Women's Health Advocates

See attached file

Comment to FDA on Generative AI-Enabled Medical Devices
Docket: FDA-2026-N-7874, Regulations.gov
Subject: Considerations for the Regulation of Generative AI-Enabled Medical Devices: Discussion Paper and
Request for Feedback (August 2026)
Comment deadline: October 19, 2026
Submitted by: Women’s Health Technology Coalition within Women’s Health Advocates
Questions addressed: 3, 6, 9

Introduction
The Women's Health Advocates appreciates the opportunity to comment on CDRH's discussion paper.
We are commenting on a narrow set of questions where we believe we can contribute evidence that the
docket is otherwise unlikely to contain.

Our comment makes one central argument. The discussion paper treats subgroup performance (element
R.2) as an element that sponsors would select based on applicability to a device’s intended use and risk
profile. For GenAI-enabled devices with broad, patient-facing intended uses, we recommend treating
subgroup performance testing by sex as presumptively applicable rather than discretionary. The same
reasoning extends to other subgroups that shape how a device performs for the women it serves,
including age and life stage, race and ethnicity, pregnancy status, comorbidities, concurrent medication
use, geography, and socioeconomic factors. We also recommend that escalation assessments account for
the documented tendency of both clinicians and general-purpose models to under-escalate for women.

We offer this comment in support of the Agency’s stated goal of enabling beneficial devices to reach
patients. Evidence of where a device does not perform is what allows a sponsor to scope an intended
use narrowly and defensibly. Without that evidence, reviewers must be cautious.

The Current Baseline for Subgroup Reporting Is Low
A cross-sectional analysis of 903 FDA-cleared AI-enabled devices found that, at the time of clearance,
clinical performance studies were publicly available for roughly half of them, and that fewer than
one-third of those studies, 145 of 505, reported sex-specific subgroup data (JAMA Network Open, 2025).

A more recent systematic analysis of 1,357 cleared AI/ML devices found that 34 were linked to registered
prospective trials, that 9 of those 34 reported any subgroup analysis, and that sex appeared in 5 (PLOS
Digital Health, 2026).

Reporting on other subgroups is weaker still. A scoping review of 692 FDA-authorized AI-enabled devices
found that 3.6% reported race or ethnicity, 99.1% provided no socioeconomic data, and 81.6% did not
report the age of study subjects (Muralidharan et al., npj Digital Medicine, 2024). An analysis of 130
FDA-approved AI devices found that 126 were evaluated only on retrospective data and 93 had no
publicly reported multi-site evaluation (Wu et al., Nature Medicine, 2021, as summarized by the authors
for Stanford HAI).

We note this not as criticism of past clearances but as evidence about what happens when subgroup
evaluation is optional. A competency-based framework that lists R.2 among elements to be chosen
based on applicability will, on this record, produce devices benchmarked without it.

We also note the current distribution of authorized AI-enabled devices by review panel. Of 1,430
authorizations between 1995 and 2025, obstetrics and gynecology accounted for 4, or 0.3%, while
radiology accounted for 76.5% (AuntMinnie summary of Cureus analysis). The general-purpose,
patient-facing GenAI devices discussed in the paper will not fit within that specialty distribution. They
will answer women’s health questions regardless of which panel reviews them.

Question 6: Under-Escalation and Over-Escalation Are not Symmetric by Sex
CDRH asks how manufacturers might characterize and weigh the two directions of escalation error. We
recommend that the weighting account for a documented directional pattern.

Research presented at the 2025 ACM Conference on Fairness, Accountability, and Transparency found
that large language models used for patient message triage made approximately 7% more errors for
female patients and were more likely to recommend that female patients self-manage at home rather
than seek care. This was held even after the researchers removed gender cues from the clinical context
(MIT EECS).
The same research makes a methodological point directly relevant to the discussion paper’s
benchmarking design: errors of this kind, in which a patient with a serious condition is advised to stay
home, are not visible in aggregate accuracy metrics. Evaluation that reports overall performance without
directional analysis will not detect them.

This pattern has a human analog that bears on the choice of comparator discussed in Section V.D.1.
Women aged 18 to 55 presenting to emergency departments with chest pain waited longer to be
evaluated and received a less thorough workup for possible heart attack than men of the same age
(American Heart Association).

A study published in the European Heart Journal – Digital Health tested this directly. Investigators took
50 de-identified cardiovascular notes from the MIMIC-IV database, swapped only the patient’s recorded
gender, and asked GPT-4o to generate differential diagnoses for each version. Diagnostic accuracy
differed significantly in 11 of 50 cases. Female versions were diagnosed less accurately for coronary
artery disease, abdominal aortic aneurysm, and atrial fibrillation, among other conditions (Krieger et al.,
EHJ – Digital Health, 2026).

