RESEARCH DOSSIER
Causal Inference in Psychology
Abstract. Causal inference in psychology examines how evidence about observed people, behaviors, and psychological outcomes can support claims about the consequences of alternative interventions. This fundamental critical narrative research monograph reconstructs the historical development of potential-outcome and graphical approaches, explains estimands and identification assumptions, and synthesizes research on randomized experiments, observational comparisons, propensity scores, longitudinal g-methods, natural experiments, regression discontinuity, difference-in-differences, instrumental variables, and causal mediation. It critically evaluates measurement validity, interference, selection, missing outcomes, unmeasured confounding, replication, effect heterogeneity, and transportability. Original methodological studies, experimental benchmark investigations, and research on the reproducibility of psychological science support a synthesis of how design, theory, measurement, and sensitivity analysis jointly determine the credibility of causal claims. A concluding analysis examines intervention definition and evidence quality in human–artificial research settings.
Keywords: causal inference in psychology; potential outcomes; counterfactuals; causal estimands; causal diagrams; confounding; randomized experiments; observational studies; propensity scores; target trial emulation; longitudinal causal inference; regression discontinuity; difference-in-differences; instrumental variables; causal mediation; interference; sensitivity analysis; replication; transportability; Artificial Era
The Scientific Problem of Causal Explanation
Causal inference in psychology concerns the effects that changes in exposures, interventions, experiences, or social conditions would produce in specified psychological outcomes. A causal question identifies a contrast between alternative conditions, a population or set of units, a time horizon, and an outcome whose measurement has substantive meaning. Whether training improves memory, whether workplace stress changes attention, or whether a social norm alters cooperation requires evidence about alternatives to the condition actually observed. The methods examined here organize those alternatives into explicit assumptions and empirical designs. Rubin (1974) Lundberg et al. (2021)
Psychological explanation often employs verbal mechanisms: an emotion changes attention, an expectation shapes behavior, or a therapeutic interaction changes symptoms. Those propositions become empirically assessable when an intervention can be described, its consequences operationalized, and rival pathways represented. Causal inference does not reduce explanation to a regression coefficient. It connects a well-defined scientific question to possible observations through a design and a theory of how observations were generated. The resulting claim has a domain, a target quantity, a set of assumptions, and a degree of uncertainty. Holland (1986) Rohrer (2018)
The particular difficulty is that the same participant cannot ordinarily be observed at the same moment both exposed and unexposed to an intervention while all other relevant conditions remain identical. Different participants, repeated periods, experimental groups, and modeled counterfactuals supply ways of learning about this missing comparison. Every approach introduces assumptions concerning assignment, time, measurement, or population exchangeability. Descriptive associations are indispensable evidence about the data, yet causal conclusions require a further account of why the chosen comparison corresponds to a meaningful intervention contrast. Neyman (1923/1990) Rubin (1974)
This dossier critically integrates experimental psychology, quantitative methods, epidemiology, and program evaluation. It is a structured critical narrative synthesis of identified theoretical and empirical sources, not a protocol-based systematic review or a pooled meta-analysis. The research object includes estimands, identification, estimation, mediation, interference, quasi-experiments, and sensitivity analysis. Neighboring methodological topics such as the construction of behavioral tasks and psychometric measurement enter when they affect causal validity. The synthesis also examines the changing evidential demands created by digital and human–artificial research environments. Athey & Imbens (2017) Westfall et al. (2014)
Historical Formation of Counterfactual Reasoning
The experimental tradition in psychology developed alongside the broader logic of comparing observed outcomes under controlled conditions. Donald T. Campbell's 1957 treatment of the validity of experiments in social settings made alternative explanations central to research design, including threats that arise from selection, history, maturation, and the circumstances under which participants encounter an intervention. This lineage matters because a study can achieve a precise numerical contrast while comparing groups that differ in the very causes of the response under investigation. Campbell (1957)
Jerzy Neyman's work on agricultural experimentation formulated potential outcomes for different treatment conditions, with the historically significant formulation appearing in the 1923 work and a later English translation published in Statistical Science in 1990. Potential outcomes make the comparison of incompatible alternatives mathematically explicit. The framework estimates averages over randomized assignment despite missing unit-level alternatives. It supplies a design-based foundation for reasoning about treatment effects and sampling variation without requiring every individual effect to be observed. Neyman (1923/1990)
Donald Rubin's 1974 article in the Journal of Educational Psychology applied potential-outcomes reasoning to randomized and nonrandomized treatments, including educational and behavioral research. Rubin distinguished the advantages of randomization from situations in which adjustment and design knowledge permit informative observational comparisons. Paul Holland's 1986 synthesis subsequently clarified why the causal language associated with experimental contrasts cannot simply be imported into unrestricted covariance models. Together these papers helped establish assignment mechanisms, potential outcomes, and design as explicit parts of scientific interpretation. Rubin (1974) Holland (1986)
Another history runs through statistical path analysis and the structural modeling of systems. Judea Pearl's 1995 study formalized causal diagrams as a language for combining substantive assumptions with observed distributions. Greenland, Pearl, and Robins later clarified the utility of diagrams for evaluating confounding criteria and adjustment choices. These contributions converge with the counterfactual tradition on a central principle: observed associations identify causal effects only within an articulated model of data generation, intervention, and selection. Different mathematical representations are useful precisely because they expose assumptions hidden in informal prose. Pearl (1995) Greenland et al. (1999)
Defining a Causal Estimand
A causal estimand is the target quantity that a study seeks to learn, defined independently of the estimation algorithm. For a binary intervention A and outcome Y, a population average treatment effect is the expectation of Y(1) minus the expectation of Y(0), where Y(a) is the potential outcome under assignment a. The target might instead be an effect among treated individuals, a conditional effect in an age group, or a difference in risk at a specific follow-up point. Stating the estimand first prevents model convenience from silently determining the scientific question. Rubin (1974) Lundberg et al. (2021)
The definition of treatment deserves unusual care in psychological research. 'Exposure to stress' can encompass events with radically different intensity, duration, meaning, and timing. 'Use of artificial intelligence' may include information retrieval, advice, delegated judgment, or ongoing interaction. If different versions of a treatment have different consequences, a single binary code can mix multiple interventions. Explicit intervention regimes, delivery protocols, adherence conditions, and time horizons help distinguish a scientifically coherent contrast from a heterogeneous label. This issue is especially consequential when outcomes respond to context and expectations. Hernán & Robins (2016) Rohrer (2018)
An intention-to-treat estimand describes the effect of assignment to a program, irrespective of subsequent adherence. A per-protocol estimand targets outcomes under sustained conformity to specified strategies and requires additional assumptions about time-varying adherence. An instrumental-variable estimand under certain assumptions can target the local effect among people whose treatment uptake responds to assignment. These quantities answer different scientific and policy questions, even when they arise from the same study. Researchers should specify which behavioral decision each contrast can inform. Angrist et al. (1996) Hernán & Robins (2016)
