Mohan W. Gupta

See attached file(s)

Public Comment: From Monitoring Plans to
Actionable Evidence for Generative AI-Enabled
Medical Devices
Docket No.: FDA-2026-N-7874​
Re: Considerations for the Regulation of Generative AI-Enabled Medical Devices​
Submitted to: Food and Drug Administration, Center for Devices and Radiological Health​
Submitted by: 1Mohan W. Gupta, PhD; 1Miguel Pinero-Jacome; 2Michael Kabbash, MD;
Michael Siegel, MD ​
Affiliation: 1Princeton University, 2University of Florida, 3Tufts University​
Capacity: Individual submission​
Questions addressed: 10, 18, 19, and 21​
Date: October 19th, 2026

Executive Summary
We appreciate the opportunity to comment on the Center for Devices and Radiological
Health's (CDRH's) discussion paper on generative AI (GenAI)-enabled medical devices.

Our central finding is that existing evaluations often identify potential clinical risks
without providing the evidence needed to determine how those risks affect patients after
deployment. AI clinical documentation systems, commonly called AI scribes, illustrate
this problem. Recent meta-analyses suggest that these systems can reduce
documentation burden, although the magnitude and generalizability of those benefits
remain uncertain [2,3]. Meanwhile, a clinical pilot identified 19 of 356 reviewed
AI-generated drafts as posing serious potential harm if left uncorrected [7]. Such
findings establish important potential failure modes, but not how frequently errors
survive clinician review, influence clinical decisions, or cause additional harm relative to
conventional documentation.

To examine this gap, we conducted an evidence-coverage assessment of 102 acquired
AI-scribe reports, provisionally representing 100 study units across real-world
evaluations, simulations, and benchmarks. Among 56 real-world-related units, 15
contained clinician-editing evidence, including some comparisons between generated
drafts and finalized notes. Although several studies examine how clinicians edit
AI-generated documentation, our assessment did not identify a published, clinically
adjudicated estimate of how frequently errors in AI-generated patient notes are
corrected before finalization. Studies linking source transcripts, AI drafts, and finalized
notes demonstrate that such measurements are feasible, but additional clinical
validation is needed to distinguish genuine error corrections from other edits [15-17].
Similarly, available severity and downstream measures generally concerned potential
harm, clinician perceptions, or clinical processes rather than actual measured patient
injury. These gaps matter because detecting an AI-generated error is not equivalent to
estimating its clinical consequences.
We therefore recommend that CDRH adopt a risk-specific monitoring adequacy
standard when considering greater reliance on postmarket evidence. For each
consequential unresolved risk, manufacturers should demonstrate how monitoring will
detect failures, produce sufficiently reliable evidence about their frequency and
consequences, and inform prespecified safety decisions. Monitoring capability should
be independently verifiable, and corrective action must be feasible before unacceptable
harm occurs.

Although not all AI scribes are FDA-regulated medical devices, they provide a concrete
case study of a broader regulatory challenge: postmarket monitoring should be judged
by the safety-relevant uncertainty it can resolve.