One finding from that study bears directly on the escalation question CDRH raises. In 36% of the cases
where the gender swap changed the output, the model more often attributed the woman’s symptoms to
anxiety or panic disorder rather than to the correct cardiac condition. The note's clinical content was
identical. Only the recorded gender changed.

We draw the Agency’s attention to this because it is the precise mechanism of under-escalation. A
function that reframes cardiac symptoms as anxiety has not merely produced a less accurate output. It
has produced an output that directs a patient away from care. Under the two-axis framework in Section
IV, that is a shift in activity, not only in accuracy, and we do not believe aggregate accuracy testing would
detect it.

Where the human comparator and the device fail in the same direction, benchmarking a device against
median clinician performance will not surface the failure. We recommend that acceptance criteria for
escalation functions specify sex-based directional performance rather than aggregate agreement with a
clinician panel.

Question 3: Patient-Facing Delivery and The Limits of "Talk to Your Doctor"
CDRH asks whether and when delivering clinical information to patients creates different or higher risk,
and what safeguards might mitigate that risk without underestimating patients' capabilities.

We share the Agency’s concern about medical paternalism, and we want it to be clear that we are not
arguing for restricting patient access to clinical information. Access is a benefit our members work to
expand.

Our concern is narrower. The discussion paper asks whether a patient-facing informational function
becomes less directive when it includes a "talk to your doctor" statement. Our answer is that for
conditions with long diagnostic delays, that statement may carry less protective weight than it appears
to. Across international studies, the average diagnostic delay for endometriosis is roughly 6.8 years,
ranging from 1.5 years in Australia to just over 11 in the United States (Health Care for Women
International, 2024). Directing a patient toward a clinical pathway that has historically taken years to
produce a diagnosis is not the same safeguard as directing a patient toward a pathway that resolves in a
visit.

We recommend evaluating the risk-mitigating weight assigned to referral language rather than assuming
it, and benchmarking under element E.4 to test whether users actually change behavior in response.

Question 9: Missing Elements and Externally Developed Standards
CDRH asks whether the benchmarking structure is adequate, whether elements are missing, and
whether externally developed standards could be leveraged.

We believe relevant external assets exist, and two independent research teams have built them and
reached converging conclusions.

The Women’s Health Benchmark comprises 96 validated model stumps spanning obstetrics and
gynecology, emergency medicine, primary care, oncology, and neurology, organized around eight error
types including missed urgency, outdated guidelines, and dosage errors. Across 13 evaluated models,
failure rates were approximately 60% (Gruber et al., arXiv 2512.17028).

A separate instrument, WHBench, uses 47 expert-crafted scenarios across 10 women’s health topics and
a 23-criterion rubric spanning clinical accuracy, completeness, safety, communication quality, equity, and
uncertainty handling. Across 22 models and 3,102 attempted responses, no model mean exceeded 75%,
and the best reached 72.1% (arXiv 2604.00024). Its authors note that existing general medical
benchmarks lack failure-mode targeting and health equity criteria.

We acknowledge that both are preprints. We offer them as proof of existence, not as an endorsement of
any particular asset. Two teams working independently, with different scenario counts, different rubrics,
and different model sets, found substantial failure rates in the same clinical domain. That convergence is
the relevant signal: it shows that domain-specific evaluation is feasible, that it surfaces failures general
benchmarks miss, and that the construct-validity concerns CDRH raises in Question 10 can be addressed
through expert-authored reference answers.

Why Subgroup Testing Cannot be Left to Sponsor Discretion
The strongest evidence for our central recommendation comes from a peer-reviewed study that
evaluated two multimodal models on the same task and found one fair and the other not. Researchers at
Vanderbilt University Medical Center and Shanghai Tech University tested ChatGPT-4 and LLaVA-1.6 on
skin disease identification from dermatoscopic images, stratified by recorded patient sex, across
melanoma, melanocytic nevi, and benign keratosis-like lesions (Wan et al., Health Data Science, 2025).
ChatGPT-4 was generally unbiased by sex and age. LLaVA-1.6 showed significant sex-related bias. [Verify
the exact accuracy figures against the published tables before filing.]
We consider this the most important finding in the evidence we reviewed, not because of the size of any
single gap. Two capable multimodal models, evaluated on the same images, in the same clinical task,
produced different fairness profiles. Neither the architecture nor the model's general capability
predicted which one would be equitable.

This is the argument against treating element R.2 as an element sponsors select based on applicability. A
sponsor cannot reason from a model’s general performance, benchmark scores, or developer reputation
to conclude whether their device performs consistently by sex. The only way to know is to measure it. A
discretionary evaluation element will often not be selected in the reporting record described earlier in
this comment, and the resulting evidence gap will be invisible in the submission.

