER_RULE_STREAMS scores each extra randomised rule on a stream keyed by the crc32 of its name, for both the scoring runs and the village random effect; a rule named x#r<j> is replicate j of x, with its surveys drawn afresh as well; NOT_IN_REFERENCE keeps replicates out of the best-rule reference. tests/test_streams.py checks that adding a rule leaves another's score bit-identical (and that the old shared stream does not), and that a replicate re-draws surveys and runs.
  • Run (experiments/m13_streams/run.py): milestone 12's run unchanged in every other respect (B = 500, S = 100, 100 draws per randomised rule, the same 30 extra rules), plus four replicates of each of census-dd-measured, census-dd-matched, adaptive-dd-0.5-s0.75-measured and -matched. Copy c (0 = primary, 1 to 4 = replicates) swaps replicate c in for those four rules and recomputes regret against the best of the primary set with the swap, so each copy is a full re-draw of those rules' Monte Carlo under the same bootstrap draws and refitted processes.
  • H31 (the Monte Carlo noise is small): for each of the four rules, the standard deviation of the joint median worst-case regret across the five copies is at most 0.25 point. Refuted if any exceeds it.
  • H32 (uneven forgetting really helps census degree discount): census-dd measured minus matched joint median is negative in all five copies and at most −0.5 point on average. Refuted otherwise; if refuted, milestone 12's H28 refutation for the census rule is read as noise.
  • H33 (the survey rule is indifferent to unevenness): adaptive-dd-0.5-s0.75 measured minus matched, averaged over copies, within ±0.5 point.
  • Predictions (not tests): switching to own streams moves milestone 12's 9 rows by at most 0.6 point at the joint median; the census gap shrinks towards zero but stays negative.
  • Caveats fixed now: replicates re-draw the randomised rules only; the deterministic rules, the bootstrap draws, the refits and the greedy searches are shared by every copy, so this measures scoring noise, not parameter uncertainty (which the joint bootstrap already carries); five copies give a rough standard deviation.
  • Outcome (experiments/m13_streams/run.py, verdicts.txt, verdicts.json, results.txt, copies.svg; 1,190 s on 4 cores; tests/test_streams.py passes, so adding a rule now re-draws no other). Joint median worst-case regret per copy (0 = primary): census-dd-measured 1.48, 1.65, 1.48, 1.50, 1.44% (mean 1.51, sd 0.08 point); census-dd-matched 1.73, 0.94, 1.47, 1.53, 2.23% (1.58, sd 0.47); adaptive-dd-0.5-s0.75-measured 2.20, 2.26, 2.22, 2.32, 2.27% (2.25, sd 0.05); -matched 1.80, 2.32, 2.40, 2.44, 2.17% (2.23, sd 0.26). Two copies of the same rule differ by a median 0.14 and at most 1.29 point (40 pairs). Reference rows (copy 0): perfect census degree discount 1.20%, census top degree 4.05%, perfect-recall half survey 1.98%.
  • H31 refuted. Monte Carlo sd 0.08, 0.47, 0.05, 0.26 point; two of the four exceed 0.25.
  • H32 refuted. Census degree discount, measured minus matched, per copy: −0.25, +0.71, +0.01, −0.03, −0.80 point (mean −0.07; negative in 3 of 5). The paired share of draws with measured lower swings 0.16 to 0.90 across copies, because one copy's scoring runs are shared by all 500 bootstrap draws. Milestone 12's H28 refutation for the census rule is read as noise, as the plan said: at a matched level, uneven forgetting makes no measurable difference to either rule.
  • H33 held. Survey rule, measured minus matched: mean +0.03 point (+0.40, −0.07, −0.19, −0.11, +0.10).
  • Predictions: own streams move milestone 12's nine rows by at most 0.6 point (missed: up to 0.80, adaptive-dd-0.5-s0.75-stress 2.9% to 2.1%; census-dd-measured 0.9% to 1.5%); the census gap shrinks but stays negative (mean −0.07, so shrinks to about zero, sign not settled).
  • Not planned: the matched rules vary five to six times more between copies than the measured ones; not explained (one candidate: under uniform recall the rule more often sits next to the best rule, where the joint median is sensitive to which of the two wins in each draw). Not tested.
  • Reading: the bootstrap intervals since milestone 6 carry parameter uncertainty, not the Monte Carlo error of a randomised rule's 100 draws, and that error (sd up to about half a point at the joint median) is as large as several differences milestones 10 to 12 reported (milestone 10's split comparison at f = 0.5, 0.41 point; milestone 11's ρ = 0.75 against 0.5; milestone 12's H28). The headline advice is far outside it: the half survey (about 2.2%) and census degree discount (about 1.5%) against census top degree (about 4%).
  • Next: pool copies (or raise draws) for every randomised rule and report Monte Carlo error next to the bootstrap interval; re-read milestones 10 to 12's sub-point comparisons on pooled scores; false-positive ties; tie strength in the contagion; the paper draft.

2026-11-17 · Plan: do respondents forget weak ties more, and does the survey advice survive recall that falls with tie strength? (milestone 12, plan written before any strength-stratified number was computed; outcome below)

  • Why: milestone 11 measured recall as one number (0.836 for a three-question name generator) and scored the advice under recall independent of the tie. Two things can be wrong with that. Lincoln–Petersen assumes every tie is equally likely to be named; if strong ties are named more by both ends, the pooled estimate is biased up (capture heterogeneity), so 0.85 may overstate recall. And a field team that forgets mostly weak ties thins the network unevenly, which a uniform model does not test. The BCDJ archive gives a tie-strength proxy for free: the count of the other survey questions that name the same pair.
  • Plumbing checked before this plan (no result seen): on all 43 microfinance villages, the model's network (data/bcdj_villages.json.gz) equals the archive's adj_allVillageRelationships_HH matrix restricted to inGiant, and equals the union of the 12 household question matrices (borrowmoney, lendmoney, keroricego, keroricecome, visitgo, visitcome, giveadvice, helpdecision, medic, rel, nonrel, templecompany) on the same households, so every model tie has a strength of 1 to 12.
  • Part A, stratified recall (experiments/m12_strength/measure_strength.py, milestone 11's measure_recall.py counts, same 43 villages, surveyed-surveyed pairs, village bootstrap B = 2,000 seed 12). Three-question generator (union of borrow money, kerosene/rice, visit against the union of their converses): stratify pairs by s<sub>6</sub>, the number of the six other questions (giveadvice, helpdecision, medic, rel, nonrel, templecompany) naming the pair, in strata 0, 1, 2+; recall of each list per stratum by Lincoln–Petersen. Each one-question converse pair: stratify by the number of the ten other questions, 0, 1, 2, 3+. The stratified recall of the generator is seen / Σ<sub>strata</sub> LP total, against milestone 11's pooled 0.836.
  • H25 (weak ties are forgotten more): the three-question recall (mean of the two lists) in stratum 2+ exceeds stratum 0 by at least 0.10, with the village bootstrap 95% interval of the difference above 0. Refuted otherwise.
  • H26 (the pooled figure stands): the stratified three-question recall is at least 0.80. Refuted below.
  • Part B, scoring (experiments/m12_strength/run.py, milestone 11's harness unchanged: milestone 6's joint bootstrap B = 500, S = 100, 100 draws per randomised rule; milestone 10's nine and milestone 11's twelve rules stay in the reference set). Recall model: a model tie with s<sub>6</sub> in stratum h is reported by a surveyed end with probability ρ<sub>h</sub>, part A's stratum recall (mean of the two lists), independently per end given the stratum; seen ties, the adaptive stage and the degree estimate as milestone 11 (seeding.survey_recall with a per-tie recall matrix). Three recall settings: measured (ρ<sub>h</sub>); matched (one uniform ρ equal to the tie-weighted mean of ρ<sub>h</sub> over the model's ties, so the difference from measured isolates the unevenness); stress (ρ<sub>0</sub> halved, the others as measured). Rules per setting: census top degree, census degree discount, adaptive-dd-0.5-s0.75 (9 new rules).
  • Sanity: milestone 11's rows re-drawn within about 0.4 point at the joint median.
  • H27 (the advice survives measured, uneven recall): adaptive-dd-0.5-s0.75 under measured recall has joint median worst-case regret at most 2.5% and a lower worst case than perfect-recall census top degree in at least 90% of draws. Refuted if either fails.
  • H28 (unevenness costs little at a matched level): for census degree discount and adaptive-dd-0.5-s0.75, the joint medians under measured and matched recall differ by at most 0.5 point. Refuted if either differs more.
  • H29 (stress): census degree discount under stress recall beats perfect-recall census top degree in at least 90% of joint draws. Refuted otherwise.
  • Predictions (not tests): stratified recall below the pooled figure by 0.01–0.04; recall rises with strength in every one-question pair; top degree barely moves across settings.
  • Caveats fixed now: s<sub>6</sub> is a proxy for strength (questions differ in how often they are asked about kin); within a stratum recall is still assumed equal, so the stratified estimate removes only the heterogeneity the proxy sees; the recall measured is for the three generator questions and is applied to all model ties, as in milestone 11; the contagion models still treat every tie as transmitting equally, so this tests forgetting weak ties, not whether weak ties matter less for adoption.
  • Outcome, part A (experiments/m12_strength/measure_strength.py, strength.txt, strength.json, strength.svg; 2 s). Three-question recall (mean of the two lists) by s<sub>6</sub> stratum: 0.606 [from 0.603, 95% 0.564–0.651; to 0.608, 0.577–0.644] for pairs no other question names (19.5% of model ties), 0.805 for one (41.1%), 0.942 for two or more (39.4%). Stratified recall 0.812 [0.787–0.839] against the pooled 0.836 [0.815–0.858]. Each one-question pair, stratum 0 to 3+ of the ten others: money 0.34, 0.46, 0.51, 0.80 (stratified 0.671 against pooled 0.719); kerosene/rice 0.53, 0.55, 0.59, 0.87 (0.782 against 0.805); visit 0.58, 0.73, 0.73, 0.90 (0.807 against 0.823). In stratum 0 Lincoln–Petersen puts the true count 18% above what either list saw (money: 76%).
  • H25 held. Stratum 2+ minus stratum 0: +0.336 [+0.303, +0.363].
  • H26 held, narrowly. Stratified three-question recall 0.812 (bar 0.80); its 95% interval reaches 0.787.
  • Predictions: stratified below pooled by 0.01–0.04 (held for all four: 0.024, 0.048, 0.023, 0.016; money is 0.048, just outside); recall rises with strength in every one-question pair (held, weakly: visit is flat from 1 to 2, 0.725 to 0.734).
  • Outcome, part B (experiments/m12_strength/run.py, verdicts.txt, verdicts.json, results.txt, regret.json; 987 s on 4 cores). Settings used: measured 0.606 / 0.805 / 0.942, matched 0.820, stress 0.303 / 0.805 / 0.942. Sanity missed its bar: milestone 11's twelve rows re-drawn move by up to 0.53 point at the joint median (census-degree-r0.5 3.8% to 4.3%; census-dd-r0.5 1.6% to 2.1%; the plan said about 0.4). The randomised rules' scoring runs share one stream that lengthens with every rule added (milestone 11 saw 0.4), so differences of about half a point between rules are inside the harness's own re-draw noise; the verdicts below are read with that in mind. Perfect-recall rows: census top degree 4.2%, census degree discount 1.2%, adaptive-dd-0.5-s0.75 1.8%.
  • H27 held. Under measured, uneven recall adaptive-dd-0.5-s0.75 has joint median worst-case regret 2.2% [5–95%: 1.4–3.4%] and beats perfect-recall census top degree in 98.4% of draws.
  • H28 refuted, in the direction not expected. Census degree discount does better under measured recall than under the matched uniform level: 0.9% [0.2–1.9%] against 1.8% [0.8–3.2%] (−0.86 point; lower in 88% of paired draws), and better than with perfect recall (1.2%); it is the minimax rule in 27% of draws. The survey rule barely moves (2.2% against 2.2%, −0.07 point; 57%). The census gap is under twice the re-draw noise above.
  • H29 held. With weak-tie recall halved (0.303), census degree discount beats perfect-recall census top degree in 100% of draws (1.6% against 4.2%).
  • Prediction: top degree barely moves (mixed: 5.1% measured, 5.0% matched, 4.2% stress, 4.2% perfect; forgetting at 0.82 costs it about a point either way, more than milestone 11's uniform 0.85 row, 3.7%).
  • Not planned: the survey rule under stress is 2.9% [1.9–4.7%] and still beats perfect-recall census top degree in 90.4% of draws, on the bar's edge.
  • Reading: respondents forget weak ties far more than strong ones (61% against 94% recall), and the pooled capture–recapture figure milestone 11 used overstates recall only a little (0.836 against 0.812), because weak ties are a fifth of the network. Forgetting that falls on weak ties does not hurt the seeding advice: the half survey stays at about 2% of adopters lost, and degree discount on a census does as well or better than with every tie recorded. Why uneven forgetting would help census degree discount was not tested; one candidate is that dropping weak ties shifts degree discount towards households with many strong, multiplex ties, which in these villages may sit nearer the middle of the network. The contagion models give every tie the same weight, so this is not evidence that weak ties carry less adoption.
  • What a programme officer gets, unchanged: survey half the households, three quarters at random, rank by degree discount on the ties named. Under the forgetting measured in the same villages, weak ties forgotten four times as often as strong ones, it loses a median 2.2% of adopters under the worst refitted model.
  • Caveats: s<sub>6</sub> includes kinship and religious company, so it is a proxy for strength, not a measure; recall is still independent across ends within a stratum, so the stratified figure is still an upper bound if the proxy misses heterogeneity; the matched setting is 0.820, not milestone 11's 0.85, so the matched and milestone 11 rows differ in level as well; the harness's re-draw noise is about half a point.
  • Next: a fixed scoring stream per rule, so adding rules stops re-drawing others (then rerun H28 to see whether the census gain survives); false-positive ties; tie strength in the contagion itself (weight ties by s<sub>12</sub>); the paper draft, with milestones 4 to 12 as its seeding section.