Outcome scales also determine the estimand. A mean difference in a validated cognitive score, a change in the probability of clinical remission, a standardized effect, and a change in an individual's daily symptom trajectory are not interchangeable summaries. Follow-up timing changes the question, because psychological responses may develop, decay, or interact with subsequent experiences. A well-posed estimand identifies treatment strategies, comparison, population, outcome, time, intercurrent events, and summary measure before statistical fitting begins. Lundberg et al. (2021) Campbell (1957)
Potential Outcomes and Identification Assumptions
Potential-outcomes reasoning separates causal quantities from the observed-data quantities used to estimate them. In the simplest two-condition case, each unit has Y(1) and Y(0), but the study records Y(A). Consistency connects the recorded outcome to the potential outcome under the treatment actually received. Positivity requires that relevant treatment possibilities occur within the covariate strata for which the effect is sought. Exchangeability states the relevant independence relation between treatment assignment and potential outcomes, possibly conditional on measured pre-treatment covariates. Rubin (1974) Rosenbaum & Rubin (1983)
Exchangeability is most transparent when a genuine randomization protocol assigns intervention conditions and compliance with that protocol is preserved. In observational psychology, exchangeability requires substantive defense. Pre-treatment severity, family environment, motivation, prior ability, access to treatment, and many other variables can shape both the exposure and response. Even a lengthy questionnaire cannot by itself establish that the important common causes have been measured or appropriately modeled. The assumption is a statement about the causal process, not a property certified by a statistical significance test. Stuart (2010) Rohrer (2018)
Positivity can fail in psychological populations when some intervention is unavailable, ethically excluded, or nearly universal in a relevant subgroup. Statistical adjustment cannot recover a comparison for which empirical support is absent without extrapolating beyond the data. Inspecting overlap, trimming unsupported regions, and distinguishing a population-wide effect from an overlap-population effect are legitimate design decisions, but they change the population represented by the estimand. Conclusions must therefore state their support domain rather than treating all target-population members as equally represented. Rosenbaum & Rubin (1983) Stuart (2010)
Consistency is similarly substantive. A school-level program delivered differently in different classrooms, or a psychotherapy condition combining variable therapist behavior and variable attendance, may not correspond to one intervention. Interference introduces another difficulty when a person's outcome depends on the treatments received by peers, classmates, colleagues, or online contacts. These complications demand treatment definitions and assignment models appropriate to social psychological processes. The familiar single-unit potential-outcome notation is a useful starting point, while richer exposure mappings and clustered designs are needed for many real settings. Neyman (1923/1990) Campbell (1957)
Causal Graphs and the Logic of Adjustment
Directed acyclic graphs encode assumptions about directional relations among variables in a causal system. An arrow depicts a direct causal dependence within the represented model rather than a measured correlation. A common cause creates a backdoor path between treatment and outcome, a mediator sits on a pathway transmitting an effect, and a collider is a variable with two incoming causal arrows. Graphical reasoning helps explain why controlling every available predictor is a poor rule for causal estimation. Pearl (1995) Greenland et al. (1999)
Suppose prior anxiety influences both the probability of receiving counseling and a later well-being outcome. A graph treating anxiety as a pre-treatment common cause supports adjustment when the estimand is the counseling effect and relevant assumptions hold. By contrast, adjusting for post-treatment coping behavior may remove part of the effect of counseling if coping mediates the response. The same measured variable may occupy different causal positions in different questions. Temporal ordering and subject-matter theory therefore determine what adjustment can mean. Rohrer (2018) Imai et al. (2010)
Conditioning on a collider can create association between otherwise independent causes. For example, inclusion in a specialist clinic might depend both on symptom severity and on access to care. An analysis restricted to clinic attendees can induce an apparent association between access and severity, even when the underlying population relation differs. Restricting samples, selecting responders, excluding attriters, and adjusting for variables influenced by both treatment and outcome causes can therefore open noncausal paths. Sampling is part of the causal diagram rather than a purely administrative preliminary. Pearl (1995) Rohrer (2018)
Graphs provide an audit language, not automatic truth. Two different causal graphs can imply the same observed statistical independences, and directional claims are often informed by experiments, timing, background knowledge, or explicit theory. Unmeasured nodes may change the adjustment set, and feedback processes require time-indexed representations to remain acyclic. A defensible analysis publishes its graph, states what arrows mean, identifies adjustment choices from the proposed graph, and considers plausible alternative graphs. Inference is then judged by the credibility of the assumptions and evidence supporting them. Greenland et al. (1999) Pearl (1995)
Randomized Experiments and the Assignment Mechanism
Randomized experiments obtain their identification advantage from the assignment mechanism, which makes treatment groups comparable in expectation before treatment. When allocation probabilities are known, researchers can estimate assignment effects and quantify sampling uncertainty under a design-based analysis. Randomization supports an inference about the intervention as delivered to the enrolled sample; claims about other populations, other intervention versions, or sustained compliance demand additional reasoning. Psychological experiments also require a clear distinction between random assignment and random recruitment. Rubin (1974) Holland (1986)
Allocation concealment, appropriate counterbalancing, pre-specified outcomes, and transparent treatment delivery affect the credibility of the design. A laboratory manipulation of fear may be randomized but still vary in interpretation across participants. Blinding may be impossible for a behavioral program, while assessor blinding or automated outcome scoring may still reduce differential measurement. Participants may infer the hypothesis and alter responding. Such expectancy and demand effects are themselves potential causal pathways, and whether they threaten validity depends on the scientific estimand. Campbell (1957) Westfall et al. (2014)
Repeated-measures experiments economize on participants and can improve precision when within-person comparisons are credible. Their interpretation depends on assumptions about carryover, fatigue, learning, treatment order, and time-varying context. Factorial designs can test interactions between interventions but may be underpowered for heterogeneous effects. Cluster randomization is appropriate when contamination or group-level implementation would make individual assignment unstable. The analysis must reflect the level at which treatment is randomized rather than treating a large number of repeated observations as independent replications. Westfall et al. (2014) Neyman (1923/1990)
Randomization itself does not validate the psychological construct. An intervention may reliably change scores because it alters response strategy, motivation, or familiarity with a task rather than the intended latent ability. When participants respond to sampled stimuli, both the participant and stimulus populations are potential sources of sampling error. Westfall, Kenny, and Judd showed that power and generalization in such experiments depend on crossed participant-by-stimulus variation. Experimental rigor requires the manipulation, measurement, sampling structure, and target of inference to align. Westfall et al. (2014)
Observational Studies and Covariate Design
Observational psychological research often studies exposures that cannot be assigned, including trauma, adverse environments, chronic occupational conditions, socioeconomic resources, and some developmental experiences. The most informative analysis begins by describing the hypothetical intervention or policy contrast, establishing eligibility and measurement time, and selecting plausible pre-exposure common causes. Data abundance increases precision for observed associations while leaving identification assumptions subject to scientific examination. A precise design statement therefore has priority over the sophistication of a prediction model. Hernán & Robins (2016) Stuart (2010)
