- Prepared: 2026-11-11
- Audience: Physicians and surgical service leads
- Style: Vancouver numbered citations, generated mechanically from stable source tokens; all PMIDs verified against NCBI E-utilities on the date of preparation
- Evidence cut-off: 2026-11-11
Abstract
A single-centre, room-randomised phase II trial from Fudan University Shanghai Cancer Center reports that locally deployed large language model (LLM)–generated, personalised written answers to patients’ questions, delivered before the routine preoperative conversation, reduced post-communication anxiety on the GAD-7 (3.2 [2.7] vs 5.7 [3.1], P = 0.001), reduced physician workload on the NASA Task Load Index (39.9 [16.9] vs 56.8 [19.5], P < 0.001), and shortened the face-to-face conversation from 19.9 to 11.3 minutes in 268 men scheduled for radical prostatectomy [1]. The same trial collected 3,507 patient questions, a mean of 13.1 per patient. Those are, on their face, large effects: roughly 0.8 standard deviations on anxiety, roughly 0.9 on a self-reported workload scale, and a 43% reduction in consultation time.
This review treats that trial as the peg for a broader question: what can an evidence review actually conclude about LLM-mediated patient communication before cancer surgery? Three questions organise the analysis. First, does the anxiety effect survive the design? The trial allocated patients by room rather than individually, which makes it a cluster design with an unspecified and probably small number of clusters; the abstract does not report a clustering-adjusted analysis. Patients could not be blinded to receiving personalised written answers, and the anxiety endpoint is patient-reported. Physician blinding protects the workload endpoint, not the anxiety endpoint. A 2.5-point GAD-7 difference is also below the best available estimate of the minimal clinically important difference on that instrument, which is 4 points [2] — a point the abstract’s framing does not address.
Second, what does an 8.6-minute saving mean? NASA-TLX is a self-report instrument, not a time-and-motion audit. The trial measures the conversation, not the system: the staff time to collect, triage, prompt, review, correct and audit 3,507 LLM answers is not reported, nor are message volume, documentation burden, or downstream contacts. In the adjacent ambient-scribe literature, randomised and audit-log studies find objective time savings of roughly one to two and a half minutes per encounter, with longer notes and unchanged “pajama time” [3] [4] [5]. An 8.6-minute saving measured by self-report in an unblinded cluster trial is an order of magnitude larger than that literature would predict.
Third, what would make such a service safe? The abstract describes no model identity, version, prompt design, retrieval corpus, hallucination audit, read-back verification or escalation pathway. That is not a criticism of the authors’ integrity; it is a statement about what is publicly visible. The failure modes that matter for an anxious preoperative patient are concrete and documented elsewhere: fabricated facts, false reassurance, sycophantic agreement with a patient’s incorrect belief, failure to escalate a red-flag symptom, and answer drift across model versions [6] [7] [8] [9].
The wider literature is neither empty nor confirmatory. Question-prompt lists reliably increase question-asking and shift topics discussed, with modest and inconsistent effects on anxiety [10] [11]. Decision aids improve knowledge and reduce decisional conflict across 209 randomised trials, but prostate-cancer decision aids have a poor record on treatment choice and, in the largest routine-care trial, no effect on the primary or secondary endpoints [12] [13] [14]. Consent-comprehension interventions work best when interactive or teach-back based, not when written [15]. The randomised LLM literature in surgery consists of a handful of small trials with effects that range from a standardised mean difference of −0.59 favouring the chatbot to +1.25 favouring the physician, with very low certainty [16].
The defensible conclusion is narrow. Personalised, LLM-drafted preoperative answers are a plausible, low-cost way to improve the informational content of the preoperative encounter, and the reported anxiety and workload effects are large enough to justify a properly designed confirmatory trial. They are not yet evidence that LLM communication improves surgical outcomes, consent validity, satisfaction at scale, readmission or survival; none of those was tested. A service that wants to use this class of tool now should treat it as a supervised quality-improvement intervention with a locked model, a constrained question domain, human review, explicit escalation rules, audit sampling, and its own measurement plan — not as an established standard of care.
1. Introduction: One Trial, One Number, and Three Questions an Evidence Review Can Answer
In 2026, a phase II trial from Shanghai reported that giving men with newly diagnosed prostate cancer personalised, LLM-generated answers to their own questions before the routine preoperative conversation made them less anxious, made their surgeons feel less loaded, and shortened the conversation by nearly nine minutes [1]. The intervention is easy to describe and hard to evaluate. It has no pharmacological mechanism, no fixed dose, no placebo, and no blinding that a patient cannot see through. Its effects are measured with questionnaires that depend on what the patient expects and on how much attention they received. Its delivery depends on a model that may be updated next month.
That combination — a plausible, cheap, scalable intervention with subjective endpoints and an unblinded design — is exactly the situation in which the clinical literature has historically generated inflated effect estimates. The purpose of this review is not to relitigate one paper. It is to place that paper inside four adjacent bodies of evidence that determine what a clinician should believe: the preoperative anxiety literature, the information-and-comprehension literature, the question-prompt and decision-aid trials, and the newer LLM evaluation literature. The trial is the peg, not the subject.
Three questions structure what follows.
Question one: is the anxiety effect real, and how large should we believe it is? The reported difference is 2.5 GAD-7 points, from 5.7 in the control arm to 3.2 in the AI-assisted arm [1]. Two issues determine the answer. The first is design: randomisation by room makes this a cluster trial, and the abstract does not say how many rooms, how many clusters, or whether the analysis accounted for within-room correlation. The second is measurement: GAD-7 is a validated screening and severity instrument [17] [18], but its responsiveness and minimal clinically important difference are context-dependent, and the best available estimate in a treatment trial is 4 points [2]. A 2.5-point between-group difference can be statistically robust and still sit below the threshold at which patients notice a change. The abstract also does not report baseline GAD-7 values, so a reader cannot tell whether the groups started equal, whether the control arm deteriorated, or whether the AI arm improved.
