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Presenting a hypothesis suggested by inspected results as if it had been specified beforehand. The misrepresentation, rather than discovery itself, is the problem. Transparent exploratory analysis, preregistration and independent testing preserve the distinction between generating and evaluating a hypothesis.^[ref]

Practices making research plans, materials, analyses and outputs inspectable and reusable where ethically appropriate. Preregistration, transparent reporting and executable analysis support distinct aspects of openness. Protecting confidentiality can require restricted data access rather than unrestricted publication.

Greater transparency and reproducibility have changed developmental psychology's estimates, measurement practices and theoretical confidence, but have not simply replaced a collection of “true” findings with “false” ones. Computational reproducibility asks whether the same data and documented analysis yield the same result. Scientific replication asks what happens with new observations. Preregistration makes planned tests distinguishable from exploratory choices; open materials permit checking whether ostensibly similar studies actually use the same procedure. None of these, by itself, guarantees construct validity or representative sampling.

The marshmallow task illustrates a substantive change in interpretation. Walter Mischel's early experiments offered preschoolers a smaller immediate reward or a preferred delayed reward and manipulated how attention was directed during waiting. Distraction increased delay. The original experimental programme therefore already showed sensitivity to cognitive strategy and setting, rather than a fixed quantity of virtue revealed by a treat. Later predictive associations are a different claim from those immediate experimental effects.^[ref]

Tyler W. Watts and colleagues revisited long-term prediction in a larger and more diverse cohort. Their 2018 conceptual replication used a waiting task at fifty-four months and adolescent achievement outcomes. Associations were substantially reduced after adjustment for family background, early cognitive abilities and the home environment; much of the achievement difference was concentrated at the lowest waiting times. An important measurement difference was the seven-minute ceiling, rather than treating all waiting tasks as interchangeable. These results weaken a simple causal story in which training a preschooler to wait longer should, by itself, transform later attainment. They do not show that self-regulation never matters, because adjustment can remove both confounding and potentially meaningful pathways.^[ref]

Celeste Kidd and colleagues supplied experimental evidence for one alternative mechanism: environmental reliability. Before the waiting task, children encountered an adult who either fulfilled or failed promises about appealing materials. Children subsequently waited longer after reliable experiences. The observation matters because apparent “poor self-control” can be an understandable response to expecting that a promised reward will not arrive. This small experiment supports contextual causation under its own conditions, not a claim that all socioeconomic differences in waiting are caused by trust. Together, the studies shift the target from an isolated child trait to the interaction between control, expectations and circumstances.^[ref]

Neonatal imitation illustrates why replicability also depends on the inferential contrast. Andrew N. Meltzoff and M. Keith Moore's 1977 report described very young infants matching facial and manual gestures. In this paradigm an adult models an action and infant responses are recorded and coded; the crucial question is whether the infant produces a given action preferentially after its matching model, not merely whether the action occurs. An increase in tongue protrusion after interesting stimulation is insufficient unless appropriate nonmatching controls exclude general arousal or exploration.^[ref]

Janine Oostenbroek and colleagues tested 106 infants longitudinally with nine social and two nonsocial models at one, three, six and nine weeks. Their broad comparisons did not support model-specific imitation, although restricted cross-sections could resemble earlier positive findings. This challenged a general innate-imitation account and highlighted the consequences of selecting particular gestures, ages and contrasts after observing results. Yet the study's breadth also created substantive questions about fatigue, presentation and how each action was scored.^[ref]

The subsequent requested-data reanalysis by Meltzoff and colleagues reported tongue-protrusion matching under pooled-control contrasts and criticised features of the elicitation and scoring procedures. That was not an independent replication: it reused the same observations. It nevertheless shows the scientific value of access to raw data. The disagreement became one about estimands, comparison sets and measurement sensitivity that another preregistered experiment could adjudicate, rather than an unsupported declaration that one team must be wrong. Evidence for one gesture would also not automatically vindicate a broad, domain-specific imitation mechanism.^[ref]

