An English-language GPT-2 playground lets you inspect the model architecture, try independent text completions and read saved Study 12/13 records. Run it locally; inference requires separately available model files. This is published source code, not a hosted chat service or a new experiment.
Completed and audited (10 September): Study 13 equal-coverage replay. Both arms replayed 80 distinct learned facts once, with matched token/step budgets. Priority-minus-random delayed accuracy: +4.50 percentage points, sample SD 2.21; paired values +6.60,+2.20,+4.70. Positive registered three-pair screen only, not significance or general superiority. Terminal-only accuracy and foil separation were mixed. Both prior policies changed; this is not an unchanged Study 12 replication or a mediation test. No new training is authorized. Study 13 write-up · Audit · Registration. See
PUBLICATION.md.
Completed earlier (10 September): Study 12 selective-replay screen. Prioritized-minus-uniform all-fact accuracy: +3.23 percentage points, sample SD 1.62; paired differences +2.40,+2.20,+5.10. Shared learned model/optimizer starts and matched 80-replay token budgets. Positive registered small-screen signal, not significance or general superiority. Wider distinct-fact coverage remains an alternative explanation; true-versus-foil separation did not consistently improve. Study 12 write-up · Audit. Study 11's gap retest was separately mixed: -1.93 points, SD 2.39. Study 11 write-up. No studies beyond the approved Study 13 are authorized.
Historical status (9 September): Study 10 replication completed and verified. Primary variable-minus-fixed accuracy: +0.01143, sample SD 0.02767, range -0.00929 to +0.04286: mixed/inconclusive. Secondary NLL delta -0.09338, SD 0.03197, range -0.12803 to -0.06502; secondary terminal accuracy delta +0.04500, SD 0.02000, range +0.02500 to +0.06500. These do not replace the primary endpoint or establish acquisition-independent forgetting. Study 10 write-up · Full evidence · Audit. Study 9 remains separately inconclusive: primary delta +0.04238, SD 0.05866, range -0.02000 to +0.09643. No pooling or additional runs.
Current Turkish explanation · Historical Study 10 infographic The infographic timelines are schematic; the numeric interval labels specify the schedule.
Follow-up clarification: the secondary true-NLL gain does not isolate factual specificity; incorrect same-template answers also improve on average and separation does not consistently improve. Post-hoc specificity check. This clarifies an existing guard, not a new independent finding or a changed primary result.
Prior control (8 September): Study 8 completed. Matching each fact's final exposure yielded random-minus-spaced retention +0.01595, sample SD 0.04427, seed range -0.03214 to +0.05500: mixed/inconclusive. NLL difference was -0.05382, SD 0.08139. No superiority or equivalence conclusion. Study 8 results. Study 9 matched both endpoints and compared fixed gaps [64,64,64,64] to permuted [32,32,64,128] in six fresh runs. Study 9 registration. See the current status above. These synthetic-fact experiments do not establish personalization or PEFT benefits. Check
PUBLICATION.mdbefore launching any training command.
Status correction, 8 September 2026: Study 6b reused a spaced control from before the filler cache grew. A registered provenance audit reproduces changed training/held-out streams for all three seeds and finds pre-intervention log differences. The claim "ordinary shuffling suffices" is withdrawn pending a fresh matched-data comparison. This does not invalidate all within-study results. Current audit and limitations · Kısa Türkçe durum.
I compared synthetic-fact training with ordinary-text controls matched for repetition timing and training budget. Across three seeds, short prompts with an EOS prefix (a special boundary token) triggered learned-topic intrusion in the consecutive synthetic-fact condition, but none was detected in the spaced or ordinary-text conditions. Repetitive output still occurred with ordinary text. No detected intrusion does not mean the answers were good.
I give the model this fact to learn:
The capital of Sheipiakvuk is Prothkunshend.
In both conditions, I show it the exact same sentence five times. Only the timing changes:
| schedule | simplified view | gap between exposures |
|---|---|---|
| Massed | fact → fact → fact → fact → fact |
1 training step |
| Spaced | fact → … → fact → … → fact … |
64 training steps |
The diagram is conceptual. In the real experiment, the gaps contain other training data; the model is not explicitly quizzed between exposures.
The intuition behind my test is simple: five updates arriving back-to-back can leave a fragile memory. The same five updates separated by other training data may leave a more durable trace. That is the idea I test here, not a universal rule.
I asked whether spreading five exposures apart helps a small language model keep a new fact through later fine-tuning, compared with showing the same five exposures consecutively. Here, later fine-tuning means 1,500 steps of filler plus new facts that can interfere with the old ones.
