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Academy · Research Data Analytics & AI · AI in clinical development

Use Cases of Artificial Intelligence and Machine Learning in Clinical Development: The Evidence

Machine learning in clinical development is applied in four principal areas: protocol and eligibility design, recruitment and prescreening, site selection, and monitoring. The published evidence supporting these applications is uneven. Most of it derives from retrospective or single-centre pilot studies, very little is randomised, and the strongest claims circulate in the areas with the weakest sources. This article distinguishes the four areas according to what has been demonstrated.

Pubrica AcademyWritten by the medical writing and biostatistics teams Reviewed byPubrica biostatistics team Published9 October 2026 Last checked9 October 2026 Reading time14 minutes Sources52 peer-reviewed

Vendors and journals frequently describe AI in clinical development as a single capability. It is instead a set of loosely related applications at very different stages of evidence. Eligibility prescreening is supported by several published comparative studies; site selection by almost none; and pharmacovigilance by a large literature of proposals but few evaluations. For authors of protocols, grant applications or reviews in this area, the essential task is to specify the application concerned, the evidence design that supports it, and the work required to resolve the remaining uncertainty.

Learning objectives

  • The four areas in which machine learning is applied in clinical development, and the state of the evidence in each
  • The outcomes measured by published prescreening and trial-matching studies, and the reasons almost all are retrospective
  • The reasons eligibility criteria are the most promising target in trial design, and the risks of optimising them
  • The requirements of SPIRIT-AI and CONSORT-AI for a protocol and a trial report involving an AI intervention
  • The rationale for DECIDE-AI and the definition of early-stage clinical evaluation of a decision support system
  • The claims in this area that currently lack an evaluative literature and should therefore be avoided

Common misconceptions

  • “AI shortens trials.” No published randomised comparison establishes a reduction in trial duration attributable to a machine learning component. The claim is a projection and should be reported as such.
  • “Prescreening studies show AI outperforms coordinators.” The published studies are predominantly retrospective or pilot evaluations in single systems, several in oncology only. They show feasibility and screening-workload effects; they are not head-to-head trials of recruitment outcomes.
  • “An AI-assisted trial is just a trial with better software.” Where the AI component forms part of the intervention or the eligibility pathway, it alters what the protocol must specify, which is why SPIRIT-AI and CONSORT-AI exist as formal extensions rather than as guidance notes.
  • “Machine learning is already established in pharmacovigilance.” The methodological literature is substantial, but the evaluative literature in the sources available for this article is not. Safety-signal applications should be regarded as an area of active development rather than settled practice.
  • “A synthetic or model-based control arm removes the need for randomisation.” It converts the question into a causal one requiring different assumptions, which must be stated and defended.

Four application areas and the case for considering them separately

Cascini and colleagues, in Frontiers in Public Health, carried out a scoping review of AI-based applications in clinical trials, and Ngayua and colleagues, in Scientometrics, a systematic mapping study of advanced technologies applied to trials. Read side by side, they show a field clustered into a small number of application types with very different maturity: trial and protocol design, participant identification and prescreening, site and feasibility work, and conduct or monitoring 19,26. Kolluri and colleagues, in The AAPS Journal, review the same ground from the pharmaceutical R&D side, and Weissler and colleagues, in Trials, from the evidence-generation side.

These applications do not constitute a single capability. They differ in what the model predicts, who acts on the output, what counts as success, and whether failure is recoverable. A prescreening model that misses an eligible patient costs a recruitment opportunity. A model embedded in an eligibility pathway can change who is enrolled and therefore what the trial measures. A monitoring model that fails without detection can allow a data-quality problem to persist. Discussing them under one heading leads to overclaiming, so the remainder of this page considers them separately.

Two framing papers merit reading before the application literature. Harrer and colleagues, in Trends in Pharmacological Sciences, set out what AI could do for clinical trial design and are reasonably clear about which parts are proposals 44. Getz and Campo, in Nature Reviews Drug Discovery, document the growth in trial design complexity that motivates much of this work — the problem being addressed is genuine, whatever the state of the proposed solutions 50.

