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Interscalar medicine / long-form research note / January 2025

Causal Analysis in Medicine: From Event Timelines to Decisions

Medicine is full of associations that are clinically useful but causally ambiguous. Patients who miss rehabilitation sessions may recover more slowly. People receiving a second-line drug may have worse outcomes. Hospitals with more incident reports may appear less safe. None of these comparisons, by itself, tells us what would happen if attendance improved, the drug changed, or the reporting system were redesigned.

Causal analysis asks a different question from description or prediction: how would an outcome change under a specified alternative action or exposure? In the potential-outcomes formulation, the causal effect compares the outcome that would occur under strategy (A) with the outcome that would occur under strategy (B) for the same target population. Only one of these potential outcomes is observed for any person at a given time. The missing alternative is the fundamental reason causal inference requires a design and assumptions, not merely a large dataset. Hernán and Robins provide an open, formal treatment of this framework in Causal Inference: What If.

This definition also sharpens an older medical intuition. Bradford Hill’s 1965 “viewpoints” help assess whether an observed association is plausibly causal, but they are not a mechanical checklist and not all must be satisfied. Hill’s decisive practical question was whether changing an exposure would change the frequency of an outcome (DOI 10.1177/003591576505800503, PMID 14283879).

2. Three questions that should not be confused

“What caused this?” can refer to at least three different tasks.

  1. Population causal effect. Would offering transport to rehabilitation increase functional independence at 12 weeks compared with usual scheduling? This is an intervention-effect question and calls for a randomized trial or a carefully designed observational study.
  2. System learning after an incident. Which interacting conditions contributed to a delayed dose or a fall, and which system changes are likely to reduce recurrence? This is a safety and improvement question. It requires records, interviews, workflow analysis and testing of corrective actions, not a search for one guilty person or one universal “root cause.”
  3. Individual treatment decision. Will this particular patient do better on strategy A than strategy B? Population average effects do not automatically identify an individual effect. When treatment is reversible, effects are rapid, carry-over is manageable and equipoise exists, an N-of-1 design may sometimes provide stronger individual evidence; the CENT statement describes reporting standards for such trials (DOI 10.1016/j.jclinepi.2015.05.004, PMID 26272792).

These tasks can share an event ledger, but they do not share an automatic inference rule.

3. A timeline is evidence, not proof

The original sequence can be made more precise:

context and prior state → intervention or exposure → intermediate events → outcome
observation and recording form a second, partially independent process

A cause must precede its effect, yet temporal precedence is not enough. A rehabilitation session may be missed before deterioration, while worsening pain caused both the absence and the poorer outcome. The absence is then a marker or mediator, not necessarily the original cause. Conversely, documentation can occur after an outcome even when the underlying exposure occurred earlier. Event time and record time must therefore be stored separately.

A clinically useful event record should capture at least:

  • event type and unambiguous identifier;
  • patient, actor, organisation, device and location;
  • planned, initiated, completed, cancelled and failed states;
  • occurrence time, decision time, entry time and later corrections;
  • indication, intended goal, comparator or available alternative;
  • dose, intensity, duration and adherence, when relevant;
  • observed result and the time window in which it was measured;
  • source system, author, transformation history and version;
  • missingness, uncertainty and data-quality flags;
  • links to preceding orders, tasks, observations and outcomes.

HL7 FHIR R5 provides relevant interoperability primitives. Its Provenance resource records who, what and when for the creation or transformation of a resource; AuditEvent records operational and security-relevant activity. These standards improve traceability. They do not certify that a recorded edge is causal or that an unrecorded event did not occur.

4. Start with a causal question, not an algorithm

Before selecting variables or a model, specify:

  • target population: whose decision is at issue;
  • strategies: the intervention and a feasible comparator, stated precisely enough to implement;
  • time zero: when eligibility, assignment and follow-up begin;
  • outcome: a clinically meaningful endpoint and measurement window;
  • causal contrast: intention-to-treat, per-protocol, sustained strategy, policy effect or another defined contrast;
  • estimand: the numerical quantity, such as a risk difference, risk ratio, mean difference or survival contrast;
  • intercurrent events: how treatment discontinuation, rescue therapy, death or other post-baseline events change the question;
  • decision threshold: what magnitude and uncertainty would be sufficient to act.

The ICH E9(R1) addendum formalises an estimand through the treatment condition, population, variable or endpoint, population-level summary and handling of intercurrent events. This discipline prevents a common failure: estimating a mathematically convenient quantity that does not answer the clinical question.

