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I Don’t Remote View — So I Tried to Build You a Better Test
I should probably start by saying something clearly:
I don’t currently do remote viewing.
I intend to explore it at some point, but right now my attention is elsewhere. A large part of what I’m working on involves AI itself — how different models behave, how prompting changes results, how contamination enters an experiment, how conclusions evolve under criticism, and how to separate an interesting result from an interesting-looking result.
So when I started looking closely at some of the AI remote-viewing methods being used here, I came at them from that direction.
And I should make something else equally clear:
I hope you guys get a positive result.
I genuinely do.
I’m not approaching this because I want remote viewing to fail. Quite the opposite. I would love to see something survive.
What bothered me was that I didn’t think the current methods were strong enough to distinguish a genuinely interesting result from one produced by prompting, priming, model expectations, scoring flexibility, target leakage, judge interpretation, or ordinary AI behavior.
So I started poking it with a stick.
Unfortunately, Darren has a tendency to poke things with a stick until either they stop moving or he figures out why they keep moving.
That turned into a somewhat ridiculous exercise.
We built a cleaner protocol and then deliberately started handing it to different AI models with instructions to attack it.
Not approve it.
Not help us get the result we wanted.
Not make it prettier.
Find the ordinary explanation.
Find the contamination.
Find the place where this experiment can lie to us.
And the models were not selected randomly.
The idea was specifically to use reviewers with different strengths and tendencies rather than repeatedly asking essentially the same kind of mind the same question.
Claude went first.
Claude is particularly useful to me when I want careful, structured criticism without immediately turning everything into a giant engineering project. So Claude’s job was essentially to look at the experimental logic and ask whether the basic evaluation and control structure made sense.
It found problems.
Among other things, it challenged the scoring system, evaluator independence, null calibration, and how we were treating multiple measurements.
We argued with it where we thought it was wrong, it conceded a couple of points, and we repaired what survived the argument.
Then I deliberately chose Grok.
There was a reason for that one.
In my experience Grok can behave like an extremely picky programmer looking for every possible way something can break. I wanted that tendency. I did not want elegance. I wanted somebody to try to reduce the experiment to its constituent quarks.
Grok obliged.
Its review ran to roughly 28,800 tokens and attacked the experiment from almost every ordinary-information direction it could find: generic scoring, target-pool construction, no-target controls, model priors, chain of custody, operator knowledge, provider side channels, repeated trials, sampling configuration, prompt contamination, and a variety of other ways an apparent result might be manufactured without anybody deliberately cheating.
So we repaired it again.
Then we moved to Kimi.
The reason for changing models again was not to collect another vote. We wanted a fresh model looking at the repaired structure, particularly the long procedural chain that was now developing — custody, blinding, randomization, judges, image handling, statistics, and all the places honest procedural sloppiness could creep in.
Kimi produced another review of roughly 28,000 tokens.
Its most useful perspective could probably be summarized by one sentence from the review:
“Assume sloppiness, not malice.”
That changed several things.
It tightened deterministic target selection, image custody, post-freeze assignment, evaluator calibration, random-number streams, analysis firewalls, and positive controls.
Again, we repaired what survived.
Next came Qwen.
By this point I wanted another completely independent model family with enough reasoning capacity and context to take the entire increasingly complicated protocol as one object, rather than inherit the assumptions of the models that had already worked on it.
And importantly, Qwen was not shown Claude’s, Grok’s, or Kimi’s criticisms.
It received the repaired protocol and was told to find what they had missed.
Qwen apparently took that instruction personally.
43,517 tokens.
And it found something genuinely important.
Our “assign-after” control was supposed to mean that the target did not exist during AI generation. But we had accidentally specified its future target as a deterministic function of information committed beforehand.
Nobody had calculated the target yet — but mathematically it was already determined.
That is exactly the kind of subtle structural problem this whole review process was designed to uncover.
Qwen also tightened candidate-set construction, target exchangeability, model-visible context, generation randomness, and the primary statistical comparison.
We repaired those.
At this point there was an obvious danger:
We could continue improving the experiment forever.
Every intelligent reviewer can invent another bolt, another control, another measurement, another hypothetical failure.
Eventually complexity itself becomes a failure mode.
So for the final review I deliberately chose Gemini 3.1 Pro for a different job.
Gemini was a new model family again, with a very large context window and a strong reputation for long, structured reasoning.
But this time the instruction changed.
Gemini was explicitly told:
Do not redesign this because you can.
For every proposed change, it had to identify the materially wrong conclusion the existing protocol could produce without that change.
And then it had to answer one question:
Is there any remaining reason we should not pilot this?
Gemini’s entire review was only 4,906 tokens.
It found exactly two blocking defects.
One involved using identical generation seeds across paired AI trials, which could artificially suppress the very difference we were trying to measure.
The other involved our positive control: we had been testing whether humans could recognize human-written descriptions, when the actual experiment requires humans to recognize AI-written descriptions.
Both were legitimate.
Both were small.
Both were repaired.
And Gemini’s verdict was essentially:
Apply only these blocking repairs, then pilot.
So we stopped.