ManyBabies 1 provides a constructive counterexample to the notion that open developmental research only dismantles effects. In a Registered report, an international collaboration used common speech stimuli and prespecified analyses to test infant-directed versus adult-directed speech preferences. The final sample included 2,329 infants from 67 laboratories. A preference for infant-directed speech survived, while its magnitude varied with age, language experience and measurement method. Laboratories used central fixation, head-turn preference or eye tracking procedures, making methodological variability an object of analysis. The result supports a reproducible average preference without treating the same effect size as universal for every infant or cultural setting.^[ref]

Several changes to our understanding follow. First, an established group-level tendency can coexist with weak prediction for an individual child. Secondly, stimulus choice, stopping rules, exclusions and coding decisions can change what has actually been measured. Thirdly, heterogeneous outcomes can identify theoretically useful boundary conditions, but a moderator discovered after a failure needs a new test rather than serving as an unlimited excuse. Finally, openly available null results reduce selective visibility of successful studies, improving the evidential base used to build developmental accounts.

The causal claim about reform itself should remain modest. Larger samples, broader recruitment and better controls often accompany transparency, so a change in an estimate cannot be attributed uniquely to preregistration. A perfectly reproducible analysis can reproduce a biased model, and an underpowered replication may be inconclusive. Reliability and measurement equivalence are especially important for looking-time and single-trial child tasks; independent coding and predefined exclusion rules help, but do not establish the intended psychological construct. Open child data also require appropriate consent and controlled access where identification is possible; useful transparency need not mean publishing recognisable videos.

By 2022, these developments justified a more conditional developmental science: waiting reflects more than a decontextualised trait; claims of newborn action matching require precise controls; and an infant speech preference can be robust while method-sensitive. The main advance is a tighter connection between a theoretical claim, an explicitly defined measure and evidence that others can inspect or independently test. Transparency changes what can be learned from disagreement, while replication establishes how far a finding travels.

Improve the sampling, measurement and dependence model before interpreting the association. Define the target population and recruit a broader sample with a transparent sampling frame, ideally using probability sampling where feasible and adequate representation across the relevant ages and roles. Justify the sample size for the intended effect size and precision. Preselection on reputation or the outcomes should be avoided or explicitly modeled.

Operationalize workplace friendliness with several relevant measures, such as independently obtained colleague reports and standardized behavioral tasks, rather than relying only on photographs. Use standardized photographs if impressions are themselves the research target, several independent raters, and blinding to power and the specific hypothesis. Measure inter-rater reliability and retain the distinction between impression and behavior. Establish what the power measure actually assesses and record plausible confounders with a causal rationale.

For a linear regression analysis, use friendliness as an explicitly declared outcome and power as a continuous predictor. Retain actual age as a continuous covariate when available instead of treating three age groups as equally spaced measurements; consider justified nonlinearity. If only age categories are available, use explicit categorical contrasts and nonoverlapping category definitions. Check regression diagnostics, influential observations, heteroscedasticity and multicollinearity. Account for executive and rater dependence with an appropriate mixed-effects model when repeated or crossed ratings are analyzed; do not count each rating as a new executive. Report estimates with confidence intervals and disclose exclusions and missing observations.

Preregistration can distinguish planned analyses from exploratory ones. A longitudinal study with repeated measures can establish temporal ordering more clearly, though it remains vulnerable to confounding. A feasible, ethical randomized experiment manipulating assigned power or role in a controlled task could test a more narrowly defined causal effect; its external validity to senior executives must still be assessed. No observational adjustment alone guarantees removal of all unmeasured alternatives.

Make the development process inspectable and separate exploratory decisions from independent confirmation. Create a preregistration for the validation stage before examining its outcome-relevant data, specifying recruitment, stopping rules, exclusions, missing-data treatment, item scoring, estimator, factor structure and criteria for evaluating it. The exploratory stage can also have a recorded protocol, including a planned parallel analysis rule; label data-driven item revisions and model changes as exploratory rather than disguising them as prior predictions. Document deviations and their reasons.^[ref]

Keep an immutable copy of the collected data, record cleaning steps, and provide a data dictionary, final item wording, scoring instructions and executable analysis code. Record software and package versions, random seeds for simulations or bootstrap calculations, and the steps needed to regenerate tables from the permitted data. These support computational reproducibility; an independently collected validation study or scientific replication addresses a different question.