I borrow the spacing effect from human memory research: the same number of study repetitions often gives better long-term retention when the repetitions are spread out instead of massed.
My pre-registered hypothesis was not supported as written. Spaced repetition looked better, but the two conditions did not learn the facts equally in Study 1:
- right after each fact's fifth exposure: massed 43%, spaced 81%;
- at the end of the injection window: massed 3%, spaced 65%;
- after 1,500 interference steps: massed 0%, spaced 14%.
I therefore treat the observed difference as a combination of learning and durability. I do not interpret it as slower forgetting after equal learning, and a lost correct output is not proof that an internal representation was erased. I keep the full paired results and failed decision rules below.
I committed the design, prediction, decision rule and named traps before any number existed (PREREGISTRATION.md); the four amendments made during calibration are recorded there with the pilot numbers that forced them.
- Model: GPT-2 (124M), full fine-tuning on Apple-Silicon MPS, AdamW
lr=1e-4, dropout off. - Facts: I use 200 invented paired-associate facts per seed, such as the example above. The pretrained model scores exactly 0 on them.
- Injection window: each fact is shown five times in 700 steps, mixed with a fixed WikiText-103 filler stream (15 chunks of 64 tokens per step).
- Schedules: the gap between exposures is 1 step (massed), 4, 16, or 64 steps (spaced). Each fact's final exposure step is shared across conditions, so the time since the final exposure is matched.
- Interference: 1,500 further steps of filler plus 50 new facts of the same kind.
- Measurement: exact-match accuracy and answer NLL at seven checkpoints.
- Runs: I ran five seeds for massed and gap 64, three seeds for the intermediate gaps, plus one repeat run. I inventory 73 main logs, but these are not 73 independent replications.
The later audit also found small differences in per-exposure batch weight. That is why the comparison is described as a schedule-policy effect rather than a perfectly isolated gap-only mechanism; see Study 6a.
Left: exact-match accuracy on the 200 injected facts at the end of the injection window (step 0) and at the seven interference checkpoints. Right: answer NLL (lower = better remembered). Thin lines are single seeds, thick lines the mean.
| condition (gap) | seeds | immediate acc | retention score | acc at step 1500 | acc right after last exposure |
|---|---|---|---|---|---|
| massed (1) | 5 | 0.03 (0.02..0.04) | 0.001 (0.000..0.001) | 0.00 | 0.43 (0.26..0.64) |
| gap 4 | 3 | 0.08 (0.06..0.09) | 0.023 (0.008..0.038) | 0.01 | 0.94 (0.92..0.95) |
| gap 16 | 3 | 0.35 (0.33..0.38) | 0.124 (0.111..0.144) | 0.05 (0.04..0.08) | 0.96 (0.94..0.99) |
| spaced (64) | 5 | 0.65 (0.62..0.68) | 0.285 (0.241..0.351) | 0.14 (0.10..0.20) | 0.81 (0.78..0.85) |
Retention score = mean exact-match accuracy over the seven interference checkpoints (the pre-registered primary outcome). Paired spaced − massed retention difference: +0.29, seed-to-seed SD 0.04, positive in every one of the five seeds (range +0.24..+0.35). One repeated run differed by 0.014 in retention and 0.000 in immediate accuracy. Historical decision rules used this as a noise band, but one pair cannot calibrate such a band. Retention is monotone in the gap in every seed where all four gaps were run.
Guards. Within a seed, every condition took the same 2,300 optimizer steps, saw the same 2,208,000 filler tokens and the same 18.5–18.9k fact tokens; pre-injection accuracy was exactly 0 in all 17 runs; weight displacement after the window was 79.5–81.1 in every condition (no condition "moved more"); held-out filler loss at the end was 3.37–3.45 everywhere, so the interference phase trained equally.
| rule | result |
|---|---|
| 1. spaced > massed retention in every seed | yes (5/5) |
| 2. mean Δ exceeds seed SD and noise band | yes (0.29 vs 0.04 and 0.014) |
| 3. immediate difference smaller than retention difference | no (+0.62 vs +0.29) |
So H1 is not supported as pre-registered. Rule 3 was written to catch the boring explanation "spaced simply learned more". It fired. Reporting that first is the point of writing the rule down beforehand.