Covariate adjustment may be implemented through regression, stratification, matching, weighting, or combinations of these approaches. These are different strategies for using measured predictors to construct a comparison under assumptions of conditional exchangeability. The analysis should prioritize common-cause variables identified before inspecting outcomes. Including strong predictors of the outcome can improve efficiency, while including consequences of treatment, colliders, or variables measured with incompatible timing can change the estimand or introduce bias. Each adjustment set requires causal justification. Rosenbaum & Rubin (1983) Rohrer (2018)
Psychological data present characteristic difficulties because prior symptoms, behavior, expectations, and access to resources often interact over time. A regression using baseline anxiety and treatment engagement can conflate pre-treatment confounding with post-treatment mediation if engagement is affected by the intervention. Selective enrollment and dropout further complicate generalization and exchangeability. Long covariate lists, automated variable selection, and excellent out-of-sample prediction of treatment assignment do not establish the absence of unmeasured confounding. Robins (1986) Rohrer (2018)
A strong observational design makes its comparison transparent through a time-zero definition, explicit treatment strategies, eligibility criteria, baseline covariate measurement, follow-up duration, and anticipated sources of loss. Hernán and Robins formalized the idea of emulating a target trial using observational records. For psychological cohorts and digital behavior traces, this discipline can expose immortal-time errors, inappropriate follow-up starts, and inconsistencies between who was eligible for each strategy and who appears in an analytic subgroup. Hernán & Robins (2016)
Propensity Scores, Balance, and Overlap
Rosenbaum and Rubin defined the propensity score as the probability of assignment to treatment conditional on observed covariates. Under conditional exchangeability, balancing on an appropriately specified propensity score can balance the distribution of those observed variables. The result motivates matching, weighting, and stratification approaches that construct more comparable treated and untreated groups. The guarantee concerns covariates represented in the model and the required assumptions; it cannot independently remove hidden causes or restore unsupported treatment comparisons. Rosenbaum & Rubin (1983)
Propensity-score analyses benefit from separating design from outcome analysis. Researchers can inspect covariate balance after weighting or matching without selecting the design that happens to produce the most attractive effect estimate. Standardized mean differences and distributional comparisons are more informative for balance than tests of whether covariate means are statistically significant. The selection of a target population depends on the weights or matched sample, so reporting who remains represented after design changes is a substantive scientific obligation. Stuart (2010) Rosenbaum & Rubin (1983)
Extreme estimated assignment probabilities create unstable inverse-probability weights, often because treatment and comparison groups occupy different regions of covariate space. Common-support diagnostics, stabilized approaches, trimming, and overlap restrictions address different manifestations of this difficulty. Their implementation changes the population contrast that can be responsibly described. A result based on a highly selected overlap subgroup cannot silently inherit claims about every person in the original sampling frame. Stuart (2010) Athey & Imbens (2017)
In developmental or clinical psychology, matching on a symptom score measured after treatment begins can undermine the intended comparison. Matching on highly noisy predictors can leave considerable residual imbalance in underlying constructs, and missing baseline variables can select participants differently across arms. Propensity scores should therefore be reported with temporal measurement details, covariate definitions, balance diagnostics, overlap plots, sensitivity analyses, and an explicit estimand. Numerical convergence among several weighting algorithms is useful robustness evidence, yet all can share the same untested assumption of no unmeasured confounding. Rohrer (2018) Cinelli & Hazlett (2020)
Regression Adjustment and Model Dependence
Regression estimates describe conditional associations under a specified functional form. Their causal interpretation requires the design assumptions connecting measured covariates to a valid counterfactual comparison. A coefficient can be accurately computed and still represent a mixture of treatment effects, selection, and post-treatment pathways. Interpreting a regression coefficient as an intervention effect also requires attention to scales and interactions, because a conditional contrast may differ from the corresponding population-average estimand even when there is no uncontrolled confounding. Holland (1986) Lundberg et al. (2021)
Model specification matters in psychology because many relationships are nonlinear, context dependent, and temporally structured. When prior symptom severity predicts both intervention uptake and later outcomes, linear adjustment may be inadequate if severity has a sharply nonlinear relation to either process. Interaction terms can encode scientifically expected moderation, but adding them after examining the outcome can overfit chance differences. Researchers can use flexible models for nuisance relationships while retaining a predeclared causal estimand and evaluating overlap and residual bias. Athey & Imbens (2017) Stuart (2010)
Conditioning on a variable has different meaning from intervening on it. A correlation between perceived control and depression after adjusting for education does not show what would happen if control were experimentally changed. Likewise, a model fitted to highly correlated psychological traits may provide unstable coefficients even while predicting the outcome reasonably well. Clear causal graphs and intervention definitions help decide whether a regression variable represents a cause to adjust, a mechanism to study, or a proxy whose interpretation is uncertain. Pearl (1995) Rohrer (2018)
Robustness analysis should compare defensible specification families rather than simply choosing models with favorable fit statistics. Alternative confounder sets, transformations, follow-up windows, and missing-data assumptions each probe a specific potential failure. Differences among estimates should be investigated as evidence about model dependence or data support. When methods disagree, the task is to determine which assumptions each method uses and which inferential question each answers, rather than average coefficients that are not estimates of the same target quantity. Cinelli & Hazlett (2020) Lundberg et al. (2021)
Time-Varying Exposure and Longitudinal Causal Effects
Repeated observations create opportunities to estimate how interventions affect evolving psychological states, but they also create time-dependent confounding. Prior treatment can change later symptoms, and those symptoms can in turn determine later treatment. Adjusting for the symptoms as though they were ordinary baseline causes can block treatment effects; failing to address them can leave confounding of later treatment. The longitudinal causal structure must therefore represent sequential treatment, intermediate covariates, dropout, and the targeted treatment regimen. Robins (1986)
Robins's work on sustained exposures and the healthy-worker survivor effect demonstrated why familiar adjustment strategies can fail when time-varying factors are affected by previous exposure. The general insight applies to psychological support programs, educational sequences, medication-use histories, and adaptive digital interventions. Sequential exchangeability, appropriate consistency, and positivity are required to relate observed longitudinal data to regime-specific potential outcomes. These assumptions are especially demanding when histories of unmeasured mental states influence subsequent engagement. Robins (1986) Hernán & Robins (2016)
Marginal structural models, g-computation, and other longitudinal g-methods can represent effects of sustained treatment strategies under stated conditions. Their value lies in the alignment between temporal causal question and identification strategy, not in the automatic removal of bias. Model choices concern the probabilities of treatment and censoring over time, outcome evolution, and the stability of weights across histories. Positivity becomes difficult when some treatment sequences almost never occur, especially in small clinical samples with complex histories. Robins (1986) Hernán & Robins (2016)