Share appropriately de-identified data where consent and re-identification risk permit, with controlled access or a clear restriction statement where they do not. Protect lecturer and rater identities and disclose the pilot's convenience sampling and all item-selection steps. Report inconclusive and unfavorable findings as well as favorable ones. A registered report can obtain peer review of the validation plan before its results are known, reducing outcome-dependent publication incentives.^[ref]

Preregistration creates a time-stamped record of research questions and planned methods before the relevant results are examined. Specify the design, recruitment and stopping rules, outcome definitions, exclusions, principal tests, model choices and any conditional decision rules. For existing data, disclose prior access and what was already known. A sufficiently precise record helps readers distinguish prior predictions from choices prompted by the results.^[ref]

It does not prohibit useful changes or new discoveries: report departures, their timing and reasons, and distinguish exploratory analysis from confirmatory analysis. A vague or selectively followed registration does not solve selective reporting, and preregistration cannot repair a poor measure or inadequate design of experiments. A registered report adds pre-result peer review and conditional publication acceptance, which are not implied by registration alone.

HARKing means presenting a hypothesis generated after inspecting results as though it had been specified beforehand. For example, after trying several possible factor structures in the lecturer data, a researcher might claim that the best-fitting structure was their original prediction. The problem is the misrepresented evidential history, not the act of discovering a pattern.

Such undisclosed selection makes apparent confirmation too persuasive because the reported test does not represent the whole search that produced the hypothesis. Label new ideas as exploratory, record prior plans through preregistration, disclose the search and evaluate the resulting prediction in independent data. Registered reports and transparent reporting can reduce incentives for that misrepresentation while preserving legitimate exploratory work.^[ref]

By June 2022, important principles of reading acquisition were established, including the need to learn written word forms and to understand the language they express. The major unanswered questions concerned how these skills become efficient and integrated, why children respond differently to experience and instruction, and how experimental gains become sustained comprehension and participation. Useful future research should target those uncertainties with explicit competing predictions rather than reopen every instructional question as if no evidence existed.

One question concerns what is learned from a successful encounter with a new written word. Does the child acquire an item-specific spelling, a reusable mapping, a contextual guess, or some combination? David L. Share's delayed learning experiments motivate the distinction, while artificial orthography work shows that strong item learning and generalisation need not move together. Future studies should therefore distinguish recognition of practised items from transfer to novel combinations and later retention, rather than use one immediate naming test as a complete index of learning.^{[ref] [ref]}

A specific experiment could randomise unfamiliar but pronounceable items to matched exposure schedules varying the consistency of a spelling–sound relation. Hold the number of encounters, visual complexity and oral vocabulary knowledge constant. Assess trained spellings against homophonic alternatives after a delay, and test untrained recombinations that require the relevant mapping. Eye tracking during text reading could establish where the new form attracts attention, while comprehension questions verify meaningful engagement. The experiment should specify whether its prediction concerns initial learning, retention or generalisation.

A second question is how the distribution of teaching examples interacts with the learner's existing knowledge. Keith S. Apfelbaum and colleagues found that varied irrelevant consonants helped first graders learn vowel mappings. It remains necessary to identify when variation helps, whether its effects depend on prior decoding and how long the advantage lasts. A multisite classroom experiment could independently vary relevant consistency and irrelevant variation while matching total teaching time and opportunities to respond.^[ref]

Pretraining measures should be collected before randomisation, and interaction tests powered prospectively. A significant benefit in one subgroup and a nonsignificant effect in another does not demonstrate different treatment effects. Instructional fidelity and actual exposure need observation because a teacher may adapt a nominally identical activity in different ways. Broader spelling, unfamiliar-word reading and later passage comprehension would distinguish a useful instructional principle from a narrow training-task effect.