1. What Existing Evidence Tells Us About AI-Scribe
Benefits and Clinical Risks
AI scribes are a useful case study for evaluating the safety of generative AI in
healthcare. They are already deployed in clinical settings, have a growing body of
empirical research, and produce documentation that can be examined before and after
clinician review. This allows us to investigate both how these systems perform and
whether existing evaluations provide the evidence needed to assess their clinical risks.
Recent systematic reviews suggest that AI scribes can reduce documentation burden.
Zhao and colleagues synthesized 23 studies and reported reductions in
documentation-related burden (standardized mean difference [SMD] = −0.71) and
broadly defined time outcomes (SMD = −0.72), although heterogeneity was substantial
(I² = 75% and 93%, respectively) [2]. Gong and colleagues likewise reported
improvements in some measures of clinician workload and exhaustion, but most of their
individual meta-analyses included only two or three studies [3].
Evidence concerning clinical risks is less developed. Coiera and Fraile-Navarro have
argued that evaluations must move beyond efficiency to assess clinically meaningful
errors and patient harms [4]. Sorin and Klang further emphasize that errors in finalized
notes may influence subsequent clinical documentation and decisions [5]. These
concerns are supported by empirical observations. For example, a UC Davis pilot
identified omissions in 64 of 356 reviewed AI-generated drafts, with 19 drafts rated as
posing serious potential harm if left uncorrected [7]. However, these findings do not
establish how often errors persisted after clinician review, caused patient harm, or
occurred relative to conventional clinical documentation.
To examine this evidence gap, we conducted a structured evidence-coverage
assessment of 102 acquired reports, provisionally representing 100 study units: 56
real-world-related evaluations, 15 simulations, 28 benchmarks, and one other (see
Appendix). We used a structured codebook, model-assisted extraction, and targeted
verification against original sources to identify which safety-relevant outcomes were
reported. The reporting-coverage findings below focus on the 56 real-world-related
units.
Our provisional evidence-coverage assessment identified workflow-related evidence in
43 of 56 real-world-related study units (77%), including qualitative and self-reported
measures. In contrast, we identified only one study that reports a clinical error against a
reviewed-note. Fifteen study units contained editing-related evidence, including some
comparisons of generated drafts with finalized notes, but they did not note the
error-interception rate. Studies reporting clinical severity or downstream outcomes
generally assessed potential harm, clinician perceptions, incidents, or clinical processes
rather than systematically measuring patient injuries.
The central limitation is that existing evaluations provide insufficient evidence to
determine how those errors translate into additional clinical risk. Establishing that
relationship requires measuring how often clinically important errors occur, whether they
survive clinician review, how frequently they influence subsequent care or contribute to
patient harm, and how those outcomes compare with conventional documentation.
Several studies have examined clinician editing in greater detail. Akhlaghi and
colleagues compared source transcripts, AI-generated drafts, and finalized clinical notes
[16], while Guo and colleagues classified clinical-content edits across 200 encounters
[17]. In a medical education setting, Talwalkar and colleagues directly measured
whether factual errors were corrected after human review [15]. These studies
demonstrate that aspects of error correction can be measured, but our assessment did
not identify a clinically validated estimate of how frequently errors in AI-generated
patient notes are corrected before finalization.

Together, these findings point to two related challenges: understanding how reliably
controlled evaluations predict performance in clinical settings, and generating the
evidence needed to assess clinical risks after deployment. The following sections
address what benchmarks can establish, when postmarket learning may justify greater
premarket uncertainty, and what monitoring should measure, to support informed safety
decisions.

2. Question 10: What Can Benchmarks Establish
About Clinical Safety?
CDRH asks how manufacturers should demonstrate that benchmark performance
predicts safe and effective clinical use, particularly when benchmarks may be
unrepresentative, contaminated, or developed by the manufacturers themselves [1]. We
recommend that the evidentiary weight assigned to a benchmark depend on what
clinical capability it has been validated to measure and what claims its results can
support.
Kim and Yoon examined 702 clinical evaluations of 85 language models and found only
a moderate correlation between medical question-answering benchmarks and clinical
evaluation performance (Spearman's ρ = 0.59) [9]. Hager and colleagues identified
limitations in clinical decision-making through simulated workflows using real patient
cases [10]. Other research has raised concerns about the construct validity of medical
benchmarks and their ability to establish deployment readiness [11,12].
Our AI-scribe evidence assessment illustrates why the choice of evaluation measures
matters. Controlled evaluations measure outcomes ranging from textual similarity and
documentation completeness to clinically rated errors and potential harm, while
real-world studies also examine documentation time, clinician workload, and clinical
note quality. Our exploratory reanalysis of Zhao and colleagues [2] found that estimated
differences between simulated and real-world documentation-time outcomes were
sensitive to which tasks were included, although neither comparison established a
reliable difference between settings (see Appendix). These findings underscore the
importance of evaluating whether measures are clinically comparable and support the
same safety claims. For example, a benchmark showing that an AI system produces
notes similar to a reference document does not establish how often it omits clinically
important medication information, whether clinicians detect those omissions, or whether
errors persist in the medical record.