2026-11-16 · Plan: how much tie-recall error does the survey's seeding advice survive, with recall measured in the BCDJ data itself? (milestone 11, plan written before the run; outcome below. Disclosed: part A ran before part B as the plan set out, and its value fixed the grid)

  • Why: milestone 10's advice (survey half the households, three quarters of that at random, rank by degree discount on the seen ties) assumes every surveyed household names every tie. Name generators miss ties, and how many is the input that decides whether the advice holds in a field team's hands. Rather than pick a recall figure, part A measures it in the BCDJ archive.
  • Part A, measuring recall (experiments/m11_recall/measure_recall.py, the BCDJ archive datav4.0 read from the public mirror milestone 1 used). The household survey asked converse questions: whom do you borrow money from / lend money to, borrow kerosene or rice from / lend it to, visit / invite home. A relationship "j lends to i" between two surveyed households should be reported twice, by i under borrow and by j under lend, so on pairs where both households were surveyed (hhSurveyed) the two lists are two independent captures of the same set (Lincoln–Petersen). Recall of the borrow question = |B ∩ L| / |L|, of the lend question = |B ∩ L| / |B|; the same for the other two pairs, and for a three-question name generator (union of the three "from" questions against the union of the three converses). Pooled over the 43 microfinance villages (counts summed), with a village bootstrap interval (B = 2,000, seed 11) and the 75-village figure alongside.
  • Caveats fixed now: the archive's household matrices are symmetrised (a tie in either direction), so a pair with relations both ways is captured twice per list; positively correlated recall (salient ties remembered by both ends) biases the estimate up, so it is an upper bound on recall under that failure; the BCDJ graph the model runs on is itself the union of 12 questions, so it is taken as the truth and the experiment's recall error comes on top of it.
  • Prediction A (not a test): one-question recall 0.5–0.8 on every converse pair; three-question recall above every one-question figure.
  • Part B, scoring under recall error (experiments/m11_recall/run.py, milestone 10's harness unchanged: milestone 6's joint bootstrap, B = 500, S = 100, 100 draws per randomised rule). Recall model: each surveyed household reports each of its true ties independently with probability ρ; a tie is seen if a surveyed end reported it; the adaptive stage ranks by stage-1 reports; estimated degree is the seen degree for surveyed households and stage-1 reports / (k<sub>1</sub>/n) otherwise, with no correction for ρ (a field team does not know it). A census with recall error surveys everyone under the same model (a tie is seen with probability 1 − (1 − ρ)<sup>2</sup>). ρ grid: 0.5, 0.75 and part A's pooled three-question recall rounded to 0.05 (dropped if it equals 0.5 or 0.75; ρ = 1 is milestone 10's rows). Rules per ρ: census top degree, census degree discount, adaptive-dd-0.5 (half split) and adaptive-dd-0.5-s0.75; milestone 10's nine survey rules stay in the set.
  • Sanity: milestone 6's rows and milestone 10's point fits as before; milestone 10's joint rows within about 0.3 point (the extra rules' runs share one stream, so the new rules re-draw them).
  • H22 (the advice survives measured recall): at part A's three-question recall, adaptive-dd-0.5-s0.75 has joint median worst-case regret at most 2.5% and a lower worst case than census top degree with perfect recall in at least 90% of draws. Refuted if either fails.
  • H23 (recall costs the survey no more than the census): at ρ = 0.5, the rise in joint median worst case from ρ = 1 is at most 1 point larger for adaptive-dd-0.5-s0.75 than for census degree discount. Refuted otherwise.
  • H24 (ties beat accuracy): at ρ = 0.5, census degree discount beats census top degree with perfect recall in at least 90% of joint draws. Refuted otherwise.
  • Predictions (not tested): top degree barely moves with recall (thinning keeps the degree order roughly); degree discount loses most where it relies on seen ties among seeds; the s0.75 split stays at or ahead of the half split at every ρ.
  • Outcome, part A (experiments/m11_recall/measure_recall.py, recall.txt, recall.json; 1 s). 43 microfinance villages, 4,414 of 9,598 households surveyed, ties counted between surveyed households only. One-question recall: borrow money 0.754 [95%: 0.724–0.786], lend money 0.683 [0.648–0.720]; borrow kerosene/rice 0.805, lend it 0.806; visit 0.834, invite 0.812. Three-question generator: 0.849 [0.828–0.872] and 0.822 [0.801–0.845], mean 0.836, so the grid value is 0.85 (grid 0.85, 0.75, 0.5). Across villages the three-question figure runs 0.72 to 0.97 (median 0.86). The 75-village figures are within 0.015 of these. Lincoln–Petersen puts the true count 3 to 8% above the union of the two lists. Prediction A half failed: only the money pair is inside 0.5–0.8; kerosene/rice (0.805, 0.806) and visiting (0.834, 0.812) are above it. The three-question figure is above every one-question one, as predicted.
  • Outcome, part B (experiments/m11_recall/run.py, verdicts.txt, verdicts.json, results.txt, regret.json; 847 s on 4 cores). Sanity: milestone 10's rows re-drawn on the longer stream move by at most 0.4 point at the joint median (adaptive-dd-0.25-s0.25 5.7% to 5.3%, above the planned "about 0.3"; the rest within 0.2; adaptive-dd-0.5 and -s0.75 unchanged at 2.0% and 1.6%). Milestone 6's point-fit column moves by up to 0.2 point (greedy-T 0.3% to 0.5%), because a recall rule can be the best rule under a model (census-dd-r0.85 is minimax in 11.6% of draws: its 100 noisy seed sets average out above the deterministic rules there). The plan did not foresee this; it shifts every regret by the same reference and changes no verdict below.
  • H22 held. At the measured recall (ρ = 0.85), adaptive-dd-0.5-s0.75 has joint median worst-case regret 1.8% [5–95%: 0.8–3.0%] against 1.6% with perfect recall, and beats perfect-recall census top degree (4.0%) in 99.2% of draws.
  • H23 held. At ρ = 0.5, the survey's median rises 0.70 point (1.6% to 2.3%) and census degree discount's 0.49 point (1.1% to 1.6%): a difference of 0.21 point, inside the 1-point bar.
  • H24 held. Census degree discount at ρ = 0.5 beats perfect-recall census top degree in 99.0% of draws (1.6% against 4.0%).
  • Predictions: top degree barely moves (held: 4.0, 4.1, 4.5, 3.8% at ρ 1, 0.85, 0.75, 0.5); s0.75 at or ahead of the half split at every ρ (held: 1.6 vs 2.0, 1.8 vs 2.0, 2.6 vs 2.6, 2.3 vs 2.6%; paired 60, 47, 65% of draws at 0.85, 0.75, 0.5, so at 0.75 it is a tie). Degree discount losing most where it relies on seen ties among seeds was not measured.
  • Not planned and not monotone: ρ = 0.75 is worse than ρ = 0.5 for three of the four rules (e.g. s0.75 2.6% against 2.3%; census top degree 4.5% against 3.8%). The intervals overlap, and each ρ has its own random reports, so this may be noise; it was not tested.
  • Reading: forgetting ties costs the survey rule about as much as it costs the census rule, and at the recall measured in the same villages it costs a fifth of a point. Ranking by degree discount on a forgetful census still beats ranking a perfect census by degree in 98 to 99% of draws, so seeing who knows whom matters more than seeing every tie.
  • What a programme officer gets, revised: milestone 10's advice survives measured recall error. Survey half the households, three quarters of that at random, rank by degree discount on the ties reported: a median 1.8% of adopters lost under the worst refitted model (5–95%: 0.8–3.0%), against 1.4% for a census with the same forgetting and 4.1% for top degree on that census.
  • Caveats: recall is independent across ties and respondents (the Lincoln–Petersen estimate assumes this too, and correlated recall would make 0.85 an overestimate); the BCDJ graph, itself a 12-question survey, is taken as the truth; three recall values; no false ties reported; no correction for recall in the degree estimate; greedy rules at the point fits only.
  • Next: correlated recall (strong ties remembered more often, which needs tie strength: the count of questions naming a pair is a proxy); false-positive ties; a finer split grid at f = 0.5 and 0.35; the controlled threshold sweep; the milestone-3b checks; the paper draft, with milestones 4 to 11 as its seeding section.