Four application areas, and the evidence design that currently supports each

Application areaWhat is typically claimedStrongest published design in the sources hereWhat would settle it
Protocol and eligibility designFewer unnecessary exclusions; faster, broader accrualAnalyses of eligibility criteria against electronic record data; design and perspective papersA prospective comparison of accrual and effect estimation under original versus model-informed criteria
Recruitment and prescreeningMore eligible patients found, with less coordinator timeRetrospective and pilot comparisons against standard screening, mostly in oncology, in single systemsSame-setting, same-period comparison with enrolment and cohort representativeness as outcomes
Site selection and feasibilityBetter-performing sites chosen; fewer non-enrolling sitesIdentified as an application area in scoping and mapping reviews; no comparative evaluation foundTrials whose sites were ranked with and without model assistance, compared on accrual and data quality
Conduct, monitoring and safetyEarlier detection of data-quality and safety problemsDescribed in review literature; primary evaluations not among the sources hereProspective evaluation of whether flagged issues are acted on, and earlier than without the model

Application areas as identified in the scoping review by Cascini and colleagues in Frontiers in Public Health and the systematic mapping study by Ngayua and colleagues in Scientometrics, with the primary studies and reviews listed below. The third and fourth rows record an absence of evaluative studies in this reference pool, not a judgement that none exists anywhere.

Trial and protocol design: eligibility criteria as the principal target

The most credible design application is the one with the clearest mechanism. Weng and Rogers, in Nature, describe how patient data can be used to optimise the selection of eligibility criteria — identifying criteria that exclude large numbers of patients while having little bearing on safety or on the ability to detect an effect 24. This is attractive because the inefficiency is well documented, the data to study it already exist in electronic records, and the output is a human-reviewable list of criteria rather than an opaque recommendation.

It also carries a specific risk that should be addressed in any protocol using it. Loosening a criterion changes the population, and therefore the effect size the trial is powered to detect, the safety profile and the generalisability of the result. The analysis indicates how many patients a criterion excludes; it cannot indicate whether the criterion was protecting the trial’s interpretability. The output should be treated as a prompt for clinical and statistical judgement, the reasoning for each criterion retained or relaxed should be recorded, and that reasoning should be carried into the clinical study protocol.

Beyond eligibility, the design literature is more speculative. Krittanawong and colleagues, in Personalized Medicine, draw lessons from oncology for cardiovascular trials; Delso and colleagues, in Seminars in Nuclear Medicine, give practical guidance on designing AI-driven trials in nuclear medicine; Hariry and colleagues, in Drug Discovery Today, offer a Pharma 4.0 perspective that is explicitly future-oriented; and Schork, in Nature, makes the case for n-of-1 designs that modelling makes more tractable 21,28,47,52. Fountzilas and colleagues’ work on trial design in the precision medicine era is taken up on our page on AI in precision medicine. These papers may be cited as indications of direction; they are not evidence that those directions are effective.

Recruitment and prescreening: the available comparative studies

This is the only area with a cluster of studies that measured something against a comparator, and it is still predominantly retrospective. Haddad and colleagues, in JMIR Medical Informatics, reported a retrospective pilot study of an AI system for cancer clinical trial eligibility screening 25. Beck and colleagues, in JCO Clinical Cancer Informatics, evaluated an eligibility screening tool in a large community cancer centre 31. Alexander and colleagues, in JAMIA Open, assessed a trial matching system in Australian lung cancer patients. Calaprice-Whitty and colleagues, in Therapeutic Innovation and Regulatory Science, compared AI-assisted with standard prescreening across three oncology trials. Vazquez and colleagues, in the Journal of Clinical and Translational Science, took a different angle, using supervised classifiers on a de-identified version of ResearchMatch to estimate the likelihood of a volunteer participating.