Question two: what is being saved, and for whom? The trial reports a 16.9-point NASA-TLX difference and an 8.6-minute shorter conversation [1]. NASA-TLX measures perceived workload across six dimensions; it is a psychometrically developed instrument, but it is self-report, and it is sensitive to expectation and to the framing of the task [19] [20]. A clinician who has been told that a tool will help may report lower load even if total work is unchanged. The time saving is measured on the conversation, not on the pathway. The 3,507 questions had to be received, understood, matched to the right patient, answered safely, and reviewed by someone. None of that labour appears in the abstract. The workload claim is therefore best read as a claim about clinician-facing consultation time, not about system workload — a distinction that matters for anyone considering a business case.
Question three: what is the safety floor? A patient-facing LLM that answers questions about cancer surgery is not a chatbot in the ordinary sense. It is a system that can reassure a patient about a symptom that should have been escalated, or give a confident answer that is wrong. The published record on LLM medical answers is not reassuring at the margins: expert audits find unsafe responses in 5–9% of answers to patient questions about benign urological and gynaecological conditions [21], pooled accuracy around 89% with completeness around 84% in a surgical single-arm meta-analysis [22], and systematic degradation of accuracy when models are trained to sound warmer [6]. None of this proves that the Shanghai pipeline was unsafe. It establishes that safety cannot be assumed from a positive anxiety result, and that a service deploying such a tool needs an auditable answer to the question “how would you know?”
This review is deliberately an evidence review rather than a trial report. It does not have the trial’s full text: the publisher’s PDF endpoint returned HTML, and the DOI was not indexed in PubMed or Europe PMC at the time of writing. Every statement about the trial is therefore restricted to the verified abstract facts listed in the seed document [1] and to the public ClinicalTrials.gov record [23]. Where the abstract is silent — model identity, prompt design, statistical model, baseline scores, follow-up, subgroup analyses, safety monitoring — this review says “not reported in the abstract” rather than inferring. That constraint is itself part of the finding: an intervention of this importance cannot be appraised from an abstract, and the fact that the full text was not retrievable is a reproducibility problem, not a formatting inconvenience.
The review proceeds in four movements. Sections 2 to 4 establish the clinical and psychological ground: why preoperative anxiety matters, why more information is not monotonically good, and what an LLM adds mechanistically that a leaflet does not. Sections 5 to 8 examine the trial and its two claims — validity and workload — and then the safety failure modes that the trial does not address. Sections 9 to 12 place the intervention in its adjacent evidence base, its regulatory environment, and the trial designs that would actually settle the question. Sections 13 to 15 translate the evidence into what a surgical service could responsibly do now, state the limitations of this review, and give a bottom line.
A note on scope. This is not a review of “AI in surgery.” It is a review of one function — communication with a patient before an operation — and of the evidence that such communication, when mediated by a language model, changes what the patient feels, knows, or does. Claims about operative outcomes, oncological outcomes, consent validity, readmission or survival are outside the evidence and are flagged as such wherever they might be tempting.
2. The Clinical Problem: Preoperative Anxiety in Radical Prostatectomy and What It Actually Predicts
2.1 How common, and how measured
Preoperative anxiety is common enough that almost any plausible intervention will find a signal. A global pooled estimate cited in a 2022 review was 48% across approximately 14,000 surgical patients [24]. A more recent meta-analysis of 46 prospective cohorts (23,628 patients) put pooled anxiety prevalence at 26% (95% CI 21–31%), with substantial heterogeneity (I² = 95%), and found the highest prevalence in cancer surgery at 29%, against 19% in orthopaedic surgery [25]. A separate meta-analysis opens with the familiar claim that preoperative anxiety affects 60–80% of surgical patients [26], and a review of measurement notes figures up to 80% in high-risk procedures [27]. These numbers are not reconcilable, and the reason is methodological rather than epidemiological: “anxiety” is measured with the State-Trait Anxiety Inventory, the Amsterdam Preoperative Anxiety and Information Scale, the Hospital Anxiety and Depression Scale, the GAD-7, visual analogue scales, and ad hoc single items, at different time points, with different cut-offs [27] [28]. A prevalence estimate is therefore only interpretable alongside its instrument and threshold.
The measurement heterogeneity matters for the Shanghai trial because it used GAD-7. GAD-7 was developed as a brief screen for generalised anxiety disorder in primary care, with a cut-point optimised at sensitivity 89% and specificity 82% [17]; pooled diagnostic meta-analysis puts acceptable performance at cut-offs of 7–10, with sensitivity 0.83 and specificity 0.84 at a cut-off of 8 [18]. It is a reasonable severity measure, but it is not a preoperative-anxiety-specific instrument, and it was not designed to detect the transient, situation-specific apprehension that a surgical consent conversation provokes. The preoperative literature more often uses STAI-State or APAIS, both of which have explicit surgical validation; APAIS correlates 0.74 with STAI-State and takes under two minutes to complete [28]. A GAD-7 score of 5.7 in a control arm is in the mild range; a score of 3.2 is in the minimal range. Whether that shift is experienced by the patient as meaningful is exactly the question the MCID literature addresses, and the answer is that a 2.5-point change is probably below the threshold of 4 points estimated in a treatment study [2].
2.2 The prostatectomy-specific picture
Radical prostatectomy is a useful stress test for this literature because the operation carries a distinctive combination of threats: cancer control, urinary continence, sexual function, and a recovery period in which the patient must interpret new symptoms without immediate access to the surgeon. The prostate-specific data are consistent with the general picture but add functional specificity.
In a retrospective analysis of 5,862 men undergoing radical prostatectomy, 28% had abnormal PHQ-4 scores and 8% scored 6 or more, indicating moderate-to-severe distress. Higher PHQ-4 scores were associated with longer length of stay, higher complication rates, and a higher risk of urinary incontinence; erectile dysfunction and biochemical recurrence were not associated [29]. The design cannot separate cause from consequence — a man who is depressed may also be a man with more comorbidity, less social support, or more advanced disease — but the association is large enough to matter for preoperative assessment.