2026-11-16 · Plan: does the half-survey adaptive design stay close to a census when the fitted parameters are uncertain? (milestone 10, plan written before the run; outcome below)

  • Why: milestone 9's headline for a programme officer (survey half the households at random, then the half named most, rank by degree discount on the seen ties: 1.6% of adopters lost against a census's 1.4%) was scored at the point fits only. Milestone 6 showed the fits are loose and that parameter uncertainty widens some rules' tails (greedy-I to 7.3%) and not others (census degree discount). A survey rule depends on the same parameters through the same scoring, so the claim needs milestone 6's refitted processes before it goes in the paper. Milestone 9 also fixed the stage-1 share at one half by fiat; this step sweeps it.
  • Method: milestone 6's joint bootstrap unchanged (grid, S<sub>fit</sub> 75 seed 0, B = 500 Dirichlet draws seed 42, refits of I, T and R per draw, S = 100 scoring runs seed 5, greedy at the point fits). Nine survey rules are added as randomised rules (100 survey draws per village, one independent run each, on their own random streams so that milestone 6's randomised rows are not re-drawn): uniform and adaptive degree discount at f = 0.25 and 0.5, adaptive top estimated degree at 0.25, and adaptive degree discount with stage-1 share s = 0.25 and 0.75 at both f (s = 0.5 is milestone 9's design; seeding.survey_design(..., split=s), k<sub>1</sub> = round(s k)). Milestone 6's survey-degree-0.25 is the uniform quarter survey ranked by estimated degree. Regret is against the best of all 32 rules in each draw; worst case is the maximum over I, T and R within a draw.
  • Sanity: every milestone-6 row reproduces m6_uncertainty/results.txt exactly unless a new rule is the best rule in some draw; the new rules' point-fit worst cases land within about 0.5 point of milestone 9's (S = 100 survey draws here against 200 there, different streams).
  • H19 (the half survey holds up): adaptive-dd-0.5 has joint median worst-case regret at most 2.5% and a lower worst case than census top degree in at least 90% of draws. Refuted if either fails.
  • H20 (the adaptive stage keeps paying): adaptive degree discount has a lower worst case than uniform degree discount in at least 80% of joint draws, at f = 0.25 and at f = 0.5. Refuted if either fails.
  • H21 (the split need not be tuned): at both f, the half split's joint median worst case is within 0.5 point of the best of s in {0.25, 0.5, 0.75}. Refuted otherwise.
  • Predictions (not tested): no survey rule is minimax in any draw; adaptive-dd-0.5 median 1.5–2%, adaptive-dd-0.25 3.5–4.5%; s = 0.25 (more on the adaptive stage) best at f = 0.5 and not best at f = 0.25, where the stage-1 degree estimate is already thin.
  • Outcome (experiments/m10_survey_uncertainty/results.txt, verdicts.txt, run.py, regret.svg, 730 s on 4 cores). Sanity: milestone 6's point-fit column is identical for all 23 of its rules (no new rule is the best rule at a point fit); its joint and fixed columns move by up to 0.3 point at the 95th percentile (median at most 0.1 point, e.g. dd-0.05 1.0% to 1.1%), because a survey rule is now the best rule under some draws' processes (adaptive-dd-0.5-s0.75 is minimax in 8% of draws), which the plan allowed for. The new rules' point-fit worst cases match milestone 9 within 0.5 point (adaptive-dd-0.5 1.6% against 1.6%; adaptive-dd-0.25 4.1% against 4.5%; uniform-dd-0.5 3.6% against 3.3%; uniform-dd-0.25 5.0% against 5.0%; adaptive-deg-0.25 5.7% against 5.9%).
  • H19 held. adaptive-dd-0.5 has joint median worst-case regret 1.9% [5–95%: 1.0–3.3%] and a lower worst case than census top degree (3.9% [3.2–5.0%]) in 96.8% of draws. Census degree discount: 1.1% [0.5–1.7%]. The gap to the census rule widens from 0.3 point at the point fits to 0.8 point at the median, and the survey rule's 95th percentile is twice the census rule's: the half survey's tail is mostly under I (worst family in 55% of draws).
  • H20 held. Adaptive degree discount beats uniform degree discount in 88.8% of joint draws at f = 0.25 (medians 4.2% against 5.0%) and in 92.8% at f = 0.5 (1.9% against 3.3%). Milestone 9's village bootstrap had it in all draws; parameter uncertainty takes the edge from certain to likely.
  • H21 held, with a lean. The half split is the best of the three at f = 0.25 (s 0.25 / 0.5 / 0.75: 5.7 / 4.2 / 4.4%) and 0.41 point behind the best at f = 0.5 (1.9 / 1.9 / 1.5%), inside the 0.5-point bar. At f = 0.5, s = 0.75 (three quarters random, one quarter adaptive) beats the half split in 72% of draws; at f = 0.25, s = 0.25 loses to it in 96%.
  • Predictions: no survey rule is minimax in any draw (failed: adaptive-dd-0.5-s0.75 in 8.0%, -s0.25 in 3.2%, adaptive-dd-0.5 in 1.4%); adaptive-dd-0.5 median in 1.5–2% (held: 1.95%), adaptive-dd-0.25 in 3.5–4.5% (held: 4.2%); s = 0.25 best at f = 0.5 (failed: s = 0.75 is best; at f = 0.25, s = 0.25 is worst, as predicted).
  • Reading (not tested): spending most of the survey at random keeps the degree estimate for unsurveyed households good (it uses stage-1 neighbours only), and a short adaptive stage is enough to see the ties among the few candidate seeds; a long adaptive stage thins stage 1 and hurts most when the whole survey is small.
  • What a programme officer gets, revised: with half the households surveyable, survey three quarters of that budget at random and the rest by most-named, then rank by degree discount on the seen ties: a median 1.5% of adopters lost under the worst refitted model (5–95%: 0.5–2.9%), against 1.1% for a full census and 3.9% for top degree on a census. A quarter survey (adaptive, half split) loses a median 4.2%, beating census top degree in 31% of draws: close, not a substitute.
  • Caveats: greedy rules still searched at the point fits only; 100 survey draws per village (milestone 9 used 200); households report every tie; stage-2 households can be found by name; each survey costs the same; three split values only.
  • Next: tie-recall error in the survey (respondents name a share of their ties); a finer split grid at f = 0.5 and 0.35; the controlled threshold sweep; the milestone-3b checks; the paper draft, with milestones 4 to 10 as its seeding section.

2026-11-16 · Plan: can a smarter quarter-sample survey seed as well as a census? (milestone 9, plan written before the run; outcome below)

  • Why: milestone 6 corrected the 25% survey rules to a 5.0–5.1% worst case, right at milestone 5's bar, while census degree discount loses 1.4%. A rollout that cannot afford a census of ties is the common case. BCDJ's own survey sampled households and recorded every tie a sampled household named, so ties reach unsurveyed households; our uniform survey already sees exactly those ties. What it does not do is spend part of the budget where the first answers point, which is what a field team can do on a second visit (link-tracing, after the friendship paradox behind Kim et al. 2015's nomination targeting). Two questions follow: does an adaptive second stage close the gap, and does degree discount, the robust census rule, carry over to the partial picture a survey gives?
  • Designs (survey budget k = round(f n) households, f in {0.1, 0.25, 0.5}): uniform (milestone 5: k random households); adaptive (k/2 random, then the k/2 unsurveyed households named by the most stage-1 households, ties broken at random); walk (k/2 random, then repeatedly a random stage-1 household names a random tie, surveyed if not yet, until k; Kim et al.'s nomination step used as a survey). Every surveyed household reports all its ties. Degree estimate: exact for surveyed households; for the rest, stage-1 neighbours / (k<sub>1</sub>/n), which stays unbiased under the adaptive stages (uniform: all surveyed neighbours / f, as milestone 5).
  • Rules on each survey: top estimated degree (milestone 5's), and survey degree discount (Chen, Wang and Yang 2009, p = 0.05 as before) with estimated degree in place of degree and seeded neighbours counted on the seen ties only. Six survey rules per share, 18 in all; at f = 1 every design and rule equals its census version (tested).
  • Scoring: milestone 5's protocol (point fits I, T, R plus sensitivity T60 and Ipub, budgets = each village's leader count, seeds-as-informed, S = 200 runs per village for deterministic rules, seed 5, greedy re-searched with milestone 5's code and seed so its rows reproduce; village Bayesian bootstrap B = 1,000, seed 42), except that every randomised rule's 200 draws get independent runs (milestone 6's correction). Reference best rule under each model: the best of milestone 5's deterministic rules and all rules here.
  • H16 (a second, adaptive stage helps): at f = 0.25, adaptive with top estimated degree has a lower worst-case regret over I, T and R than uniform with top estimated degree, and a lower one in at least 80% of bootstrap draws. Refuted if either fails.
  • H17 (degree discount carries over to a survey): at f = 0.25 with the uniform design, survey degree discount has a lower worst-case regret than top estimated degree. Refuted otherwise.
  • H18 (a quarter survey can match a census ranked by degree): the best f = 0.25 design and rule pair has worst-case regret at most census top degree's (4.1% in milestone 5). Refuted otherwise.
  • Predictions (not tested): adaptive top estimated degree at f = 0.25 about 3–4%; walk between uniform and adaptive; adaptive degree discount at f = 0.5 within 2%; survey degree discount helps less at f = 0.1, where few seeded neighbours are seen.
  • Sanity: budgets (exactly k surveyed, exactly b seeds), f = 1 equals census (tests); milestone 5's deterministic rows reproduce its results.txt exactly; uniform top estimated degree at f = 0.25 near milestone 6's point-fit 5.1% (independent runs, different streams).
  • Outcome (experiments/m9_survey/results.txt, run.py, survey.svg, 217 s on 4 cores). Sanity held: 4 new tests pass (budgets; f = 1 equals census top degree and census degree discount under every design; uniform reproduces milestone 5's survey draws; adaptive stage 2 takes the most-named households; walk's stage 2 was named by stage 1); every milestone-5 deterministic rule's adopter count reproduces milestone 5 (under T: greedy-T 43.91, degree discount 43.56, top degree 42.11; under R: degree discount 45.51, greedy-R 45.50); uniform top estimated degree at f = 0.25 has worst case 5.2% (milestone 6, point fit: 5.1%).
  • H16 refuted. Adaptive with top estimated degree is worse than uniform at f = 0.25 (worst case 5.9% against 5.2%) and better in none of the 1,000 draws. It is worse at f = 0.1 too (9.4% against 7.1%) and only level at f = 0.5 (4.3% against 4.4%, better in 94% of draws). The walk design is worse than uniform with either ranking at f = 0.1 and 0.25.
  • H17 held, narrowly. With the uniform design at f = 0.25, survey degree discount loses 5.0% against top estimated degree's 5.2%, lower in all 1,000 draws. At f = 0.5 the gap is wide (3.3% against 4.4%); at f = 0.1 it is 0.1 point (lower in 94% of draws).
  • H18 refuted, narrowly. The best quarter-sample rule is adaptive degree discount at 4.5% [90%: 4.0–5.1%], above census top degree's 4.1%; it beats census top degree in 7% of draws.
  • Not pre-registered: the adaptive stage pays only together with degree discount. Adaptive degree discount beats uniform degree discount in all 1,000 draws at f = 0.25 (4.5% against 5.0%) and at f = 0.5 (1.6% [1.3–2.0%] against 3.3%), where it comes within 0.2 point of census degree discount (1.4%) and beats census top degree in every draw. Its seeds have the lowest tie density of any survey rule (0.083 at f = 0.25, 0.089 at f = 0.5; census degree discount 0.092). Reading (not tested): stage 2 surveys the households most likely to be chosen, so the ties among candidate seeds are seen and the discount can act on them; ranking by estimated degree alone has nothing to discount, and pays for stage 2 with a noisier estimate for the unsurveyed (only stage-1 neighbours count).
  • Predictions: adaptive top estimated degree at f = 0.25 in 3–4% (failed: 5.9%); walk between uniform and adaptive (failed: it is the worst design at f = 0.25 and with top degree at f = 0.5); adaptive degree discount at f = 0.5 within 2% (held: 1.6%); survey degree discount helps less at f = 0.1 (held: 0.1 point against 0.2 at 0.25 and 1.1 at 0.5).
  • What a programme officer gets: if the rollout can survey half the households, survey half at random, then the households the first half named most, and rank by degree discount on the ties seen: about 1.6% of adopters lost under the worst fitted model, against 1.4% for a full census. With a quarter, the same design loses 4.5%, about what top degree on a full census loses. Below that, a plain uniform sample is best, and friend nomination (6.4%) is close to a quarter survey.
  • Caveats: point fits only (not milestone 6's refitted draws); households report every tie (no recall error); stage-2 households can be found by name; each surveyed household costs the same; budgets, seeding-as-informing and no homophily as before.
  • Next: score adaptive degree discount over milestone 6's refitted processes; split the adaptive budget other than half and half; survey designs with tie-recall error; the controlled threshold sweep; the milestone-3b checks; the paper draft.