We support CDRH's proposed combination of competency-based benchmarking and
clinical confirmation. To strengthen this approach, we recommend three expectations for
benchmarks used to support regulatory decisions:

1.​ Define and validate the clinical capability being measured. Manufacturers
should identify the specific competency or failure mode each benchmark
measures, explain how its scoring method captures that construct, and provide
evidence supporting that interpretation. Benchmarks used to support clinical
safety claims should measure clinically relevant errors and consequences rather
than relying exclusively on general similarity or quality scores.
2.​ Establish independent, prespecified performance standards. Evaluation
methods, clinically justified acceptance criteria, and relevant comparison groups
should be defined before testing. Results should include uncertainty and
performance across relevant patient populations and clinical conditions.
Manufacturer-developed benchmarks should be subject to particular scrutiny,
including independent evaluation, protected test cases where appropriate, and
disclosure of benchmark selection and prior optimization. This would reduce the
risk of developers selecting or designing tests that make their systems appear
safer or more effective than they are.
3.​ Confirm safety-critical performance under clinically representative
conditions. When a safety claim depends on clinician interaction or the clinical
workflow, testing should examine the complete system rather than isolated model
outputs. For AI scribes, this could involve clinicians using the system on
representative cases while researchers measure errors in generated drafts,
whether those errors are corrected, and what remains in the finalized notes.
Depending on device risk, retrospective clinical adjudication, realistic simulations,
shadow deployment, or prospective clinical studies may provide appropriate
evidence. Higher-risk claims should generally require stronger clinical
confirmation.

Finally, manufacturers should identify corresponding clinical outcomes that can be
monitored in practice and evaluate whether benchmark results predict those outcomes.
Where that relationship remains uncertain, FDA should treat benchmark scores as
evidence of performance under tested conditions rather than established evidence of
clinical safety. This would connect premarket evaluation to the postmarket monitoring
requirements discussed below.

3. Question 18: When Can Postmarket Monitoring
Justify Greater Premarket Uncertainty?
CDRH asks whether stronger postmarket monitoring could justify accepting greater
uncertainty about a device's benefits and risks before deployment. We recommend that
this flexibility be considered only when manufacturers can demonstrate that the
remaining uncertainty can be meaningfully reduced through postmarket evidence, that
the resulting evidence will support specific safety decisions, and that corrective action
can occur before unacceptable harm.

We recommend that CDRH consider requiring a risk-specific monitoring adequacy
assessment as part of the evidence supporting such flexibility. For each important
unresolved risk, manufacturers should establish a clear pathway connecting the
uncertainty, the monitoring method, the evidence it will produce, the safety decision that
evidence will inform, and the corrective action that will follow. Critically, this pathway
should be supported by demonstrated monitoring capability rather than documentation
alone.

We propose four requirements:

1.​ Demonstrate that the risk is measurable. Manufacturers should identify the
clinical failure, its potential severity, and the outcomes that monitoring can reliably
observe. Monitoring methods should be tested against appropriate reference
assessments, including independently reviewed cases, to establish their ability to
detect clinically important failures. Where monitoring relies on indirect measures,
manufacturers should provide evidence connecting those measures to the
underlying clinical risk and identify uncertainties they cannot resolve.
2.​ Demonstrate that monitoring can inform a safety decision. Manufacturers
should establish clinically justified thresholds for unacceptable performance and
show that the proposed sampling and detection methods can distinguish
acceptable from unacceptable risk with sufficient precision. This requires
accounting for failure frequency, severity, detection sensitivity, and statistical
uncertainty. The appropriate sample size should follow from the risk and decision
threshold, rather than a universal monitoring quota. For consequential risks,
independent clinical review should verify the reliability of the monitoring evidence,
including sampling cases that automated systems did not flag.
3.​ Demonstrate that intervention is possible before unacceptable harm.
Manufacturers should compare the expected time required to detect, investigate,
and respond to a failure with the time over which that failure could cause harm. A
monitoring system that identifies a serious problem only after substantial
irreversible harm has occurred cannot adequately compensate for uncertainty
 about that problem before deployment. Manufacturers should establish
prespecified escalation criteria, responsible decision-makers, and corrective
actions, and demonstrate that these responses are operationally feasible.
4.​ Demonstrate that the monitoring pathway remains reliable. Manufacturers
should identify how changes in patient populations, clinical workflows, device
configurations, or underlying models could undermine detection and risk
estimates. They should establish conditions requiring reassessment or intensified
surveillance. Where monitoring supports greater premarket flexibility, its
continued adequacy should be periodically verified, with independent review
proportionate to the potential consequences of failure.