A prospective Norwegian cohort of 416 men found that high pre-biopsy distress predicted worse urinary incontinence domain scores at six months (58.9 vs 66.8, P = 0.028), more urinary bother, and a higher rate of pad use (70.6% vs 54.2%, P = 0.034); sexual bother was also higher, although sexual function scores did not differ [30]. At twelve months the differences attenuated. A smaller Italian series of 33 patients found anxiety significantly associated with incontinence in the early postoperative months and noted that erectile dysfunction affected 90% at three months [31]; the sample is too small for inference but the direction is consistent. A multicentre Korean prospective study using HADS and the Distress Thermometer found distress highest preoperatively, improving over the year, but roughly one in five patients still had a Distress Thermometer score of 4 or more at twelve months, a level that warrants clinical attention [32].
Two negative or null observations keep this honest. In 149 men, state and trait anxiety did not differ between open retropubic and robot-assisted prostatectomy [33] — the surgical approach, which patients often fixate on, was not the driver. And in the Norwegian cohort, the association with adverse effects was present at six months but largely gone at twelve [30], which argues against a fixed psychological trait and for a modifiable, time-limited state. That is the space in which a preoperative communication intervention could plausibly act.
2.3 What anxiety predicts, and what it does not
The strongest outcome data are associative and come from heterogeneous surgical populations. A 2025 meta-analysis found preoperative anxiety associated with increased anaesthetic requirements (standardised mean difference 0.67, 95% CI 0.32–1.01), increased analgesic requirements (SMD 0.89, 95% CI 0.65–1.12), postoperative delirium in adults (OR 1.90, 95% CI 1.11–3.26), slower achievement of an Aldrete score of 9 (SMD 0.79), and longer extubation time (SMD 0.89); there was no significant association with postoperative pain [26]. A separate meta-analysis of 23 studies found preoperative anxiety associated with chronic post-surgical pain, with an SMD of 0.31 (95% CI 0.20–0.41), corresponding to roughly 0.34 points on a 0–10 numeric rating scale, with high heterogeneity [34]. The anxiety–delirium and anxiety–length-of-stay associations survived in the larger cohort meta-analysis: anxiety was associated with 0.55 additional hospital days (95% CI 0.29–0.82), with no heterogeneity (I² = 0%) [25].
These are not causal estimates. Anxiety co-varies with depression, pain catastrophising, poor sleep, comorbidity and socioeconomic disadvantage, and most cohorts adjust for only some of these. The practical implication is not that treating anxiety shortens stay by half a day. It is that anxiety is a marker of a patient who is more likely to struggle, and that a preoperative interaction which identifies and addresses that struggle is defensible on clinical grounds even before one claims an outcome benefit.
2.4 Why the endpoint choice in the Shanghai trial is both sensible and vulnerable
GAD-7 is a sensible choice for a trial that wants a brief, validated, self-administered measure that can be repeated immediately before and after an encounter. It is vulnerable for three reasons. First, it measures generalised anxiety symptoms over the past two weeks, not the acute state of the preoperative hour; a change measured immediately after an intervention may capture transient reassurance rather than a change in the underlying symptom burden. Second, it is transparently a psychological measure, so a patient who has just received a lot of personalised attention knows what is being measured and can reasonably be expected to report improvement. Third, the MCID is not a fixed property of the instrument; the 4-point estimate comes from a depression-treatment cohort [2], and different populations may yield different thresholds. The trial’s own abstract reports means and standard deviations with P values, but not confidence intervals for the difference, not baseline scores, and not an MCID justification [1]. Those omissions are not unique to this paper, but they limit what a reader can conclude.
The deeper clinical point is that anxiety is not the only thing that matters before prostatectomy. A man can be calm and badly informed, or anxious and well informed. The outcomes that a surgical service should care about — comprehension of the operation and its functional consequences, recall of what was said, decisional regret, and the ability to recognise and report a complication — are not the same as a GAD-7 score. Section 3 examines why information and anxiety do not move together.
3. Information, Comprehension and Anxiety: Why “More Information” Is Not a Monotonic Good
3.1 The monitoring–blunting problem
The naive model of preoperative communication is hydraulic: patients are anxious because they do not know what will happen; give them information and anxiety falls. The literature does not support that model. Patients differ in coping style. In a consecutive sample of 3,087 surgical patients, 1,205 of whom had high preoperative anxiety, about two-thirds were “monitors” who believed information would help them cope, while the remaining third were “blunters” who declined further education and preferred self-distraction. Anxiety scores did not differ between the two groups, and the educational conversation was the coping effort rated highest by monitors [35]. A leaflet handed to a blunter may increase vigilance without reducing distress. An interactive system that lets the patient choose how much and when is, in principle, better matched to this heterogeneity — but only if the patient is the one choosing.
This is the strongest theoretical argument for an LLM over a leaflet, and it is also the argument that the Shanghai trial does not test. The intervention gave every patient in the AI arm the same opportunity to ask questions and receive written answers; the abstract does not report whether patients could decline, how many questions they actually read, or whether the answers were tailored to coping style. The mean of 13.1 questions per patient suggests high engagement, but a mean conceals a distribution: some men may have asked two questions, others forty.
3.2 What question-prompt lists actually do
Question-prompt lists (QPLs) are the closest pre-LLM ancestor of the intervention. A QPL is a structured list of questions that a patient can bring to a consultation; it personalises content only to the extent that the patient selects items. The randomised evidence is substantial and modest.
The original 1994 trial randomised 142 cancer patients to a prompt sheet or a general information sheet. The prompt sheet increased questions about prognosis (35% vs 16%) but did not increase the mean number of questions overall, and it did not change satisfaction or adjustment [36]. A 1999 trial of 60 patients found that a prompt sheet endorsed and worked through by the clinician increased total questions and questions about tests and treatment, while a separate coaching session added nothing; psychological outcomes did not differ [37]. A 2023 double-blind RCT in advanced cancer (n = 130) found no difference in perceived helpfulness (7.2 vs 7.1, P = 0.79) and no difference in anxiety (2.3 vs 1.6, P = 0.19), although the QPL group had a more positive global view and felt prompted to generate new questions [38]. A 2020 multicentre breast-cancer RCT (n = 324) found that oncologists perceived more patients as “difficult” in the QPS arm than in a question-listing arm (20.6% vs 11.8%), and that perceived difficulty correlated with lower patient satisfaction [39] — a reminder that interventions which increase patient assertiveness can have relational costs.