Three characteristics of this body of work should be stated in any review of it. First, it is heavily weighted towards oncology, which is relevant because oncology eligibility criteria are unusually structured and unusually dependent on documented molecular and staging data. Second, the designs are retrospective comparisons, pilots and single-system evaluations — appropriate for establishing feasibility, insufficient for establishing that recruitment improves 25,31,34. Third, the outcomes measured are mostly screening-workload and matching-concordance outcomes rather than enrolment, time to full accrual, or the representativeness of who was enrolled.

Yao and colleagues, in the American Heart Journal, are the useful exception in design terms: a rationale-and-design paper for a digital trial using batch enrolment for an AI-guided intervention in undiagnosed atrial fibrillation 27. That is a prospective design in which the role of the AI component is specified in advance, which is the direction in which the field needs to develop. Woo’s feature in Nature gives the field’s own account of where it expects this to go.

Site selection and feasibility: claims without an evaluative literature

Site selection and feasibility forecasting are among the most commonly advertised applications and among the least documented. In the sources available for this page, the scoping and mapping reviews by Cascini and colleagues and by Ngayua and colleagues identify the application area, and the broader reviews by Kolluri and colleagues and Weissler and colleagues discuss it as a use case, but there is no body of comparative evaluation of the kind that exists for prescreening 16,19,26,30.

This absence should be stated plainly rather than obscured with plausible description. The mechanisms proposed — using historical enrolment, site performance and population data to rank candidate sites — are sensible, and the data required exist within sponsors and contract research organisations (CROs). What does not exist, in the published literature drawn on here, is evaluation: a comparison of trials whose sites were selected with and without model assistance, measured on accrual, screen-failure rate, data quality or retention. In a review, this is a gap to be stated; in a grant application, it is an opportunity; in promotional material, it is a claim to be omitted.

Trial conduct, monitoring and safety: the scope of the available evidence

Risk-based monitoring, data-quality anomaly detection and operational forecasting are discussed as application areas in the reviews above, and the underlying techniques — outlier detection in accumulating trial data, forecasting of enrolment and query rates — are not novel. The accurate position is that these are described in the review literature rather than evaluated in it, and a paper that claims demonstrated benefit should be asked for the primary study.

Pharmacovigilance requires a specific caution because the gap between the volume of writing and the volume of evaluation is largest there. Machine learning for safety-signal detection, case triage and literature screening is widely proposed, and the sources available for this page do not include primary evaluations of those applications. A pharmacovigilance section containing specifics that cannot be attributed has therefore not been included. Where such material is required, the appropriate approach is to search the pharmacovigilance methods literature directly rather than rely on a general AI-in-trials review’s summary of it, and to treat any performance figure identified as specific to one signal-detection task on one database. Our periodic safety reporting and risk management plan pages cover the documents those tools would feed.

One cross-cutting point applies to everything in this section. Kelly and colleagues, in BMC Medicine, argue that the obstacles to clinical impact from AI are predominantly in evaluation, integration and monitoring rather than in model performance 48. In a trial-operations context that means the question is rarely whether a model can rank sites or flag anomalies, and almost always whether the people receiving its output change what they do, and whether anyone measured that.

Criteria for evidence of tool effectiveness

Park and colleagues, in JAMIA Open, propose a phased framework for evaluating AI in medicine analogous to the phases of clinical research, and it is the most useful single organising idea for this field 33. Its value is that it prevents a feasibility study from being interpreted as an effectiveness study: each phase has a question, and a result at one phase does not answer the next.

Vasey and colleagues’ DECIDE-AI statement in Nature Medicine addresses the stage that the trials literature had previously omitted. It is a reporting guideline for the early-stage, small-scale clinical evaluation of AI-driven decision support systems — the live-setting work that sits between offline validation and a full comparative trial, covering how the system behaved with real users, the nature of the human–algorithm interaction, what safety issues emerged, and how the implementation was configured 18. Most applications in this page’s four areas have never been studied at that stage, which is why their effect on trial conduct is unknown rather than merely unquantified.