Not all devices or uncertainties are suitable for this approach. This approach may be
appropriate where failures are detectable, consequences are limited or reversible, and
exposure can be controlled through staged deployment or effective human oversight.
Conversely, unresolved risks involving serious or irreversible harm before detection or
intervention should require stronger premarket evidence. Examples include autonomous
medication decisions or emergency triage recommendations that could delay urgent
treatment without reliable opportunities for human verification.

AI scribes illustrate both the value and limits of postmarket learning. For example, an AI
scribe might omit a newly reported medication allergy that has not yet entered the
medical record, inaccurately document that a patient denied symptoms they actually
reported, or fabricate elements of their medical or surgical history. If these errors persist
in the finalized note, they could influence subsequent clinical decisions, potentially
leading to an allergic reaction following an inappropriate prescription or a missed
diagnosis based on inaccurate clinical information. Monitoring should therefore measure
how frequently such errors occur, whether clinicians correct them before finalization,
and whether remaining errors affect subsequent care. Even these measurements would
not necessarily establish the additional risk of patient harm relative to conventional
documentation. Where that relationship cannot be reliably established, additional clinical
research, validated surrogate measures, or stronger premarket safeguards may be
necessary.

The relevant test is whether monitoring provides a demonstrated, independently
verifiable pathway from unresolved risk to actionable evidence and timely intervention.
Where that pathway cannot be established, greater premarket uncertainty should not be
justified by postmarket monitoring alone.

4. Question 19: What Evidence Should Postmarket
Monitoring Produce?
CDRH asks about periodic re-benchmarking, sample-based clinician review,
performance degradation monitoring, and how the frequency and triggers for
reassessment should be determined. We support combining these approaches, but
recommend that monitoring be judged by its demonstrated ability to detect clinically
important failures, estimate their frequency and severity, and support timely safety
decisions.

4.1. Connect monitoring to clinically meaningful outcomes

Postmarket monitoring should begin with the specific clinical risks identified during
premarket evaluation. Manufacturers should establish what evidence is needed to
characterize each risk and how that evidence will inform safety decisions.

Our AI-scribe research illustrates why this matters. We recommend distinguishing three
stages of clinical risk:

1.​ Error occurrence: How frequently does the device produce clinically important
errors, and how severe are they?
2.​ Error interception: When human review is part of the workflow, how often are
those errors identified and corrected before the output is used?
3.​ Clinical consequences: How often do remaining errors influence clinical
decisions or contribute to patient harm, and how do these outcomes compare
with conventional practice?

Each stage requires different evidence. Error occurrence requires clinically meaningful
definitions and valid denominators. Error interception requires tracking identified errors
through clinician review and into finalized records. Clinical consequences require
examining downstream decisions or patient outcomes, although direct attribution of
harm may not always be feasible.

For devices without human review, monitoring should instead measure whether other
safeguards intercept failures or whether those failures directly affect patients. The
monitoring requirements should follow the device's actual pathway to harm.

4.2. Combine monitoring approaches and independently verify their reliability

We recommend three complementary monitoring approaches:

Periodic re-benchmarking. Manufacturers should reassess safety-critical capabilities
and previously identified failure modes against clinically justified performance
thresholds. Protected or refreshed test cases can help limit overfitting. However,
passing a benchmark repeatedly does not establish that performance remains safe
under changing clinical conditions, so results should be evaluated alongside real-world
evidence.

Sample-based clinical review. Qualified clinicians should assess representative
samples of real-world inputs, outputs, and their disposition after human review.
Sampling should include routine and higher-risk cases, with appropriate representation
across patient populations and clinical settings. For AI scribes, reviewers could compare
source encounters, generated drafts, clinician corrections, and finalized notes to
distinguish generated errors from errors that persist into the clinical record.
Performance degradation monitoring. Manufacturers should track changes in
clinically relevant error rates, deployment conditions, patient populations, and device
configurations. Model updates, prompt changes, retrieval-system modifications, and
unexpected performance signals should trigger targeted reassessment when they may
affect clinical safety.