A third question is how best to coordinate word-level and language-level support. Margaret J. Snowling and colleagues' longitudinal profiles show that dyslexia, DLD and their co-occurrence can lead to comprehension difficulty through different constraints. The unresolved question is not whether either dimension matters, but which combination, timing and intensity of support helps a specified child. Diagnostic categories are too coarse to substitute for a measured profile.^[ref]

A factorial teaching trial could retain adequate core reading instruction for everyone and independently randomise additional decoding and oral language components, with contact and resource use measured. Include children across the skill distribution rather than only extreme, mutually exclusive categories. Prespecify primary outcomes for word reading, language and comprehension, with delayed follow-up. A subsequent adaptive stage could randomise a well-defined change for children not responding, instead of attributing improvement after an uncontrolled adjustment to personalisation itself.

The trial would also address a fourth question: what constitutes meaningful transfer? Janice M. Keenan and colleagues showed that comprehension assessments differ in their reliance on component skills. An intervention can look more successful simply because its outcome task resembles training. Future evaluations need independent passages, several assessment formats and checks that the construct retains a comparable meaning across time and groups. Function in the classroom and the child's experience should accompany test scores, without treating either as a substitute for accurate measurement.^[ref]

A fifth uncertainty concerns how findings generalise across writing systems, language backgrounds and educational environments. Artificial-script work offers experimental control, but Joanne S. H. Taylor and colleagues' instruction study used adults learning small novel vocabularies. It cannot establish the full trajectory of a multilingual child encountering an unfamiliar language of instruction. Coordinated cross-language studies should define the mappings and language experiences that differ, rather than merely compare national averages.^[ref]

Recruitment should include varied socioeconomic circumstances and children whose language development differs from the majority sample. Assessment needs to separate opportunity to learn from persistent difficulty and to examine the validity of the measures in each context. Shared protocols and culturally appropriate materials can coexist. The aim is to test which mechanisms generalise and which depend on script, vocabulary or teaching, not presume that every observed group difference reveals an intrinsic deficit.

Computational models can sharpen all these questions. A model should learn from a specified developmental input, make predictions for held-out items and trajectories, and face comparison with alternatives that use different representations or learning rules. Matching average skilled-reader accuracy is weaker than predicting the effect of an experimental change in input. Parameters should not be allowed to absorb every individual difference without independent constraints; failure should inform revision rather than invite unrestricted refitting.

Finally, the timescale of research must match the educational claim. Short experiments identify candidate processes, longitudinal cohorts reveal ordering and trajectories, and controlled implementation studies assess delivery and lasting benefit. Preregistration, transparent exclusions, appropriate handling of school clustering and missing follow-up, and independent replication make the chain more credible. The central unanswered problem is how to connect the child's particular learning history and profile with an instructionally manipulable process that produces durable, generalisable gains.

The evidence supports some prospective associations between violent media exposure and later aggression, but it does not establish a large, general causal effect on serious violence outside the laboratory. Aggression is behavior intended to harm; violence is its severe physical subset. Angry thoughts, physiological activation and an aggression-task score are not interchangeable with either. The relevant claim requires an exposure contrast, an outcome that captures harmful behavior in everyday life, and a design that distinguishes influence from selection.

Laboratory experiments can randomize immediate exposure, but a brief game followed by a noise-blast choice mainly tests a short-term response in an artificial setting. Competition, frustration, difficulty and expectations can differ between games as well as violent content. A statistically detectable laboratory effect therefore needs both construct validity and ecological validity before it supports a claim about everyday aggression. A plausible social learning mechanism supplies a hypothesis about acquiring aggressive responses; it does not by itself demonstrate that media caused a particular real-world outcome.

An important source of evidence is L. Rowell Huesmann and colleagues' follow-up from childhood television viewing to young adulthood. The study related violent television exposure at ages six to ten to later aggression, using follow-up interviews and archival information. Associations persisted after adjustment for measured childhood and family characteristics. Unlike a single laboratory task, the design addressed a long interval and outcomes beyond the immediate viewing session. It also tested exposure before the later outcome, making simple simultaneity an inadequate explanation.^[ref]

Temporal order is necessary but insufficient for causal inference. Earlier aggression may both encourage violent-media selection and persist into adulthood. Family conflict, peer environments or poorly measured dispositions may influence both variables. Adjustment for baseline aggression helps, but imperfect measurement leaves residual confounding, and including a variable in a model does not ensure that its causal role was correctly represented. Attrition can further change the composition of the observed follow-up sample. These limitations qualify the causal interpretation without making the association irrelevant.