Calibration failure, as Amendment 2 requires it to be called. Amendment 2 committed to checking the immediate-accuracy band [0.5, 0.95] in the main runs and to reporting a violation as a calibration failure rather than repairing it. Three of the four conditions violate it: massed 0.03, gap 4 0.08, gap 16 0.35. Only spaced (0.65) is inside the band. Nothing was re-tuned; the runs stand as they are, and the floor in the massed condition is the reason the pre-registered framing could not be tested. The Amendment 4 probe below was added before the main runs to make that floor interpretable, not after.
The pre-registered "immediate" probe sits at a fixed step, up to 444 steps after a fact's last exposure, inside a window that is itself dense with interference (the other 199 facts). A low immediate score can therefore mean never encoded or encoded and lost inside the window. Amendment 4 added a probe of each fact right after the optimizer step of its own last exposure. That probe separates the two:
- massed facts are encoded: 43 % exact-match right after the fifth consecutive step (NLL 1.1), against 81 % for spaced and 94–96 % for gaps 4 and 16;
- and they do not last. Take only the facts that were correct at that moment. At the end of the window, 6 % of them are still correct for massed vs 77 % for spaced. Averaged over the seven interference checkpoints that follow, 0.2 % vs 33 %.
Exploratory, pooled over seeds: split facts by how long they waited between their last exposure and the end-of-window probe. Massed facts that waited under 50 steps survive at 24 %; over 50 steps, 0 %. Spaced facts survive at 100 %, 99 %, 92 %, 63 % and 20 % for waits of 0–50, 50–100, 100–200, 200–300 and 300–450 steps. Restricting to strongly encoded facts (NLL < 0.1 right after the last exposure) changes nothing for massed: 9.5 % survive to the end of the window, against 93 % for spaced.
What the massed model says instead is telling: it produces invented-looking names of the right kind ("Zusvrox", "Prairhenv") but not the associated one. It learned the format of the facts and lost the item.
Honest summary of Study 1. The pre-registered framing ("equal encoding, then who keeps more") could not be tested, because consecutive exposures never produce a memory that survives to the first probe. The finding that replaced it is stronger and simpler: the same five gradient steps on the same sequence produce a durable memory when spread out and a memory with a half-life of tens of steps when consecutive, with total steps, tokens, filler, and time-since-last-exposure held fixed. gap 4 is almost as bad as gap 1; gap 16 is half-way; gap 64 is the best we tested (we did not test larger gaps, so we do not know where the benefit stops).
Study 2: four follow-ups, pre-registered in Amendment 5 (2a, 2b, 2d before their runs; 2c's prediction was written while its first run was already going)
Solid = Study 2 runs (thin: seeds, thick: mean). Dashed = the matching Study 1 curves.
| sub-study | question | prediction (written first) | result | verdict |
|---|---|---|---|---|
| 2c massed with K = 10, 20 (seed 0) | can more consecutive repeats reach spaced's immediate level? | no: stays < 0.30 | acc right after last exposure 0.99 / 0.995; end of window 0.025 / 0.06; retention 0.005 / 0.014 | prediction held; a learning-matched massed control is not reachable this way |
| 2a Adam with beta1 = 0 (3 seeds) | is momentum the mechanism? | penalty persists | spaced − massed retention +0.30 (seeds +0.33, +0.28, +0.30; Study 1: +0.29). massed now encodes 0.95–0.98 right after the last exposure (was 0.43) and still ends the window at 0.06–0.08 | Adam's first-moment momentum is not required for the gap (β₂ untested); β₁ only weakened massed encoding |
| 2b LoRA (3 seeds) | does it hold for adapters? | same direction | calibration failed: ranks 16/64, lr 3e-4..1e-2, best immediate 0.245. At rank 64 / lr 1e-3: end-of-window 0.31 vs 0.015 in every seed, but both reach 0.00 by interference step 800–1500; retention Δ +0.03 (SD 0.015, noise 0.014) | rules 1–2 pass formally, by two hundredths; the ordering replicates at the end of the window, but the retention comparison is a floor effect and no size is read |
| 2d five paraphrases instead of five copies (3 seeds) | does wording diversity substitute for spacing? | partial substitution | massed+para − massed = +0.002; spaced+para − spaced = −0.20 (every seed). Right after its 5th exposure a massed+para fact is correct in the canonical form only 0.5–2.5 % of the time | prediction failed; no substitution, not additive. Confounded: the probe uses the canonical sentence, seen once in this condition (see below) |
2c in words. Twenty consecutive exposures push the fact to 99.5 % right after the last step and it is at 6 % by the end of the window. The pre-registered contingency ("raise K until massed matches spaced immediately") cannot be executed because no number of consecutive repeats produces a memory that survives to the probe. That is itself the finding: the problem with massed exposures is not how much they teach, it is how long it lasts.