We also note evidence pointing the other way, because we believe it strengthens, rather than weakens,
the case. A demographic-perturbation benchmark built on MedQA evaluated several models on
examination-style questions whose correct answer should not change with patient gender, and we
understand it found no significant aggregate differences in male-female accuracy (DiversityMedQA, arXiv
2409.01497). [Verify the reported figures and the final publication venue before filing.]

The contrast is instructive. A general medical knowledge benchmark showed no sex-related gap.
Task-specific evaluations on clinical images and on real patient notes did. This bears directly on Question
10, which asks how a sponsor should establish that benchmark performance predicts safe real-world
behavior. On this evidence, aggregate performance on a general medical benchmark does not predict
subgroup performance on the clinical task a device actually performs and should not be accepted as a
substitute.

We want to state the limits of this evidence plainly. It does not establish a universal female disadvantage
across models, specialties, or task types. Results vary by model, disease, modality, and evaluation design.
That variability is our point. When the direction and magnitude of subgroup performance cannot be
predicted in advance, it must be measured for each device rather than assumed from the class.

Sex Is One Of Several Subgroups That Matter For Women
Our central recommendation focuses on sex because that is where our members' evidence is deepest.
The same logic applies to the other subgroups listed in our introduction. For each, the discussion paper
already raises the same question about public benchmarks: whether the underlying evidence represents
the population the device will serve.

These dimensions interact. Chest X-ray classifiers trained on large public datasets consistently
underdiagnosed female patients, patients under 20, Black and Hispanic patients, and patients with
Medicaid insurance, with compounding effects in intersectional subgroups (Seyyed-Kalantari et al.,
Nature Medicine, 2021). Generative AI shows the same pattern. Across nine large language models and
1,000 emergency department cases, each rewritten for 32 patient profiles with the clinical details held
constant, recommendations on triage, testing, treatment, and mental health evaluation shifted with the
patient’s race, income, housing status, and sexual orientation (Omar et al., Nature Medicine, 2025). A
2025 systematic review found bias in 22 of 24 studies examining demographic disparities in medical large
language models (Omar et al., International Journal for Equity in Health, 2025).

Race and ethnicity effects are well documented. One study tested four commercial chatbots and found
they repeatedly repeated debunked race-based medicine, including on kidney function and lung capacity
(Omiye et al., npj Digital Medicine, 2023). Dermatology AI models performed substantially worse on
darker skin tones, and fine-tuning on diverse, biopsy-confirmed images closed the gap (Daneshjou et al.,
Science Advances, 2022). That study also found that dermatologists, who often label training data,
performed worse on darker skin, so diverse images alone do not guarantee representative labels.

Pregnancy deserves particular attention because the evidence base itself is thin. The federal Task Force
on Research Specific to Pregnant Women and Lactating Women found that these populations are often
excluded from clinical research and recommended that investigators be required to justify exclusion
(PRGLAC Report, 2018). Tools validated on the general adult population do not reliably transfer. Using
data from the WHO Global Maternal Sepsis Study, researchers found obstetric-specific early warning
scores outperformed general ones, and no single score was accurate enough to identify maternal sepsis
on its own (EClinicalMedicine, 2025). In a 2026 study, two large language models did not consistently
convey the urgency of stopping isotretinoin, which causes birth defects, when pregnancy was suspected
(JMIR Formative Research, 2026).

Comorbidities and concurrent medications follow the same pattern. Of 319 ongoing trials for common
chronic conditions, 79% excluded patients with other chronic conditions, even though 91% of patients
with coronary heart disease had one (BMJ Open, 2016). A systematic review of trial exclusion rates found
that older people and people with comorbidities or multiple prescriptions were noticeably excluded
(Trials, 2020). Models trained on that literature inherit its gaps. A preprint benchmark of 750
clinician-annotated drug interaction scenarios found that large language model consistency fell as the
number of drugs rose (Blotske et al., medRxiv preprint, 2025). For women, hormonal contraception and
menopause hormone therapy are common concurrent medications a patient-facing device should be
tested against.

Geography matters because training data are concentrated. US patient cohorts used to train clinical deep
learning algorithms came disproportionately from California, Massachusetts, and New York, with little or
no representation from the other 47 states (Kaushal, Altman, and Langlotz, JAMA, 2020). Performance
can fall sharply outside the development setting. An independent external validation of a widely
deployed proprietary sepsis model found it missed 67% of sepsis cases while generating alerts for 18% of
all hospitalized patients (Wong et al., JAMA Internal Medicine, 2021).