Critically, these monitoring methods must themselves be validated. A low reported error
rate may indicate good device performance, insufficient sampling, or failures that
monitoring does not detect. We recommend independent clinical review of samples that
include cases not flagged by automated monitoring systems. For higher-risk devices,
independent evaluators should verify the sampling procedures, detection performance,
and resulting safety estimates.

Controlled seeded-error audits could supplement this process. Known errors of varying
clinical severity could be introduced into simulated, nonclinical test cases to assess
whether automated detectors and human reviewers identify them. Repeating these
audits could help identify declining detection sensitivity or review fatigue.

Existing research demonstrates that some monitoring measures can be validated at
scale. Garcia-Agundez and colleagues examined clinician editing across 268,379
encounters and reported an 88.9% positive predictive value for identifying clinically
meaningful edits [6]. However, detecting meaningful editing does not establish whether
clinically important errors were identified and corrected, or how frequently errors went
undetected.

Monitoring adequacy must also be evaluated quantitatively. If 300 independent,
representative clinical reviews detect zero errors, the approximate upper 95%
confidence bound on the error rate is still 1%, assuming perfect detection. Imperfect
detection or correlated observations increase uncertainty. Surveillance sample sizes
should therefore reflect clinically justified risk thresholds, expected failure severity, and
demonstrated detection performance rather than universal quotas.

4.3. Establish risk-based surveillance and corrective-action triggers

Monitoring should combine scheduled reassessment with additional reviews triggered
by safety-relevant changes. Surveillance frequency should reflect failure severity and
frequency, detection sensitivity, exposure volume, and the time available to intervene
before harm.

We recommend that CDRH identify common categories of reassessment triggers,
including significant device or configuration updates, increases in clinically important
errors, serious incidents or near misses, declining monitoring sensitivity, and
deployment in new clinical settings or patient populations.

Manufacturers should establish prespecified criteria and timelines for investigation,
intensified monitoring, additional safeguards, software correction, restricted deployment,
or suspension of use. The required response should reflect the potential harm: a serious
error presenting imminent clinical consequences may warrant immediate intervention,
while a gradual increase in lower-severity errors may justify additional sampling and
targeted remediation.

Corrective action should also be independently verifiable. Following an intervention,
manufacturers should demonstrate that the identified failure has been reduced without
introducing new clinically significant problems. The degree of independent
reassessment should reflect the potential consequences of failure.

The objective is a closed evidence-and-response process: detect failures, determine
their clinical significance, intervene when warranted, and verify that the intervention
reduced risk. Where monitoring cannot reliably perform these functions, it should not be
treated as sufficient evidence that the device's remaining risks are adequately
controlled.

5. Question 21: Who Should Collect, Share, and Act on
Postmarket Evidence?
CDRH asks how clinicians, healthcare institutions, professional societies, and other
stakeholders should contribute to postmarket monitoring without diffusing manufacturer
accountability [1]. We recommend separating responsibility for device safety from
responsibility for independently verifying safety evidence. Manufacturers should remain
accountable for applicable regulatory obligations and corrective actions, but should not
have exclusive control over how safety data are sampled, evaluated, or reported.

We recommend the following division of responsibilities:

1.​ Manufacturers and software developers: Maintain accountability and
implement corrective action. The responsible device manufacturer should track
deployed model versions and configurations, investigate safety signals across
sites, and implement necessary corrections or restrictions. Where third-party
developers supply underlying models or software, manufacturers should
establish access to the information and technical controls needed to investigate
failures. Outsourcing these activities should not transfer applicable regulatory
responsibilities.
2.​ Healthcare institutions and clinicians: Generate clinical evidence and
protect patients. Healthcare institutions should contribute information about
device use, identified errors, clinician review, and downstream clinical
consequences. They should retain authority under their clinical governance
processes to restrict or suspend local use when patient safety is threatened.
Clinicians should have protected channels for reporting errors and near misses,
but monitoring should not depend exclusively on voluntary reporting.
3.​ Independent clinical evaluators: Verify monitoring performance. For devices
with consequential unresolved risks, qualified clinician-evaluators independent of
the manufacturer should validate detection methods, review prespecified
 samples of clinical outputs, and assess the reliability of reported safety
estimates. Reviews should include cases that manufacturer-operated monitoring
did not flag. Evaluators should have access to relevant underlying evidence,
conflict-of-interest safeguards, and the ability to communicate serious unresolved
concerns through appropriate reporting channels without manufacturer approval.
4.​ Professional societies and standards-setting bodies: Support consistent
evaluation. These organizations can help establish common error definitions,
clinical-severity classifications, adjudication procedures, and monitoring
performance standards, improving comparability across manufacturers and
institutions.