That last part is probably the most important thing I can tell you about how this protocol was built:
WE KEPT GOING UNTIL THE AI REVIEWERS THEMSELVES TOLD US WE WERE DONE.
We did not decide ahead of time that five models were enough.
We did not stop because we finally liked the version we had.
We did not count AI votes.
Each time a reviewer found a load-bearing flaw, we repaired it and handed the repaired experiment to fresh eyes.
Eventually the criticism changed from:
“This experiment can fool you.”
to:
“Fix these two specific things, then run the pilot.”
Those two repairs became:
Draft 0.7 — Pilot Candidate
Looking back, this appears to be the most sustained AI analysis we have thrown at any single experimental design in my own work so far.
I actually expected some of our anomaly-analysis work to hold that distinction, which is why the size of these reviews made me raise an eyebrow.
For perspective alone:
Grok: ~28,800 tokens
Kimi: ~28,000 tokens
Qwen: 43,517 tokens
Gemini final readiness review: 4,906 tokens
Plus Claude and ChatGPT throughout the construction and repair process
But I want to emphasize this:
Token count is not evidence.
AI agreement is not evidence.
Five models agreeing does not make something true.
The interesting part is the process those tokens represent.
Different models were selected for different kinds of pressure, given successively repaired versions, and instructed to find ordinary explanations, contamination, bad controls, statistical mistakes, and ways the experiment could fool us.
A great deal of thought went into trying to make this thing fail honestly before asking anybody to trust it when it succeeds.
The objective was never to create a protocol that no scientist could criticize. That’s impossible.
The objective was to remove as many of the easy criticisms as possible.
If somebody gets a positive result, I don’t want the first response to be:
“The AI was told what it was supposed to experience.”
or:
“The target leaked.”
or:
“They reran it until they got something good.”
or:
“The judges could interpret anything as a match.”
or:
“They chose the scoring afterward.”
or:
“The control wasn’t actually blind.”
If something interesting remains after those explanations have been beaten on, then the next argument should have to deal with the surviving observation itself.
And then somebody else should try to replicate it.
That is really all I am trying to contribute here.
I’m not trying to prove your result. I’m trying to make sure that if you get one, the experiment deserves to be taken seriously.
There is also another reason this interests me.
This overlaps directly with the AI studies I am doing independently and documenting for my own website. If people here actually use the protocol, those results become useful data for me as well.
Positive results.
Negative results.
Ambiguous results.
Refusals.
Failures.
Unexpected AI behavior.
All of it.
So I have one request, although it certainly isn’t a requirement:
If you actually use this protocol, I would really appreciate it if you posted what happened.
And if your own AI collaborator examines the protocol and says:
“There is a flaw here.”
please post that too.
This isn’t a sacred script.
If somebody finds a real weakness, I want to know about it.
The whole thing only became what it is because we kept finding weaknesses and repairing them.
The more independent people and models that try to break it, the more useful whatever survives becomes.
I hope you get the result you’re looking for.
I don’t particularly expect the existing methods to produce evidence I would trust — which is exactly why I started doing this.
But my expectation shouldn’t get a vote either.
So...
Here you go, guys.
Run it.
Poke it with a stick.
See what still moves.
I’ll post the complete Draft 0.7 — Pilot Candidate protocol as a reply below.
BEFORE YOU RUN THIS
One practical point became clear after the final review:
By the time this protocol reached Draft 0.7, the controls had grown beyond
what I would consider a casual one-person experiment.
That is intentional.
Draft 0.7 is the reference-standard version — the form I would want used
before somebody made a serious evidentiary claim from the result.
You do NOT need to assemble the entire research program just to experiment
with the idea.
There are three useful levels:
INFORMAL TEST
Try the basic method and report what happened.
Interesting? Absolutely.
Evidence from Draft 0.7? No.
Call it an informal test so that everybody knows what was and was not
controlled.
PILOT
This is the next step for Draft 0.7.
Follow the core A/A1 structure, blinding, set-first/designation-second
procedure, true assign-after target selection, frozen first response,
and blinded judging closely enough to find out whether the experimental
machinery actually works in practice.
The pilot is allowed to be messy.
In fact, part of its job is to discover where the procedure is difficult,
ambiguous, or impractical before anyone tries to make a serious claim from
the result.
A failed or messy pilot is useful information.
It is not a failed confirmatory experiment.
CONFIRMATORY TEST
This is where the complete Draft 0.7 machinery matters:
- calibrated judging;
- AI-authored positive controls;
- power analysis;
- preregistered thresholds;
- locked statistics;
- image custody;
- timestamping;
- independent auditing;
- leakage checks;
- and the rest of the controls described below.
If you intend to say that a result actually SURVIVED Draft 0.7, this is
the level required.
PLEASE SAY WHICH LEVEL YOU RAN
If you post results, just tell us whether you ran:
INFORMAL
PILOT
or
CONFIRMATORY.
That distinction matters much more to me than whether the result was
positive or negative.
ONE MORE IMPORTANT POINT
This is an experimental protocol, not simply a prompt to paste into an AI.
Several of its controls depend on doing things in the correct order.