The meta-analytic picture is consistent with these individual trials. A 2024 meta-analysis of seven RCTs (1,059 patients) found that QPLs increased the total number of questions asked (SMD 0.73, 95% CI 0.28–1.18, I² = 83%) and patients’ expectations for the future (SMD 0.67, 95% CI 0.08–1.25, I² = 88%), with no significant improvement in anxiety or quality of life [10]. A 2021 systematic review of ten RCTs found a shift in topics discussed and only weak indications that QPLs increase anxiety shortly before and after consultation, possibly followed by a decline at follow-up; the overall impact on communication and psychological outcomes was limited [11]. A 2025 meta-analysis of 14 RCTs found improved shared decision-making engagement and question-asking, with QPLs plus instructions superior to QPLs alone [40]. A surgical-specific systematic review identified only seven eligible RCTs, three at high risk of bias, and judged meta-analysis inappropriate because of heterogeneous outcomes [41].
The honest summary is that QPLs change the process of the consultation reliably and the psychology of the patient unreliably. The Shanghai trial’s anxiety effect is therefore not a simple extrapolation of the QPL literature; it is a larger effect than that literature would lead one to expect, which raises the question of what else changed.
3.3 Preoperative education and anxiety: small effects, high heterogeneity
Structured preoperative education is a better-powered literature than QPLs, and its effect on anxiety is consistently small. A 2026 meta-analysis of 19 RCTs in hip and knee arthroplasty found a standardised mean difference of −0.37 (95% CI −0.63 to −0.11) for anxiety, +0.37 for knowledge, and −0.31 for pain [42]. A 2025 network meta-analysis of 40 RCTs (4,113 patients) found improvements in length of stay, analgesic use, pain, anxiety, quality of life, satisfaction and knowledge, with human-contact interventions reducing length of stay by about one day [43]. These are real but modest effects, achieved with interventions that are much less personalised than an LLM conversation. A 2.5-point GAD-7 difference, if it represents a true between-group effect, is larger than the pooled effect of preoperative education on anxiety — which is possible, but demands explanation.
3.4 Consent, recall and comprehension: the part patients actually need
If the purpose of preoperative communication is to support informed consent, then the relevant endpoint is comprehension, not calm. The consent literature is sobering. A classic study of 38 patients who had demonstrated correct understanding before operation found that, six months later, only 25% recalled the risk of infection and only one patient recalled the risk of nerve or artery damage; 22% recalled relief of pain and improved function as benefits [44]. A review of 13 high-quality studies found that 21–86% of patients could recall potential risks and complications, with understanding declining with age [45]. A systematic review of 23 surgical studies found adequate overall understanding in only 29% and adequate understanding of risks in 36% [46].
What improves comprehension is specific. A 2020 systematic review of 52 studies and 60 interventions found statistically significant improvement in 43% of written interventions (6/14), 56% of audiovisual interventions (15/27), 67% of multicomponent interventions (2/3), 85% of interactive digital interventions (11/13), and 100% of verbal discussion with test/feedback or teach-back (3/3); 44% of studies were at high risk of bias for the comprehension outcome [15]. In a trial of 575 patients across four operations, including 81 radical prostatectomies, independent predictors of comprehension included age, race, ethnicity, operation type, repeat-back, and total consent time [47]. A review of cardiac surgery consent interventions found that additional written information and multimedia presentations improved risk recall, but that only one randomised trial supported audiotaped consultations [48].
The implication for LLM-mediated communication is double-edged. On one side, an interactive system that answers the patient’s own questions in plain language is structurally closer to the interventions that work (interactive digital, teach-back) than to the ones that do not (written leaflets). On the other, comprehension is not the same as satisfaction, and a fluent answer can produce a feeling of understanding without the ability to restate the risks. The Shanghai trial measured satisfaction and illness perception but, in the abstract, not comprehension or recall [1]. That is a gap with direct clinical consequences: a man who feels informed but cannot describe the risk of incontinence to his wife has not necessarily been well served.
3.5 Why anxiety can rise with information
There is a coherent psychological account of why information can increase anxiety in the short term. Information makes threats specific. A patient who did not know that anastomotic leak, urinary incontinence or erectile dysfunction were possible cannot worry about them specifically; after a detailed explanation, they can. The QPL review’s finding of a possible transient increase in anxiety shortly before and after consultation, followed by a later decline, fits this account [11]. So does the observation that illness uncertainty correlates with preoperative anxiety (r = 0.411) and that mental health literacy moderates the relationship [49]: uncertainty is aversive, but certainty about a bad outcome is also aversive.
This is why the timing and framing of an LLM intervention matter more than the volume of information. An answer delivered a week before surgery, with time for the patient to process it and to ask follow-up questions, is a different intervention from an answer delivered in the preoperative holding area. The Shanghai trial delivered answers before the routine face-to-face communication [1], which is the right side of that distinction — but the abstract does not report the interval, the setting, or whether patients could ask follow-up questions of a clinician.
4. What an LLM Adds That a Leaflet Cannot: Personalisation, Iteration, Timing, and the Mechanism by Which It Could Reduce Anxiety
4.1 Four properties that are genuinely different
A leaflet is fixed. A question-prompt list is a menu. An LLM, in the configuration described by the trial, is a system that takes a patient’s own question, in the patient’s own words, and produces an answer addressed to that question. Four properties follow.
Personalisation. The answer can refer to the patient’s stage, planned procedure, comorbidities, and previous experience. The trial’s population was newly diagnosed prostate cancer patients scheduled for radical prostatectomy, a group with a fairly standard set of concerns — continence, sexual function, pain, catheter, length of stay, pathology — but also a group in which the relative importance of those concerns varies enormously. A generic leaflet cannot allocate attention to the concern that is keeping a particular man awake.