Liu and colleagues’ meta-analysis in The Lancet Digital Health illustrates how strict the comparison condition must be: across the imaging literature they could pool algorithm and clinician performance only for the small subset of studies that had tested both on the same sample 41. The equivalent discipline in clinical development is to compare a model-assisted process with the current process, in the same setting, over the same period — which almost none of the published prescreening work does.

Requirements of SPIRIT-AI and CONSORT-AI

Where an AI component is part of a trial’s intervention or pathway, two extensions govern the write-up. Cruz Rivera and colleagues’ SPIRIT-AI extension in BMJ covers the protocol; Liu and colleagues’ CONSORT-AI extension, also in BMJ, covers the trial report. Both add items that a conventional protocol or report has no place for, and the items are the ones that make an AI-enabled trial reproducible: a clear statement of the intended use and the intended user, the version of the algorithm and whether it changed during the trial, the input data requirements and how poor-quality or out-of-range input was handled, the on-site integration and the human–AI interaction, and an analysis of performance errors 35,38.

These are not formalities. The version question alone determines whether the trial evaluated one intervention or several, and it is routinely unaddressed. Together with DECIDE-AI for the early-stage work, they give a sequence a programme can be planned against. For the general checklist landscape see reporting guidelines, and for registration obligations trial protocol registration.

Formulating defensible use-case claims

The characteristic failure in this literature is a sentence that reports a retrospective concordance result and concludes an operational benefit. A side-by-side comparison of the two versions is instructive, because the difference lies not in length or tone but in whether the reader can determine what was done.

The same discipline applies to grant applications, where the temptation to overstate is strongest. A proposal that states the evidence gap accurately and proposes the study that would close it is more fundable than one that implies the gap is already closed; see grant writing for how that argument is usually structured.

A prescreening result, reported two ways

Concludes beyond the design

An artificial intelligence system was applied to identify patients eligible for our trial portfolio and demonstrated high accuracy against manual screening, showing that AI-based prescreening accelerates recruitment and reduces the burden on study teams.

“High accuracy” against what reference? Coordinator decisions are themselves a fallible standard and no agreement statistic is given.

“Accelerates recruitment” was not measured. No enrolment or timing outcome appears anywhere in the design described.

“Reduces burden” was not measured either — screening time is the obvious outcome and it is absent.

Retrospective application is not prescreening. No patient’s pathway was affected, so the operational claim has no support.

Single centre, three trials, one specialty, with none of those limits visible in the conclusion.

Reports what was done

We retrospectively applied the system to all patients screened for three oncology trials at a single centre over a defined period, with manual coordinator screening as the reference. We report concordance with the coordinator decision, sensitivity and specificity for eligibility with 95% confidence intervals, and the distribution of discordant cases by reason. Screening time was not measured. Because the evaluation was retrospective and no patient was enrolled on the basis of the system’s output, these results establish concordance under the documentation available in this record system; they do not establish an effect on enrolment, time to accrual or coordinator workload, which would require a prospective comparison in the same setting.

The reference standard is named and acknowledged as fallible, so the concordance figure can be interpreted.

What was measured and what was not are both stated, which closes off the two unsupported claims in the first version.

Discordant cases are reported by reason — the most informative element for a reader, and the one that indicates where the system fails.

The retrospective design is named as the limit on inference rather than buried in a limitations paragraph.

The study that would support the operational claim is specified, which makes this paper a step in a programme rather than an endpoint.

The second version makes a narrower claim and is the one a reviewer, a sponsor and a subsequent trial can all use. It also protects the authors: the first version will be cited as evidence that AI prescreening accelerates recruitment, which the study did not show, and such a citation is eventually subject to public correction.

Gaps in current knowledge

The list is short, but it is the most useful part of this page for authors of a review or a discussion section.