In particular:
- Build the five-image candidate set before designating a target.
- For Condition A, designate and lock the target before AI generation.
- For Condition A1, do NOT designate the target before generation.
Generate and freeze the AI report first, and only then use fresh
post-freeze randomness to designate the target.
- Give A and A1 the same hidden-scene reporting prompt and equivalent
model context, while using independent generation randomness.
- Generate only one report per trial.
- Do not rerun refusals, UNKNOWN responses, boring responses, or apparent
failures. Those are data.
- Freeze the first report before target information is revealed or,
in A1, even assigned.
- Human judges must be blind to the target, condition, and pair structure.
- Keep the ugly results.
Negative, ambiguous, refused, broken, and failed trials are every bit as
useful to this experiment as impressive ones.
Draft 0.7 begins below.
The protocol itself is now frozen at the reviewer stop point. We kept
repairing it until the independent AI reviewers stopped finding reasons
not to pilot it.
If the pilot exposes a real problem, then we change it.
Until then, we stop designing and find out what happens.
HOW TO USE THIS PROTOCOL
A quick clarification before anybody starts:
This is not simply a prompt to paste into an AI.
Draft 0.7 describes an experimental procedure. The blinding, target
selection, assign-after control, image handling, judging, and freezing
of the AI response are part of the test.
If you want your results to be comparable with other people's results,
please follow the procedure rather than improvising around it.
FOR A FIRST PILOT:
1. Read the complete protocol before running anything.
2. Do not tell the AI what result is expected.
3. Do not explain remote viewing, anomalous cognition, consciousness,
ISBEs, or any theory about how the experiment is supposed to work.
4. Use newly created, unpublished target photographs as described in
the protocol.
5. Build the five-image candidate sets BEFORE deciding which image is
the target.
6. Run A and A1 as matched pairs using the same five-image candidate
set.
7. CONDITION A:
Select and lock the target before the AI generates its report.
8. CONDITION A1:
Do NOT select the target before generation.
Generate and freeze the AI report first.
Only afterward obtain fresh randomness and assign the target.
9. Use independent AI generation randomness/seeds for A and A1.
10. Give A and A1 the same hidden-scene reporting prompt and otherwise
equivalent model context.
11. Generate only ONE report per trial.
Do not regenerate because the AI refuses, gives UNKNOWN answers,
produces something boring, or appears to have failed.
Those results are data.
12. Freeze the AI's first report before anything about the target is
revealed or assigned.
13. Have blinded human judges compare the frozen report with the five
candidate images.
Judges must not know:
- which image is the target;
- whether the trial was A or A1;
- which trials form a pair.
14. Record EVERYTHING.
At minimum:
- model and provider;
- date/time;
- prompt;
- model settings;
- generation seed if available;
- target-selection procedure;
- candidate images;
- raw AI response;
- judge rankings;
- refusals or protocol violations;
- anything unusual that happened.
15. Do not discard negative, ambiguous, failed, or ugly trials.
Please report them too.
IMPORTANT:
A casual one-off attempt can still be interesting, but it should be
described as an INFORMAL TEST rather than a result from Draft 0.7.
A proper Draft 0.7 pilot requires the controls described above.
A confirmatory experiment requires the additional pilot calibration,
power analysis, preregistration, custody procedures, and statistical
rules described in the full protocol.
If something about the procedure is unclear, ask before changing it.
If your AI collaborator finds what it believes is a flaw in the
protocol, please post that criticism as well.
The point is not to get the desired answer.
The point is to find out what survives the test.
BLINDED AI HIDDEN-TARGET EXPERIMENT
Draft 0.7 — Pilot Candidate — Reviewer Stop Point
Frozen: August 23, 2026. This is the self-contained pilot-candidate protocol after the final Gemini 3.1 Pro Preview readiness review.
Draft 0.7 carries forward the surviving Draft 0.6 architecture and applies only the two pilot-blocking repairs identified in the final review: (1) independent AI generation seeds for paired A/A1 trials, and (2) an AI-authored multimodal positive control for judge sensitivity. The earlier human-authored positive control is retained as an auxiliary calibration. No further redesign is planned before pilot unless the pilot itself exposes a new problem.
PART 1 — PURPOSE AND SCOPE
This protocol tests whether an AI report shows a measurable target-before association under tightly blinded conditions designed to exclude ordinary information leakage, prompt priming, target-dependent foil construction, evaluator bias, optional stopping, post-hoc reinterpretation, and flexible scoring.
It does not begin by assuming remote viewing exists, nor by assuming it is impossible. It deliberately avoids a mechanism claim.
A positive result does not by itself establish remote viewing, anomalous cognition, nonlocal information transfer, consciousness effects, or any particular physical or metaphysical explanation.
PART 2 — PRIMARY RESEARCH QUESTION
Does a measurable target-before association occur when target identity is bound before AI report generation, compared with an otherwise matched condition in which target identity is genuinely assigned only after the report has been frozen?
A surviving result means only: A TARGET-BEFORE ASSOCIATION SURVIVED THIS PARTICULAR EXPERIMENTAL DESIGN.