Experience sampling, passive sensing, and ecological momentary assessment increase temporal resolution without converting observational association into random assignment. An hourly association between stress and smartphone use may reflect a causal effect in either direction or common determinants such as work demands. Reverse causation can operate at different lags; time-indexed graphs help express the alternatives. Longitudinal analysis should distinguish within-person contrasts, between-person differences, dynamic intervention rules, and the conditions under which each could support a causal claim. Rohrer (2018) Lundberg et al. (2021)
Natural Experiments and Quasi-Experimental Comparisons
A natural experiment exploits assignment variation created by a process outside the researcher's direct intervention, such as a policy, institutional rule, resource threshold, or administrative change. Its scientific value depends on why this variation can approximate a meaningful intervention comparison. The term natural experiment alone does not establish randomization. Psychology researchers must reconstruct the assignment mechanism, describe which individuals were exposed, and examine whether concurrent changes or selection processes could explain the resulting outcome differences. Campbell (1957) Athey & Imbens (2017)
Quasi-experimental analysis can be more credible than an elaborate conventional regression when a setting offers a sharp policy discontinuity or plausibly exogenous timing. Conversely, it can be weaker than a modest observational comparison if institutional assignment is poorly understood. Designs should be evaluated by their causal assumptions, not by a hierarchy of attractive labels. Policy reforms, educational admissions rules, community interventions, and workplace scheduling changes can all be informative, provided the potential outcomes under competing strategies are defined carefully. Thistlethwaite & Campbell (1960) Imbens & Lemieux (2008)
A useful methodological check is whether the same observed difference would plausibly emerge if the intervention had no effect. Pre-existing group differences, simultaneous reforms, measurement reclassification, anticipation, and differential attrition can each generate an apparently causal change. Placebo outcomes, negative-control periods, pre-intervention trends, and alternate comparison groups can test particular implications of the proposed design. Passing these tests strengthens credibility within their scope but cannot prove every causal assumption. Athey & Imbens (2017) Cinelli & Hazlett (2020)
Shadish, Clark, and Steiner constructed a particularly instructive evaluation by randomly allocating participants to randomized versus nonrandomized assignment systems, with mathematics or vocabulary training then assigned differently. The study isolated the consequences of self-selection and evaluated how measured covariates and adjustment changed the recovered contrasts. It illustrates that the reliability of a nonrandomized design is an empirical question requiring benchmarks and substantive design knowledge. One successful correction in a bounded experiment cannot justify universal claims for observational adjustment. Shadish et al. (2008)
Regression Discontinuity and Threshold Assignment
Regression discontinuity designs exploit a rule that changes treatment assignment at a known cutoff in a continuous running variable. The causal comparison is local to individuals situated just above and just below that threshold, under continuity assumptions about potential outcomes. Scholarship eligibility scores, service triage thresholds, and educational placement rules provide possible psychological research settings. Estimation focuses on the discontinuity in the expected outcome at the threshold rather than a global linear trend over the full score distribution. Thistlethwaite & Campbell (1960) Imbens & Lemieux (2008)
Thistlethwaite and Campbell's 1960 study introduced regression-discontinuity analysis in an educational context by comparing students close to a merit-recognition boundary. The historically important contribution was to identify a setting in which treatment assignment may be discontinuous while plausible background determinants vary smoothly through the cutoff. This is a design assumption subject to assessment, and a local result cannot automatically establish an effect for individuals far from the threshold. The interpretation also depends on whether the cutoff controls assignment or actual treatment receipt. Thistlethwaite & Campbell (1960)
Modern practice examines possible manipulation of the running variable, sorting near the cutoff, discontinuities in pre-treatment characteristics, sensitivity to bandwidth selection, and alternative functional specifications. Local linear methods and careful bandwidth reporting generally align more transparently with the design than fitting an unrestricted high-order polynomial over a wide interval. The precise identification conditions vary with sharp or fuzzy assignment. If individuals or administrators strategically alter scores near the cutoff, the local comparison may no longer behave as assumed. Imbens & Lemieux (2008)
Applied to psychological services, a discontinuity at a symptom-score eligibility threshold can estimate a local effect of access or referral, with uptake and subsequent adherence requiring separate analysis. The score itself may be noisy, manipulable, or influenced by incentives to obtain treatment. A result near a narrow service threshold answers a question about that local policy margin. Generalizing to people with much greater or much lower baseline severity requires an additional transportability argument supported by evidence rather than an implicit extension of the graph. Imbens & Lemieux (2008) Lundberg et al. (2021)
Difference-in-Differences and Policy Exposure
Difference-in-differences compares a change in outcomes in an exposed group with a change over the same period in a comparison group. The familiar estimate subtracts the comparison-group change from the treated-group change. Identification relies on a condition concerning the counterfactual trend that the exposed group would have followed without intervention, with additional design requirements concerning composition, anticipation, treatment timing, and measurement. Similar observed pre-intervention patterns can be informative, but they do not logically demonstrate that the counterfactual trend assumption holds later. Callaway & Sant'Anna (2021) Athey & Imbens (2017)
Psychological applications might examine distress before and after changes in employment policy, learning outcomes following school reforms, or behavioral responses to shifts in information environments. A study needs repeated comparable measures and a precise date at which exposure begins. Selective migration, differential survey participation, developmental change, and changing assessment instruments can create a spurious divergence. The strongest design descriptions specify which population remains comparable across periods and whether intervention anticipation was possible. Callaway & Sant'Anna (2021)
When different groups adopt an intervention at different times, standard two-way fixed-effects regressions can aggregate comparisons in ways that complicate interpretation under heterogeneous treatment effects. Callaway and Sant'Anna developed identification and estimation strategies for group-time effects under multiple periods and staggered timing, including conditional parallel-trend approaches. Researchers should identify cohort-specific effects, event-time patterns, and weighting choices rather than present a single coefficient as though it necessarily represented the intended population-average causal effect. Callaway & Sant'Anna (2021)
Event-study figures are useful diagnostic and communication tools when their comparison periods, weighting, and identification assumptions are explicit. A statistically nonsignificant pretrend test may be inconclusive in a small sample; a significant pretrend can expose a clear design weakness, depending on context. Placebo intervention dates, alternative unaffected outcomes, and sensitivity to the comparison population sharpen interpretation. The causal question should remain anchored in a plausible treatment process rather than in an appealing pattern of coefficient estimates. Athey & Imbens (2017) Callaway & Sant'Anna (2021)
Instrumental Variables and Treatment Noncompliance
An instrumental variable is a source of variation associated with treatment receipt that, under specified assumptions, affects the outcome through the treatment pathway of interest. Randomly assigning an invitation to counseling while actual counseling uptake varies can create a possible instrument. Identification additionally relies on an exclusion restriction and assumptions about the relation between assignment, potential outcomes, and treatment uptake. The instrument must be defended as part of an empirical design; statistical strength alone cannot establish the exclusion restriction. Angrist et al. (1996)