2026-11-16 · Plan: do the complex-centrality rules keep their place when the fitted parameters are uncertain? (milestone 8, plan written before the run; outcome below)

  • Why: milestone 7 scored complex centrality (Guilbeault and Centola 2021) at the three point fits only, with a village bootstrap. Milestone 6 showed the fits are not tight (T refits to θ 0.4, 0.5 or 0.6 in 17, 37 and 44% of draws; I to σ > 0 in 81%), and complex centrality is the one rule family whose premise turns on the threshold. If its gap to degree discount, or its narrow edge over top degree (89% of village draws in milestone 7), were an artefact of the point fit, the seeding section would say the wrong thing about the rule built for this case. This was milestone 7's first "next".
  • Method: milestone 6's run unchanged (same grid, S<sub>fit</sub> 75 seed 0, B = 500 Dirichlet draws seed 42, refit of I, T and R per draw, S = 100 scoring runs seed 5, greedy at the point fits, randomised rules on independent runs), with milestone 7's six complex-centrality rules added to the deterministic set (m6_uncertainty/run.py gains an EXTRA_RULES hook and an output directory; with neither set it runs as before). Regret is against the best of all 29 rules under each draw's process; worst case is the maximum over I, T, R within a draw.
  • Sanity: every milestone-6 row (point fit, joint and fixed columns) reproduces m6_uncertainty/results.txt exactly unless a cc rule becomes the best rule in some draw (milestone 7 found none at the point fits); the cc rules' point-fit worst cases are within about 0.5 point of milestone 7's (S = 100 here against 200 there).
  • H13 (milestone 7's ranking survives parameter uncertainty): degree discount (p = 0.05) has a strictly lower worst-case regret than every cc rule in at least 95% of the joint draws. Refuted if any cc rule matches or beats it in more than 5%.
  • H14 (cc-abs2's edge over top degree survives): cc-abs2's worst-case regret is below top degree's in at least 50% of the joint draws. Refuted otherwise.
  • H15 (the threshold is where complex centrality should pay): under the refitted T, cc-abs2's median regret is lower in draws that refit to θ ≥ 0.6 than in draws that refit to θ ≤ 0.4. Refuted otherwise; untestable if either group is empty. Prior about 50%: higher thresholds make reinforcement matter more, but milestone 4 found clustered seeds lose under every fit.
  • Predictions (not tested): no cc rule is the minimax rule in any draw; cc-abs2's median worst case is 3–4.5%; the cc rules' worst case falls under T in most draws.
  • Outcome (experiments/m8_cc_uncertainty/results.txt, verdicts.txt, run.py, 666 s on 4 cores). Sanity held: with the six cc rules added, every one of milestone 6's 23 rows (point fit, joint and fixed columns, per-family medians, minimax shares, H8 and H9) is identical to m6_uncertainty/results.txt; no cc rule is the best rule in any draw. The cc rules' point-fit worst cases at S = 100 are within 0.5 point of milestone 7's at S = 200 (cc-abs2 3.8% against 3.7%).
  • H13 held. Degree discount (p = 0.05) has a lower worst-case regret than every cc rule in all 500 draws (largest share in which a cc rule matches or beats it: 0). Joint medians [5–95%]: cc-abs2 3.3% [2.4–5.3%], cc-spread-frac 4.5% [3.6–6.4%], cc-frac 5.5%, cc-frac25 7.8%, cc-hood-frac 10.0%, cc-hood-abs2 12.6% [9.5–16.6%]; degree discount 1.0% [0.3–1.6%]; top degree 3.9% [3.2–4.8%].
  • H14 held. cc-abs2's worst case is below top degree's in 73.6% of draws (milestone 7, village bootstrap at the point fits: 89%). cc-spread-frac beats top degree in 8.4%; the other four never do.
  • H15 held. Under the refitted T, cc-abs2's median regret falls as the refitted threshold rises: 4.9% at θ 0.4 (86 draws), 3.7% at 0.5 (184), 2.7% at 0.6 (218), 2.4% at 0.75 (12); top degree's falls less (4.2, 4.1, 3.6, 3.6%), so cc-abs2 is behind top degree at θ 0.4 and ahead from 0.5 up. Degree discount's T regret is 0 to 1.0% throughout. The comparison is across draws, so the threshold moves together with the draw's village weights and other refitted parameters; it is an association, not a controlled sweep.
  • Predictions: no cc rule is minimax in any draw (held); cc-abs2's median worst case 3.35% (in the predicted band); the cc rules' worst case falls under T in 72–100% of draws (held; for degree discount it is mostly I, 55%).
  • Reading: parameter uncertainty does not move complex centrality's place. It pays in the direction its theory says (the higher the fitted adoption threshold, the more the absolute-2 measure helps against top degree), but even at the highest refitted threshold it loses 2.4% under T where degree discount loses about 1%. On these villages the cheap rule for a simple contagion stays the robust rule for the complex one.
  • Caveats: greedy rules searched at the point fits only, as in milestone 6; the grid's threshold values are coarse (four values, 12 draws at 0.75); reach-first ordering of the measure is our reading; budgets, seeding-as-informing and no homophily as before.
  • Next: a controlled threshold sweep (T refitted at each fixed θ, all else at the point fit) to separate the threshold from the other parameters behind H15; survey designs closer to BCDJ's; the milestone-3b checks; the paper draft.

2026-11-16 · Plan: does complex centrality, the seeding measure built for complex contagions, seed these villages as well as degree discount? (milestone 7, plan written before the run; outcome below)

  • Why: complex centrality (Guilbeault and Centola 2021) has been on the "next" list since milestone 4. It is the published rule built for exactly the case this programme cannot rule out (a threshold contagion), so a seeding section that omits it would be missing its most relevant baseline. Milestones 4 to 6 found that clustered seeding loses under every fitted model, while the measure's own premise is that a node's neighbourhood is seeded; this step tests both readings.
  • Measure (seeding.complex_paths, complex_centrality): for every household i, its seed neighbourhood (i and all its ties) starts active and a deterministic threshold contagion runs on the network: a household activates when at least a share θ of its ties are active (fractional) or at least 2 are (absolute, the threshold Guilbeault and Centola use most). Complex path length i→j = the step at which j activates. Score: reach (share of the village activated) first, then shorter mean complex path length to the households reached outside the neighbourhood, then degree. Ranking by reach first is our choice: a probe on the 43 villages before the run showed that at θ = 0.5 the median neighbourhood reaches little beyond itself (mean reach 0.09; rank correlation of reach with degree 0.96), so the mean length alone would be undefined for most households, while at absolute 2 most neighbourhoods reach the whole village (mean reach 0.85) and the path length does the ranking.
  • Rules (budget and seeds-as-informed exactly as milestones 4 and 5): cc-frac (top b by the θ = 0.5 measure, the T fit's threshold), cc-frac25 (θ = 0.25), cc-abs2 (absolute 2); cc-hood-frac and cc-hood-abs2 (neighbourhood seeding: the most central household not yet seeded, then its unseeded ties in degree order, repeated until b); cc-spread-frac (the θ = 0.5 order with no two seeds adjacent while possible, spread degree's rule).
  • Scoring: milestone 5's protocol unchanged (point fits I, T, R plus sensitivity T60 and Ipub; seed 5, 200 runs per village, common random numbers; greedy re-searched with milestone 5's code and seed so its rows reproduce; regret against the best rule; village Bayesian bootstrap B = 1,000, seed 42). The reference rule set is milestone 5's deterministic rules plus random, so the best rule under each model is the same unless a new rule beats it.
  • H10 (a complex-centrality rule is as robust as degree discount): some cc rule has worst-case regret over I, T, R at most 2% (degree discount: 1.4%). Refuted if all six exceed 2%.
  • H11 (it pays where it should): under T, the best cc rule has more adopters than top degree. Refuted otherwise.
  • H12 (seeding neighbourhoods costs, as clustering did in milestone 4): cc-hood-frac and cc-hood-abs2 each have fewer adopters than their single-household versions (cc-frac, cc-abs2) under every one of I, T and R. Refuted if any of the six comparisons goes the other way.
  • Predictions (not tested): cc-frac ≈ top degree (seed overlap above 0.8); cc-abs2 picks lower-degree seeds than top degree; cc-spread-frac ≈ spread degree; H10 refuted (best cc rule 2.5–4%), H11 held narrowly by cc-abs2 or cc-spread-frac, H12 held.
  • Sanity: the measure on a path graph and on two cliques joined by a wide or narrow bridge matches hand counts (tests); every rule returns exactly b seeds; milestone-5 rules' adopter counts reproduce milestone 5's results.txt.
  • Outcome (experiments/m7_complex/results.txt, run.py, 197 s on 4 cores). Sanity held: 17 new tests pass (path graph, wide and narrow bridges, budgets, neighbourhood seeding, no adjacent spread seeds); every milestone-5 rule's adopter count reproduces milestone 5 to the second decimal (e.g. under T: greedy-T 43.91, degree discount 43.56, top degree 42.11, random 38.61 per village). Bootstrap intervals are narrower than milestone 5's because the noisy survey rules are not in this step's reference set; point regrets are unchanged.
  • H10 refuted. No complex-centrality rule comes within 2% of the best rule under every fitted model. The best, cc-abs2 (absolute threshold 2), loses at most 3.7% [90%: 3.1–4.3%], under T; cc-spread-frac 4.9%, cc-frac 5.6%, cc-frac25 7.9%. Degree discount (1.4%) beats every cc rule's worst case in all 1,000 bootstrap draws.
  • H11 held, narrowly. Under the threshold model cc-abs2 gets 42.30 adopters per village against top degree's 42.11 (regret 3.7% against 4.1%), and its worst case beats top degree's in 89% of draws. The fractional versions lose to top degree under T (cc-frac 41.46).
  • H12 held. Seeding the central household's whole neighbourhood, as the measure assumes, loses to seeding the central households alone in all six comparisons, by 1.2 to 3.9 adopters per village; cc-hood-abs2 (worst case 12.6%) is worse than uniform random (12.1%).
  • Predictions: cc-frac's overlap with top degree is 0.79 (predicted above 0.8; failed narrowly) and its seeds are about as clustered (tie density 0.26 against 0.24); cc-abs2 picks lower-degree seeds (20.1 against 23.1, held) with an overlap of 0.59, about degree discount's (0.58); cc-spread-frac does not match spread degree (4.9% against 3.4% worst case, though the same seed degree, 12.9 against 13.3); H10's best cc rule landed in the predicted 2.5–4% band.
  • Reading (not tested): on these networks the fractional measure is mostly degree (a seed neighbourhood at θ = 0.5 rarely reaches past itself), and the absolute-2 measure, which does rank by complex path length, helps only as much as it moves seeds off the dense core. The models fitted here inform households by simple word of mouth and apply the threshold only to adoption, so a measure built for a contagion where information needs reinforcement is not targeted at the process the data support; that is a property of the fitted models, not a test of Guilbeault and Centola's claim on their own processes.
  • Caveats: point fits only (milestone 6's joint bootstrap not repeated for these rules); our reach-first ordering is one reading of the measure; leader-count budget, seeding-as-informing, no homophily, as before.
  • Next: score cc-abs2 and degree discount over milestone 6's refitted processes; survey designs closer to BCDJ's; the milestone-3b checks; the paper draft.