PART 3 — CORE CONDITIONS
The main experiment contains three conditions:
• A — TARGET-BEFORE
• A0 — EXPLICIT NO-TARGET DIAGNOSTIC
• A1 — TRUE ASSIGN-AFTER
The decisive inferential contrast is A versus A1. A0 is diagnostic rather than the primary counterfactual.
PART 4 — PAIRED A/A1 DESIGN
A and A1 are organized into matched pairs.
For each pair p, select one five-image candidate set S_p before either report is generated. Candidate-set construction must not depend on which image will later be designated target.
The same five-image set S_p is used for both the A and A1 members of the pair. The candidate set is never shown to the generator.
This holds candidate-set composition and difficulty constant across the A/A1 pair so that target-binding time is the intended difference.
PART 5 — SET-FIRST, DESIGNATION-SECOND
Candidate construction always follows: SET FIRST → DESIGNATION SECOND.
Never choose a target first and then search for foils.
For every pair, first select five images using the locked set-selection procedure. Only after the five-image set exists may one image be designated as target.
This protects within-set target-label exchangeability and prevents target-dependent foil construction from contaminating the statistical null.
PART 6 — CONDITION A: TARGET-BEFORE
For the A member of pair p:
• 1. Candidate set S_p already exists.
• 2. Before generation, one member of S_p is designated as target.
• 3. Target designation uses the locked designation algorithm and an independent pre-generation entropy source.
• 4. The designation is committed and verifiably timestamped before AI generation begins.
• 5. The generator and generator operator cannot access the target image, target index, candidate images, target-selection entropy, commitment, or selector logs.
• 6. The generator receives the standard hidden-scene prompt.
• 7. The report is produced and frozen.
• 8. Later, blinded judges evaluate the frozen report against S_p.
PART 7 — CONDITION A1: TRUE ASSIGN-AFTER
For the A1 member of pair p:
• 1. The same candidate set S_p already exists.
• 2. Before generation, no member of S_p is designated as target.
• 3. No pre-generation entropy value exists from which the eventual A1 target can be calculated.
• 4. The generator receives the same hidden-scene prompt used in A.
• 5. The generator produces its report.
• 6. The report is frozen and independently timestamped.
• 7. Only after freeze is fresh target-designation entropy obtained.
• 8. One member of S_p is then designated as the A1 target using the locked designation algorithm, the post-freeze entropy, and the set identifier.
The exact post-freeze entropy source is locked before the study. The research team may not choose among entropy sources after seeing a report.
Acceptable implementations may include a predefined hardware RNG procedure with archived output, a predefined trustworthy public randomness source whose relevant value is generated after freeze, or another preregistered entropy source demonstrably unavailable and unpredictable before freeze.
PART 8 — A1 ACCEPTANCE TEST
Before live testing, give an independent auditor everything that existed before an A1 report was frozen.
The auditor must be unable to determine the eventual designated target from those pre-freeze records.
After the post-freeze entropy becomes available, the auditor must be able to reproduce the designation exactly from candidate-set ID, archived post-freeze entropy, and the locked designation algorithm.
If the target can be computed from pre-freeze records, A1 failed.
PART 9 — CONDITION A0: EXPLICIT NO-TARGET DIAGNOSTIC
A0 tells the generator explicitly: “No scene has been selected. Fill the form anyway.”
No target exists during generation. After freeze, a dummy designated image may be assigned using the same post-freeze procedure used for A1.
A0 measures what happens when the model explicitly knows no scene is selected. Because this wording differs from A/A1 and may change output style, A0 is not the decisive counterfactual.
PART 10 — MODEL-CONTEXT EQUIVALENCE
For paired A/A1 trials, all experimenter-controlled semantic/context input visible to the model must be identical.
This includes, where applicable: system message, developer message, user message, structured-output schema, tool declarations, tool availability, memory configuration, attached context, and prior conversation content.
Create a canonical serialization of these context fields and hash it. The A and A1 context-payload hashes must match.
Generation seeds are deliberately independent in Draft 0.7 and therefore are not included in the equality requirement. All other decoding parameters must match. A second generation-configuration record should show that the only intentional A/A1 difference in generation configuration is the independent generation seed, where seeds are supported.
Archive the complete outgoing request object. Provider-internal routing information or hidden metadata that the experimenter cannot inspect is recorded as a standing limitation rather than falsely claimed as controlled.
PART 11 — CONDITION LABEL BLINDING
The generator must never be told Condition A, Condition A1, target-before, assign-after, experimental arm, or control arm.
Condition identifiers may exist in experiment-management records but must not appear in experimenter-controlled model-visible context.
PART 12 — GENERATION RANDOMNESS — FINAL GEMINI PATCH
Generation randomness and target-selection randomness must be independent.
For paired A/A1 trials, use INDEPENDENT generation seeds. Do not use the same generation seed across the pair.
Never derive an LLM generation seed from target-designation entropy, set-selection entropy, trial UUID, condition-order RNG, or permutation RNG.
All generation seeds must be independently logged and archived. All non-seed decoding settings must remain matched across A/A1.