Death and other competing events make that choice concrete. Death from another cause prevents later observation of a cause-specific death; death also prevents a future non-fatal event such as another hospital admission. Treating death as ordinary non-informative censoring can therefore target a hypothetical direct effect under strong assumptions, whereas comparing cumulative incidences while retaining death in the process can target a total effect that includes pathways through survival. Neither is automatically the “right” effect, and hazard-ratio contrasts generally lack a simple causal interpretation. Young and colleagues formalise these distinctions for failure-time estimands (DOI 10.1002/sim.8471, PMID 31957017). A clinical protocol should say whether the decision concerns overall patient benefit, a cause-specific biological pathway or another explicitly defined quantity.

5. Make assumptions visible with a causal graph

A directed acyclic graph (DAG) is a compact statement of the assumed relations among exposure, outcome, confounders, mediators, selection variables and measurement processes. It can show which variables should be adjusted for and, equally important, which should not. Conditioning on a mediator can remove part of the effect of interest; conditioning on a collider can create an association that was not present before. Greenland, Pearl and Robins introduced the formal use of causal diagrams in epidemiology and showed why traditional variable-selection rules can fail in multivariable settings (DOI 10.1097/00001648-199901000-00008, PMID 9888278).

A DAG is not discovered truth. Its arrows encode clinical and organisational assumptions that should be agreed before inspecting the final outcome analysis, versioned, challenged by domain experts and connected to a data dictionary. Automated causal-discovery methods can generate hypotheses, but their output depends on strong assumptions such as adequate measurement of common causes, correct time ordering, stable data-generating processes and, for many methods, acyclicity and faithfulness; the major constraint-, score- and functional-model families are reviewed by Glymour, Zhang and Spirtes (DOI 10.3389/fgene.2019.00524, PMID 31214249). Several graphs may fit the same observed conditional independences. Clinical knowledge and experimental or quasi-experimental evidence remain necessary.

Three outputs should remain separate. Effect estimation asks how an outcome would change under defined alternatives. Mediation analysis asks how much of an effect operates through a specified pathway. Causal discovery searches for graph structures compatible with the data and its assumptions. A discovery algorithm may nominate an arrow without identifying the magnitude of an intervention effect; conversely, a well-designed trial can estimate a total effect without revealing its mechanism. Mediation claims are especially demanding because causal direct and indirect effects require additional assumptions about exposure–outcome, exposure–mediator and mediator–outcome confounding, including post-treatment common causes. VanderWeele’s practitioner guide explains these requirements and sensitivity analyses (DOI 10.1146/annurev-publhealth-032315-021402, PMID 26653405). A plausible pathway should therefore be reported as a mechanism hypothesis unless the relevant mediation estimand and assumptions have been defended.

6. Choose a design that approximates the missing comparison

Random assignment is usually the clearest way to make treatment groups exchangeable at baseline. Randomized trials nevertheless may be infeasible, unethical, too slow, too small for rare harms, or unrepresentative of routine practice. Observational data can then be informative, but “real world” does not mean “unbiased.”

The target-trial approach starts by writing the protocol of the pragmatic randomized trial that would answer the question: eligibility, strategies, assignment, time zero, follow-up, outcomes, causal contrast and analysis. The observational emulation is then mapped to each element. This exposes errors such as comparing prevalent users with non-users, using future information to classify treatment, or starting follow-up at different times. Hernán and Robins describe the method in the primary framework paper (DOI 10.1093/aje/kwv254, PMID 26994063). The 2025 TARGET reporting statement adds a 21-item checklist (DOI 10.1136/bmj-2025-087179).

Depending on the question, useful designs may include:

  • a conventional or pragmatic randomized trial;
  • a cluster-randomized or stepped implementation design for organisational changes;
  • a new-user, active-comparator cohort;
  • a target-trial emulation from routinely collected data;
  • an interrupted time series when a policy changes at a clear point, with adequate pre- and post-intervention observations (DOI 10.1093/ije/dyw098, PMID 27283160);
  • a valid natural experiment or instrumental-variable design, only if its assumptions are defensible;
  • a case-crossover, self-controlled case series or N-of-1 design for appropriate transient exposures and outcomes.

Design is part of causal identification. A more complex estimator cannot repair a comparison that was defined incorrectly.

7. Identification assumptions must be stated

For a causal interpretation of an observational estimate, analysts usually need assumptions including:

  • consistency: the observed outcome under the received strategy corresponds to the relevant potential outcome; versions of treatment must be defined well enough for this to be meaningful;
  • conditional exchangeability: after adjustment, there are no unmeasured common causes of strategy and outcome;
  • positivity: each strategy has a non-zero probability within every covariate stratum in the target population;
  • limited interference or an explicit interference model: one patient’s treatment does not affect another patient’s outcome, unless such spillovers are modelled;
  • correct temporal alignment and measurement: eligibility, treatment assignment, covariates and outcomes are measured without biases that invalidate the comparison;
  • correct handling of selection, censoring and missing data.