  • Whether any of this shortens trials. No randomised comparison in the available literature attributes a change in trial duration to a machine learning component.
  • Whether model-assisted prescreening improves enrolment, as opposed to reducing screening workload or matching records concordantly. The outcome measured is usually not the outcome claimed.
  • Whether AI-assisted site selection works at all. The application is advertised; comparative evaluation in the published literature is absent.
  • Whether eligibility-criteria optimisation preserves interpretability. The analysis identifies restrictive criteria; it cannot identify which ones were protecting the trial.
  • Whether these tools affect who gets enrolled. Models trained on historical enrolment learn historical participation patterns, including their inequities, and representativeness of the resulting cohorts is rarely reported.
  • Whether machine learning improves safety-signal detection in practice. The proposals are numerous; the evaluations in the sources available here are not.

Topol’s review in Nature Medicine and Dart’s shorter piece in Nature Reviews Cancer both frame the general expectation, and Wong and colleagues, in Biostatistics, and Wouters and colleagues, in JAMA, document respectively the attrition and the investment that make the expectation economically attractive 32,45. An attractive prospect is not a demonstrated effect, and in a discussion section this distinction is essential.

Key points

Key points

AI in clinical development does not constitute a single capability but four application areas at very different stages of evidence. Analysis of eligibility criteria has a clear mechanism and a genuine risk of altering what the trial measures. Prescreening is supported by a cluster of published comparisons, almost all retrospective and mostly in oncology, that measure concordance and workload rather than enrolment. Site selection and monitoring are widely promoted but, in this literature, have not been evaluated comparatively. Park and colleagues’ phased framework identifies which question a given study answers; SPIRIT-AI and CONSORT-AI specify what a protocol and report must contain; and DECIDE-AI addresses the early live-setting stage that most of these tools have not reached. Claims should be stated at the level the design supports, with the study that would support a stronger claim identified.

Application to your study

Application to your study

  1. Identify which of the four areas is under discussion in the first paragraph, and keep the areas separate throughout. Most overclaiming in this field arises from a sentence that applies evidence from one area to another.
  2. For every cited application study, record the design in a single term (retrospective, pilot, single-centre, prospective or randomised) before recording its result, and include that term in the text.
  3. Confirm that the outcome measured corresponds to the outcome claimed. Concordance with coordinator decisions is not enrolment, and screening workload is not time to accrual.
  4. When optimising eligibility criteria, document the rationale for each criterion relaxed, including its effect on the population, the powered effect size and generalisability. The analysis cannot supply that judgement.
  5. Use SPIRIT-AI for the protocol and CONSORT-AI for the report where an AI component forms part of the intervention or pathway, and address the algorithm-version question explicitly, since it determines whether one intervention or several were evaluated.
  6. Plan an early clinical evaluation consistent with DECIDE-AI before proposing a comparative trial. Human–algorithm interaction and implementation details are common points of failure for these systems, and they are not observable offline.
  7. Report the representativeness of any cohort a model helped assemble. Models trained on historical enrolment learn historical participation patterns, including their inequities.
  8. Avoid pharmacovigilance performance claims that cannot be attributed to a primary evaluation. Cite the specific signal-detection study and its database, or state that the area is under development.

Frequently asked questions

Four applications, at very different stages of maturity: analysing eligibility criteria against electronic record data to find criteria that exclude many patients for little methodological gain; prescreening and matching patients to open trials; ranking candidate sites for feasibility; and flagging data-quality or operational anomalies during conduct. Cascini and colleagues, in Frontiers in Public Health, and Ngayua and colleagues, in Scientometrics, map this landscape. Prescreening has the most published comparative work, almost all retrospective and heavily weighted towards oncology. Site selection and monitoring are widely offered commercially but, in this literature, lack comparative evaluation. Treating the four as one capability is the principal means by which unsupported claims spread.