2a in words. Turning off Adam's first moment changes absolute levels a little (both conditions encode more) and the paired gap not at all. Under Adam the normalised step for five identical consecutive gradients is the same with or without momentum, so this was the expected outcome, but the "it's just momentum overshoot" objection needed a measurement, not an argument. It also corrects something I wrote earlier in this run: massed's weak at-last encoding in Study 1 (0.43) was a momentum artefact; the decay was not.
2b in words. LoRA at every setting we tried holds these 200 facts poorly: even random placement (the pilot) peaks at 0.25 immediate and 0.00 after 400 interference steps. At the best setting, massed still ends the window near zero (0.01–0.02) and spaced at 0.31 in all three seeds, so the direction is the same as in full fine-tuning. Nothing survives 1,500 interference steps in either condition, so the retention score cannot separate them. We report the ordering, not a size. Weight displacement is larger for massed under LoRA (89.7 vs 78.1), the opposite of "spaced moved more".
2d in words. This one died. Five different sentences in five consecutive steps leave the canonical form at 0.5–2.5 % right after the fifth step, so there is nothing to retain. Spaced paraphrases lose about 20 points against spaced copies on the canonical probe, and NLL goes the same way (+0.79). Two readings, and the design cannot separate them: (i) with one exposure per wording, the model does not merge the five wordings into one fact retrievable from any of them; (ii) the probe is unfair to paraphrase conditions because their eval sentence was seen once instead of five times. Study 4 below ran the fair probe and settled it: reading (ii).
Guards, Study 2. Steps and filler tokens identical to Study 1 within seed; fact tokens identical for 2a/2b, +2.9 % for 2d (paraphrases are slightly longer), 1.8× / 3.5× for 2c by design. Pre-injection accuracy 0 in all 20 Study 2 runs. Held-out filler loss at the end 3.37–3.43 for 2a/2d (same as Study 1), 3.56–3.63 for LoRA.
Study 3: is the massed memory erased, or only hidden? (Amendment 6, pre-registered)
Two fair objections to reading exact-match accuracy: NLL on the true answer falls for massed too (8.5 → 5.0), so something is retained; and a memory can vanish at the output while a trace remains in the weights. Two measurements were added, each with a control that cancels the obvious confound, and six runs (massed vs spaced, seeds 0–2) were made.
Discrimination = NLL(foil answer) − NLL(true answer), the foil being another fact's invented name from the same template. Format learning affects both equally and cancels. Sanity check passed: the pretrained model scores +0.05, i.e. no preference.
Savings (Ebbinghaus): after interference, every old fact and every one of 200 never-seen control facts is shown exactly once; both sets are then probed.
| massed (3 seeds) | spaced (3 seeds) | |
|---|---|---|
| discrimination at end of window | +0.19 .. +0.25 | +2.67 .. +3.03 |
| discrimination after 1,500 interference steps | +0.24 .. +0.46 | +2.06 .. +2.60 |
| share of facts where true answer beats foil | 54–60 % | 91–95 % |
| accuracy gain from one re-exposure, old facts | 0.000, 0.000, −0.005 | +0.105, +0.240, +0.200 |
| same for never-seen controls | 0.000 | 0.000 |
| NLL of old facts after one re-exposure vs controls | 3.8–4.1 vs 5.7 | 1.2–1.5 vs 5.7 |
Reading, corrected 8 September. Prediction 1 held: massed discrimination is above zero in every seed, and below spaced. Prediction 2 failed under the registered one-re-exposure test. However, both massed and unseen controls are at the accuracy floor; this does not establish absence of savings or unusability of the remaining trace. Spaced old facts improve by 10.5–24 percentage points, but their starting accuracy differs from controls, so this is not a clean savings estimate. The old "90% format, not knowledge" claim is withdrawn: one chosen foil does not identify that causal decomposition. Multiple re-exposure budgets and continuous measures would be needed to assess relearning sensitivity.
One oddity for the record: for spaced facts the single re-exposure raised accuracy but lowered discrimination (2.6 → 1.6). The relearning batch also contained 20 unseen facts per step, which pull the format prior toward "any invented name"; accuracy and the foil-relative margin can move in opposite directions under that pressure. Not investigated further.