These conditions cannot generally be proven from the same observational dataset. Positivity can be partly inspected through overlap diagnostics, but structural contraindications may make some comparisons impossible. Unmeasured confounding remains a scientific, not merely computational, uncertainty.

Interference is not exotic in healthcare. One patient’s intervention can consume a scarce appointment, alter staff workload, change infection risk, teach a shared caregiver or change a clinician’s practice for later patients. In such settings the potential outcome may depend on both the patient’s own strategy and the treatment allocation of others. The analysis must then define the relevant policy or coverage contrast and use a cluster, network or other explicit interference design instead of silently invoking “no interference.” Hudgens and Halloran provide a foundational formal treatment (DOI 10.1198/016214508000000292, PMID 19081744).

8. Longitudinal care makes standard adjustment dangerous

Rehabilitation and chronic care are dynamic. Pain today affects attendance tomorrow; attendance affects later pain; later pain affects subsequent treatment. A time-varying variable can therefore be both a confounder for a future treatment and a mediator of an earlier treatment. Conventional regression adjustment may block part of the effect or introduce bias.

Marginal structural models, the parametric g-formula and g-estimation were developed for such settings. Robins, Hernán and Brumback’s marginal structural model paper states the central problem and the inverse-probability-weighting solution (DOI 10.1097/00001648-200009000-00011, PMID 10955408); an accessible worked introduction to g-methods is available from Naimi, Cole and Kennedy (DOI 10.1093/ije/dyw323, PMID 28039382). These methods still depend on measured confounders, adequate models and adequate overlap.

Sometimes the intervention itself must adapt. A dynamic treatment regime is a sequence of decision rules that maps the evolving clinical history to the next action; it is not simply a risk score recomputed every day. Sequential multiple-assignment randomized trials (SMARTs) can compare adaptive sequences at clinically meaningful decision stages, while micro-randomized trials repeatedly randomize the availability of a small, just-in-time component and estimate its proximal effect. The former is useful for questions such as when to intensify rehabilitation; the latter for questions such as whether a reminder sent under particular circumstances increases activity in the next hour. Reviews of dynamic regimes describe their estimands and non-standard inference (DOI 10.1146/annurev-statistics-022513-115553, PMID 25401119); the original micro-randomized trial design and sample-size framework is reported by Liao and colleagues (DOI 10.1002/sim.6847, PMID 26707831). A proximal notification effect must not be relabelled as a long-term clinical benefit without a separate estimand and evidence.

9. Estimation is only one part of validation

A credible analysis should be designed to fail informatively. It should include:

  • balance and overlap diagnostics after weighting or matching;
  • negative-control exposures or outcomes chosen because no causal effect is expected, while recognising that negative controls have their own assumptions (DOI 10.1097/EDE.0b013e3181d61eeb, PMID 20335814);
  • sensitivity analysis for unmeasured confounding, including an E-value where appropriate but not as a substitute for domain-specific bias analysis (DOI 10.7326/M16-2607, PMID 28693043);
  • alternative exposure, outcome and time-window definitions;
  • explicit checks for immortal-time, protopathic and informative-censoring bias; immortal time can produce implausibly protective drug effects when future survival is built into exposure classification (DOI 10.1093/aje/kwm324, PMID 18056625);
  • quantitative assessment of missingness and measurement error;
  • replication across sites, periods or data sources where possible;
  • subgroup analyses defined in advance and supported by enough information;
  • calibration against randomized evidence when a comparable trial exists;
  • transportability analysis before applying an effect estimate to a different population or care system.

Even when the primary exposure coefficient answers the prespecified question, the other coefficients in the same adjusted regression do not automatically estimate the causal effects of those covariates. They can mix direct and total effects or remain confounded—the “Table 2 fallacy” (DOI 10.1093/aje/kws412, PMID 23371353). Each claimed causal effect needs its own estimand, graph and adjustment strategy.

EHR data also have an observation mechanism. Sicker people may visit more often, undergo more tests and generate denser records; the biomarker value that appears in the database is partly selected by the visit process. Simulations and paediatric EHR analyses show that adjusting for prior visit intensity may reduce but need not eliminate this informative presence bias (DOI 10.1093/jamia/ocac050, PMID 35438796). A robust event architecture should therefore model why and when an observation was made, not only its value, and should test visit-type restrictions or other sensitivity analyses.