The published studies do not establish that, because they mostly did not measure it. Haddad and colleagues in JMIR Medical Informatics, Beck and colleagues in JCO Clinical Cancer Informatics, Alexander and colleagues in JAMIA Open and Calaprice-Whitty and colleagues in Therapeutic Innovation and Regulatory Science report concordance with manual screening, screening-workload effects and matching performance, in retrospective or pilot designs, mostly in oncology and in single systems. Those are feasibility findings. Establishing a recruitment effect requires a prospective comparison of the model-assisted process against the current process in the same setting over the same period, with enrolment and cohort representativeness as outcomes. Yao and colleagues’ digital trial design in the American Heart Journal is a step in that direction.

Cruz Rivera and colleagues’ SPIRIT-AI extension and Liu and colleagues’ CONSORT-AI extension, both in BMJ, add items specific to an AI component: a statement of the intended use and intended user; the algorithm version and whether it changed during the trial; the input data requirements and how poor-quality or out-of-range inputs were handled; how the system was integrated on site and what the human–AI interaction was; whether the output could be overridden and how often it was; and an analysis of performance errors. The version item alone is decisive, because an algorithm that updated mid-trial means more than one intervention was tested under one protocol.

DECIDE-AI, published by Vasey and colleagues in Nature Medicine, covers the stage before a comparative trial: the early-stage, small-scale clinical evaluation of an AI-driven decision support system in a live setting. CONSORT-AI governs the reporting of a completed trial. DECIDE-AI exists because systems that perform well offline frequently fail on contact with real users, real workflows and real data quality, and those failures had gone unreported because no guideline required them to be reported. It covers human–algorithm interaction, implementation configuration, safety and error analysis, and user training. Most applications in clinical development have never been evaluated at this stage, which is why their operational effects are unknown.

It can identify which criteria exclude large numbers of patients without much apparent methodological justification — Weng and Rogers, in Nature, describe the approach — and that is useful. It cannot, however, indicate whether a given criterion was protecting the trial. Relaxing a criterion changes the population, and so changes the effect size the trial is powered for, the expected safety profile and the interpretability of the result. The defensible practice is to treat the model output as a prompt for clinical and statistical review, to record in the protocol the reasoning for each criterion retained or relaxed, and to recheck the power calculation against the revised population rather than the original one.

The methodological and proposal literature is large; the evaluative literature is thinner than the volume of writing suggests, and the sources assembled for this page do not include primary evaluations of safety-signal applications. Performance figures have therefore deliberately not been given. Where this material is required, the appropriate approach is to search the pharmacovigilance methods literature directly rather than rely on a general AI-in-trials review’s summary, and to treat any figure identified as specific to one task on one database — signal detection in spontaneous reports, case triage and literature screening are different problems with different base rates and are not interchangeable.

No published randomised comparison in this literature attributes a reduction in trial duration or cost to a machine learning component, so the claim should be written as a projection rather than a finding. What the literature does document is the problem that makes the projection attractive: Getz and Campo, in Nature Reviews Drug Discovery, on rising trial design complexity; Wong and colleagues, in Biostatistics, on clinical trial success rates and attrition; Wouters and colleagues, in JAMA, on the investment required to bring a medicine to market. Citing those papers to establish the size of the problem is legitimate. Citing them to imply that AI has solved any part of it is not.

The application area should be stated precisely, the strongest published design given rather than the strongest published claim, and the gap then presented as the opportunity the proposal addresses. A sentence of the form “model-assisted prescreening has been evaluated retrospectively in single-centre oncology settings, measuring concordance with coordinator decisions; no prospective comparison of enrolment outcomes has been published, and this proposal supplies one” is both accurate and a stronger case for funding than an implied consensus. Reviewers in this area are now sufficiently familiar with the literature to recognise an overstated premise, and an overstated premise undermines the methods section that follows it.

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Every source above is a peer-reviewed article, a publisher’s record of one, or a standard issued by the body that owns it. Each carries the date it was last read. Where a standard moves, this article is revised rather than left up with a note.