Socioeconomic bias can also enter through the training target. A widely used care-management
algorithm predicted health care costs rather than illness, so Black patients assigned the same risk score
as White patients were considerably sicker; correcting it would have raised the share of Black patients
identified for extra help from 17.7% to 46.5% (Obermeyer et al., Science, 2019). Any GenAI-enabled
device trained or tuned on utilization data carries the same risk.
We are not asking that every device be tested on every dimension. We ask that the intended-use
population define which subgroups element R.2 covers, that sponsors report how training and
benchmark data compare with that population, and that any subgroup left untested be justified rather
than silently omitted. That is the principle the PRGLAC task force applied to clinical research, and it is
consistent with the discussion paper’s own recognition that public benchmarks can lack
representativeness.

Peer-Reviewed Evidence on Interaction and Degradation Risks
A review published in Nature on August 19, 2026, by an interdisciplinary team at the Else Kröner
Fresenius Center for Digital Health at TU Dresden and collaborating institutions, synthesizes evidence on
LLM safety in healthcare across medical AI, cybersecurity, regulatory science, ethics, and behavioral
psychology (Clusmann et al., Nature, 2026). Several of its findings bear directly on the benchmarking
elements in Appendix A.

●​ Confident or persuasive model responses can produce overreliance through automation bias, or
reinforce a user’s existing beliefs through confirmation bias. This is the risk element E.4 already
names, now supported in a peer-reviewed venue.
●​ Lengthy or complex interactions reduce response reliability, supporting the
degradation-across-long-conversations consideration under element R.1 and the multi-turn
concern raised in Question 5.
●​ Models may adapt their responses too strongly to user expectations, reinforcing incorrect
assumptions. This supports the element S.1 consideration of resistance to over-reassurance
when users minimize symptoms.
●​ Prompt injection through hidden instructions can produce clinically dangerous outputs,
supporting the element A.1 consideration for agentic devices.
The review also finds that only a small proportion of AI systems in clinical use are formally approved as
medical devices, and that existing regulatory frameworks were not designed for adaptive systems that
continuously evolve. We read this as support for the Agency’s Section VI premise that postmarket
monitoring must carry substantial weight for this device class.

We note that this review shares authorship with work CDRH cites at footnote 16 of the discussion paper.
We raise it not to claim endorsement, but because the evidence base the Agency has already drawn on
has been extended since the discussion paper was drafted.

Precedent: The Pulse Oximeter Pathway
CDRH has done this before. The 2013 pulse oximeter guidance recommended verifying performance in
10 or more healthy participants of varying ages and genders. The January 2025 draft guidance
recommends substantially larger and more diverse cohorts and explicit subgroup analyses stratified by
skin tone to support performance claims, applying to currently marketed devices as well as new
submissions (FDA draft guidance, docket FDA-2023-N-4976).
The underlying evidence was concrete. In two large cohorts, Black patients had nearly three times the
frequency of low blood oxygen that pulse oximetry failed to detect as White patients (Sjoding et al., New
England Journal of Medicine, 2020).

That change followed publicly disclosed evidence of differential performance. We submit this comment
in the same spirit, and earlier, when incorporating subgroup evaluation into a framework costs less than
retrofitting it.

Recommendations
1.​ Treat element R.2, subgroup performance, as presumptively applicable for any GenAI-enabled
device with a general or patient-facing intended use, rather than as an element selected at
sponsor discretion
2.​ For escalation functions, require directional reporting of under-escalation and over-escalation by
sex, rather than aggregate agreement with a comparator.
3.​ Where a clinician panel serves as the comparator under Section V.D.1, require sponsors to
address whether the comparator itself carries documented differential performance for the
subgroup in question.
4.​ Under element E.4, evaluate whether referral language changes user behavior rather than
assuming it mitigates directive risk.
5.​ In any Foundation Model Master File program, include performance across clinically meaningful
subgroups among the content elements, consistent with the discussion paper’s footnote 24.
6.​ Define the subgroups covered by element R.2 by the device’s intended-use population. For
patient-facing devices, these should include at minimum sex, age and life stage, race and
ethnicity, and, where users include people of reproductive age, pregnancy status. Comorbidities,
concurrent medications, geography, and socioeconomic factors should be assessed where
clinically relevant.
7.​ Require sponsors to report the composition of training and benchmark data on these dimensions
relative to the intended-use population, and to justify any subgroup left untested.

Signatories
Nada Hanafi, MSc, MPH
Liz Powell, Esq., MPH
Mitzi Krockover, MD
Leslie Cohen, MBA
Geri Stengel
Women’s Health Technology Coalition within Women’s Health Advocates