Finally, transportability is a new causal problem rather than a clerical reweighting step. Applying an effect from a trial or one health system to another population requires assumptions about which effect modifiers differ and are measured. The choice of effect scale matters: conditional risk-ratio transportability is generally not compatible with risk-difference transportability except under stronger conditions. Dahabreh, Robertson and Steingrimsson formalise this limitation (DOI 10.1007/s10654-023-01067-4, PMID 38724763). A system should state the target population and scale instead of asserting that an effect is universally “portable.”

Uncertainty includes more than a confidence interval. It includes uncertainty about the graph, data provenance, outcome definition, missing data, model, target population and the plausibility of identifying assumptions.

10.1. Practical scenario: missed rehabilitation sessions

Suppose patients who miss two or more sessions have worse walking performance after 12 weeks. Calling missed attendance “the cause” is premature.

Candidate common causes include baseline severity, pain, fatigue, depression, work schedule, transport, caregiver availability and clinician decisions. Some are recorded poorly; some change over time. Attendance may also mediate the effect of reminders or transport assistance.

A decision-ready question is narrower: among eligible patients beginning outpatient rehabilitation, what is the 12-week difference in independent walking if a transport-and-reminder programme is offered from day one, compared with usual scheduling? A pragmatic randomized or cluster-randomized trial may answer this directly. If only observational data exist, the analysis should emulate that trial with aligned time zero, pre-specified confounders and an estimand that distinguishes offering the programme from actually attending sessions.

The action should target a modifiable condition supported by the estimate. Penalising a patient for non-attendance would not follow from evidence that transport support improves attendance.

10.2. Practical scenario: an unavailable medicine

A stockout creates a sequence—prescription, failed dispensing, substitution or delay, outcome—but the sequence alone does not identify the effect of unavailability. Stockouts may coincide with holidays, staffing shortages, supply disruptions, disease surges or changes in case mix. Clinicians may reserve remaining stock for the sickest patients.

The intervention should be defined as a supply policy, not as the mere recorded absence of a product. Depending on scale and timing, a controlled interrupted time series, difference-in-differences analysis, stepped implementation or valid natural experiment may be possible. Difference-in-differences requires a credible comparison group and a defensible counterfactual trend; design and robustness checks matter more than the label (DOI 10.1146/annurev-publhealth-040617-013507, PMID 29328877). A proposed instrument such as formulary preference is useful only if it affects the outcome through treatment received, is not associated with unmeasured outcome causes and satisfies the other instrumental-variable assumptions. Those conditions are substantive and often contestable.

10.3. Practical scenario: an organisational gap

A delayed referral may involve a missing order, queue rules, handoff failure, staffing, software defaults and patient communication. Searching for a single root cause can hide these interactions.

The WHO guidance on incident reporting and learning systems (ISBN 978-92-4-001033-8) warns that incident-report data have strengths and limitations and should be interpreted cautiously. The current NHS Patient Safety Incident Response Framework explicitly promotes system-based learning rather than simplistic linear identification of a single cause. The clinical systems tradition is also described by Vincent, Taylor-Adams and Stanhope (DOI 10.1136/bmj.316.7138.1154, PMID 9552960) and the SEIPS work-system model (DOI 10.1136/qshc.2005.015842, PMID 17142610).

Incident analysis should therefore produce a testable intervention—such as automatic escalation after a queue threshold—and then evaluate whether it reduces delay and harm. Narrative plausibility is the beginning of improvement, not the final evidence of effect.

11. Counterarguments and their limits

“Only randomized trials can support causal claims.” Randomization is the preferred design for many intervention questions because it protects against baseline confounding. But trials may be unethical or impossible, may not cover rare or delayed harms, and may poorly represent routine care. Well-designed observational studies can supply the best available evidence when their causal question and assumptions are explicit. The answer is not to treat all observational associations as causal, nor to ban causal questions from observational research; it is to judge whether a causal interpretation is tenable. A 2024 JAMA framework proposes six core questions for doing so (DOI 10.1001/jama.2024.7741, PMID 38722735).

“Enough data and machine learning will discover the causes.” More observations reduce random error; they do not automatically remove confounding, selection bias or systematic measurement error. Prediction estimates (P(Y\mid X)); intervention questions require a counterfactual quantity such as (P(Y\mid do(A=a))) or its potential-outcome equivalent. A highly accurate risk model can be unsafe as a treatment-effect model.

“A DAG is subjective.” It is. That is a reason to expose, version and challenge its assumptions, not to leave the same assumptions hidden inside feature selection and regression code. Agreement among experts does not make a graph true, so sensitivity analyses and external evidence remain necessary.

“Root-cause analysis already solves this.” Incident-learning methods and causal-effect estimation overlap but answer different questions. A contributory-factor map can guide interventions; only subsequent comparison under a defined design estimates whether the intervention changes outcomes.