How to cite this article

Pick your referencing style and copy it. Your university or target journal may vary the punctuation — check its guide if it has one.

Pubrica Academy. (2026, October 9). Use Cases of Artificial Intelligence and Machine Learning in Clinical Development: The Evidence. Pubrica. https://pubrica.com/academy/medical-writing/use-cases-of-artificial-intelligence-and-machine-learning-in-clinical-development/

This article is written to be learned from. Cite it if you are referring to what it says; if you are using the evidence behind it, cite the sources listed above instead.

Use-case appraisal grid you can copy

One row should be completed for each application to be cited or proposed. Completing the grid before drafting prevents the commonest error in this field, which is borrowing evidence from one application area to support a claim about another. Any row in which the measured outcome and the claimed outcome differ indicates a sentence that needs rewriting.

AI IN CLINICAL DEVELOPMENT -- USE-CASE APPRAISAL GRID
Project / manuscript: ______________________   Date: ______________

For each application you cite or propose, complete one block.

APPLICATION BLOCK
  Area (circle one):
     protocol & eligibility design / recruitment & prescreening /
     site selection & feasibility / conduct, monitoring & safety
  What the tool predicts or ranks: _________________________________
  Who acts on the output: __________________________________________
  What happens if it is wrong: _____________________________________

  EVIDENCE
  Primary study cited: _____________________________________________
  Design (one word): retrospective / pilot / single-centre /
                     prospective / randomised
  Setting and specialty: ___________________________________________
  Comparator: ______________________________________________________
  Same setting and period as comparator?                   yes / no
  OUTCOME MEASURED: _______________________________________________
  OUTCOME I WANT TO CLAIM: ________________________________________
  Are those the same?                                      yes / no
     -> if no, rewrite the claim to the measured outcome and add
        the design that would support the intended one:
        _______________________________________________________

  POPULATION AND EQUITY
  [ ] Cohort representativeness reported
  [ ] Model trained on historical enrolment?  If so, inequity risk noted
  [ ] Subgroup performance available

  IF THIS IS A TRIAL WITH AN AI COMPONENT
  [ ] SPIRIT-AI used for the protocol
  [ ] CONSORT-AI used for the report
  [ ] DECIDE-AI-level early clinical evaluation done or planned
  Algorithm version: ______________  Changed during study?  yes / no
  Intended use statement: __________________________________________
  Intended user: ___________________________________________________
  Input requirements and handling of poor-quality input:
     _______________________________________________________________
  Override possible? ______  How often overridden? ______
  Error analysis performed?                                yes / no

  IF OPTIMISING ELIGIBILITY CRITERIA
  Criteria flagged as restrictive: _________________________________
  For each, reasoning recorded for relaxing or retaining?   yes / no
  Power recalculated for the revised population?            yes / no
  Safety profile reconsidered for the revised population?   yes / no
  Generalisability statement updated?                       yes / no

CLAIM LEDGER -- things I will NOT write without a primary source
  [ ] "shortens trials" / "reduces timelines"
  [ ] "improves enrolment" (when concordance was measured)
  [ ] "reduces coordinator burden" (when time was not measured)
  [ ] any site-selection performance claim
  [ ] any pharmacovigilance performance figure

Pubrica AcademyWritten and maintained by Pubrica’s subject matter experts. Articles are revised when the underlying standards change, and each article states the date on which it was last reviewed.

How Pubrica can help

Pubrica’s medical writing and regulatory teams construct the evidence table before the narrative, specifying the application area, primary study, design and outcome measured. Pubrica drafts protocols and trial reports according to SPIRIT-AI and CONSORT-AI, plans early clinical evaluations according to DECIDE-AI, and identifies where a draft claims an operational benefit that the cited design cannot support.

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Pubrica can review a draft or protocol and identify which use-case claims the cited evidence can support.

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