Iteration. The patient can ask again, rephrase, or follow a thread. This is the property that most closely resembles the interactive-digital and teach-back interventions that performed best in the consent-comprehension review [15]. It is also the property that creates the safety problem: an iterated conversation can drift into territory that the clinician never authorised.
Timing. The answer can be available when the question occurs — at 11 p.m., after a Google search, or in the car on the way home — rather than at the next clinic visit. The trial’s design placed the answers before the face-to-face conversation, which may have allowed the conversation to start at a higher level of understanding [1].
Volume. The trial collected 3,507 questions from 268 patients, a mean of 13.1 per patient [1]. A 20-minute consultation cannot answer 13 questions well, especially when the same consultation must also cover consent, logistics, anaesthesia, and the patient’s emotional state. The arithmetic is the strongest argument for an asynchronous component: not that the LLM is wiser than the surgeon, but that the surgeon has 20 minutes and the patient has 13 questions. A mean of 13.1 questions is also a statement about demand — these patients wanted to ask far more than the standard encounter accommodates.
4.2 The plausible mechanism: uncertainty, illness representations, and rehearsal
The trial’s secondary endpoints — emotion, illness perception, satisfaction — hint at a mechanism. The illness-perception literature provides the framework. The Brief Illness Perception Questionnaire measures cognitive and emotional representations of illness across identity, cause, timeline, consequences, control, and emotional response; it has good test–retest reliability and predictive validity for functioning after myocardial infarction [50]. A meta-analysis of 188 papers found pooled correlations between illness perceptions and depression, anxiety, and quality of life in the range of 0.25–0.49 for consequences, identity, and emotional representations, and −0.12 to −0.27 for personal control, with sensitivity to change after intervention [51]. If a preoperative conversation changes a patient’s representation from “this operation will leave me incontinent and impotent forever” to “this operation has a temporary and manageable effect on continence, and here is what we do about it,” it could reduce anxiety without changing the objective risk.
A second mechanism is rehearsal. Answering a patient’s questions before the consultation may allow the patient to rehearse what they will say, to identify what they still do not understand, and to arrive with a clearer agenda. The QPL literature shows that priming questions changes which topics are discussed [36] [37]. The LLM version may simply be a more efficient priming device.
A third mechanism is attention. A patient who receives a personalised written answer has evidence that someone thought about them. That is not a trivial component; it is also the component that cannot be separated from the intervention in an unblinded trial. The trial’s own design — physicians blinded, patients not — means that attention, novelty, and expectation are all bundled into the anxiety effect [1].
4.3 What the trial did not measure, and why it matters for the mechanism
The abstract reports that emotion, illness perceptions and satisfaction were significantly better in the AI-assisted arm, but gives no effect sizes [1]. It does not report a mediation analysis. It does not report whether the anxiety effect was concentrated in patients with high baseline anxiety, in those who asked more questions, or in those whose illness perceptions changed most. It does not report comprehension or recall. It does not report whether the face-to-face conversation was shorter because the questions had been answered, or because the physician skipped material that the patient had already read, or because the physician spent less time on rapport.
Those are not academic distinctions. If the mechanism is “questions answered,” then the intervention can be improved by improving answer quality and coverage. If the mechanism is “attention,” then the effect may decay when the novelty wears off, and a cheaper intervention — a nurse call, a personalised letter — might achieve the same result. If the mechanism is “the physician skipped content,” then the time saving may come at the cost of the very discussion that consent requires. The trial as published cannot distinguish these.
4.4 The counterfactual: what a good leaflet plus a nurse call would do
The relevant comparator for an LLM is not “nothing.” It is the best available low-tech alternative: a procedure-specific leaflet, a preoperative nursing visit, and an invitation to call with questions. That package has its own evidence. A preoperative nursing visit was associated with lower anxiety and depression scores in a retrospective series of 199 radical prostatectomy patients, although the incidence of complications did not differ [52], and preoperative education more broadly has a small pooled anxiety effect [42]. The Shanghai trial’s control arm received routine preoperative communication, not an active information package; the abstract does not describe what that routine consisted of [1]. If routine care was a brief verbal conversation with no written material, then part of the observed effect may reflect the addition of written, personalised information rather than the addition of an LLM. That is a design question a confirmatory trial must answer with an attention-matched control.
The point is not that the trial is invalid. It is that the effect size is a function of the comparator, and the comparator is underdescribed. A 2.5-point GAD-7 difference against “routine communication” is not the same claim as a 2.5-point difference against “leaflet plus nurse call.” The former is plausible; the latter would be surprising.
5. The Trial: Design, Endpoints and Results
5.1 What is publicly known
The trial was a prospective, randomised, single-blinded phase II study conducted in the Department of Urology at Fudan University Shanghai Cancer Center. Patients were newly diagnosed with prostate cancer and scheduled for radical prostatectomy. Randomisation was by room, with rooms allocated to control or AI-assisted groups rather than patients randomised individually. The trial randomised 268 patients: 130 to control and 138 to AI-assisted communication. In the AI-assisted group, patients received locally deployed LLM-generated personalised responses to their questions before the routine face-to-face communication; physicians were blinded to allocation. The co-primary endpoints were patient anxiety and physician workload, with emotion, illness perception, satisfaction and communication time as secondary outcomes. The trial collected 3,507 patient questions, a mean of 13.1 per patient [1].
The results, as reported in the abstract, are summarised in Table 1.
Table 1. Reported results of the phase II trial (abstract data only)
| Outcome | AI-assisted (n = 138) | Control (n = 130) | Reported P | Difference |
|---|---|---|---|---|
| Post-communication anxiety, GAD-7, mean (SD) | 3.2 (2.7) | 5.7 (3.1) | 0.001 | 2.5 points lower |
| Physician workload, NASA-TLX, mean (SD) | 39.9 (16.9) | 56.8 (19.5) | <0.001 | 16.9 points lower |
| Communication time, minutes, mean (SD) | 11.3 (4.5) | 19.9 (6.1) | <0.001 | 8.6 minutes shorter |
| Emotion | “significantly better” | reference | not reported | effect size not reported |
| Illness perception | “significantly better” | reference | not reported | effect size not reported |
| Satisfaction | “significantly better” | reference | not reported | effect size not reported |
Source: verified abstract facts in the seed document [1]. Baseline GAD-7, baseline NASA-TLX, follow-up duration, and the statistical model are not reported in the abstract.