2026-11-15 · Plan: do the robust rules stay robust when the fitted parameters are uncertain? (milestone 6, written before the run)

  • Why: milestones 4 and 5 scored every rule under three point fits (plus two sensitivity points), so their regret intervals carry village sampling only, not the uncertainty in the parameters the rules are scored under. Milestone 3b found that uncertainty is not small: the I fit's σ-hat was 0 in only 20% of bootstrap draws. Degree discount, the one model-free rule within 2%, also used a p (0.05) taken from the I fit and never swept.
  • Fits: the milestone-3b grid restricted to σ in {0, 0.25, 0.5, 0.75} (q<sub>N</sub> 5 values, q<sub>P</sub> 10, δ 3, θ 4 for T, γ 4 for R: I 600, T 2,400, R 2,400 points), nine moments, S = 75, seed 0, the milestone-3b code. Sanity: the full-sample fit must return milestone 3b's three point fits.
  • Joint bootstrap (B = 500, Dirichlet village weights, seed 42): in each draw, each family is refitted with the draw's weights, every rule is scored under the three refitted processes, and adopters are summed with the same weights. Regret is against the best rule under that draw's process; worst-case regret is the maximum over I, T and R within the draw. The same draws scored under the fixed point fits give the milestone-5-style comparison.
  • Rules: leaders, top degree, eigenvector, diffusion, ball, patches, spread degree, single discount, degree discount with p in {0.01, 0.025, 0.05, 0.075, 0.1, 0.15, 0.2, 0.3}, greedy under I, T and R (searched at the point fits exactly as milestone 5, so they are not re-searched per draw); randomised: random, friend nomination, top estimated degree and spread on a 25% survey, 100 draws each. Scoring: S = 100 runs per village under every distinct fitted process (seed 5; a process with σ > 0 draws its village effects from their own stream), common random numbers across rules.
  • H8 (robustness survives parameter uncertainty): degree discount (p = 0.05) has median worst-case regret at most 2% over the joint draws, and a lower worst-case regret than top degree in at least 90% of draws. Refuted if either fails. Greedy-T is reported against the same bars, not tested.
  • H9 (p need not be fitted): degree discount's median worst-case regret varies by at most 1 point across p in [0.01, 0.1], and p = 0.05 is within 0.5 point of the best p in the grid. Refuted if either fails.
  • Predictions (not tested): refitted points stay on neighbouring grid values; T keeps θ = 0.5 in most draws; intervals widen but greedy-T, greedy-R and degree discount stay the top three on the worst case.
  • Changed after the first full run (kept as experiments/m6_uncertainty/results_shared_runs.txt): the randomised rules' 100 draws were scored, as in milestone 5, on one shared simulated run per village (the batched simulator tiles its random numbers across columns). Their means were noisy, and the per-draw maximum picked the noise up: the 25% survey rules came out as the minimax rule in 18% of draws despite a 5% median regret, and every deterministic rule's 95th percentile was inflated (greedy-T 8.8%). The rerun gives each draw its own run (simulate_batch(..., independent=True), tested) and adds two diagnostics labelled post hoc (regret against the best deterministic rule; the 25 worst draws for degree discount). Hypotheses, grid, weights and every other setting unchanged.
  • Outcome (experiments/m6_uncertainty/results.txt, run.py, 616 s on 4 cores). Sanity held: the full-sample fit returns milestone 3b's three point fits exactly, and the point-fit worst-case regrets match milestone 5 to within 0.2 point at half its runs (greedy-T 0.3%, degree discount 1.3%, top degree 4.1%).
  • The fits are uncertain. Across 500 draws I refits to 38 distinct grid points (the point fit in 7%; σ > 0 in 81%, q<sub>P</sub> 0.2 in 55%), T to 47 (θ 0.4 / 0.5 / 0.6 in 17 / 37 / 44%), R to 120 (q<sub>P</sub> anywhere from 0.1 to 1.0). 205 distinct processes were scored.
  • H8 held. Degree discount (p = 0.05) has median worst-case regret 1.0% [5–95%: 0.3–1.6%] and beats top degree in all 500 draws. Greedy-T (reported, not tested): median 0.5%, but 95th percentile 2.4%.
  • H9 held. Degree discount's median worst-case regret is 0.9–1.2% for every p from 0.01 to 0.15 (spread over [0.01, 0.1]: 0.3 point); best p 0.075, 0.09 point better than 0.05; p = 0.3 rises to 1.8%.
  • Not pre-registered: parameter uncertainty widens the greedy rules' tails, not degree discount's. Fixed fits on the same weights: greedy-T 0.1–0.7%, greedy-R 0.7–1.3%, greedy-I 2.4–3.1%; refitted: 0.1–2.4%, 0.1–4.1%, 0.7–7.3%. Degree discount: 0.9–1.7% fixed, 0.3–1.6% refitted. In degree discount's 25 worst draws its worst case is under I (17) or R (6), and greedy-I is the best rule there: the processes with stronger word of mouth from non-adopters or high q<sub>P</sub> reward greedy-I's spread-out, low-degree seeds.
  • Prediction partly failed: refitted points do not stay on neighbouring values (R's q<sub>P</sub> spans the grid, T's θ splits three ways), yet the top three on the median worst case are greedy-T, degree discount (p 0.075 and 0.05) and greedy-R, as predicted.
  • Correction to milestone 5: with independent runs, the 25% survey rules' point-fit worst case is 5.0% (spread) and 5.1% (top estimated degree), at milestone 5's 5% bar rather than under it (milestone 5: 4.5%, shared runs, 200 draws); friend nomination 6.7% (milestone 5: 6.2%). Milestone 5's H7a ("held, narrowly") is not robust to this. Its deterministic-rule results are unaffected.
  • Caveats: greedy sets were searched at the point fits only (a greedy rule re-searched per draw would do better under its own draw); the grid is coarse, so the bootstrap distribution is a grid histogram; budgets, seeding-as-informing and the absence of homophily as before.
  • Next: a survey design closer to BCDJ's (named relationships) and an adaptive survey; complex centrality; the milestone-3b moment checks; begin the paper draft (milestone 6 of the proposal) with milestones 4 to 6 as its seeding section.

2026-11-15 · Plan: can a rule without a fitted model, or without a full network census, seed as well as greedy? (milestone 5, written before the run)

  • Why: milestone 4 found greedy under the threshold model within 0.5% of the best rule under every fitted model, but greedy needs the whole network and a fitted model. Top degree, which needs only the network, lost up to 4.1%. Greedy's seeds were spread out (tie density 0.04–0.07) and of moderate degree. This step asks whether a cheap rule that copies that pattern closes the gap, and how much of the network a rollout must survey to use it.
  • Models, budgets, seeds-as-leaders, scoring (seed 5, 200 runs per village), regret definition and bootstrap (B = 1,000): exactly as milestone 4. The reference "best rule" under each model is the best of all milestone-4 and milestone-5 rules, so milestone-4 greedy sets are searched again with the same code and seed.
  • New census rules (whole network, no model): (a) spread degree: households in degree order, skipping any next to a seed; if that runs out, the highest-degree households left; (b) single discount (Chen, Wang and Yang 2009): repeatedly take the highest degree, counting only ties to unseeded households; (c) degree discount (same paper) with p = 0.05, the information model's fitted q<sub>N</sub> (the one model number it needs; not tuned).
  • New survey rules (part of the network): a random share f in {0.1, 0.25, 0.5} of households is surveyed and reports its ties. A surveyed household's degree is known; an unsurveyed one's is estimated as its number of surveyed neighbours / f. Then (d) top estimated degree and (e) spread degree on the ties the survey saw. (f) Friend nomination, no network data (after Kim et al. 2015's nomination targeting): draw random households, each names a uniform random tie, seed the named until the budget is met. Survey and nomination rules are scored like the random rule: 200 independent draws, one run each.
  • H6 (a cheap census rule suffices): spread degree or a discount rule has worst-case regret at most 2% over I, T and Rδ (top degree: 4.1%). Refuted if all three exceed 2%.
  • H7 (a partial survey suffices): with f = 0.25, some survey rule has worst-case regret at most 5%, and friend nomination beats uniform random under all three models. Refuted if either half fails; the halves are reported separately.
  • Predictions (not tested): spread degree ≈ single discount, both within 2%; degree discount close to them; survey rules degrade smoothly, f = 0.5 about top degree's level; friend nomination between random and top degree.
  • Sanity: rules return exactly b seeds; spread degree has no adjacent seeds whenever an independent set of size b exists; survey rules with f = 1 equal their census versions (tests); milestone-4 rows reproduce milestone 4's regrets for rules it already had.
  • Outcome (experiments/m5_cheap/results.txt, run.py, 200 s on 4 cores). Sanity held: 46 tests pass (budgets, no adjacent spread seeds, f = 1 surveys equal the census rules); spread degree needed no adjacent seeds in any of the 43 villages; the milestone-4 rules' adopter counts reproduce milestone 4 exactly (e.g. under Rδ: greedy-Rδ 45.50, top degree 44.75, random 41.56 per village); regrets under Rδ move by at most 0.1 point because degree discount (45.51) is the new best there.
  • H6 held, through one rule only. Degree discount loses at most 1.4% (I 1.4%, T 0.8%, Rδ 0, where it ties greedy-Rδ; 90% interval of the worst case 1.0–3.2%), and beats top degree's worst case in every bootstrap draw. Single discount 2.4% and spread degree 3.4% miss the 2% bar.
  • Prediction failed: spread degree is not close to the discount rules. No two of its seeds are neighbours, but its mean seed degree falls to 13.3 (greedy-T 15.0, degree discount 20.5, top degree 23.1), and it loses to patches of four under T. Degree discount is the closest copy of greedy's shape: high-ish degree with few ties among seeds (tie density 0.09).
  • H7 held, narrowly, both halves. At f = 0.25 the survey rules lose at most 4.5% (top estimated degree 4.5%, spread 4.5%; intervals 1.7–9.7%) and beat census top degree in only 34–36% of draws. Spreading on seen ties helps only at f = 0.5 (3.7% against 3.9%). f = 0.1: 6.5–6.7%. Friend nomination beats random under I, T and Rδ (42.8/41.2/43.3 against 41.6/38.6/41.6 adopters per village) with worst-case 6.2%, close to a 10% survey.
  • Prediction partly held: survey rules degrade smoothly, but f = 0.5 reaches top degree's level only on the worst case (3.7–3.9% against 4.1%), not on every model (under Rδ 3.2–3.5% against 1.7%).
  • Caveats: point fits; degree discount's p (0.05) not swept; uniform household sampling with complete tie reports; a model's counterfactual.
  • Next: sweep p and score over the bootstrap distribution of fits; nomination-based and adaptive survey designs; complex centrality; the milestone-3b checks.