Study 2d's probe was the canonical sentence, which copy conditions saw five times and paraphrase conditions once. Study 4 re-ran all four conditions (seeds 0–2, 12 runs) with an added probe through a sixth wording no condition ever saw. Training is unchanged; the canonical-probe numbers replicate Study 1 and 2d on the same seeds to within 0.01 (a third replication).
| retention, mean of 3 seeds | canonical probe | unseen-wording probe | discrimination, unseen |
|---|---|---|---|
| massed | 0.002 | 0.001 | +0.18 |
| massed + paraphrases | 0.002 | 0.002 | +0.29 |
| spaced (5 copies) | 0.306 | 0.060 | +1.13 |
| spaced + paraphrases | 0.092 | 0.108 | +1.34 |
End-of-window accuracy tells the same story more sharply: five copies give 0.667 on the trained sentence and 0.275 on the unseen one (a 40-point drop); five paraphrases give 0.348 and 0.365 (no drop at all; prediction 1, "everyone scores lower on the unseen wording", failed for this condition).
Pre-registered rule. spaced+para − spaced on unseen-wording retention: +0.056, +0.043, +0.044, all above the 0.041 spread, so the rule calls it "diversity buys generalisation". The margins are two to fifteen thousandths above the threshold, and I would not have believed the call on retention alone. What makes it credible is that the same ordering holds at the end of the window by a wider margin (+0.055, +0.080, +0.135) and in discrimination (+0.27, +0.18, +0.18). massed+para stays at zero (prediction 3).
What this corrects. Study 2d's reading (i) was wrong and reading (ii) was right: the paraphrase penalty was the probe, not the model. The honest summary of both studies is a trade, not a loss: copies help the trained wording; paraphrases help the tested unseen wording. This is one held-out wording per relation, not proof of wording- independent factual knowledge. Neither wording condition rescues massed accuracy in this protocol.
Window doubled to 1,400 steps so gaps of 128 and 256 fit; all gaps re-run in that window (seeds 0–2).
| retention score | gap 1 | gap 16 | gap 64 | gap 128 | gap 256 |
|---|---|---|---|---|---|
| seed 0 | 0.004 | 0.171 | 0.366 | 0.280 | 0.296 |
| seed 1 | 0.000 | 0.108 | 0.194 | 0.274 | 0.222 |
| seed 2 | 0.002 | 0.104 | 0.224 | 0.161 | 0.175 |
| mean | 0.002 | 0.128 | 0.261 | 0.238 | 0.231 |
Reading. The rising limb 1 < 16 < 64 replicates in every seed (prediction 1). Prediction 2, "128 beats 64", failed: 128 is below 64 in two of three seeds (−0.086, −0.063) and above in one (+0.080). Beyond 64 the curve is a plateau whose seed-to-seed wobble (gap 64 alone spans 0.19–0.37) is larger than any gap-to-gap difference. The pre-registered rule for 256 vs 128 (+0.016, −0.051, +0.014; two of three inside the 0.041 spread) returns "saturates". Prediction 3 (diminishing returns in every seed) also failed: in seed 1 the 64 → 128 change was positive, followed by a negative 128 → 256 change; in seeds 0 and 2, a negative change was followed by a positive one. These are not monotone diminishing increments. Encoding right after the last exposure also weakens at large gaps (gap 64: 0.84 → gap 128: 0.61 → gap 256: 0.58 in seed 0): when the earlier exposures are hundreds of steps back, the fifth one has less to build on. That is the shape of the human lag effect (Cepeda et al. 2008), where too much spacing stops helping because each repetition no longer finds the previous trace. Scope: one window length, one interference length; the human result says the optimum moves with the retention interval, which we did not vary.
Practical restatement. Larger tested gaps did not consistently improve retention over 64 in these three seeds. This does not establish equivalence or a universal optimal gap.
An outside review raised two objections worth answering before anything else. The exported review transcript is not included in this public snapshot; see Amendment 9.
6a. Did only the gap change? The per-step loss is a mean over sequences (15 filler
plus n facts), so one fact exposure weighs 1/(15 + n) in its step. Massed exposures
cluster, so n is larger when facts are present. Reconstructed from every schedule
(spacinglab.audit, no training):
| Study 1 window | steps with facts | facts/step when present | max facts/step | mean weight per exposure |
|---|---|---|---|---|
| massed | 403 | 2.48 | 9 | 0.0553 |
| gap 4 | 406 | 2.46 | 8 | 0.0554 |
| gap 16 | 428 | 2.34 | 9 | 0.0556 |
| spaced | 504 | 1.98 | 8 | 0.0569 |
| random | 538 | 1.86 | 7 | 0.0577 |
Massed exposures carry 2.8 % less loss weight than spaced ones (3.0 % in the Study 5 window). It falls inside the pre-declared 5% operational threshold, but that threshold does not establish equivalence. Extra-exposure controls do not bound this confound's causal effect: optimization is not linear in repetition count. Gradient-clip ratios were not logged and cannot be reconstructed. Interpret the comparison as a total schedule-policy effect, not an isolated gap-only mechanism.