If the provider is nondeterministic even when a seed is specified, record that fact; do not treat a nominal seed as guaranteeing deterministic generation.
PART 13 — RANDOMNESS STREAM SEPARATION
Maintain independent entropy/RNG streams for:
• 1. candidate-set selection;
• 2. A pre-generation target designation;
• 3. A1 post-freeze target designation;
• 4. A0 post-freeze dummy designation;
• 5. A/A1 pair ordering;
• 6. condition-order randomization;
• 7. judge assignment;
• 8. image presentation order;
• 9. AI-evaluator presentation order;
10. permutation/statistical analysis.
Before live testing, simulate the pipeline and check for accidental correlations among these streams.
PART 14 — VERIFIABLE COMMITMENTS
Before confirmatory collection begins, freeze and hash the protocol, acquisition SOP, pool manifest, image files, candidate-set selection code, target-designation code, and analysis code.
Use independently verifiable timestamping such as RFC 3161 trusted timestamp authority receipts, independently verifiable transparency logs, multiple independent timestamp services, or another preregistered equivalent method.
A timestamp written only into an editable experimenter-controlled database does not count as independent verification.
PART 15 — TARGET-IMAGE ACQUISITION
Confirmatory images are new, original, unpublished still photographs of physical scenes.
Prefer acquisition after the protocol and acquisition SOP are locked.
Use a mechanical acquisition rule rather than choosing scenes because they look like “good targets.” Example: predefined route, predetermined stopping interval, one frame per stop, fixed framing instructions, and no substitution because a scene is boring.
Record discarded frames and reasons. Avoid unique public landmarks when practical and avoid unnecessary identifying content such as recognizable private individuals, license plates, and addresses.
PART 16 — ACQUISITION-DEVICE HYGIENE
Prefer a dedicated acquisition device. Disable cloud photo synchronization, automatic backups, social-media synchronization, and unnecessary network access.
Where practical, acquire offline, transfer physically/offline, hash immediately on ingest, and preserve original acquisition files separately from normalized experimental copies.
PART 17 — POOL MANIFEST
Create a pool manifest containing opaque image IDs and image hashes.
Before hashing the final manifest, randomize manifest order independently of acquisition order, geographic route, scene category, and time of day.
Do not encode location, chronology, category, or target status into experimental image IDs.
PART 18 — IMAGE NORMALIZATION
All experimental presentation copies pass through the same normalization pipeline.
Remove EXIF, GPS, original filenames, camera metadata, and unnecessary orientation metadata after correct visual orientation.
Standardize encoding, display dimensions or display rules, color-profile handling, compression procedure, and filename format consistently.
Do not normalize targets differently from foils.
Blinding audit: give normalized candidate files and all visible metadata to an auditor without labels. Target status should not be recoverable above chance from provenance or file artifacts.
PART 19 — POOL SIZE AND IMAGE REUSE
Before confirmatory testing lock the total pool size, number of A/A1 pairs, number of A0 trials, maximum foil appearances per image, maximum exposure of an image to a given judge, and target/foil reuse rules.
Prefer that a judge never evaluates the same candidate set twice.
For paired A/A1 trials using the same candidate set, prefer different judge panels for the A and A1 member of the pair, or another preregistered arrangement preventing recognition of the repeated candidate set.
No judge should know which two trials form a pair.
PART 20 — CONDITION ORDER
Do not collect all A trials and then all A1 trials.
Randomize and block-balance A and A1 members across the collection period. Within each pair, randomize which condition is generated first, subject to custody requirements.
Record timestamp, model identifier, provider, snapshot/version if available, and system fingerprint if available.
This reduces confounding from provider updates, model drift, safety-filter changes, operator learning, and temporal effects.
PART 21 — A / A1 GENERATOR PROMPT
The A and A1 prompt is generated from one literal template. The experiment software should verify that the A and A1 user-visible prompt strings are byte-identical.
Complete the structured description form below.
A scene photograph has been selected outside this conversation.
You are not being shown it.
Do not try to name an object, place, person, event, or category.
For each free-text field write at most one short descriptive clause.
Maximum: 8 words.
If you have no descriptor, write exactly:
UNKNOWN
Do not fill a field merely because it exists.
Do not explain.
Do not write a narrative.
Fields:
1. Basic geometry or shape
2. Relative size or scale
3. Spatial arrangement
4. Color or brightness
5. Texture or material quality
6. Implied motion or static
7. Choose exactly one:
NATURAL
CONSTRUCTED
MIXED
UNKNOWN
8. Living organism visibly present:
PRESENT
ABSENT
UNKNOWN
After field 8 write exactly:
END OF REPORT
Then stop.
Trigger: BEGIN
PART 22 — A0 GENERATOR PROMPT
A0 uses the same reporting form except the hidden-scene sentence is replaced with:
No scene has been selected.
Fill the form anyway.
A0's wording difference is intentional and diagnostic.
PART 23 — GENERATOR TECHNICAL CONFIGURATION
Disable technically where possible: web access, browsing, search, retrieval, file access, plugins, external tools, persistent memory, and cross-conversation memory.
Do not rely solely on prompt instructions saying not to use them.