2026-11-14 · Plan: whom should a rollout seed, under each model the data cannot reject? (milestone 4, written before the run)

  • Why: milestones 2 to 3b found that the moments cannot reliably tell the information model (I) from the reinforcement (Rδ) and threshold (T) models, and that T alone reproduces how unevenly the real villages place their adopters. If seeding advice is the same under all three, the identification problem does not matter for a rollout; if it differs, a rule with bounded regret is what a programme officer needs. This step answers programme H4 and H5.
  • Models (the milestone-3b real-data fits, σ = 0, beta = the leader logit): I q<sub>N</sub> 0.05, q<sub>P</sub> 0.3; T θ 0.50, δ −0.25, q<sub>N</sub> 0.075, q<sub>P</sub> 0.1; Rδ γ 0.10, δ −0.25, q<sub>N</sub> 0.10, q<sub>P</sub> 0.1. Sensitivity, reported not tested: T60 (θ 0.60, δ 0, q<sub>N</sub> 0.075, q<sub>P</sub> 0.1, the milestone-2/3 fit) and I at the published point (q<sub>N</sub> 0.10, q<sub>P</sub> 0.50).
  • Seeds: in every rule a village gets as many seeds as it had leaders (10 to 51, 1,140 in all). Seeds play the leaders' role in the model: informed at the start, and they adopt by the model's own rule, not by fiat. Periods, covariates and networks as in milestones 1 to 3.
  • Rules (src/civ_seeding/seeding.py): (1) the observed leaders; (2) uniform random; (3) top degree; (4) top eigenvector centrality; (5) top diffusion centrality, Σ<sub>t=1..T</sub> (A/λ<sub>1</sub>)<sup>t</sup> 1 with the village's own period count T (our choice of q = 1/λ<sub>1</sub>, after Banerjee et al. 2013's definition; not fitted); (6) one clustered ball: breadth-first from the top-degree household, nearer layers first, higher degree first within a layer; (7) patches of four: the highest-degree household not yet seeded or next to a seed, plus its three highest-degree unseeded neighbours, repeated; (8–10) greedy under I, T and Rδ: add the household with the largest gain in mean adopters, 32 simulations with common random numbers per step, all households as candidates. Complex centrality (Guilbeault and Centola 2021) is not implemented this step.
  • Evaluation: every rule's seed set is scored under every model with fresh simulations (seed 5, 200 runs per village; random: 200 independent seed sets, one run each). Metric: expected adopters, summed over the 43 villages. Regret of a rule under a model = 1 − its adopters / the best rule's under that model. Intervals: village Bayesian bootstrap (B = 1,000) of the regret, and the share of draws in which each rule is best.
  • H4 (policy depends on the model): among I, T and Rδ, the best rule differs between some pair, or the rank order of the ten rules has Kendall τ < 0.6 between some pair. Refuted if the same rule is best under all three and every τ ≥ 0.6.
  • H5 (a robust rule exists): some rule's regret is at most 10% under all three models. Refuted otherwise. The minimax-regret rule is reported with its worst-case regret.
  • Predictions written now (not tested): greedy under each model is best under that model; degree and diffusion centrality beat leaders and random under I and Rδ; under T, clustered rules (6, 7) close the gap on central ones because a threshold of one half is easier to reach among neighbours who are seeded together; the observed leaders, chosen by the NGO for their standing rather than their position, lose to every centrality rule.
  • Sanity: the batched simulator with one candidate reproduces complex.simulate draw for draw (a test), and the leaders rule's simulated take-up matches milestone 3b's fitted level.
  • Outcome (experiments/m4_seeding/results.txt, run.py, 174 s on 4 cores). Sanity held: the batch-of-one simulator matches complex.simulate exactly (tests), and with the leaders as seeds the models give non-leader take-up 0.195 (I), 0.182 (T), 0.197 (Rδ) against the data's 0.187. Greedy seed sets were searched on one stream (seed 0) and scored on another (seed 5), so their scores carry no search optimism.
  • H4 held, but only in its weak half. The best rule differs by model because each model's own greedy set wins under it (as predicted). The rankings of the seven structural rules barely move: Kendall τ 0.81 (I–T), 0.81 (I–Rδ), 1.00 (T–Rδ); with the three greedy rules, 0.78, 0.82, 0.96. The τ < 0.6 half of H4 is refuted.
  • H5 held, by a wide margin. Greedy under the threshold model loses at most 0.5% of adopters against the best rule under any of the three fitted models (I 0.5%, T 0, Rδ 0.2%; 90% bootstrap interval of the worst case 0.2–0.8%) and under both sensitivity points (T60 0, published-point I 0.7%). It is the minimax-regret rule in 94% of bootstrap draws. Greedy under I is the most model-specific (2.6% lost under T).
  • How much seeding matters at all: between the best and the worst rule, 7% (I) to 12% (T) of adopters. Against the best rule, the NGO's actual leaders lose 6.2% (I), 10.4% (T), 6.2% (Rδ); top degree 3.2%, 4.1%, 1.7%; uniform random 6.9%, 12.1%, 8.6%. The model choice the data cannot settle moves these regrets by about a factor of two, not their order.
  • Prediction failed: clustering does not help, even under the threshold model. The one clustered ball is the worst or second-worst non-random rule under every model (T: 10.5% lost, worse than the leaders). Greedy sets are the opposite of clustered: mean seed degree 12–15 (top degree 23, all households 9.7) and tie density among seeds 0.04–0.07 (degree 0.24, ball 0.22, leaders 0.08). Reading (not tested): with information spreading from every seed and a household deciding when it is told, overlapping seeds waste budget, and under a fractional threshold of one half a seed's low-degree neighbours tip more easily than a hub's. Eigenvector and diffusion centrality, which pick a dense core, lose 4–10%.
  • Prediction partly failed: the leaders are not beaten by every centrality rule. Under I they beat eigenvector centrality and the ball; under T and Rδ they beat the ball and random only. Top degree and patches of four beat them under every model.
  • Caveats: the seed budget is the leaders' count; the models are point fits (parameter uncertainty only through two sensitivity points); seeds are informed rather than made to adopt; homophily is not modelled; greedy needs the full network and a fitted model, which a rollout rarely has, so the practical result is the structural one (top degree within 4.1% everywhere). Complex centrality is not yet implemented.
  • Next: (a) parameter uncertainty: score the rules over the bootstrap distribution of fits, not three points; (b) a cheap rule that mimics greedy (spread-out, moderate degree: e.g. degree with a no-neighbours constraint) and how much network data it needs (a sampled-survey version); (c) the moment standardisation and homophily checks left from milestone 3b; (d) complex centrality.

2026-11-14 · Plan: does a village random effect on the base adoption rate explain the misfit? (milestone 3b, written before the run)

