From Effective Intelligence to Cognitive Development and Collaborative Divergence: An Integrated, Testable Research Framework for LLM-Assisted Growth, Human Steering, and Path-Dependent Outcomes
From Effective Intelligence to Cognitive Development and Collaborative Divergence
An Integrated, Testable Research Framework for LLM-Assisted Growth, Human Steering, and Path-Dependent Outcomes
John Swygert | Version 4 — Final Publication Draft | 26 October 2026
Status: scientific hypotheses and proposed research protocols; no original experimental findings or validated EIQ scale are claimed.
Abstract
Large language models (LLMs) can change the performance of a human–AI team without necessarily changing the unaided cognitive ability of the human participant. This paper distinguishes baseline psychometric IQ, assisted effective intellectual performance (EIQ), durable unaided cognitive change, and collaborative divergence: the possibility that users with different baseline abilities follow different intellectual trajectories while using the same model. It preserves the original four hypotheses and randomized instructional study, and adds a complementary controlled experiment separating identical-output evaluation from adaptive, multi-turn steering. It specifies longitudinal trajectory measures, collaboration-history transfer tests, alternative explanations, and falsification conditions. Neither general-IQ gains nor systematic advantage for higher-IQ users is assumed.
1. Scientific Question and Construct Boundaries
Can repeated, active interaction with an LLM improve independently assessed cognitive performance after assistance is withdrawn? The question is causal and longitudinal. It must not be answered by measuring what the LLM can do for a user during an assisted task.
2. Hypotheses and Predictions
H1 — Augmentation: on eligible tasks, LLM-assisted participants will outperform their own unaided performance and matched unaided controls, with heterogeneity by domain and occasional negative effects from AI error.
H2 — Pedagogical design: Socratic LLM use, requiring attempts, explanations and retrieval, will produce larger unaided post-training gains than answer-first LLM use, given comparable time and task exposure.
H3 — Far transfer: sufficiently intensive, scaffolded LLM use may improve untrained standardized reasoning outcomes beyond active-control and retest effects; this is an exploratory, high-threshold claim, not an assumed result.
H4 — Moderation: baseline performance, prior knowledge, motivation, cognitive engagement, feedback fidelity, usage dose and dependency will alter treatment effects. Moderator tests are secondary unless powered and preregistered.
3. Proposed Mechanisms and Competing Mechanisms
Positive pathway: guided exposure → self-generated attempt → feedback and explanation → retrieval after delay → strategy abstraction → independent use → possible transfer. Countervailing pathway: effortless answer access → reduced productive struggle → shallow encoding → dependence or overconfidence → weaker unaided performance. Both pathways should be measured, not merely described.
4. Operationalizing EIQ Without Inventing IQ Points
Construct a domain-balanced task battery (e.g., verbal reasoning, quantitative problem solving, evidence evaluation and structured planning). For each task, predefine an objective or blinded rubric-based accuracy score, completion time, and critical-error count. Standardize task scores using a separately recruited reference sample tested under the same assisted condition. Weight domains equally in the pilot unless a preregistered psychometric model supports alternative weights. Report a composite z-score and percentile with uncertainty, alongside domain scores. Label the result “EIQ performance index,” not IQ-equivalent intelligence. Reference-sample feasibility should be established in a pilot: recruit a demographically characterized independent calibration cohort, prespecify a precision target for percentile estimates, and budget consistent model access and repeated scoring checks; the required cohort size follows from pilot reliability and precision rather than an arbitrary fixed number.
Illustrative calculation: EIQ_index = mean(z_verbal, z_quantitative, z_evidence, z_planning). This is a proposed index requiring reliability, factor-structure, measurement-invariance and test–retest validation; it is not a validated quotient. Comparisons of IQ 100 and “EIQ 125” must remain illustrative until separately normed and justified.
Assisted-condition standardization
Freeze model identifier/checkpoint where feasible, decoding settings (including temperature), tool access, system-prompt family, maximum context and token budgets, session duration, and permitted retries. Archive exact prompt templates, scoring rubrics, model version and access date. If the provider cannot guarantee version stability, log all changes and treat model version as a protocol deviation or predefined factor. For both studies, archive the model configuration and prompt artifacts. If the provider updates a model during data collection, follow a preregistered decision rule: pause and document, use a pinned version where possible, or include version blocks and sensitivity analyses rather than silently pooling changed conditions.
5. Minimal Assessment Battery
Use professionally validated instruments when available and legally licensed; the examples above are conceptual task families, not claims that any one instrument cleanly measures general intelligence. Build multiple alternate forms and equate their difficulty. Pretest item leakage and avoid using training items in outcome batteries. Estimate broad-factor change only if sample size and measurement properties support a latent-variable model.