Angrist, Imbens, and Rubin showed how an instrumental-variable contrast can identify a local average treatment effect for compliers under random assignment of an instrument, relevant exclusion and monotonicity conditions, and appropriate consistency assumptions. In the encouragement example, compliers are individuals whose uptake changes in response to encouragement. The resulting estimand may be particularly relevant to policies that operate through encouragement, yet it differs from the effect among all eligible individuals or all eventual users. Angrist et al. (1996)
Psychological trials with nonadherence distinguish effects of assignment from effects of receipt. Comparing only those who completed treatment can reintroduce selection: motivation, symptom improvement, resources, and social support may influence completion and outcomes simultaneously. Instrumental-variable methods can sometimes address this problem, but invitations may affect expectations, perceived support, or behavior independent of treatment. If so, the exclusion assumption is questionable for psychological outcomes. Researchers must investigate those mechanisms rather than treat random encouragement as a universal solution. Angrist et al. (1996) Rubin (1974)
Weak instruments produce unreliable estimation and inference, especially in modest behavioral samples. Even a strong instrument may identify effects in an unusual subgroup whose responses differ from noncompliers. Reporting should therefore separate instrument assignment, actual exposure, first-stage relevance, substantive exclusion reasoning, monotonicity plausibility, estimation uncertainty, and the population of compliers. A local effect is a scientifically valuable quantity when appropriately described, not a shortcut to a global causal statement. Angrist et al. (1996) Lundberg et al. (2021)
Mediation, Pathways, and Mechanistic Claims
Psychological theories frequently propose that interventions change outcomes through intermediate processes: cognitive reappraisal may mediate an emotion-regulation intervention, perceived norms may transmit a social message, and improved sleep may contribute to subsequent attention. Causal mediation distinguishes an intervention's total effect from quantities describing particular pathways, under defined counterfactual comparisons. A variable's statistical position between exposure and outcome does not alone establish that it transmits the causal effect. Temporal order and intervention mechanisms must be established. Imai et al. (2010) VanderWeele (2016)
Imai, Keele, and Tingley developed a general framework that separates definitions and identification assumptions for mediation effects from the restrictions of a particular linear regression model. Their approach emphasizes that causal mediation commonly requires assumptions concerning mediator–outcome confounding that remain untested by randomizing only the initial exposure. Mediation estimates can be highly sensitive to these assumptions. Researchers should report their estimand and sensitivity analysis rather than infer a causal mechanism merely from changes in regression coefficients. Imai et al. (2010)
Bullock, Green, and Ha highlighted the difficulty of mechanistic identification even in randomized experiments. Randomizing an intervention does not randomize the mediator it induces; common causes of mediator and outcome can continue to distort pathway estimates. Attempts to manipulate a mediator can themselves create additional pathways or alter the intervention meaning. Mechanistic research is strongest when multiple experimental manipulations, careful temporal measurement, and converging designs test the implied causal chain. Bullock et al. (2010)
Natural direct and indirect effects, interventional indirect effects, and controlled direct effects represent distinct questions and demand different identification assumptions. Cross-world counterfactual assumptions used for some natural effects are especially consequential for interpretation. In practical psychological work, mediator measurements need construct validity, known timing, sufficient precision, and a defensible causal graph. Substantive conclusions should specify the mediated contrast and the assumptions rather than broadly announce that a mechanism has been proved. VanderWeele (2016) Imai et al. (2010)
Interference, Networks, and Social Contexts
Interference occurs when one unit's outcome depends on the treatment received by another unit. Social influence, classroom climate, family interaction, peer networks, collaborative decision-making, and online information diffusion make interference a central psychological issue. An intervention addressed to one member of a group may change the behavior of untreated members through imitation, expectation, resource sharing, or norm formation. The causal contrast therefore depends on how individual and group exposure are defined. The standard no-interference assumption cannot be imported without inspection into relational settings. Neyman (1923/1990) Campbell (1957)
Researchers can distinguish a direct effect of personal exposure from spillover effects transmitted by others, but doing so requires an exposure mapping appropriate to the network and assignment mechanism. In a school study, the relevant exposure may be the proportion of classmates assigned to a new practice rather than simply one's own assignment. Cluster randomization can reduce between-arm contamination under particular conditions while introducing cluster-level variation and changing statistical power. These designs require a clear statement about whether clusters themselves exchange information. Westfall et al. (2014) Rubin (1974)
An apparently individual psychological mechanism may be mediated by collective behavior. A change in one employee's feedback practices can affect colleagues' effort, social comparison, and perceived safety; those colleagues' responses can feed back to the employee. Interference and feedback can coexist, and causal graphs that ignore time may obscure their dynamic structure. Measurement must cover the relevant social network or approximate it under explicit assumptions. Simple participant-level regression standard errors do not correct the underlying problem of omitted peer exposure. Pearl (1995) Greenland et al. (1999)
In human–artificial interaction, a digital assistant may affect multiple participants through shared recommendations, collaborative documents, or cascades of adoption. One person's use can alter another person's exposure, even when the technology itself is assigned individually. The scientific task is to specify which unit is treated, what information is shared, what outcomes are observed, and which paths connect participants. The framework of explicit intervention contrasts remains applicable, but estimands and designs require new social exposure definitions suitable for digitally mediated networks. Lundberg et al. (2021) Rohrer (2018)
Measurement Validity and Construct-Causal Claims
Psychological constructs are frequently latent: anxiety, attentional control, trust, identity, resilience, and motivation are inferred from patterns of responses. A causal effect on an instrument's score is an effect on the recorded score under the research conditions. Inferring an effect on the intended construct requires additional validity evidence. A manipulation may change response thresholds, language comprehension, motivation to report symptoms, or familiarity with test stimuli. These pathways can change the observed outcome without equivalent change in the latent process of theoretical interest. Campbell (1957) Westfall et al. (2014)
Measurement timing can generate bias when the treatment affects whether, when, or how the outcome is recorded. In digital psychological research, use of an application can alter the amount of behavior logged, independently of genuine behavior change. A therapy condition can change willingness to disclose distress, creating a response shift on self-report scales. Researchers should examine measurement invariance, differential missingness, assessor expectations, and the stability of the scoring rule across experimental conditions. These questions belong to the causal interpretation of the measurement process. Rohrer (2018) Campbell (1957)
Baseline adjustment often increases statistical precision, but it can also interact with regression to the mean and imperfect construct measurement. An extreme-score eligibility rule may cause the average measured score to move toward a population mean even in the absence of treatment. The appropriate counterfactual is not the individual's unobserved prior score, but the outcome trajectory expected under a defined comparison strategy. Randomized controls and carefully constructed threshold designs can help distinguish intervention effects from selection associated with noisy baseline measurement. Thistlethwaite & Campbell (1960) Rubin (1974)