  • Why: milestone 3 found that the real held-out losses (I 0.174, T 0.184, Rδ 0.191) lie above the 95th percentile of every fitted process's synthetic losses: the 43 villages differ from each other more than any model allows, and that misfit is bigger than the simple-against-complex difference. The obvious missing piece is village-level heterogeneity in the base rate (a microfinance branch's local reputation, credit demand, a loan officer). This step adds it to all three families, estimates its size, and redoes milestones 2 and 3 with it.
  • Model (complex.simulate(..., shift=)): in each village and simulation, every household's adoption logit is shifted by u = σ z, z ~ N(0, 1), one draw per village and run (common random numbers: z comes from its own stream, so σ = 0 reproduces milestone 3 exactly). Everything else as in milestones 2 and 3; beta stays at the real-data leader logit, which ignores the random effect (leaders are averaged over villages, so it estimates a population-average intercept; disclosed, not corrected).
  • A ninth moment identifies σ: the squared non-leader take-up rate of the village, simulated as the mean over runs of each run's squared rate. Matched on average over villages, it fits the cross-village variance of take-up (the real rates: mean 0.187, SD 0.081, range 0.07–0.44). Its simulated value does not depend on the data, so the milestone-3 reuse of grid simulations across synthetic datasets stays exact.
  • Grid: milestone 3's families and grids, each crossed with σ in {0, 0.25, 0.5, 0.75, 1.0, 1.25}, and I and T also given the intercept shift δ in {0, −0.25, −0.5} that Rδ already has (a random effect on the logit raises mean take-up below 50% by Jensen's inequality, so the intercept must be free to absorb it): I 900 points, T 3,600, Rδ 3,600. S = 75, seeds 0 (fit) and 1 (score), as before.
  • Fits: each family in sample on the nine moments; held-out (leave one village out) on the nine for fitting, scored on the extended eight so losses compare with milestone 3. Data-generating processes for the synthetic check are the real-data nine-moment fits found in this run, 200 datasets each (seeds 2000+).
  • H6 (heterogeneity is there): the nine-moment fit of I has σ-hat > 0, and in a village Bayesian bootstrap (B = 1,000) σ-hat = 0 in fewer than 2.5% of draws. Refuted otherwise. Reported for T and Rδ too.
  • H7 (it explains the misfit): under the fitted I-with-random-effect process, the real held-out loss of I is below the 95th percentile of the synthetic held-out losses (at least 5% of synthetic datasets reach it). Refuted if fewer than 5% do. Reported for T and Rδ, and the real "Rδ better than I in 13 of 43 villages" against each process's spread.
  • Reported, not tested: the leave-one-out confusion matrix under the three random-effect processes (milestone 3 without them: I 58.5%, T 82.0%, Rδ 55.5%), and whether the real data still prefer I to Rδ out of sample. Prediction written now: recovery falls, because village noise swamps the eight moments' contagion signal.
  • Sanity check: the σ = 0, δ = 0 subgrid must reproduce milestone 3's real-data held-out losses and the 13/43 count digit for digit.
  • Added after a smoke run on a tiny grid (before the full run), labelled in run.py: the smoke fit already matched the ninth moment at σ = 0, so the run also breaks the held-out loss of the I family down by moment, real against each process's 5–95% band.
  • Outcome (experiments/m3b_hetero/results.txt, run.py, 931 s on 4 cores). Sanity held: the milestone-3 subgrid gives held-out losses I 0.1742, T 0.1837, Rδ 0.1906 and Rδ better in 13/43 villages (milestone 3: 0.1743, 0.1841, 0.1906, 13/43; the fourth digits differ because this run stores the per-household mean adoptions in float32 to fit 8,100 points in memory, which can move a near-tied fold choice; the 13/43 count is unchanged). H6 refuted: every family's nine-moment fit has σ-hat = 0 (I at q<sub>N</sub> 0.05, q<sub>P</sub> 0.3, δ 0, unchanged from milestone 1), and σ-hat = 0 in 20.1% of 1,000 bootstrap draws for I (0.25 in 42%, 0.5 in 36%); T 73.6%, Rδ 70.9%. At σ = 0 the I fit already matches the mean squared village take-up rate (simulated minus data −0.0004): the run-to-run randomness of word of mouth in a 200-household village gives the model as much spread in the take-up level as the real villages show. A base-rate random effect is not what the models lack.
  • H7 refuted: under the fitted I process (σ = 0) no synthetic dataset reaches the real I held-out loss (0.181 against 5–95% 0.044–0.068); the same under Rδ (0.210 against 0.049–0.084). The threshold process does reach it: with δ now free, T fits θ 0.50, δ −0.25, q<sub>N</sub> 0.075, q<sub>P</sub> 0.1 (in-sample criterion 2.80e−3, against I 4.22e−3 and Rδ 2.47e−3), and its synthetic villages are far more dispersed (held-out loss of I 0.062–0.369); 19% of them reach the real I loss, 17% the real T loss. A threshold cascade makes a village's outcome close to all-or-nothing, and that is the dispersion the real villages have. Out of sample on the real data T is now the best of the three (0.169, against I 0.181 and Rδ 0.210; better than I in 23 of 43 villages). Reported, not tested.
  • Diagnostic: the real misfit is above the I band in all nine moments and is concentrated in one: m5, own adoption times second-neighbour adopters divided by degree (a quirk of the authors' moments.m), carries 0.103 of the real 0.181 (57%), against an I band of 0.012–0.027 for that moment. Then m2 (0.030 against 0.010–0.020), m8, k ≥ 3 adopting neighbours (0.013 against 0.003–0.006), m4 (4× the band's top) and m9 (4×). The T band covers the real value in seven of nine moments (not m1 and m3, both just above).
  • Confusion under the random-effect processes (leave one out, fit 9, score 8): recovery I 37.0%, T 77.5%, Rδ 49.5% (milestone 3: 58.5%, 82.0%, 55.5%); the prediction that recovery falls held, and I data are now called Rδ 39% of the time. In sample the bigger-model bias persists (I recovered 16.5%, Rδ 96.5%). σ itself is poorly recovered: with true σ = 0, the I fit returns 0 in 42% of datasets and 0.25 or 0.5 in the rest.
  • Reading: the villages are not over-dispersed in how many people adopt; they are over-dispersed in where adoption sits in the network, the clustering that m5, m4 and m8 measure. The two models with a fixed per-household chance (I, Rδ) cannot produce it; the threshold model, whose outcome depends on local cascades, can. Next: (a) standardise the moments by their synthetic SD (or drop the m5 quirk) and check the ranking survives; (b) a degree-band take-up moment to separate a threshold cascade from homophily, which also clusters adopters; (c) then seeding (milestone 4) under T and I, the two models the data reject least.

2026-11-14 · Plan: can these moments tell the three models apart? (milestone 3, identification by simulation, written before the run)

  • Why: milestone 2 found that reinforcement (Rδ) and threshold (T) models fit the 43 villages better in sample and predict held-out villages worse than the information model (I). That verdict means something only if the same protocol, run on data where the truth is known, picks the true family. This run generates synthetic villages on the real networks from each fitted model and asks how often each selection rule recovers the model that made them (programme H2).
  • Data-generating processes (the milestone-2 extended-moment fits): I at q<sub>N</sub> 0.05, q<sub>P</sub> 0.3; T at θ 0.60, q<sub>N</sub> 0.075, q<sub>P</sub> 0.1; Rδ at γ 0.10, δ −0.25, q<sub>N</sub> 0.10, q<sub>P</sub> 0.1. 200 synthetic datasets per process, each one adoption draw per village on the real networks, covariates and leaders (simulation seeds 1000+, independent of the fitting seeds).
  • Refit grids, families disjoint so that a choice is a family: I: q<sub>N</sub> in {0.025, 0.05, 0.075, 0.10, 0.15}, q<sub>P</sub> in {0.1, ..., 1.0}; T: the same × θ in {0.4, 0.5, 0.6, 0.75}; Rδ: the same × γ in {0.05, 0.10, 0.15, 0.20} × δ in {0, −0.25, −0.5}. S = 75 simulations per village and point, seed 0 to fit and seed 1 to score held-out villages, as in milestone 2. The simulated moments do not depend on the data except through moments 2 and 3 (which classify households by the data's leader take-up), and those are linear in the simulated adoption, so each grid point is simulated once and reused for all 600 datasets (exact, not an approximation).
  • Simplification written now: beta (the leader logit) is held at the real-data estimate rather than refitted to each synthetic dataset. That gives the selection rules slightly more information than they would have, so recovery rates here are, if anything, optimistic.
  • Selection rules: (a) in sample: the family whose best grid point has the lowest criterion; (b) leave one village out: the family with the lowest mean held-out loss, the milestone-2 protocol. Each on the BCDJ five moments and on the extended eight. Output: four 3 × 3 confusion matrices, and pairwise recovery (for process a against family b, the share of a's datasets where a scores lower than b).
  • H2 (programme): with the BCDJ five moments, in sample, some process is recovered in fewer than 70% of its datasets. Refuted if pairwise recovery is at least 80% for every ordered pair. Reported, not tested, for the other three rules.
  • H2b (what milestone 2's verdict is worth): under the Rδ process, the leave-one-out rule on the extended moments prefers Rδ to I in fewer than 80% of datasets (i.e. the real-data result "Rδ predicts held-out villages worse" is weak evidence against reinforcement). Refuted if it prefers Rδ in at least 80%. Also reported: in what share of Rδ datasets Rδ is better in 13 or fewer of 43 held-out villages, as it was on the real data.
  • Local identification: Jacobian of the village-mean extended moments in (q<sub>N</sub>, q<sub>P</sub>, γ, δ) at the Rδ fit, central differences with common random numbers (S = 1,000; steps 0.01, 0.02, 0.02, 0.05). Prediction: the right singular vector of the smallest singular value loads mainly on q<sub>P</sub> and γ with opposite signs (the trade-off milestone 2 saw). Reported with the singular values and the condition number of the Jacobian scaled to unit parameter ranges of the grids.
  • Outcome (experiments/m3_identify/results.txt, run.py, 107 s on 4 cores). Sanity: on the real data this grid reproduces the milestone-2 fits and held-out losses digit for digit (R better than I in 13/43 villages). H2 held: in sample with the BCDJ five moments the criterion picks the bigger model whatever made the data: recovery I 14.5%, T 8.5%, Rδ 82.5% (I data are called Rδ 85% of the time). With the eight moments in sample: 27.0%, 48.5%, 99.5%. Leaving one village out removes most of that bias: recovery I 58.5%, T 82.0%, Rδ 55.5% (eight moments); with the BCDJ five, Rδ data are recovered in only 12.5%. H2b held: under the Rδ process, leave-one-out with the eight moments prefers Rδ to I in 67.0% of 200 datasets, so the real-data verdict against reinforcement is weak evidence. But the real data are not like any process's data: under Rδ, Rδ beats I in a median 25 of 43 held-out villages (5–95%: 18–32), never as few as the real 13; under I the median is 20 (15–28) and 13 or fewer happens in 2.5% of datasets.
  • Jacobian (S = 1,000, scaled to grid ranges): singular values 0.94, 0.14, 0.075, 0.012, condition 79 (256 with the BCDJ five alone). The prediction failed: the weakest direction is not q<sub>P</sub> against γ but the intercept δ against q<sub>N</sub> and γ (loadings −0.40, −0.10, −0.40, +0.82): raising the base adoption rate while slowing non-adopters' word of mouth and reinforcement leaves the moments nearly unchanged. Within-family recovery agrees: under Rδ the fitted δ is −0.5 in 73% of datasets (true −0.25) and γ is 0.15 in 62% (true 0.10); q<sub>P</sub> is spread from 0.1 to 1.0. Under I, q<sub>N</sub> is recovered in 94% and q<sub>P</sub> in 58%.
  • Post hoc, added after seeing the village counts (labelled in run.py and results.txt): the real held-out losses (I 0.174, T 0.184, Rδ 0.191) lie above the 95th percentile of every process's synthetic losses (I process: 0.042–0.067 for I; T process: 0.050–0.124; Rδ process: 0.052–0.095); at most 1.5% of any process's datasets reach the real level. The real villages differ from each other two to four times more than any of the three fitted models lets them. That misfit, likely village-level heterogeneity in the base adoption rate or the spread that none of the models has, is larger than the simple-against-complex difference the programme is trying to measure.
  • Reading: with these moments, in-sample fit cannot choose a contagion model (it picks the bigger one), and out of sample it chooses correctly a little over half the time for I and Rδ. Milestone 2's "complex models predict held-out villages worse" is therefore weak evidence either way, and the larger fact is that every model so far is too homogeneous across villages. Next: add a village random effect to the base rate (and to q) and redo milestones 2 and 3 with it, before the seeding comparison of milestone 4.