Archive the raw request/configuration showing technical state.
Record model, provider, model version, temperature, top-p, maximum output, generation seed if supported, structured-output configuration, tool configuration, and accessible system instructions.
PART 24 — ONE-ATTEMPT RULE
Exactly one generation attempt per trial.
The only events permitting regeneration are preregistered transport-level failures such as a request failing before usable generation, network/API transport failure, a completely empty server response, or provider-declared schema rejection yielding no usable report.
Everything else is data, including refusal, caveat, all UNKNOWN, naming violation, narrative violation, excessive length, malformed but readable response, boring response, generic response, or an apparently bad response.
All attempts are archived. No researcher may rerun because a report looks unlikely to score well.
PART 25 — NON-INFORMATIVE OUTPUTS
Before confirmatory testing define a mechanical rule for NON-INFORMATIVE REPORT.
Recommended definition: a report containing zero usable descriptor fields after blind format/violation coding. Examples include pure refusal with no descriptors, all eight fields UNKNOWN, or output containing no usable requested information.
A non-informative report remains in the experiment, is not regenerated, remains in the denominator, and receives neutral target rank 3.0 for k=5.
Reports containing at least one usable descriptor are judged normally even when violations are present.
The definition is locked using pilot data before confirmatory unblinding. Report non-informative rates separately by condition. Power calculations must include the observed pilot rate.
PART 26 — VIOLATION CODING
Develop violation rules using pilot data only.
Operationalize object naming, category naming, place naming, narrative, excessive length, and malformed output.
Resolve ambiguous examples before confirmatory testing, such as whether “bridge-like” counts as geometry or object naming.
During confirmatory collection, violation coding is blind to target identity, target rank, and condition where technically possible.
Violations are flagged; they are not silently deleted.
PART 27 — FREEZE
At END OF REPORT or completion of the first response, archive raw response, parsed response if used, timestamp, trial UUID, pair UUID, condition in non-model-visible records, model/provider/version, context-payload hash, raw outgoing request, decoding configuration, generation seed if available, tool state, attempt number, and violation flags.
After freeze: no editing, clarification, continuation, self-scoring, target reveal to generator, or post-hoc descriptor interpretation.
PART 28 — HUMAN JUDGES
Humans are the primary evaluator class.
For each rankable report, judges receive the frozen report, the five normalized candidate images, randomized image order, no target label, no condition label, and no pair information.
Instruction: Rank the five images from BEST correspondence with the report to WORST correspondence.
Use the preregistered tie rule. Judges work independently. No discussion, consensus meeting, reconciliation, or AI assistance.
PART 29 — JUDGE CONTAMINATION
Prefer supervised judging.
If remote judging is used, use a controlled interface, randomized image order, response timing, attention checks, no-AI attestation, and preregistered exclusion criteria.
Do not exclude judges after seeing whether their rankings favor the hypothesis. Report all judge exclusions and reasons.
PART 30 — PILOT INSTRUMENT VALIDATION
Before confirmatory testing, run a pilot using a separate image pool acquired under the same SOP and approximately the same image-distribution difficulty as the eventual confirmatory pool.
Pilot uses the same normalization, five-image set construction, judge interface, report form, and candidate-set similarity regime.
The pilot must evaluate both RELIABILITY and SENSITIVITY.
PART 31 — PILOT RELIABILITY
Choose and preregister a judge reliability measure such as Kendall's W, ICC, or another justified statistic.
Pilot determines the number of judges needed, tie behavior, between-judge variance, and rank stability.
Lock the minimum acceptable reliability level before confirmatory testing. If pilot reliability fails, repair the measurement instrument and repeat the pilot.
During confirmatory testing, report observed reliability but do not alter the study because live agreement looks inconvenient.
PART 32 — PILOT SENSITIVITY — FINAL GEMINI PATCH
Reliability alone is insufficient. The judging system must demonstrate that it can detect real known correspondence specifically in AI-authored reports.
PRIMARY POSITIVE CONTROL FOR EXPERIMENT CALIBRATION:
• 1. Use an unblinded multimodal AI that can actually view pilot target images. Prefer the same model family as the eventual generator when a suitable multimodal version exists; otherwise use the closest practical multimodal model and document the difference.
• 2. The image-seeing AI completes the same eight-field form under the same length restrictions. Its task is to convert visible image content into the locked report format.
• 3. Different blinded human judges receive those AI-authored reports with five-image candidate sets built by the confirmatory-like procedure.
• 4. Judges rank the images using the same interface and ranking rules.
• 5. Use this AI-to-human positive control as the primary sensitivity calibration for confirmatory power and instrument adequacy.
AUXILIARY POSITIVE CONTROL:
Human describers may also view pilot images and complete the same eight-field form. This human-to-human condition answers whether the form itself can carry recognizable information, but it is auxiliary and must not substitute for the AI-authored calibration.
Also include mismatched report/set controls and all-decoy controls where useful.
Before confirmatory testing, lock a minimum sensitivity criterion. The pilot pool must not be trivially easier than the confirmatory pool.