Psychology experiments frequently sample participants and stimuli from broader populations. A lexical decision result obtained with a narrow set of words may be statistically precise for those words while having uncertain generality across language materials. Westfall, Kenny, and Judd formalized the consequences of crossing participants and stimuli for statistical power. Similar reasoning applies when studies sample therapists, classrooms, videos, conversational prompts, or artificial-system responses. Identifying the intended units of generalization is necessary before an experimental treatment contrast can support a broader psychological theory. Westfall et al. (2014)
Selection, Attrition, and Missing Outcomes
Selection bias can arise before a study begins, during participation, or through the construction of an analysis sample. Recruitment via a specialized clinic, online platform, or school program can select individuals on causes of exposure and outcome. Even a randomized treatment within that selected population may support internal assignment-effect inference while offering limited information about the broader population. External validity and confounding are separate problems, although selection processes can also introduce causal bias inside an analyzed sample. Campbell (1957) Rohrer (2018)
Attrition is particularly concerning when treatment changes participation and unobserved outcomes influence the willingness or ability to remain in a study. Participants who improve may stop completing follow-up surveys, while participants experiencing distress may withdraw or seek additional care. Complete-case analysis then conditions on a post-assignment event potentially influenced by both treatment and outcome causes. Random allocation at baseline does not guarantee that retained observations remain exchangeable at follow-up. Hernán & Robins (2016) Rohrer (2018)
Inverse-probability-of-censoring weights, multiple imputation, outcome modeling, and explicit missing-not-at-random sensitivity analysis can address parts of the problem under distinct assumptions. The appropriate choice depends on the causal process behind missingness and on the estimand. Weighting requires sufficient information to predict selection, while imputation depends on assumptions concerning missing values conditional on observed data. None of these methods universally recovers an outcome process that was systematically never observed. Robins (1986) Stuart (2010)
Transparent research reports specify initial eligibility, assignment, enrollment, follow-up completion, exclusion decisions, reasons for missingness, and how these quantities differ by exposure condition. They compare conclusions under plausible selection models and avoid interpreting a retained-sample effect as though it necessarily represented all initially enrolled participants. In longitudinal digital studies, technical logging failures should be distinguished from behavioral nonuse, because the two imply different causal and measurement mechanisms. Hernán & Robins (2016) Lundberg et al. (2021)
Unmeasured Confounding and Sensitivity Analysis
Sensitivity analysis assesses how conclusions change under violations of assumptions that cannot be resolved by the observed data alone. A central question in observational psychology is how strongly an omitted common cause would need to influence both intervention assignment and outcome to explain an estimated association. Examples include unrecorded prior symptoms, family context, motivation, treatment access, or a shared environmental event. Quantitative sensitivity analysis translates these concerns into parameters and effect changes rather than adding a ritual sentence about possible confounding. Cinelli & Hazlett (2020) VanderWeele & Ding (2017)
Cinelli and Hazlett developed sensitivity tools relating omitted-variable bias to partial associations in regression settings, including comparisons with observed covariates as benchmarks. Such benchmarks can make assumptions more interpretable, but an observed covariate need not be a valid upper bound on a hidden cause. The scientific task is to justify the chosen sensitivity range using subject knowledge, historical data, or competing causal explanations. A numerical robustness estimate is meaningful only with the corresponding scale, model assumptions, and interpretation. Cinelli & Hazlett (2020)
VanderWeele and Ding introduced the E-value for particular risk-ratio-scale questions: it describes the minimum association strength that an unmeasured confounder would need with exposure and outcome, conditional on measured covariates, to explain away an observed association. The measure is useful in its defined setting but does not establish that a confounder of such strength exists or does not exist. It also cannot replace analysis of selection bias, measurement problems, treatment versions, or model misspecification. VanderWeele & Ding (2017)
Negative-control exposures or outcomes can test whether presumed causal isolation is plausible when an informative null relation is expected under a proposed model. Placebo periods, alternate outcome definitions, and falsification checks similarly probe distinct threats. A single negative-control result does not guarantee that every hidden cause has been addressed, and an unexpected association may reflect either bias or an incomplete substantive theory. Strong causal conclusions combine explicit estimands, credible assignment mechanisms, appropriate diagnostics, and sensitivity arguments grounded in the psychological domain. Athey & Imbens (2017) Rohrer (2018)
Reproducibility, Researcher Degrees of Freedom, and Evidence Quality
Statistical identification and scientific reproducibility are linked but distinct. A study can identify its claimed effect under defensible assumptions and still yield a highly variable estimate because of a small sample, unreliable measurements, or selective reporting. Conversely, a precise and reproducible association can consistently reflect a shared confounding process. Credible cumulative psychology therefore evaluates causal design, estimation uncertainty, measurement reliability, independent replication, and the transparency of analytic choices together. Rubin (1974) Open Science Collaboration (2015)
The Open Science Collaboration's 2015 project attempted replications of 100 experimental and correlational studies from three psychology journals. Its published abstract reported that 36 percent of replications produced statistically significant results, compared with 97 percent of the originals, alongside several other nonidentical replication metrics. These figures characterize a specific sampled corpus and operational definitions, not a universal probability that a psychological finding is true. The project nonetheless provides direct evidence that nominal statistical significance cannot be equated with dependable generalizable knowledge. Open Science Collaboration (2015)
Outcome switching, flexible inclusion rules, unreported subgroup analyses, and choices made after viewing treatment contrasts can distort inference. Preregistration and registered analysis plans can make the estimand, primary outcomes, sample exclusions, covariates, and sensitivity analyses auditable. Open materials and code aid computational reproducibility; well-designed independent replications probe external and internal consistency. Preregistration cannot repair a fundamentally implausible causal graph, and a replication using the same design may reproduce its systematic biases. Open Science Collaboration (2015) Rohrer (2018)
A cumulative evidence review should classify what each paper actually establishes: design assumptions, mathematical identification results, empirical intervention contrasts, validation of an estimator, observational estimates, or demonstrations of methodological vulnerabilities. It should attend to sample support, study settings, effect uncertainty, and competing explanations. A theoretical proof of identification under assumptions is not itself proof those assumptions hold in a psychological population. Similarly, a controlled simulation of a method's performance supports claims about its specified simulation environment. Shadish et al. (2008) Athey & Imbens (2017)
Heterogeneous Effects and Psychological Subgroups
An average causal effect can conceal variation across developmental stages, baseline severity, cultural settings, cognitive profiles, and social contexts. Heterogeneity is a scientific feature of psychological intervention research because treatment mechanisms may depend on resources, prior learning, expectations, and environmental opportunity. A conditional average treatment effect describes a contrast within a defined covariate stratum, while an individual causal effect is generally not identified from ordinary parallel-group data. The statistical distinction should guide both the question and claims about personalized treatment. Rubin (1974) Athey & Imbens (2017)