Manufacturers may fund external assessments, but should not control case selection,
change adjudication criteria after reviewing results, or suppress unfavorable findings.
The required degree of independent verification should be proportionate to the device's
clinical risks.

These arrangements should be established before deployment. Where manufacturers
seek to justify greater premarket uncertainty through postmarket monitoring, CDRH
should consider requiring evidence of data-sharing agreements, independent validation
procedures, escalation channels, and clearly assigned corrective-action responsibilities.
Appropriate privacy safeguards should allow clinical review without unnecessary
disclosure of identifiable patient information.

For devices subject to premarket review, these arrangements could form part of the
risk-specific monitoring adequacy assessment proposed in Question 18. Existing
postmarket mechanisms, including section 522 surveillance orders for qualifying
devices, may provide additional pathways. Broader independent-auditing requirements
would require consideration of FDA's statutory authority.

Conclusion and Recommendations to CDRH
Our evidence assessment of AI scribes illustrates a broader challenge in regulating
GenAI-enabled medical devices. Here, we showcased that even if errors can be
identified, this does not necessarily establish how often those errors reach patients or
what clinical consequences follow. Postmarket monitoring can help resolve these
uncertainties, but only when it generates reliable evidence that can inform timely safety
decisions.

We recommend that CDRH establish risk-specific monitoring adequacy assessments as
a central component of its approach to postmarket surveillance, particularly when
manufacturers seek to justify greater premarket uncertainty through postmarket
evidence.

These assessments should demonstrate the following:

1.​ Measurable safety risks. Manufacturers should identify consequential failure
modes and demonstrate how monitoring will detect them, estimate their
 frequency and clinical significance, and account for relevant device versions and
deployment conditions.
2.​ Independent verification. For consequential unresolved risks, monitoring
methods and findings should be subject to risk-proportionate independent
assessment. Manufacturers should not control external case selection, alter
adjudication criteria after examining results, or suppress unfavorable findings.
3.​ Clear responsibilities and access to evidence. Monitoring arrangements
should establish data-sharing agreements, independent validation procedures,
and responsibilities for collecting, reviewing, and investigating safety evidence.
Appropriate privacy safeguards should enable clinical review without
unnecessary disclosure of identifiable patient information.
4.​ Prespecified intervention and corrective action. Manufacturers should identify
which findings trigger investigation, escalation, deployment restrictions, or other
corrective measures, who is authorized to act, and how the effectiveness of
interventions will be verified. Monitoring should demonstrate that intervention can
occur before unacceptable harm.

These requirements should form a unified assessment of monitoring adequacy, rather
than separate procedural commitments. CDRH should clarify how existing authorities,
including Section 522 surveillance orders for qualifying devices, can support these
expectations and identify any remaining gaps requiring additional authority.

Where monitoring cannot reliably characterize consequential risks or support sufficiently
timely intervention, it should not justify accepting greater premarket uncertainty.

Thus we recommend that postmarket monitoring should be evaluated by whether they
can produce credible evidence about unresolved risks and act on that evidence to
protect patients.

Respectfully submitted,
Mohan W. Gupta, PhD; Miguel Pinero-Jacome; Michael Kabbash, MD; Michael Siegel,
MD
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Appendix
We conducted an evidence-coverage assessment of AI clinical documentation systems,
supplemented by targeted verification of original sources and an exploratory reanalysis of
published meta-analytic estimates. The objective was to assess what existing evaluations
measured, whether their outcomes were comparable across evaluation settings, and whether
they supported inferences about clinically important errors, clinician correction, and downstream
consequences.

A1. Evidence identification and eligibility
A1. Evidence identification and eligibility

The search archive contains PubMed, Scopus, and Web of Science strategies addressing AI
scribes, ambient clinical documentation, conversational clinical data, and automated
documentation generation. Merged exports contained 1,054 records before deduplication and
527 afterward.