“Personalised causal AI tells us what will work for one patient.” Heterogeneous treatment-effect estimates are usually conditional averages for groups with similar measured characteristics. They are not direct observations of both potential outcomes for one person. Individual recommendations require calibration, uncertainty, applicability checks, prospective validation and clinical oversight.

Person-level variation and group-level effect modification must also be distinguished. A subgroup can have a different average effect without every member benefiting, and the subgroup contrast can change with the effect scale. The same patient can belong to several defensible “reference classes” that yield different estimates. Dahabreh, Hayward and Kent explain these limits of applying group evidence to individuals (DOI 10.1093/ije/dyw125, PMID 27864403). A recent review of machine learning for heterogeneous treatment effects reaches the same design-first boundary: flexible estimation does not remove the counterfactual problem or identification assumptions (DOI 10.1146/annurev-biodatasci-103123-095750, PMID 40203240). Operationally, a system should report the target population, effect scale, subgroup rule, uncertainty and evidence that the rule improves outcomes when used—not label an unstable conditional mean as an individual truth.

12. Risks of operational causal systems

A causal decision-support system can cause harm even when its statistics are sophisticated.

  • Confounding by indication: sicker patients receive more intensive treatment, making effective care appear harmful.
  • Selection and collider bias: conditioning on referral, testing, survival or complete records can create spurious paths.
  • Time-related bias: treatment classification uses information that was unavailable at time zero.
  • Informative observation: people are measured more often because they are unwell; “missing” does not mean “normal.”
  • Coding drift: a code, device or workflow changes meaning across sites or time.
  • Treatment variation: the same label hides differences in dose, operator, timing or co-interventions.
  • Feedback loops: a model changes clinician behaviour, which changes the data used to update the model.
  • Automation bias: a causal label appears more authoritative than the evidence warrants.
  • Inequity: poor access can be misread as poor adherence; historical allocation can be reproduced as a recommendation.
  • Privacy and function creep: linking detailed timelines increases re-identification and secondary-use risk.
  • Liability and governance gaps: no one owns graph approval, monitoring, overrides, incident review or retirement.

If the system influences diagnosis or treatment, its intended use and jurisdiction determine the applicable clinical, software and medical-device controls. ISO 14971:2019 specifies a lifecycle process for medical-device risk management, including software as a medical device, but it is not a causal-inference standard and does not validate clinical claims.

13. Minimum governance for implementation

A deployable system should have:

  1. a registered causal question, protocol, estimand and analysis plan;
  2. a version-controlled DAG, data dictionary and rationale for each adjustment variable;
  3. immutable or reconstructable event provenance, with occurrence and recording times separated;
  4. documented data fitness, missingness, linkage quality and known site differences;
  5. independent clinical, epidemiological, statistical, safety, privacy and patient review;
  6. external validation and prospective evaluation at the point of intended use;
  7. calibrated uncertainty and an explicit “insufficient evidence” state;
  8. human-readable evidence paths, without presenting a path as proof;
  9. monitoring for drift, subgroup performance, overrides, adverse outcomes and feedback effects;
  10. a change-control, rollback and retirement process.

For studies based on routine health data, reporting should follow the relevant guideline: STROBE for observational studies (PMID 18064739), RECORD for routinely collected health data (PMID 26440803), TARGET for explicit target-trial emulations, and ROBINS-I when assessing risk of bias in non-randomized studies of interventions. Reporting guidelines improve transparency; they do not turn a weak design into a strong one.

Regulatory evidence has additional requirements. The FDA’s final July 2024 guidance, Real-World Data: Assessing Electronic Health Records and Medical Claims Data to Support Regulatory Decision-Making (docket FDA-2020-D-2307), addresses data relevance and reliability for drug and biological-product decisions. The EMA’s current real-world evidence guidance page recommends target-trial emulation as one strategy for non-interventional studies with causal objectives while noting that it is not mandatory and does not fit every design.

The final 2025 ICH M14 guideline now provides harmonised principles for planning, designing, analysing and reporting non-interventional studies that use fit-for-use real-world data for post-marketing medicine-safety assessment. It explicitly covers data-source suitability, selection, information and time-related bias, confounding, variable validation, quality control, sensitivity analyses and documentation. Its scope is narrower than “all causal AI”: treatment-assignment studies and several other study types are excluded, and the guideline says it does not address AI methods. Its principles may inform other RWD studies, but compliance with M14 does not validate an effectiveness claim outside its scope.