2026-11-14 · Plan, post hoc: a fine reinforcement grid with a free intercept (written after the pre-registered run, before this one)

  • Why: in the pre-registered run (entry below) γ-hat was 0 in every one of 1,000 bootstrap draws, but the criterion rose 13-fold from γ = 0 to the next grid point (0.25) and 1,000-fold at 0.5: the grid cannot see a small γ. And beta is fixed by the leader logit, fitted to leaders' final take-up, so any γ > 0 adds adoption on top of a level that is already matched; R never had a fair chance at the level. Both are our design faults, found by the run, so this is a second, labelled post-hoc test, not a replacement.
  • Method (experiments/m2_complex/refine.py): R with γ in {−0.1, −0.05, 0, 0.05, 0.1, 0.15, 0.2, 0.3, 0.4} and an intercept shift δ in {0, −0.25, −0.5, −0.75, −1.0, −1.5} added to every household's logit, q<sub>N</sub> in {0.025, 0.05, 0.075, 0.10}, q<sub>P</sub> as before. Families compared: I (γ = 0, δ = 0), Iδ (γ = 0, δ free) and Rδ (both free). Same leave-one-village-out protocol, seeds and paired bootstrap as the pre-registered run.
  • Prediction, held to the pre-registered H3 threshold: Rδ is lower than Iδ out of sample in fewer than 95% of paired draws (extended moments). Also reported: bootstrap of γ-hat.
  • Descriptive check, also post hoc: the empirical take-up among non-leaders with 4+ adopting neighbours (0.350) sits above the fitted I model's 0.272. Paired village bootstrap of that gap, to say whether the data's steeper curve is beyond village noise.
  • Outcome (experiments/m2_complex/refine.txt, 234 s): with the fine grid and a free intercept, reinforcement is picked in sample: Rδ fits γ = 0.10, δ = −0.25, q<sub>N</sub> = 0.10, q<sub>P</sub> = 0.1 (extended moments), criterion 2.47e−3 against I's 4.22e−3 (41% lower); γ-hat is positive in 99.5% of 1,000 bootstrap draws (0.05 to 0.20). Freeing δ alone does nothing (Iδ picks δ = 0). Out of sample the prediction held: Rδ is lower than I in 12.2% of 2,000 paired draws (extended set; 22.8% on the BCDJ five), better in 13 of 43 held-out villages, mean held-out loss 0.191 against 0.174. So the in-sample gain does not transfer across villages. Note the fitted q<sub>P</sub> fell from 0.3 to 0.1 when γ was freed: reinforcement and adopters' word of mouth trade off, the identification question of milestone 3.
  • Outcome, take-up by adopting neighbours (paired village bootstrap, B = 2,000): data against the I fit at k = 0: 0.083 vs 0.081 (gap interval [−0.017, +0.022]); k = 1: 0.143 vs 0.184 ([−0.063, −0.018]); k = 2: 0.203 vs 0.227 ([−0.050, −0.000]); k = 3: 0.243 vs 0.248; k = 4+: 0.350 vs 0.272 ([+0.037, +0.117]). The data curve is more convex than the information model's: too few adopters next to one adopter, too many next to four or more. That is the shape reinforcement predicts, and also the shape homophily or a degree effect would give; these data alone cannot say which (Shalizi and Thomas 2011).

2026-11-14 · Plan: fit reinforcement and threshold models, compare out of sample (milestone 2, written before the run)

  • Why: the programme's first question is whether these cross-sectional data can tell a simple contagion from a complex one. Milestone 2 fits two complex-contagion families next to the information model and asks whether either predicts held-out villages better (programme H3). Milestone 3 (identification by simulation) needs these fitted models as its data-generating processes.
  • Models (src/civ_seeding/complex.py; all three share BCDJ's information spread with q<sub>N</sub>, q<sub>P</sub>, leaders informed first, trimesters, beta from the leader logit). Each household draws one uniform U at the start. Information (I): adopts when first informed if U < p(z) = logistic(beta · [1, z]); the M1 model, re-simulated. Reinforcement (R), parameter γ: an informed household adopts in any period where U < logistic(beta · [1, z] + γ k), k its number of adopting neighbours at the start of the period; the cumulative chance of adopting after k adopters is the logit, and γ = 0 is I exactly. Deviation from the proposal written now: k counts adopting neighbours, not adopting neighbours who told the household, because per-tie memory costs n × n × S per village; a household that has been told has usually heard of its adopting neighbours' choice too. Fractional threshold (T), parameter θ: an informed household adopts if U < p(z) or the share of its neighbours who adopted is at least θ; θ > 1 is I.
  • Grids: q<sub>N</sub> in {0, 0.025, 0.05, 0.075, 0.10, 0.15, 0.20}, q<sub>P</sub> in {0.1, 0.2, ..., 1.0}; γ in {−1, −0.5, 0, 0.25, 0.5, 0.75, 1, 1.5, 2}; θ in {0.2, 0.3, 0.4, 0.5, 0.6, 0.75, 1, off}. S = 75 simulations per village and grid point, common random numbers.
  • Moments: the BCDJ five (M1) and an extended set of eight that adds take-up among households with exactly 1, 2 and 3 or more adopting neighbours (the reinforcement signature). Identity weights, as in M1.
  • Out of sample: leave one village out. Fit each family on 42 villages with simulation seed 0, score the held-out village's squared moment divergence at the fitted point with an independent simulation seed (1), so a family cannot win by fitting simulation noise. Paired Bayesian bootstrap over villages (exponential weights, B = 2,000) of the mean loss difference.
  • H3 (programme): R does not beat I out of sample: R's held-out loss is lower in fewer than 95% of paired bootstrap draws, for both moment sets. Refuted if R wins in at least 95% of draws for either set.
  • H3b: the same for T against I.
  • H3c (in sample): the bootstrap 95% interval of γ-hat (extended moments, B = 1,000 village draws) contains 0. Refuted otherwise. BCDJ (2013) reported no endorsement effect; this is the reinforcement analogue.
  • Descriptive, reported not tested: empirical non-leader take-up by number of adopting neighbours (0, 1, 2, 3, 4+), and the same curve simulated at each family's fit. A rising curve alone does not show reinforcement: under I, a household with more adopting neighbours is more likely to have been told.
  • Caveats written now: leaders' logit is fitted to their final take-up, which in R and T includes later reinforced adoption, so beta slightly overstates the intrinsic rate there; grids are coarser than M1's.
  • Outcome (experiments/m2_complex/results.txt, run.py, 123 s on 4 cores). Empirical non-leader take-up by adopting neighbours 0, 1, 2, 3, 4+: 0.083, 0.143, 0.203, 0.243, 0.350. H3 held, uninformatively: on this grid R's fit is γ = 0 for both moment sets and every leave-one-out fold, so R is I; the criterion profile rises 13-fold from γ = 0 to 0.25 and over 1,000-fold by 0.5 (with beta fixed, positive γ adds adoption the level cannot absorb). H3b held: T fits better in sample (θ = 0.75 with the BCDJ five, Q 8.9e−4 against 1.06e−3; θ = 0.60 with the extended set, 3.45e−3 against 4.22e−3) but is lower than I out of sample in only 23.8% of 2,000 paired draws for both sets (better in 20 and 19 of 43 villages; mean held-out loss 0.184 against 0.174, extended set). H3c held, uninformatively: γ-hat = 0 in all 1,000 draws. θ-hat: 0.60 in 65% of draws, 0.50 in 12%, 0.75 in 14%, off in 9%. The two "uninformative" verdicts are design faults of the grid and of fixing beta; the post-hoc entry above repairs both.

2026-11-13 · Plan: reproduce the information model's estimate (milestone 1, written before the run)

  • Why: every later milestone (complex contagion, identification, seeding policies) is scored against the model Banerjee, Chandrasekhar, Duflo and Jackson (2013) fitted to these 43 villages. If our port of their code does not land on their estimate, nothing built on it can be compared with the paper. Targets, from the NBER working paper w17743 (January 2012), read this session: non-leader take-up 18.5% (SD 8.4%), leader take-up 24.8% (SD 12.5%); information model q<sub>N</sub> = 0.10, q<sub>P</sub> = 0.50, both different from 0 (Table 4, Panel A.1); with q<sub>N</sub> set to 0, take-up falls "from more than 20.2 percent to 13.7 percent" and the informed share "from over 81 percent to 57 percent".
  • Data: data/bcdj_villages.json.gz, built by data/build_dataset.py from the replication archive (doi:10.7910/DVN/U3BIHX, CC0; read from a public GitHub mirror because the Dataverse file sits behind a guestbook form). 43 villages, 9,126 households in giant components, 44,367 ties.
  • Method: src/civ_seeding/bcdj.py ports diffusion_model.m, moments.m (version 1, five moments), divergence_model.m and the identity-weighted grid criterion of Main_models_1_3.m: the same grid (31 q<sub>N</sub> by 39 q<sub>P</sub> values), S = 75 simulations per village, trimesters, beta from a logit of leaders' take-up on the six covariates. Common random numbers across grid points (the Matlab code redraws). Standard errors by the authors' Bayesian bootstrap over villages (exponential weights), B = 1,000.
  • H1 (descriptives): non-leader and leader take-up within 0.5 points of 18.5% and 24.8%. Refuted otherwise.
  • H2 (estimate): the grid minimiser is within one grid step of (0.10, 0.50): q<sub>N</sub> in {0.05, 0.10, 0.15} and q<sub>P</sub> in {0.45, 0.50, 0.55}. Refuted otherwise.
  • H3 (q<sub>P</sub> > q<sub>N</sub>): in at least 95% of bootstrap draws. Refuted otherwise.
  • H4 (counterfactual): at our estimate, setting q<sub>N</sub> = 0 cuts simulated take-up by between a quarter and a half (paper: about a third). Refuted otherwise.
  • Robustness, reported not tested: three seeds for the common random numbers.
  • Caveats written now: the published Science version may report different decimals from the 2012 working paper; we test against the working paper because that is the text we read.
  • Outcome (experiments/m1_reproduce/results.txt, run.py, 123 s on 4 cores): H1 held: non-leader take-up 0.187 (SD 0.082), leaders 0.247 (SD 0.126). H2 refuted: the grid minimum is q<sub>N</sub> = 0.05, q<sub>P</sub> = 0.30 for all three seeds (q<sub>N</sub> within one step, q<sub>P</sub> four steps below 0.50); the published point scores 11.3 times our minimum. H3 held: q<sub>P</sub> > q<sub>N</sub> in 98.4% of 1,000 bootstrap draws (q<sub>N</sub> 95% interval [0.05, 0.10], q<sub>P</sub> [0.15, 1.00]; restricting q<sub>N</sub> = q<sub>P</sub> doubles the criterion). H4 held: with q<sub>N</sub> = 0, take-up falls 0.194 to 0.129 (drop 0.337; informed 0.78 to 0.55), against the paper's 0.202 to 0.137 and 0.81 to 0.57.
  • Not pre-registered, run after seeing H2 (twostep.py, periods.py): two-step optimal weights give q<sub>P</sub> 0.20 to 0.25 (q<sub>N</sub> 0.05) whether the weight matrix comes from our first step or from the code's (0.09, 0.45); quarterly periods give (0.05, 0.15), monthly (0.01, 0.10). Nothing tried moves toward (0.10, 0.50). The criterion profile at q<sub>N</sub> = 0.05 stays within a factor 2 of its minimum for q<sub>P</sub> 0.25 to 0.50; at q<sub>N</sub> = 0.10 it is 2 to 16 times the minimum everywhere.
  • Reading: the port reproduces the data, the adopter effect and the counterfactual, not the point. Unresolved causes: other moments, weights or grid in the published table; the Science version against the 2012 working paper; a port difference the tests miss. The weak identification of q<sub>P</sub> is itself a first data point for H2 of the programme. Next (milestone 2): reinforcement and threshold models on the same moments plus take-up by number of adopting neighbours; before that, read the Science version's supplementary table if any host serves it.

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