We conducted LLM-model-assisted title and abstract screening using a structured,
sensitivity-prioritized rubric. Each record was assessed against five criteria: (1) whether it
described an AI system generating clinical documentation from conversational encounter data,
(2) whether it reported original empirical research, (3) relevance to clinical or healthcare
settings, (4) presence of relevant system-specific outcomes, and (5) eligible publication type.
Studies involving simulated encounters and technical benchmarks were eligible. Records were
excluded only when the available information clearly established ineligibility; ambiguous records
were retained for further assessment.

On August 15, 2026, an automated date prefilter excluded 37 records published before 2022. Of
the remaining 490 records, 182 were classified as advancing and 95 as uncertain but potentially
eligible, yielding 277 records for full-text acquisition. Of these, 129 reports were acquired and
148 remained unacquired because of publisher access restrictions, unavailable retrieval routes,
or unresolved document identification.

Full-text eligibility was assessed using a separate structured rubric covering original empirical
evidence, eligible documentation systems, clinical context, reported outcomes, publication type,
publication date, and English-language availability. This process retained 102 acquired reports,
provisionally representing 100 study units.

A2. Extraction, reconciliation, and units of analysis
Each acquired report underwent three separate model extraction requests using gpt-5.6-sol
through the OpenAI Batch API with low reasoning effort. Requests included the main-paper
PDF, bibliographic title and abstract, eligibility rubric, and a structured 146-field codebook
covering study characteristics, outcomes, effect estimates, monitoring, errors, and extraction
auditing.

All acquired reports were extracted regardless of provisional eligibility classification.
Supplements were not systematically included in the initial extraction; relevant supplements
were examined during subsequent targeted source review.

Schema validation and automated field-level comparisons assessed agreement across
extractions. A separate model-assisted reconciliation step grouped outcome, effect, and error
records, followed by structural checks. Representative records supported by two or three
agreeing extractions were retained where permitted by the analysis rules; unresolved conflicts
remained flagged. Effect sizes and sampling variances were calculated programmatically rather
than accepted as model-generated calculations.

To supplement these automated procedures, we conducted targeted manual checks against
original articles and available supplementary materials. These checks examined whether
extracted findings were supported by the source text, whether outcome definitions and
denominators were interpreted correctly, and whether measures of potential harm, clinician
editing, and observed clinical consequences were appropriately distinguished. Of 51 manually
assessed claims, 35 were narrowly source-verified, 10 remained ambiguous, five conflicted with
the source interpretation, and one measure was not identified in the reviewed report.

These checks were targeted rather than comprehensive. Agreement between model extractions
was treated as consistency, not independent human confirmation, and the full corpus did not
undergo independent human re-extraction or adjudication.

The 100 provisional study units comprised 56 real-world-related, 15 simulation, 28 benchmark,
and one other unit. Reporting units were distinguished from independent clinical cohorts:
multiple models, outcomes, raters, time points, or extraction replicates did not constitute
additional studies. Related publications and possible cohort overlap were flagged, including
companion reports from the UC Davis deployment.

A3. Evidence-coverage definitions and findings
Coverage was assessed at the study-unit level, counting a unit once for each domain with
admissible reported evidence.

The workflow domain included documentation time, total or after-hours electronic health record
time, time to note closure, visit duration, visit volume, and productivity. Quantitative,
self-reported, and qualitative evidence could contribute. A controlled comparator, calculable
effect, statistically significant result, or demonstrated benefit was not required. Workload and
burnout were classified separately.

Editing coverage included editing time, text changes, clinician note contribution, qualitative
accounts, and draft-to-final comparisons.
Clinical error-frequency claims required source-confirmed numerator and denominator
definitions, including whether the numerator counted error instances, notes containing errors, or
responses to a feedback item. Overlapping error categories were not summed into unique
erroneous-note counts.

Severity and downstream measures were distinguished as potential harm, perceived harm,
observed incidents or consequences, clinical-process measures, or systematically collected
patient outcomes.