The publisher abstract concludes that “AI-assisted preoperative communication significantly reduces patient anxiety and improves psychological and cognitive outcomes while decreasing physician workload” [1]. That sentence is a fair summary of the reported numbers. It is not a summary of the design’s ability to support them.
5.2 The registry record and the paper do not quite match
The public ClinicalTrials.gov record (NCT07082049, “AI-LLM Communication Aid in Prostate Cancer Care”) adds information that the abstract does not contain, and it also creates discrepancies that a careful reader has to hold in view [23].
Table 2. Registry record versus published abstract
| Item | ClinicalTrials.gov record [23] | Published abstract [1] |
|---|---|---|
| Title | AI-LLM Communication Aid in Prostate Cancer Care (AI-CAP) | LLM-assisted preoperative communication in prostate cancer |
| Status | Active, not recruiting | Not stated |
| Start date | 2025-07-27 | Not stated |
| Primary completion | 2027-06-01 | Not stated |
| Phase | “NA” | Phase II |
| Design | Randomised, single masking | Randomised, single-blinded, phase II |
| Enrolment | 160 (registry enrolment field) | 268 randomised |
| Primary outcomes | Change from baseline in GAD-7; difference in NASA-TLX | Patient anxiety; physician workload |
Three observations follow, and none of them is an accusation.
First, the registry lists a planned enrolment of 160, while the paper reports 268 randomised. A trial can legitimately exceed its planned enrolment, and registries are often updated late; but a reader cannot tell from the public record whether the sample size was pre-specified, whether the target was revised, or whether the analysis was powered for the co-primary endpoints. The discrepancy matters because an unpowered co-primary analysis is more likely to produce a fragile positive result.
Second, the registry describes the phase as “NA” while the paper calls the study phase II. This is a labelling inconsistency, not a scientific one, but it affects how the result should be weighted: a phase II signal is hypothesis-generating, and the paper’s own framing is appropriately modest.
Third, the registry lists a primary completion date of June 2027, while the paper reports results in 2026. Possible explanations include an earlier-than-planned analysis, a registry entry that was not updated, or a distinction between the primary completion date and an interim analysis. The public record does not say. For an evidence review, the practical consequence is that the protocol, the statistical analysis plan, and the date of database lock are not available to check against the published numbers.
These are documentation problems, not proof of misconduct. But they illustrate a general point about AI trials: the registry record is often the only place where the pre-specified design is visible, and when it disagrees with the paper, the reader’s confidence in the effect estimate should decrease rather than increase.
5.3 What the abstract does not report
The following items are absent from the abstract and are material to interpretation:
- Model identity and version. No model name, parameter count, vendor, or version is given. A locally deployed model may be a fine-tuned open-weight model, a quantised commercial model, or a retrieval-augmented system; these have very different failure modes.
- Prompt design and guardrails. No system prompt, no instruction hierarchy, no refusal policy, no retrieval corpus, no citation requirement, no answer-length constraint.
- Question triage. No description of how 3,507 questions were collected, whether they were screened for red flags, who reviewed the answers, or what happened if a question was outside the model’s competence.
- Statistical model. No description of whether clustering was accounted for, whether baseline scores were adjusted, whether the co-primary endpoints were alpha-protected, or how missing data were handled.
- Baseline scores. No baseline GAD-7 or NASA-TLX, so the reported post-intervention values cannot be interpreted as change scores.
- Follow-up. No data beyond the immediate post-communication period; no durability, no decisional regret, no postoperative distress.
- Safety monitoring. No adverse-event reporting, no hallucination audit, no incident log, no read-back verification.
- Equity analysis. No subgroup by age, education, digital literacy, or language.
Any one of these omissions would be acceptable in a short research letter. Taken together, they mean that the published article cannot be used to reproduce the intervention, to assess its safety, or to judge whether the effect would survive a more rigorous design. That is the central limitation of the evidence base, and it is a limitation of the field rather than of this trial alone.
6. Threats to Validity: Room-Level Allocation, Absence of Patient Blinding, Subjective Co-Primary Endpoints, Single Centre, Phase II Horizon
6.1 Room-level allocation is a cluster design with few clusters
Randomising by room means that the unit of allocation is the room, not the patient. Patients within a room share a physical space, a nursing team, a scheduling pattern, and often a surgeon. Their outcomes are therefore correlated. The correct analysis is a cluster-adjusted one — a mixed model with a random effect for room, a cluster-robust variance estimator, or a permutation test at the cluster level. The abstract does not say that any of these was used [1].
The consequences of ignoring clustering are well characterised. With few clusters, the risk of chance imbalance in baseline characteristics rises, the type I and type II error rates can both increase, and standard errors are underestimated when the intracluster correlation is ignored [53]. The magnitude of the problem depends on the number of clusters and the intracluster correlation coefficient (ICC). Published ICCs for patient-reported outcomes in cluster trials are often in the range of 0.01–0.10; a meta-analysis of cluster trials in major depression reported a pooled ICC of 0.07 (95% CI 0.05–0.09) [54], while neonatal data show lower ICCs for mortality (0.005) and higher ICCs for care-delivery outcomes such as duration of intensive care (0.024) and parenteral nutrition (0.027) [55]. Cancer-cooperative-group trials show that ICCs vary by outcome and cluster type, and that they should always be estimated for the specific outcome [56].