6. Randomized Study: Concrete Protocol
Sample and assignment
Illustrative adult sample: 240 participants (60 per arm), subject to an a priori power calculation using pilot variance, target minimum detectable effect, clustering and anticipated attrition. Stratify randomization by baseline cognitive score band and prior LLM familiarity. This number is a planning placeholder, not a claim of adequate statistical power.
Four arms
Dosage and adherence
Illustrative intervention: 16 weeks, three 45-minute sessions weekly (36 scheduled hours). Minimum meaningful exposure for per-protocol sensitivity analysis: ≥75% sessions and ≥70% assigned task attempts; primary analysis remains intention-to-treat regardless of adherence. Record active minutes, completed attempts, hint requests, retrieval success, off-platform LLM use, and self-reported outside study time. Explore dose–response descriptively, not as causal proof. To limit contamination, obtain a nonpunitive participant commitment regarding off-platform AI use and, where consent and feasibility permit, verify in-study usage with platform logs; retain self-reports as imperfect supplementary measures.
Timeline
Baseline (week 0), midline engagement check (week 8), unaided post-test (week 17), and unaided follow-up at 3 and 6 months. All outcome assessments are proctored without LLM access; raters are blinded to assignment. Counterbalance equivalent test forms. Document noncompliance and likely contamination.
7. Core Instructional Protocols
Socratic LLM prompt principles — abbreviated reproducible adapter
“Act as a reasoning tutor, not an answer dispenser. Ask for the learner’s first attempt before revealing a solution. Offer the smallest useful hint, then ask the learner to explain the next step. Identify errors accurately without feigning certainty. After completion, require a concise unaided summary and schedule a later retrieval question. If the learner requests the direct answer or faces a time-critical need, provide it and log the deviation. Do not fabricate feedback.”
Answer-first comparison adapter
“Respond directly to each task with a worked solution and clear explanation. Do not require an initial independent attempt, graduated hints or delayed retrieval. Follow the same accuracy, safety and length constraints as the Socratic arm.”
Keep all shared prompts, curricular materials and safety instructions constant except the instructional manipulation. Pilot for differences in actual model behavior; instruction labels alone do not ensure distinct treatments.
8. Outcomes, Analysis and Preregistration
Study A primary endpoint: between-arm difference (A versus B) in baseline-adjusted, unaided near-transfer composite z-score at week 17. Primary estimator: ANCOVA of week-17 outcome on randomized arm and baseline outcome, with prespecified strata and robust confidence intervals. Define the primary comparison before data collection. The active-control contrast (A versus C) is a key secondary test.
Secondary endpoints: blinded unaided far-transfer composite at week 17 and months 3/6; retained gains; EIQ index while assisted; task completion accuracy; speed–accuracy tradeoffs; metacognitive calibration (confidence versus correctness); willingness to attempt difficult problems independently; assistance dependence; and frequency/severity of learned errors.
A far-transfer claim requires prespecified cross-domain outcomes, superiority to active controls, confidence intervals excluding trivial effects under the registered criterion, and persistence at follow-up. Correct for multiple secondary comparisons (e.g., Holm) and report all effect sizes and intervals, including null and adverse effects. Treat broad-IQ change as an additional, higher evidentiary bar requiring validated standardized measures and independent replication.
Missing data: preregister multiple imputation or mixed-model approaches under stated assumptions; report attrition by arm and sensitivity analyses for missing-not-at-random scenarios. Keep intention-to-treat primary; mark per-protocol and dose–response as sensitivity/exploratory. Publish anonymized analysis code, instruments when licensed, deviations and a reproducibility manifest.
9. Adverse Outcomes and Safety Monitoring
Track unaided decline relative to baseline and controls; overconfidence after incorrect LLM feedback; false strategy acquisition; reduced independent attempts; frustration or disengagement; and inequitable benefit across subgroups. Prespecify thresholds for human review of harmful instructional failures. Do not present IQ labels as judgments of worth. Collect only necessary data, encrypt identifiable records, support withdrawal and provide transparent retention/deletion policies.
10. Falsification and Interpretation Matrix
11. Replication and Research Roadmap
Phase 1: pilot scoring reliability, alternate forms, manipulation fidelity, and EIQ reference norms. Phase 2: preregister and run randomized study with fixed model configuration and active controls. Phase 3: independently replicate with different populations and model families. Phase 4: investigate durability, adaptive dosage, accessibility and cross-language generalization. Distinguish model-independent design from model-identical replication.