For clinical software, standards must be matched to the claim and lifecycle stage. The final IMDRF/SaMD WG/N41FINAL:2017 framework concerns clinical evaluation of software as a medical device. The peer-reviewed DECIDE-AI guideline focuses on transparent reporting of early-stage clinical evaluation, including actual clinical performance, safety and human factors (DOI 10.1136/bmj-2022-070904, PMID 35584845). The NICE Evidence Standards Framework ECD7 stratifies evidence expectations for digital health technologies by intended purpose and risk and includes AI, adaptive algorithms and early deployment within evidence-generation programmes. For a prediction component, TRIPOD+AI supplies reporting guidance (DOI 10.1136/bmj-2023-078378); it does not convert prediction into causal effect estimation and is not itself a risk-of-bias tool. None of these documents substitutes for the applicable law, regulator, prospective clinical evaluation or post-deployment surveillance.

Prospective trials involving AI need protocol and report detail beyond a generic algorithm label. SPIRIT-AI adds protocol items for the intervention, inputs, outputs, required user expertise, human–AI interaction and error handling (DOI 10.1038/s41591-020-1037-7, PMID 32908284); CONSORT-AI adds corresponding reporting items for completed randomized trials, including integration context and error-case analysis (DOI 10.1038/s41591-020-1034-x, PMID 32908283). They improve transparency, not efficacy by declaration: the trial still needs an appropriate comparator, clinically meaningful outcomes, enough power, and analysis of workflow and downstream harms.

Regulatory classification is a separate question. The FDA’s final January 2026 Clinical Decision Support Software guidance (docket FDA-2017-D-6569) explains when certain professional-facing CDS functions may satisfy the US statutory exclusion from the device definition; it is not a universal exemption for anything called “decision support.” Among other conditions, the healthcare professional must be able to independently review the basis of a recommendation rather than rely primarily on it. For AI-enabled devices intended to change over time, the final August 2025 Predetermined Change Control Plan guidance (docket FDA-2022-D-2628) describes an optional marketing-submission mechanism covering planned modifications, their development and validation method, and impact assessment. By contrast, FDA’s broader January 2025 AI-device lifecycle document remains explicitly draft and not for implementation as of this source check. These US classifications do not determine status in another jurisdiction and do not replace causal or clinical validation.

14. Conclusion

Event-based medicine becomes causally useful when it does more than draw arrows between timestamps. It must preserve what happened, when, to whom, under which decision, from which source and with what uncertainty. On top of that record, causal analysis must define an intervention and comparator, align time zero, make assumptions explicit, choose a design that approximates the missing counterfactual and test how fragile the result is.

The practical promise is substantial: distinguish treatment failure from access failure, identify modifiable system conditions, evaluate dynamic care strategies and learn from routine practice. The boundary is equally important: a coherent story, a causal graph, a patent claim or a high-performing model is not proof. The responsible output is not “the system found the cause,” but “under these stated assumptions and this design, changing this factor is estimated to change this outcome by this amount, with these uncertainties.”

References / Список литературы

The list below is separate from the article body and records the sources used to substantiate its methodological, regulatory and technical claims. Links resolve to the primary publication, PubMed record, standards body, regulator or patent document wherever available. / Приведённый ниже список отделён от основного текста и фиксирует источники методологических, регуляторных и технических утверждений. По возможности ссылки ведут непосредственно на публикацию, запись PubMed, орган стандартизации, регулятора или патентный документ.

Peer-reviewed publications and open scholarly resources / Рецензируемые публикации и открытые научные материалы