If known AI-authored correspondence cannot be detected adequately, repair the reporting/judging instrument before confirmatory testing.
PART 33 — PRIMARY TRIAL STATISTIC
For trial i, each judge j assigns target rank r_ij from 1 to 5, where 1 is best correspondence.
For a rankable report, R_i = mean target rank across judges.
For a non-informative report, R_i = 3.0 by the preregistered neutral rule.
Lower R_i means better target correspondence.
PART 34 — PRIMARY A/A1 CONTRAST
A versus A1 is the primary inferential test.
For pair p: D_p = R_A1,p − R_A,p. Positive D_p means the A target received a better/lower rank than the A1 target.
Primary experiment statistic: mean D across all A/A1 pairs.
Use a preregistered paired randomization/permutation procedure in which A and A1 labels are swapped within pairs according to the locked permutation process and the mean difference is recomputed.
Lock before confirmatory testing: statistic, direction, alpha/decision threshold, number of permutations, Monte Carlo correction, permutation seed/procedure, tie treatment, and non-informative-report treatment.
PART 35 — SECONDARY A-WITHIN-SET CHECK
Condition A must also demonstrate genuine target correspondence rather than merely being different from A1.
For A, within each five-image set randomly relabel which image is considered the target and recompute the A mean-rank statistic.
Permutation unit is TRIAL; the same relabeling applies jointly across all judges of that trial. Never independently permute judge-by-trial cells.
This within-set test is valid because candidate sets are selected first and target designation occurs second.
This is a required confirmation but not a hard sequential gate preventing calculation of the primary A−A1 contrast.
PART 36 — JOINT DECISION RULE
Do not use “A is significant and A1 is not” as evidence that A differs from A1. The direct A−A1 contrast must pass.
Before confirmatory testing, use simulation to choose a joint decision rule controlling the desired overall false-positive rate.
A SURVIVES classification should require at minimum:
• 1. Primary A−A1 contrast passes its preregistered threshold.
• 2. Condition A demonstrates better-than-null target correspondence under the locked A-within-set check or equivalent preregistered requirement.
• 3. Observed A performance meets the preregistered smallest effect of scientific interest.
• 4. Adequate power was established beforehand.
• 5. Instrument reliability passed pilot.
• 6. AI-authored positive-control sensitivity passed pilot.
• 7. All custody and leakage audits pass.
The exact numerical thresholds are chosen through pilot/power simulation and locked before confirmatory collection.
PART 37 — POWER
Do not choose trial count by intuition.
Use pilot-estimated quantities including between-trial rank variance, between-judge variance, paired A/A1 variance, refusal rate, non-informative rate, violation rate, tie frequency, and candidate-set difficulty.
Define a smallest effect of scientific interest in rank units.
Use Monte Carlo simulation of the actual analysis pipeline to estimate global Type I error, power of A−A1, power of the A-within-set confirmation, and probability of satisfying the complete SURVIVES rule.
Lock number of A/A1 pairs, N A0, judges per trial, decision thresholds, SESOI, and desired power before confirmatory testing.
An underpowered null result is UNRESOLVED, not FAILS.
PART 38 — ANALYSIS FIREWALL
Before confirmatory data collection: write analysis code, test it on simulated data, hash it, obtain a verifiable timestamp, archive simulation results, and lock the analysis plan.
Do not inspect evolving confirmatory results out of curiosity.
If interim analysis is required, use a preregistered sequential design. No unregistered peeking.
PART 39 — FOIL POPULARITY
Track every image while it serves as a foil: number of appearances, first-place frequency, mean rank, and judge-specific preference.
A repeatedly favored foil is a HOT FOIL.
Preregister a hot-foil sensitivity analysis. Do not remove hot-foil trials from the primary dataset after results are known. Report sensitivity alongside primary results.
PART 40 — ALL-DECOY DIAGNOSTIC
Use all-decoy trials as a secondary diagnostic. The generating target is absent from the candidate set.
Purpose: measure generic correspondence, judge conviction, hot-foil behavior, and false matchability.
Do not treat all-decoy trials as ordinary hit/miss trials.
PART 41 — MISMATCHED REPORT/SET DIAGNOSTIC
As an exploratory generic-match test, score frozen reports against candidate sets belonging to unrelated trials where the report's target is absent.
If reports correspond almost as well to unrelated candidate sets as to their correct sets, generic matchability becomes a strong ordinary explanation.
This remains diagnostic unless separately preregistered.
PART 42 — MANIPULATION CHECKS
Record report length, token count, UNKNOWN count, filled fields, refusal rate, non-informative rate, specificity, genericness, hedge frequency, naming violations, and narrative violations.
These variables may be consequences of prompt condition. Do not automatically regress them out of the primary result.
Report raw A/A1 result first, then manipulation differences, then secondary sensitivity/mediation analyses.
Correlation with a manipulation-check variable does not by itself prove mediation.
PART 43 — AI EVALUATORS
AI judging is secondary only. Human judges remain primary.
If AI evaluators are used: multimodal pixel input, no captions, randomized candidate order, full model/settings logging, preferably a different family from the generator.