6b. Does ordinary shuffling already give you this? Condition random: each fact's
five exposures at five uniformly random steps of the window, seeds 0–2, with nominal
settings from Study 1. This synthetic placement is not a literal epoch-wise data
shuffle, and it is deliberately not last-exposure-matched. The 8 September audit
found that the intended filler-stream matching cannot be sustained.
| seeds 0–2 | immediate | retention score | acc at step 1500 |
|---|---|---|---|
| massed | 0.03 | 0.001 | 0.00 |
| spaced (gap 64) | 0.66 | 0.298 (0.351, 0.266, 0.277) | 0.16 |
| random | 0.75 | 0.360 (0.439, 0.292, 0.347) | 0.23 |
random − spaced = +0.088, +0.026, +0.070 (mean +0.061, sample SD 0.032). The historical decision rule labeled this "ordinary shuffling suffices". That interpretation is withdrawn: the comparison reused an old control, and both input-stream reconstruction and pre-intervention logs now indicate a matching problem. These numbers remain descriptive, not an isolated placement effect. Recency, variable gaps, and batch composition also differ by design; neither equivalence nor a real-world shuffle recommendation follows from this comparison.
The robust engineering lesson from the audit is to freeze and fingerprint the actual training and held-out streams, rather than equating equal seeds or token counts with equal data. Within this GPT-2 synthetic-fact protocol, clustered repetition performed poorly and spaced repetition warrants further testing. We do not yet have a validated shuffle replacement, universal minimum gap, or evidence for a brain-like mechanism.
First rerun both random and spaced conditions freshly in three pairs, with immutable data/model/software provenance and acquisition, NLL, batch-weight and clipping guards. Do not reuse historical spaced controls. This estimates a total placement-policy effect, not equal-acquisition forgetting. Three seeds screen direction, not equivalence.
Worth continuing: yes, at this bounded comparison. A calibrated multi-budget savings test and a second small model are later steps. Mechanism work and publication should not outrun validation of the practical baseline.
One model (GPT-2 124M), one fact format (single-sentence synthetic paired associates), one filler and interference corpus (WikiText-103), one learning rate, K = 5. Studies 1–4 test gaps up to 64 steps in a 700-step window; Study 5 extends gaps to 256 in a 1,400-step window. Nothing here speaks to larger models, real-world facts, or other interference domains. The mechanism story (why consecutive identical steps leave a fragile trace) is a hypothesis; Study 2a tests one piece of it and no more.
Prior work (see docs/literature.md) has studied duplication vs paraphrase and corpus-level repetition, and Chang et al. (2024) report that duplicated injections forget faster than paraphrased ones; we found no earlier measurement that varies only the gap between repeats of one fact with everything else matched.
uv sync
uv run pytest
scripts/main_runs.sh # 17 runs, ~2.7 h on an M-series laptop
uv run python -m spacinglab.analyze # Study 1 pre-registered analysis
uv run python -m spacinglab.explore # Study 1 exploratory analyses
uv run python -m spacinglab.plot # results/retention.png
scripts/study2_runs.sh && scripts/study2b_runs.sh && scripts/study2d_runs.sh # Study 2 (~3.5 h)
uv run python -m spacinglab.analyze2 # Study 2 paired analysis, Amendment 5 rules
uv run python -m spacinglab.plot2 # results/study2.png
scripts/study3_runs.sh && uv run python -m spacinglab.analyze3 # Study 3 (~1 h)
scripts/study4_runs.sh && uv run python -m spacinglab.analyze4 # Study 4 (~2 h)
scripts/study5_runs.sh && uv run python -m spacinglab.analyze5 # Study 5 (~3 h, resumable)
uv run python -m spacinglab.audit # Study 6a (no training)
scripts/study6_runs.sh # Study 6b (3 runs, ~30 min)Pilot logs: results/pilot*.log. Main-run logs (per-fact evaluations, generated
answers, guards): results/runs/*/log.json.