Evidence-coverage results
Measurement Provisional findings Interpretation
domain

Workflow-related 43/56 study units Includes quantitative, qualitative, and
evidence self-reported evidence; not necessarily
demonstrated efficiency benefits

Errors with 4/56 initially flagged; one of Other flags involved conditional
denominators these source-confirmed with feedback, anecdotal evidence, or
an appropriate reviewed-note unresolved counts; not four validated
denominator clinical-error-rate studies

Clinical severity 3/56 study units Includes potential-harm ratings,
clinician perceptions, and incident
grading; not systematic patient-injury
rates

Downstream 3/56 study units Includes a reported incident, a
clinical outcomes qualitative account, and clinical-process
measures

Clinician-editing 15/56 study units Includes editing proxies and some
evidence draft-to-final comparisons

Clinically validated No complete estimate Does not establish that no study
error interception confirmed in the targeted measured correction or that the
source audit interception rate is zero

These categories differ in their inclusion criteria and should not be interpreted as directly
comparable frequencies of demonstrated benefit and harm. The counts represent provisional
reporting classifications, with targeted rather than exhaustive source verification.

Measuring clinical error correction
We distinguished two related safety outcomes:

Error interception rate: The proportion of independently identified clinical errors in an
AI-generated draft that were corrected before finalization.

Change in error burden: The difference in clinically adjudicated error frequency between the
initial draft and the finalized note.

These outcomes are not equivalent. Clinicians may correct some errors while introducing
others, so a change in the overall error count does not necessarily establish the proportion of
original errors intercepted.

For a clinically verified interception estimate, we required an identified clinical error in an
AI-generated patient note, observation of whether that same error was corrected, and traceable
disposition in the finalized record. Text similarity, mandatory review, editing frequency, or
self-reported corrections alone were insufficient.

Several studies linked drafts with finalized notes, and one additionally compared them with
source transcripts. However, the targeted audit did not confirm a complete clinically validated
interception estimate in the acquired patient-documentation studies. Studies of educational
feedback notes that directly measured factual correction were considered separately because
they did not evaluate patient clinical records [15].

A4. Exploratory comparison of evaluation settings
Published-review analyses were kept separate from the 100-unit coverage census.

For the documentation-time comparison, we transcribed study-level standardized effects and
95% confidence limits from Zhao and colleagues' published forest plot and assigned evaluation
settings using their study-characteristics table [2]. Approximate sampling variances were
recovered from the printed confidence intervals. Within each setting, effects were pooled using
inverse-variance random-effects models with restricted maximum-likelihood estimation of
between-study variance. Rounded published inputs limited exact numerical replication.

We compared the original broad time family of 17 contributors with an exploratory subset of
eight studies measuring per-encounter note-writing time: Cao, Duggan, Owens, Stults, Liu,
Tierney, Barak-Corren, and van Buchem.

The narrower subset excluded binary timely-completion measures, inbox reply writing, total
electronic health record or whole-encounter time, half-day or per-physician aggregates, line
completion, insufficiently specified documentation denominators, and legacy
structured-data-entry protocols. Membership was based on task and outcome definitions, not
effect magnitude or statistical significance. The restriction was exploratory rather than
preregistered.
The setting contrast was defined as the pooled simulated-setting estimate minus the pooled
real-world estimate. Its standard error was calculated from the subgroup-estimate variances,
assuming independence, with normal 95% confidence intervals conditional on the fitted
variances.

Exploratory sensitivity results
Outcome definition Studies Simulation minus real-world SMD
(95% CI)

Documentation burden, broad definition 14 +0.26 (−0.04 to +0.55)

Documentation time, broad definition 17 −0.17 (−0.86 to +0.52)

Documentation time, per-encounter note 8 +0.36 (−0.20 to +0.93)
writing

The broad analyses approximately reproduced Zhao and colleagues' published subgroup
results [2]. The narrower documentation-time analysis changed the direction of the estimated
setting contrast, but its confidence interval remained wide and included zero. The study sets
overlapped, and neither contrast established a reliable difference attributable to evaluation
setting.

A5. Limitations
The main limitations included acquisition and screening restrictions, incomplete independent
eligibility and cohort adjudication, absence of a complete formal risk-of-bias assessment,
heterogeneous reference standards, potential selection of reviewed outputs, and repeated
observations.

The evidence-coverage findings concern published reporting, not necessarily all data collected
in clinical deployment. Neither the coverage assessment nor the exploratory meta-analysis
estimates the incidence of AI-related patient harm or establishes whether simulated evaluations
systematically overestimate or underestimate real-world performance.