Subgroup analysis is especially vulnerable to selective reporting and instability when a study has many potential moderators but few participants within each group. A significant estimate in one subgroup and a nonsignificant estimate in another does not itself establish that the effects differ; a direct interaction contrast with uncertainty is required. Researchers should declare theoretically motivated moderators, consider multiplicity, model effect variation cautiously, and separate hypothesis generation from confirmatory evidence. A strongly fitted heterogeneity model may reflect noise if it was selected using the same outcome data. Athey & Imbens (2017) Open Science Collaboration (2015)
Flexible machine-learning tools can assist with estimation of nuisance functions or exploration of heterogeneous treatment effects. Their contribution depends on causal identification assumptions established by design and knowledge rather than by predictive performance. Cross-fitting, honest sample separation, or external validation can mitigate some overfitting concerns, while overlapping treatment support remains necessary. An algorithm that predicts who reports improvement after treatment is not necessarily predicting who would benefit more from receiving treatment instead of its alternative. Athey & Imbens (2017) Lundberg et al. (2021)
Clinical and educational decisions require considering effect magnitude, uncertainty, accessibility, and likely harms in the specific target population. Even a well-identified effect modifier may be measured unreliably or reflect a proxy for social conditions rather than an intervention-relevant mechanism. The evidential threshold for deploying individualized recommendations is generally higher than for describing a sample-average effect. A useful heterogeneity analysis reports the distribution of covariates, uncertainty for subgroup contrasts, support boundaries, and how any resulting decision rule would be evaluated prospectively. Stuart (2010) Westfall et al. (2014)
Generalizability, Transportability, and Population Change
External validity concerns whether a causal result learned in one experimental or observational setting informs a target population, time, institution, or intervention version. Randomization can produce credible internal contrasts among enrolled participants while recruitment and exclusion rules make them unusual relative to those who would later receive the intervention. Generalization requires an explicit target and evidence about effect-modifying characteristics, treatment implementation, outcome measurement, and environmental conditions. The validity question is which causal relation can reasonably travel, under which assumptions. Campbell (1957) Athey & Imbens (2017)
Psychological studies often recruit college students, online workers, patients at particular institutions, or technology users with distinctive resources and motivations. Even within a country, language, age, income, disability, access to care, and cultural context can change how a manipulation is understood and which outcome is registered. Transportability cannot be demonstrated by merely renaming the population in a conclusion. Comparable measurements, adequate coverage of effect modifiers, and explicit weighting or modeling of population differences can improve a transport argument when the necessary causal assumptions are plausible. Stuart (2010) Lundberg et al. (2021)
A repeated intervention may change across decades as ordinary experience, media environments, social norms, and available technologies change. A laboratory task measuring persuasion under one communication platform may not implement the same psychological exposure on another. Moreover, a published intervention can affect participants' expectations once its purpose becomes widely known. Researchers should distinguish transport of a functional mechanism from transfer of a fixed protocol and state which aspects of the causal question remain invariant. Campbell (1957) Rohrer (2018)
Multisite studies, prospective population sampling, replication across languages and institutions, and purposeful examination of effect modifiers help delimit generalizability. Synthesis should compare contrasts measured on compatible outcomes and examine differences in implementation rather than simply count the number of statistically significant replications. Where transport requires untestable assumptions, the conclusion should identify the target subgroup for which existing support is credible and describe what additional measurements or experiments would expand that domain. Open Science Collaboration (2015) Athey & Imbens (2017)
Empirical Applications Across Psychological Domains
Educational psychology illustrates the continuum from randomized assignment to quasi-experimental identification. An instructional intervention can be compared through individual or classroom randomization when feasible, while eligibility cutoffs and institutional reforms may create local or time-based comparisons. The principal outcome may be test performance, retention, school attendance, or later educational participation, each with different measurement and follow-up requirements. Thistlethwaite and Campbell's historical regression-discontinuity study and Rubin's treatment-effect framework remain instructive because they connect assignment to the interpretation of outcomes. Thistlethwaite & Campbell (1960) Rubin (1974)
In mental-health research, randomized assignment can estimate the effects of access to a treatment program, yet treatment completion, cointerventions, therapist variation, outcome reporting, and missing follow-up create additional causal questions. A comparison of people who complete therapy with those who stop is vulnerable to self-selection even within an initially randomized trial. Mediation claims about emotional processing, therapeutic alliance, or behavioral activation require assumptions and designs beyond assignment to the treatment arm. Longitudinal treatment pathways may require sequential causal models. Angrist et al. (1996) Imai et al. (2010) Robins (1986)
Social psychology frequently uses randomized messages, social cues, or group assignments and then interprets changes in behavior or reported attitudes. Such designs can establish assignment effects within the tested context but face demand characteristics, stimulus sampling, spillovers, and uncertain construct equivalence. Mediation is particularly attractive when theories posit attitudes or norms as intermediate states; Bullock, Green, and Ha explain why that explanatory step requires separate identification. Replications using different social materials and populations are relevant to the generality of the effect. Bullock et al. (2010) Westfall et al. (2014)
Developmental and organizational psychology often rely on observational cohorts, administrative policies, and repeated measurement of changing environments. Causal interpretations require attention to cohort selection, age-related trends, intervention timing, and group-level exposure. Workplace programs may diffuse among colleagues, while developmental support may be determined by prior observed difficulties. Quasi-experimental tools can contribute when their assignment rules are documented; longitudinal models can clarify dynamic confounding, and sensitivity analysis can estimate how much hidden selection would undermine a proposed effect. Callaway & Sant'Anna (2021) Robins (1986) Cinelli & Hazlett (2020)
Causal Research in the Artificial Era
The Artificial Era broadens the set of agents, environments, and interventions encountered in psychological research. Human participants use recommendation systems, conversational assistants, adaptive tutors, and automated decision support in settings where treatment content may change from interaction to interaction. For causal inference, the first task is to define what is assigned: access to a system, a specific version, a protocol for interaction, a recommendation policy, or an adaptive sequence of responses. These are different interventions with different potential outcomes. Lundberg et al. (2021) Hernán & Robins (2016)
Research on human–artificial relations must distinguish user selection from intervention effects. People who repeatedly consult an artificial system may differ in knowledge, uncertainty, digital literacy, or social opportunity before their first interaction. A comparison between frequent users and nonusers can therefore mix system effects with pre-existing differences and subsequent selection. Randomized access or recommendation policies can be informative when ethically and practically feasible, while observational analyses require carefully measured pre-treatment histories and appropriate sensitivity analyses. Rosenbaum & Rubin (1983) Rohrer (2018)
Artificial-system outputs also create measurement and interference challenges. Two participants receiving nominally the same model may encounter different content because of prompts, session history, personalization, or model updates. An automated score may measure compliance with a benchmark rather than the psychological function whose causal change matters. Recommendations shared among classmates or colleagues can create spillovers. Researchers should archive versioned conditions, record treatment delivery, make sampling of outputs explicit, and distinguish changes in human performance from changes in how performance is measured. Westfall et al. (2014) Pearl (1995)