Topic Primary source Identifier
Practical causal reasoning Hill AB. The Environment and Disease: Association or Causation? DOI 10.1177/003591576505800503; PMID 14283879
Causal diagrams in epidemiology Greenland S, Pearl J, Robins JM. Causal diagrams for epidemiologic research. DOI 10.1097/00001648-199901000-00008; PMID 9888278
Causal-discovery method families Glymour C, Zhang K, Spirtes P. Review of Causal Discovery Methods Based on Graphical Models. DOI 10.3389/fgene.2019.00524; PMID 31214249
Potential outcomes and causal methods Hernán MA, Robins JM. Causal Inference: What If (open author-hosted book). Official open book page
Target-trial framework Hernán MA, Robins JM. Using Big Data to Emulate a Target Trial When a Randomized Trial Is Not Available. DOI 10.1093/aje/kwv254; PMID 26994063
Target-trial reporting Cashin AG et al. Transparent reporting of observational studies emulating a target trial: the TARGET Statement. DOI 10.1136/bmj-2025-087179; BMJ full text
Modern causal language in medical journals Dahabreh IJ, Bibbins-Domingo K. Causal Inference About the Effects of Interventions From Observational Studies in Medical Journals. DOI 10.1001/jama.2024.7741; PMID 38722735
Mediation and mechanisms VanderWeele TJ. Mediation Analysis: A Practitioner’s Guide. DOI 10.1146/annurev-publhealth-032315-021402; PMID 26653405
Interference and spillovers Hudgens MG, Halloran ME. Toward Causal Inference With Interference. DOI 10.1198/016214508000000292; PMID 19081744
Failure-time estimands with competing events Young JG, Stensrud MJ, Tchetgen Tchetgen EJ, Hernán MA. A causal framework for classical statistical estimands in failure-time settings with competing events. DOI 10.1002/sim.8471; PMID 31957017
Time-varying confounding Robins JM, Hernán MA, Brumback B. Marginal structural models and causal inference in epidemiology. DOI 10.1097/00001648-200009000-00011; PMID 10955408
g-methods tutorial Naimi AI, Cole SR, Kennedy EH. An introduction to g methods. DOI 10.1093/ije/dyw323; PMID 28039382
Dynamic treatment regimes Chakraborty B, Murphy SA. Dynamic Treatment Regimes. DOI 10.1146/annurev-statistics-022513-115553; PMID 25401119
Micro-randomized trials Liao P, Klasnja P, Tewari A, Murphy SA. Sample size calculations for micro-randomized trials in mHealth. DOI 10.1002/sim.6847; PMID 26707831
Interpretation of adjusted coefficients Westreich D, Greenland S. The table 2 fallacy: presenting and interpreting confounder and modifier coefficients. DOI 10.1093/aje/kws412; PMID 23371353
Informative presence in EHR data Harton J, Mitra N, Hubbard RA. Informative presence bias in analyses of electronic health records-derived data: a cautionary note. DOI 10.1093/jamia/ocac050; PMID 35438796
Transportability and effect scale Dahabreh IJ, Robertson SE, Steingrimsson JA. Learning about treatment effects in a new target population under transportability assumptions for relative effect measures. DOI 10.1007/s10654-023-01067-4; PMID 38724763
Group evidence and individual decisions Dahabreh IJ, Hayward R, Kent DM. Using group data to treat individuals: understanding heterogeneous treatment effects in the age of precision medicine and patient-centred evidence. DOI 10.1093/ije/dyw125; PMID 27864403
Machine learning and heterogeneous treatment effects Abécassis J, Dumas É, Alberge J, Varoquaux G. From Prediction to Prescription: Machine Learning and Causal Inference for the Heterogeneous Treatment Effect. DOI 10.1146/annurev-biodatasci-103123-095750; PMID 40203240
Negative controls Lipsitch M, Tchetgen Tchetgen E, Cohen T. Negative controls: a tool for detecting confounding and bias in observational studies. DOI 10.1097/EDE.0b013e3181d61eeb; PMID 20335814
Sensitivity to unmeasured confounding VanderWeele TJ, Ding P. Sensitivity Analysis in Observational Research: Introducing the E-Value. DOI 10.7326/M16-2607; PMID 28693043
Immortal-time bias Suissa S. Immortal time bias in pharmaco-epidemiology. DOI 10.1093/aje/kwm324; PMID 18056625
Interrupted time series Bernal JL, Cummins S, Gasparrini A. Interrupted time series regression for the evaluation of public health interventions: a tutorial. DOI 10.1093/ije/dyw098; PMID 27283160
Difference-in-differences Wing C, Simon K, Bello-Gomez RA. Designing Difference in Difference Studies: Best Practices for Public Health Policy Research. DOI 10.1146/annurev-publhealth-040617-013507; PMID 29328877
N-of-1 reporting Vohra S et al. CONSORT extension for reporting N-of-1 trials (CENT) 2015 Statement. DOI 10.1016/j.jclinepi.2015.05.004; PMID 26272792
Systems analysis of clinical incidents Vincent C, Taylor-Adams S, Stanhope N. Framework for analysing risk and safety in clinical medicine. DOI 10.1136/bmj.316.7138.1154; PMID 9552960
Work-system model for safety Carayon P et al. Work system design for patient safety: the SEIPS model. DOI 10.1136/qshc.2005.015842; PMID 17142610
Observational-study reporting von Elm E et al. The STROBE statement. DOI 10.1016/S0140-6736(07)61602-X; PMID 18064739
Routinely collected data reporting Benchimol EI et al. The RECORD statement. DOI 10.1371/journal.pmed.1001885; PMID 26440803
Risk of bias in non-randomized studies Sterne JAC et al. ROBINS-I. DOI 10.1136/bmj.i4919; BMJ full text
Early clinical evaluation of AI decision support Vasey B et al.; DECIDE-AI expert group. Reporting guideline for the early stage clinical evaluation of decision support systems driven by artificial intelligence: DECIDE-AI. DOI 10.1136/bmj-2022-070904; PMID 35584845
Reporting clinical prediction models Collins GS et al. TRIPOD+AI statement: updated guidance for reporting clinical prediction models that use regression or machine learning methods. DOI 10.1136/bmj-2023-078378; PMID 38626948; BMJ full text
AI trial protocols Cruz Rivera S et al. Guidelines for clinical trial protocols for interventions involving artificial intelligence: the SPIRIT-AI extension. DOI 10.1038/s41591-020-1037-7; PMID 32908284
AI randomized-trial reports Liu X et al. Reporting guidelines for clinical trial reports for interventions involving artificial intelligence: the CONSORT-AI extension. DOI 10.1038/s41591-020-1034-x; PMID 32908283