The trial does not report the number of rooms. If we assume, purely for illustration, that 268 patients were allocated across 12 rooms, the average cluster size would be about 22. At an ICC of 0.05, the design effect would be 1 + (22 − 1) × 0.05 = 2.05; at an ICC of 0.07, it would be 2.47. The effective sample size for a patient-level anxiety analysis would then be roughly 109–131 rather than 268. If there were 20 rooms, the average cluster size would be about 13, and the design effect would be 1.60–1.84, giving an effective sample of 146–168.
Table 3. Illustrative design-effect sensitivity analysis (not trial data)
| Assumed rooms | Mean cluster size | ICC 0.02 | ICC 0.05 | ICC 0.07 |
|---|---|---|---|---|
| 12 | 22 | 1.42 | 2.05 | 2.47 |
| 16 | 17 | 1.32 | 1.80 | 2.12 |
| 20 | 13 | 1.24 | 1.60 | 1.84 |
| 30 | 9 | 1.16 | 1.40 | 1.56 |
Calculated by the reviewer from the reported sample size and standard design-effect formula; the number of rooms and the ICC are unknown. The table shows how much the effective sample could shrink, not what happened in the trial.
Even at the most favourable plausible assumption, the effective sample is substantially smaller than 268. The reported P value of 0.001 for the anxiety difference implies a t-statistic of about 3.3–3.5; dividing by the square root of a design effect of 1.6–2.5 would reduce it to roughly 2.1–2.7, which could still be significant but with a much wider confidence interval. At a design effect of 2.5, a difference that was P = 0.001 unadjusted could become P ≈ 0.01–0.03. The effect might survive; the precision would not. And because the abstract reports no confidence interval for the difference, the reader cannot see this.
There is a second, subtler problem. Room-level allocation can confound the intervention with who works in the room. If the AI-assisted rooms were served by a particular nursing team, or scheduled on particular days, or used by surgeons with a particular communication style, the room effect and the intervention effect are entangled. The trial says physicians were blinded, which addresses one channel, but it does not say whether the same physicians covered both arms, whether rooms rotated, or whether the allocation was concealed until the patient arrived. A cluster design can be executed well; this abstract does not provide the information needed to judge whether it was.
6.2 Patients cannot be blinded, and the primary endpoint is patient-reported
The intervention is a personalised written communication. A patient who receives it knows. The primary anxiety endpoint is a self-report questionnaire. Therefore the anxiety effect is not protected by blinding in the way that, say, a mortality endpoint would be. Three non-specific effects are bundled with the specific effect: expectation (I have been given something that is supposed to help), attention (someone has addressed my questions), and novelty (this is new and interesting). A usual-care control arm receives none of these.
This does not make the trial uninformative. It makes the effect estimate an upper bound on the specific effect of LLM-generated content. The appropriate comparison for a confirmatory trial is an attention-matched control: a generic information leaflet plus a structured nurse call, or a human-written personalised answer, or an LLM-generated answer that is deliberately generic. Without that, the trial answers “does adding a personalised written Q&A service reduce anxiety?” rather than “does the LLM component add anything?”
The physician blinding is real but partial. Physicians were blinded to allocation, which protects the NASA-TLX to some degree. But a physician in the consultation can often infer that a patient has received written answers: the patient may arrive with a printout, refer to “the answers,” or ask fewer questions. The abstract does not report a blinding-integrity check [1]. If physicians could guess allocation, their workload ratings could be influenced by knowing that a tool was supposed to help — or, conversely, by the extra work of addressing written answers they had not seen. The direction of that bias is not predictable, which is why blinding assessment matters.
6.3 Co-primary endpoints and multiplicity
Two co-primary endpoints — anxiety and workload — were reported. When two endpoints are co-primary, a trial must either alpha-split (for example, 0.025 each) or use a hierarchical test, or the familywise error rate is inflated. The abstract reports P = 0.001 and P < 0.001, both of which would survive a 0.025 threshold, so multiplicity is unlikely to overturn the primary conclusions. But the abstract does not state the alpha strategy, and the secondary outcomes — emotion, illness perception, satisfaction, communication time — are reported as “significantly better” without effect sizes or P values [1]. With five or more secondary comparisons, some will be significant by chance. The abstract’s language (“significantly better”) is not enough to distinguish a pre-specified secondary endpoint from a exploratory finding.
6.4 Single centre, single procedure, single population
The trial was conducted at one academic cancer centre in Shanghai, in one operation, in a predominantly older male population. That is not a fatal limitation for a phase II signal, but it constrains generalisability in specific ways. Prostatectomy patients are a highly selected group: they have chosen surgery, they have a treating relationship with a urology team, and they are likely to be engaged with their care. A text-based LLM intervention requires a smartphone or a computer, a degree of digital confidence, and literacy in the language of the answers. The trial reports no data on digital access, education, or language [1]. The populations that might benefit most — older men with low health literacy, men whose first language differs from the clinician’s, men in rural areas — are also the populations least likely to engage with a text-based tool. Section 9 examines that asymmetry in detail.
The single-centre design also means that the “routine communication” comparator is specific to that centre. In a system where the preoperative conversation is already structured, supported by a specialist nurse, and accompanied by a procedure-specific leaflet, the incremental value of an LLM may be smaller. The trial’s control condition is described only as “routine preoperative communication” [1], which is not a reproducible description.
6.5 Phase II horizon and surrogate endpoints
The trial measured anxiety, workload and communication time immediately after the intervention. It did not measure postoperative anxiety, decisional regret, comprehension, recall, unplanned contacts, readmission, or any clinical outcome. That is appropriate for a phase II study, but it means the result cannot support claims about surgical recovery or consent quality. The abstract’s conclusion — “improves psychological and cognitive outcomes” — is a statement about questionnaire scores, not about clinical benefit [1].
The most important missing endpoint is decisional regret. Prostate cancer treatment decisions have a long tail: a man who chose surgery may regret it years later if continence or sexual function is worse than he expected. A cross-sectional survey of 122 survivors found that 14.9% reported lacking understanding of the impact of treatment on erections and 11.5% on urinary continence, and that radical prostatectomy and low pre-treatment understanding predicted decisional regret [57]. If an LLM intervention improves understanding before surgery, it could reduce regret; if it merely reassures, it could increase it. The trial cannot tell.