Propositions concerning artificial cognition, identity, agency, or psychological organization require operational definitions and identified evidence appropriate to their claims. A causal study of human trust in an artificial assistant can estimate how a defined system condition changes user behavior without thereby establishing the system's subjective experience or philosophical status. Theoretical proposals within Aisentica provide an interpretive horizon, while empirical claims require independently inspectable observations, counterfactual contrasts, and a clearly stated scope. This distinction supports cumulative research linking Psychology of Homo, Psychology of Artificial, and Psychology of Human–Artificial Relations. Holland (1986) Lundberg et al. (2021)
Conclusion
Causal inference in psychology is an organized practice of defining intervention contrasts, identifying the assumptions linking observed data to potential outcomes, and evaluating the credibility of those assumptions in substantive contexts. Its foundational works establish complementary contributions: design-based reasoning about randomized assignment, potential-outcome formulations, causal graphs, and methods for observational estimation. None of these tools alone determines whether a given intervention has a specified psychological effect. The scientific result depends on alignment among the estimand, intervention, measurement, assignment process, analysis, and target population. Neyman (1923/1990) Rubin (1974) Pearl (1995)
Evidence is strongest when research designs directly address plausible rival explanations and expose remaining uncertainty. Randomization supports treatment-assignment contrasts under clear design conditions. Propensity-score and regression approaches organize observational comparisons under measured-confounder assumptions. Quasi-experimental thresholds, differential policy timing, and instruments can identify informative local or design-specific effects when their defining assumptions hold. Longitudinal methods address sequential selection; mediation methods study pathways under additional assumptions. Sensitivity analyses and independent replications reveal the limits of any single estimate. Rosenbaum & Rubin (1983) Imbens & Lemieux (2008) Angrist et al. (1996) Imai et al. (2010) Cinelli & Hazlett (2020)
The central unresolved scientific challenges are substantive as well as statistical. Psychological interventions have multiple versions, outcomes are often measured imperfectly, mechanisms are intertwined, participants influence one another, and effects can depend on history and culture. Accurate causal inference therefore requires direct engagement with developmental, clinical, social, and biological theory. A sophisticated statistical procedure cannot compensate for an undefined treatment, an incoherent outcome construct, or an unsupported comparison population. Campbell (1957) Rohrer (2018) Westfall et al. (2014)
The emerging agenda combines more explicit estimands, longitudinally appropriate design, transparent causal graphs, calibration of observational estimates against credible benchmarks, quantitative sensitivity analysis, multisite replication, and precise documentation of human–artificial interventions. These practices permit psychology to explain both the conditions under which a measured effect appears and the conditions under which the corresponding causal statement remains credible. Within the Artificial Era, the same discipline of counterfactual definition and evidence evaluation is essential for investigating changing forms of cognition, behavior, and relation. Lundberg et al. (2021) Hernán & Robins (2016) Open Science Collaboration (2015)
References
- Angrist, J. D., Imbens, G. W., & Rubin, D. B. (1996). Identification of causal effects using instrumental variables. Journal of the American Statistical Association, 91(434), 444–455. https://doi.org/10.1080/01621459.1996.10476902
- Athey, S., & Imbens, G. W. (2017). The state of applied econometrics: Causality and policy evaluation. Journal of Economic Perspectives, 31(2), 3–32. https://doi.org/10.1257/jep.31.2.3
- Bullock, J. G., Green, D. P., & Ha, S. E. (2010). Yes, but what's the mechanism? (Don't expect an easy answer). Journal of Personality and Social Psychology, 98(4), 550–558. https://doi.org/10.1037/a0018933
- Callaway, B., & Sant'Anna, P. H. C. (2021). Difference-in-differences with multiple time periods. Journal of Econometrics, 225(2), 200–230. https://doi.org/10.1016/j.jeconom.2020.12.001
- Campbell, D. T. (1957). Factors relevant to the validity of experiments in social settings. Psychological Bulletin, 54(4), 297–312. https://doi.org/10.1037/h0040950
- Cinelli, C., & Hazlett, C. (2020). Making sense of sensitivity: Extending omitted variable bias. Journal of the Royal Statistical Society: Series B (Statistical Methodology), 82(1), 39–67. https://doi.org/10.1111/rssb.12348
- Greenland, S., Pearl, J., & Robins, J. M. (1999). Causal diagrams for epidemiologic research. Epidemiology, 10(1), 37–48. https://pubmed.ncbi.nlm.nih.gov/9888278/
- Hernán, M. A., & Robins, J. M. (2016). Using big data to emulate a target trial when a randomized trial is not available. American Journal of Epidemiology, 183(8), 758–764. https://doi.org/10.1093/aje/kwv254
- Holland, P. W. (1986). Statistics and causal inference. Journal of the American Statistical Association, 81(396), 945–960. https://doi.org/10.1080/01621459.1986.10478354
- Imai, K., Keele, L., & Tingley, D. (2010). A general approach to causal mediation analysis. Psychological Methods, 15(4), 309–334. https://doi.org/10.1037/a0020761
- Imbens, G. W., & Lemieux, T. (2008). Regression discontinuity designs: A guide to practice. Journal of Econometrics, 142(2), 615–635. https://doi.org/10.1016/j.jeconom.2007.05.001
- Lundberg, I., Johnson, R., & Stewart, B. M. (2021). What is your estimand? Defining the target quantity connects statistical evidence to theory. American Sociological Review, 86(3), 532–565. https://doi.org/10.1177/00031224211004187
- Neyman, J. (1990). On the application of probability theory to agricultural experiments: Essay on principles, section 9 (D. M. Dabrowska & T. P. Speed, Trans.). Statistical Science, 5(4), 465–472. (Original work published 1923). https://doi.org/10.1214/ss/1177012031
- Open Science Collaboration. (2015). Estimating the reproducibility of psychological science. Science, 349(6251), aac4716. https://doi.org/10.1126/science.aac4716
- Pearl, J. (1995). Causal diagrams for empirical research. Biometrika, 82(4), 669–688. https://doi.org/10.1093/biomet/82.4.669
- Robins, J. (1986). A new approach to causal inference in mortality studies with a sustained exposure period—Application to control of the healthy worker survivor effect. Mathematical Modelling, 7(9–12), 1393–1512. https://doi.org/10.1016/0270-0255(86)90088-6
- Rohrer, J. M. (2018). Thinking clearly about correlations and causation: Graphical causal models for observational data. Advances in Methods and Practices in Psychological Science, 1(1), 27–42. https://doi.org/10.1177/2515245917745629
- Rosenbaum, P. R., & Rubin, D. B. (1983). The central role of the propensity score in observational studies for causal effects. Biometrika, 70(1), 41–55. https://doi.org/10.1093/biomet/70.1.41
- Rubin, D. B. (1974). Estimating causal effects of treatments in randomized and nonrandomized studies. Journal of Educational Psychology, 66(5), 688–701. https://doi.org/10.1037/h0037350
- Shadish, W. R., Clark, M. H., & Steiner, P. M. (2008). Can nonrandomized experiments yield accurate answers? A randomized experiment comparing random and nonrandom assignments. Journal of the American Statistical Association, 103(484), 1334–1344. https://doi.org/10.1198/016214508000000733
- Stuart, E. A. (2010). Matching methods for causal inference: A review and a look forward. Statistical Science, 25(1), 1–21. https://doi.org/10.1214/09-STS313
- Thistlethwaite, D. L., & Campbell, D. T. (1960). Regression-discontinuity analysis: An alternative to the ex post facto experiment. Journal of Educational Psychology, 51(6), 309–317. https://doi.org/10.1037/h0044319
- VanderWeele, T. J. (2016). Mediation analysis: A practitioner's guide. Annual Review of Public Health, 37, 17–32. https://doi.org/10.1146/annurev-publhealth-032315-021402
- VanderWeele, T. J., & Ding, P. (2017). Sensitivity analysis in observational research: Introducing the E-value. Annals of Internal Medicine, 167(4), 268–274. https://doi.org/10.7326/M16-2607
- Westfall, J., Kenny, D. A., & Judd, C. M. (2014). Statistical power and optimal design in experiments in which samples of participants respond to samples of stimuli. Journal of Experimental Psychology: General, 143(5), 2020–2045. https://doi.org/10.1037/xge0000014