Official standards and guidance / Официальные стандарты и руководства

Scope Source Stable identifier or link
Estimands and intercurrent events International Council for Harmonisation, ICH E9(R1) Official Step 4 guideline PDF
Good Clinical Practice and data integrity International Council for Harmonisation, ICH E6(R3) Official Step 4 guideline PDF
Non-interventional RWD studies for medicine-safety assessment International Council for Harmonisation, ICH M14, Step 4, 2025 Official final guideline PDF
EHR and claims data for regulatory decisions US FDA, final Level 1 guidance, July 2024 FDA guidance; docket FDA-2020-D-2307
US clinical decision-support software classification US FDA, final guidance, January 2026 FDA guidance; docket FDA-2017-D-6569
Planned modifications to AI-enabled device software US FDA, final guidance, August 2025 FDA guidance; docket FDA-2022-D-2628
Non-interventional real-world evidence European Medicines Agency EMA real-world evidence guidance hub
Incident reporting and learning World Health Organization, 2020 WHO publication; ISBN 978-92-4-001033-8
System-based incident response NHS England, PSIRF, published 2022; updated 2025 Official framework
Health data provenance HL7 FHIR R5 Provenance; AuditEvent
Medical-device lifecycle risk ISO 14971:2019, edition 3 Official ISO record
Clinical evaluation of software as a medical device International Medical Device Regulators Forum, IMDRF/SaMD WG/N41FINAL:2017 Official final technical document
Evidence for digital health technologies NICE Evidence Standards Framework, ECD7, published 2018; updated 2022 Official NICE framework; ISBN 978-1-4731-4117-9

Relevant patent documents / Релевантные патентные документы

Patent documents are included because the requested research scope asks for them and because they show concrete claimed implementations. They are not peer-reviewed clinical evidence, proof of validity, a freedom-to-operate opinion or a complete patent landscape. Status labels below were checked on the linked public records on 2026-07-29; formal legal status should be rechecked in the relevant patent office before reliance.

  1. Bayesian causal inference using real-world patient data. US20220093271A1, application US17/310,176, priority 2019-01-25; later grant US12444507B2, published 2025-10-14. The claims describe Bayesian marginal structural models combining matching, weighting and estimation for treatment comparisons.
  2. Personalised intervention recommendations from individual time series. US20240047042A1, application US18/365,899, priority 2022-08-05, listed as pending; assignee shown as Evidation Health, Inc. The application describes “model-twin randomization” and estimation of an average treatment effect from health-behaviour and health-condition time series.
  3. Causal discovery and inferencing for medical systems. US20250285766A1, application US19/074,278, priority 2024-03-11, listed as pending; assignee shown as Auris Health, Inc. The application maps procedure telemetry and clinical metrics to a DAG and includes claimed uses for inferences, simulated trials and root-cause identification.
  4. International family publication for item 1: WO2020154573A1, PCT/US2020/014912.
  5. Adverse-drug-reaction signal discovery from EHR data. US20240145059A1, application US18/364,470, priority 2022-11-02, published 2024-05-02; Google Patents lists the US application as abandoned. The document claims construction of a Bayesian network, selection of proposed confounders and propensity-score matching for a drug–adverse-event comparison. Its language that matched group differences thereby have causal significance illustrates precisely why patent claims must not be treated as validation of exchangeability or completeness of confounder measurement.
  6. Causal-effect estimation from knowledge graphs. US12444503B2, application US17/731,590, priority 2021-05-14, granted and published 2025-10-14; public record lists Accenture Global Solutions Ltd as assignee and the patent as active. The disclosure uses knowledge-graph representations and neural architectures for subgroup treatment-effect estimation in healthcare examples while explicitly assuming no hidden confounding and a structural causal model. Those assumptions remain scientific conditions, not consequences of the graph representation.