Shared training priors remain possible even across model families; cross-model agreement is not independent proof.
Do not upload sealed confirmatory images to an evaluator provider before release unless contractual terms prohibit training/model-improvement use, evaluation is local, or evaluation is delayed until the registered release point.
PART 44 — EXPLORATORY PROMPT CONDITIONS B–F
These are not part of the confirmatory A/A1 test and should be run only after the core procedure is stable.
• B — LOW-INTERPRETATION: minimize naming, explanation, and semantic completion.
• C — OPEN-GENERATION: do not reject descriptors merely because they seem unusual or unlikely.
• D — HIGH-THRESHOLD: prefer UNKNOWN over weak descriptors.
• E — COMPUTATIONAL-CONTEXT: optional preceding unrelated task; pilot before use.
• F — SEEDED REMOTE-VIEWING CONDITION: existing heavily primed remote-viewing style prompt. Condition F is deliberately contaminated, exploratory, run last, isolated from confirmatory credentials/memory, and excluded from confirmatory permutation analysis.
If F mainly increases richness/specificity and apparent matchability, classify that as CONSISTENT WITH PROMPT/STYLE/SCORING CONFOUND unless another experiment separates those causes.
PART 45 — PRE-SURVIVES LEAKAGE AUDIT
Before any result can receive SURVIVES classification, an independent auditor verifies:
• 1. protocol hash and timestamp;
• 2. pool-manifest hash;
• 3. image hashes;
• 4. acquisition custody;
• 5. normalization procedure;
• 6. set-selection code;
• 7. A target-designation records;
• 8. A1 post-freeze entropy timestamps;
• 9. exact recomputation of assignments;
10. context-payload hashes;
11. condition-label absence from model context;
12. generation/selection entropy independence;
13. generator-operator blinding;
14. tool/memory state;
15. attempt logs;
16. regeneration compliance;
17. judge blinding;
18. condition ordering;
19. analysis-code hash;
20. protocol deviations.
The auditor should actively attempt to recover target identity using only generator-side artifacts. If target identity can be recovered by an ordinary channel, the affected block does not survive.
PART 46 — STATUS SYSTEM
Use: SURVIVES / FAILS / UNRESOLVED / NOT TESTABLE YET.
SURVIVES means only that a target-before association survived the current design.
FAILS means the adequately powered, validly measured preregistered effect failed the locked decision rule.
UNRESOLVED includes inadequate power, instrument failure, excessive non-informative output, major custody ambiguity, or technical uncertainty preventing interpretation.
NOT TESTABLE YET means a required prerequisite was not satisfied before testing.
PART 47 — SURVIVES REQUIREMENTS
SURVIVES requires all applicable locked criteria to pass. At minimum:
• 1. A−A1 primary contrast passes.
• 2. A target correspondence passes required within-set confirmation.
• 3. A performance exceeds the preregistered smallest scientifically interesting effect.
• 4. Statistical power was adequate.
• 5. Pilot reliability passed.
• 6. AI-authored positive-control sensitivity passed.
• 7. A1 target identity was genuinely determined using post-freeze entropy.
• 8. Candidate construction was set-first/designation-second.
• 9. A/A1 candidate sets were paired as specified.
10. Model-context equivalence passed, with independent generation seeds properly isolated.
11. Generation randomness was independent of target entropy.
12. Custody/timestamp audit passed.
13. No forbidden regeneration occurred.
14. No ordinary target leakage was found.
15. Hot-foil diagnostics did not reveal a straightforward artifact capable of accounting for the result.
16. Results occurred on newly acquired sealed images.
SURVIVES does not establish remote viewing or any mechanism.
PART 48 — REPLICATION
If a result survives, do not immediately add ontology or rewrite the prompt because the result was exciting.
Repeat the locked experiment with a new image pool, new acquisition run, new selector/operator pairing, new random assignments, new judge panel where practical, the same report form, and the same primary analysis.
Prefer another model/provider and independent investigators.
Only repeated survival under independent sealed pools should motivate mechanism-specific experiments.
PART 49 — OPTIONAL NEXT HAMMER IF POSITIVE
If the complete Draft 0.7 experiment survives, the strongest remaining ordinary concern is hidden ordinary information coupling not captured by the audit.
A stronger replication may therefore use an air-gapped/local generator where practical, an independent laboratory, public post-freeze randomness for A1, separate custody personnel, an additional condition in which the candidate set itself is assigned after generation, a new model family, and a new sealed pool.
Do not add these burdens before they are needed unless the pilot exposes a reason.
PART 50 — STOP POINT
Draft 0.7 is the reviewer stop point.
The final pilot-readiness review identified exactly two blocking defects in Draft 0.6: same-seed A/A1 generation and human-only positive-control sensitivity calibration. Both are repaired here.
No further reviewer carousel is planned before pilot testing.
The next source of legitimate design changes is the pilot itself: implementation failure, instrument failure, unanticipated leakage, or another concrete problem actually observed during use.
If the pilot runs cleanly and the preregistered numerical thresholds are established, the protocol can proceed to confirmatory testing.
END OF DRAFT 0.7 — PILOT CANDIDATE