Andrew K. Przybylski and colleagues provide a useful contrasting design: a registered report studied 1,004 adolescent–carer pairs, combining adolescent gaming information and independently rated violent content with carers' reports of aggressive behavior. The confirmatory analysis did not support the predicted positive relationship. Separating the exposure and outcome reporters reduced one source of common-method bias, while preregistration reduced flexibility in choosing an attractive analysis. The design was a cross-sectional study, however, so it did not estimate a randomized causal effect or settle effects of earlier exposure.^[ref]

A null finding constrains a claim under the measurements and precision of that study. It does not prove that every form of violent media has exactly zero effect on every child. Conversely, explaining away every null result after observing it makes a general hypothesis difficult to test. The useful question is whether a prespecified exposure–outcome prediction survives an adequately sensitive test, and whether any estimated effect is large enough to matter outside the measurement scale.

Longer experiments strengthen a different part of the argument. Simone Kühn and colleagues randomized adults with little recent gaming to a violent game, a nonviolent game or no gaming for two months, with later testing. They did not find the predicted increase in aggression across their outcome battery. Exposure occurred beyond a brief laboratory session, which improves the relevance of the manipulation. Yet many endpoints were questionnaires or experimental tasks, rather than observed assaults, and the modest adult sample cannot settle small effects in children. The violent and nonviolent games also differed in more than violent content.^[ref]

The distinction between naturalistic exposure and naturalistic outcome is crucial. A home-based intervention can establish a change in a laboratory score without demonstrating everyday harm; a real-world outcome can be valuable even when its exposure is assessed in an observational study. No single study here simultaneously supplies perfectly isolated content, prolonged exposure, representative participants and high-quality measurement of rare violence. Triangulation should ask whether the different weaknesses plausibly explain a pattern, rather than counting positive and negative papers as votes.

Meta-analysis helps estimate that pattern, but pooling does not repair a shared design limitation. Anna T. Prescott and colleagues combined 24 prospective studies with over 17,000 participants. They found a small positive association between violent-game exposure and later physical aggression after baseline adjustment; estimates decreased when available additional covariates were included. Aaron Drummond and colleagues' later meta-analysis emphasized weak associations and their sensitivity to study quality. The disagreement makes inclusion rules, measurement and analytic decisions central to interpretation.^[ref][ref]

Even a small, reproducible association would not automatically identify a small causal effect: a consistent confound can also replicate. On the other hand, limited statistical power means an individual nonsignificant experiment need not contradict a small association. Effect sizes and uncertainty should therefore be compared on compatible outcome scales. Publication bias and selective analysis can favor alarming positive findings, while insensitive measures can hide genuine effects; both possibilities require evidence rather than assertion. The available studies also concern particular media, populations and time intervals, so their conclusions should not be extended automatically to all violent content.

The strongest next tests would preregister longitudinal exposure contrasts, measure baseline behavior carefully, obtain outcomes from independent sources and retain participants across follow-up. Where ethical and practical, randomization to matched content would separate violent imagery from competition and frustration. Everyday aggression and severe violence would be analyzed separately. By the examination date, large causal claims about real-world violence exceeded the evidence; small or context-dependent effects on aggression remained possible and required better identification. This conclusion takes the positive prospective findings seriously while keeping their causal and behavioral scope explicit.

Advances in Methods and Practices in Psychological Science 3, 24–52; Participants, preregistered analyses and Discussion.

A publication format involving review of the question and methods before outcomes are known, with in-principle publication acceptance conditional on adequate adherence and reporting. It differs from preregistration alone, which need not involve peer review or publication commitment.^[ref]

A research collaboration conducting coordinated developmental experiments across laboratories, including a preregistered study of infant-directed speech preference.^[ref]