12. Conclusion
LLM access may amplify immediate task performance without changing the user. Structured engagement might yield durable near or far transfer, but such gains require independent unaided assessment. A separate and complementary question is whether baseline cognitive ability, metacognitive control, and accumulated collaboration history predict the trajectory of human–AI work. EIQ remains a proposed assisted-performance index rather than an IQ equivalent; collaborative divergence is an empirical hypothesis rather than a presumed hierarchy. The research program succeeds by distinguishing these outcomes and identifying the conditions under which each does or does not occur. Collaborative divergence, steering-mediated advantage, and path-dependent gains remain predictions to be tested, not established empirical outcomes.
Selected Foundational References
Ritchie, S. J., & Tucker-Drob, E. M. (2018). How much does education improve intelligence? A meta-analysis. Psychological Science, 29(8), 1358–1369. https://doi.org/10.1177/0956797618774253
Noy, S., & Zhang, W. (2023). Experimental evidence on the productivity effects of generative artificial intelligence. Science, 381(6654), 187–192. https://doi.org/10.1126/science.adh2586
Brynjolfsson, E., Li, D., & Raymond, L. R. (2025). Generative AI at Work. Quarterly Journal of Economics, 140(2), 889–942. https://doi.org/10.1093/qje/qjae044
Research note: These references motivate the research question but do not establish LLM-induced increases in general intelligence. All numerical protocol settings in this document are illustrative and require pilot validation and preregistration.
13. Version 3 Extension: Human–AI Collaborative Divergence
Research question. Holding the model, project brief, goals, resources, time, and scoring criteria constant, do users with different baseline cognitive abilities produce systematically different output quality or reasoning trajectories? If so, is the difference mediated by steering, error detection, synthesis, or other observable interaction behaviors? This extension does not replace the longitudinal cognitive-development study in Sections 1–12; it tests a separate between-person mechanism.
13.1 New hypotheses
H5 — Baseline ability interaction: the association between baseline cognitive ability and final project quality will vary by task openness and complexity. The sign and magnitude are empirical; no fixed advantage or linear IQ-to-output mapping is presumed.
H6 — Adaptive steering: in open-ended tasks, baseline ability may predict output partly through problem decomposition, critique accuracy, productive revision, and synthesis quality. These mediators require independently reliable coding.
H7 — Task-contingent gap: AI may compress performance differences on tightly specified, objectively verifiable tasks while preserving or widening them on ambiguous, multi-constraint projects. Reversal remains possible.
H8 — Collaborative history: established human–AI working conventions and accessible project history may improve output fidelity and efficiency relative to fresh-start interaction. A transferable briefing may recover some or all of this advantage.
H9 — Longitudinal feedback: repeated cycles of independent reasoning and AI-directed exploration may change future steering effectiveness. Growth, plateau, dependence, and deterioration are competing predictions.
13.2 Why IQ 125 versus 165 is an illustration, not the sampling plan
A 40-point contrast dramatizes the question but samples near IQ 165 are uncommon and subject to measurement ceiling and selection effects. Recruit across a broad, adequately represented baseline-ability distribution, use validated age-normed instruments, and analyze ability continuously. Predefine nonlinearity checks. A matched-pairs subgroup analysis may illustrate contrasts, but must not substitute for a powered design. Baseline IQ must not be conflated with domain expertise, motivation, literacy, prompt experience, or personality. Study B recruitment should ensure adequate participant density throughout the measured ability range rather than concentrating only on tails; quantify score reliability, ceiling effects, and measurement error at high scores. Power Study B separately using simulations for the prespecified three-way interaction and plausible within-participant correlations.
14. Complementary Experimental Design
Use a randomized crossover design across multiple project types, counterbalancing order and task variants. Participants receive the same model checkpoint, decoding policy, retrieval/tools, initial instructions, maximum interaction time, and output constraints. Separate model randomness by fixing seeds where supported and replicating trials across seeds. Log all prompts, responses, edits, tool calls, timing, and final artifacts. Do not claim identical outputs unless the output is literally replayed. Where deterministic replay cannot be guaranteed, perform multiple independent model runs per participant/task condition, with prespecified seed or run identifiers where available; estimate within-person, between-run variability and propagate it into uncertainty intervals.
Tasks should include (i) constrained factual/problem-solving work with objectively scored answers, (ii) multi-constraint applied design with hidden feasibility tests, and (iii) open-ended creative or strategic work evaluated by blinded multi-rater rubrics. Task difficulty, domain familiarity, and scoring reliability must be piloted. Include independent experts and nonexpert raters where appropriate; report disagreement.
14.1 Outcome and trajectory measures
Study B primary endpoint: the preregistered baseline-ability × interaction-condition × task-type effect on blinded final-project quality. Define a single primary quality composite or one primary task family before recruitment. Secondary measures: objectively detected critical errors; constraint satisfaction; originality where reliably scored; completion time; prompt efficiency; quality at fixed checkpoints (e.g., after turns 1, 5, 10, 20); number of substantive revisions; correction success; and confidence calibration. Evaluate trajectories at standardized turn or time checkpoints, not only at project completion. Creative/open-ended quality must be scored by multiple blinded raters; report both mean composite scores and inter-rater agreement (e.g., intraclass correlation coefficients, with confidence intervals). A single evaluator’s creative judgment cannot serve as primary evidence.
Analysis: hierarchical mixed-effects model with participant and task random effects, baseline ability as a continuous predictor, condition, task type, and prespecified interactions. Adjust for preregistered covariates (prior LLM experience, domain expertise, motivation, education) without conditioning on post-treatment mediators in the primary causal model. Estimate marginal effects with uncertainty. Mediation by steering and critique behavior is secondary and requires stronger assumptions than randomized condition effects.
14.2 Operational coding of human steering
Problem framing: specificity of subgoals, constraints, and success criteria.
Error detection: proportion of planted or naturally occurring errors correctly identified; false alarms separately counted.
Iteration quality: share of revisions that improve blinded quality, not merely total prompt count.
Synthesis: consistency, traceability, and reconciliation across intermediate outputs.
Metacognitive control: calibrated confidence, strategic switching, and stopping decisions.
Code interactions using blinded independent raters and a preregistered rubric; measure inter-rater reliability. Avoid defining “good steering” by the final outcome alone, which would make the explanation circular.
15. Accumulated Collaboration and Replicability
A distinct test asks whether extended collaboration creates path-dependent creative or intellectual advantages. Compare (1) established user with established context, (2) same user with fresh context, (3) matched new user with a detailed distilled project brief, and (4) matched new user with no history. Where practical, also compare transfer of full accessible project history versus condensed documentation. Randomize task order and keep model and evaluation constant. Distinguish effects of user learning from the availability of stored context; the model itself need not have retrained.
A high-quality brief that fully eliminates the experienced-pair advantage would support transferability rather than irreproducible uniqueness. An advantage remaining after matched documentation could reflect tacit practice, but not prove that a particular relationship is impossible to reproduce. Quality should be judged blind, with separate ratings for originality, technical coherence, and fidelity to an independently defined artistic or project objective.
16. Falsification, Boundaries, and Publication Criteria
If adaptive and fixed-response conditions show equivalent ability-related slopes, the proposed special role of interactive steering is not supported.
If task type does not moderate ability-linked differences within sufficiently precise estimates, the compression/widening prediction is not supported.
If coded steering behaviors fail to predict trajectory changes after appropriate controls, the proposed mediation account is weakened.
If a transferable brief closes the collaboration-history gap, claims of unique nontransferable collaborative capability are weakened.
If the longitudinal study improves near transfer only, do not claim general IQ gains; if assisted scores rise only, do not claim cognitive development.
If higher baseline IQ predicts poorer performance on some tasks, report the reversal without treating it as a protocol failure.
Interpretation safeguards. A single IQ score is an imperfect indicator of multidimensional ability; a 125/165 thought experiment is not an observed result. A common project brief does not guarantee identical LLM outputs under adaptive interaction. More turns do not necessarily mean better reasoning. Creative judgments require explicit reliability assessment. Neither the original V2 study nor this extension currently provides experimental data.
17. Practical Research Sequence
First publish the integrated framework as a hypothesis/protocol proposal, explicitly marked as untested. Next pilot both the unaided transfer battery and the collaborative task battery, including blinded rating reliability and model-version stability. Then preregister two linked but separately powered experiments: (A) instructional design and cognitive development; (B) baseline ability, task type, and adaptive collaboration. Finally test replication across populations, LLM families, and accessible-history conditions. Do not merge primary endpoints post hoc. Study A and Study B have distinct primary estimands, separate sample-size and power justifications, and separate confirmatory error-control plans. Study A prioritizes the randomized Socratic-versus-answer-first near-transfer contrast because it directly tests pedagogical design with a tractable primary endpoint; Study A far transfer and the active-control comparison remain secondary and subject to stricter interpretation. Study B prioritizes the baseline-ability × interaction-condition × task-type effect; neither study’s significance substitutes for the other’s.
Selected Additional Methodological References
Cronbach, L. J., & Meehl, P. E. (1955). Construct validity in psychological tests. Psychological Bulletin, 52(4), 281–302. https://doi.org/10.1037/h0040957
Campbell, D. T., & Fiske, D. W. (1959). Convergent and discriminant validation by the multitrait-multimethod matrix. Psychological Bulletin, 56(2), 81–105. https://doi.org/10.1037/h0046016
Open Science Collaboration. (2015). Estimating the reproducibility of psychological science. Science, 349(6251), aac4716. https://doi.org/10.1126/science.aac4716
These methodological references motivate measurement and reproducibility practices; they are not evidence that the proposed EIQ or divergence effects have been demonstrated.
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