6.6 The general problem of single-centre AI trials
The trial’s design weaknesses are not unique. A scoping review of 86 randomised trials of AI in clinical practice found that 70 (81%) reported a positive primary endpoint, that single-centre trials predominated, that demographic reporting was sparse, and that operational efficiency was inconsistently reported [58]. That is a description of a literature with a positivity bias. A single positive phase II trial in that literature should be read as a hypothesis, not as a confirmed effect — especially when the endpoint is subjective and the intervention is unblinded.
7. The Workload Claim: NASA-TLX, the 8.6 Minutes, and the Difference Between Clinician Time and System Time
7.1 What NASA-TLX measures
The NASA Task Load Index is a multidimensional self-report measure of perceived workload. It asks the operator to rate mental demand, physical demand, temporal demand, performance, effort, and frustration, and it combines them into a weighted or unweighted score. It was developed for aviation and has been used widely in healthcare. It is a reasonable instrument for comparing how demanding two tasks feel. It is not a stopwatch, and it is not a cost-accounting system.
The broader literature on measuring documentation burden makes the limitation explicit. A systematic review of 135 articles identified 11 categories of measures, found that electronic health record log data were the most common source, that direct time-motion analysis was uncommon, and that evidence of validity was “limited and incomplete” [19]. A scoping review of 35 studies found 15 measurement characteristics and concluded that standard, validated measures of documentation burden are lacking [20]. In that context, a 16.9-point NASA-TLX difference is a signal about perceived load, not a measurement of work performed.
7.2 The 8.6-minute saving in context
The trial reports communication time of 11.3 (4.5) minutes in the AI arm versus 19.9 (6.1) minutes in the control arm, a difference of 8.6 minutes, or a 43% reduction [1]. That is a large saving for a communication intervention. To calibrate it, consider the adjacent literature on ambient AI scribes, which also aim to reduce clinician administrative work and which have been evaluated with randomised designs and audit-log outcomes.
A 13-month retrospective cohort of 10,344 emergency department encounters found that ambient AI scribe use was associated with a 72.6-second reduction in on-shift documentation time per encounter (95% CI 63.8–81.4) [3]. A 20-site study of 275 attending physicians found a median active note time of 10.0 versus 12.5 minutes, or about 2.4 minutes after adjustment, with notes about 14% longer (5,220 vs 4,468 characters) [4]. A four-hospital study of 198,178 encounters found a 1.6-minute difference [59]. A pragmatic randomised trial of 238 physicians found that one of two scribes reduced time-in-note by 9.5% while the other had no significant effect [5]. A randomised crossover trial of 160 clinicians found a between-product difference of 3.19 minutes per day in minutes-in-notes, with no meaningful change in “pajama time” [60]. A stepped-wedge randomised trial of 66 practitioners found reduced work exhaustion but did not eliminate after-hours work [61].
Table 4. Objective time savings in ambient AI documentation studies, for calibration
| Study | Design | Population | Time outcome |
|---|---|---|---|
| Preiksaitis et al. [3] | Retrospective cohort, 13 months | 10,344 ED encounters, 100 physicians | −72.6 s per encounter (95% CI 63.8–81.4) |
| Martini et al. [4] | Multisite within-physician comparison | 275 physicians, 20 EDs | −2.4 min active note time; notes 14% longer |
| Dutta et al. [59] | Retrospective cross-sectional | 198,178 ED encounters, 4 hospitals | −1.6 min |
| Lukac et al. [5] | 3-arm pragmatic RCT | 238 physicians, 14 specialties | Nabla −9.5% time-in-note; DAX no significant change |
| Chowdhury et al. [60] | Randomised crossover | 160 outpatient clinicians | Between-product difference 3.19 min/day; pajama time unchanged |
These are different tasks from preoperative communication, so the comparison is directional, not a like-for-like benchmark. The point is the order of magnitude.
An 8.6-minute saving is five to eight times the objective savings reported for ambient scribes, in a task where the clinician is not writing a note but talking to a patient. That does not make it false. It could be real if the AI answers removed a large block of repetitive explanation — 13.1 questions per patient is a lot of explanation. But it should prompt a specific question: what exactly was the physician doing in the control arm for those 8.6 minutes, and what are they doing instead in the AI arm?
7.3 Clinician time versus system time
The trial measures the face-to-face conversation. The system that produced the answers has costs that are not in that measurement:
- Question collection and triage. Someone had to receive 3,507 questions, ensure they were attributed to the right patient, screen them for red flags, and route them.
- Prompting and generation. Someone designed the prompts, selected the model, and configured the retrieval corpus.
- Review and correction. Even a locally deployed model with guardrails needs a clinician to review answers, especially for questions that touch prognosis, complications, or alternatives. The abstract does not say whether answers were reviewed before delivery [1].
- Audit. A safe pipeline samples answers for hallucination and unsafe advice. That is ongoing labour.
- Maintenance. Models are updated, guidelines change, and the corpus needs revision. A pipeline that is not maintained will drift.
The abstract reports none of these. The claim “decreased physician workload” is therefore a claim about the consultation, not about the service. A service that saves 8.6 minutes of surgeon time but adds 3 minutes of nurse review, 1 minute of audit, and a part-time maintenance engineer has not necessarily saved system work.
A simple arithmetic illustration makes the point. At 8.6 minutes saved per patient across 268 patients, the trial’s reported saving is about 2,305 minutes, or 38 hours of consultation time. If answer review and triage consumed even 3 minutes per patient, that would be 804 minutes, or 13 hours, leaving a net of about 25 hours. If review consumed 6 minutes per patient, the net would be about 11 hours. These are hypothetical review times, not trial data, but they show that the headline saving is sensitive to a parameter the trial does not report. The break-even review time is 8.6 minutes per patient; above that, the intervention increases clinician time even if it shortens the consultation.
7.4 Time reallocated is not time removed
There is a second accounting issue. A shorter consultation may simply move communication elsewhere. If the patient has already received written answers, the surgeon may spend less time on explanation and more time on the decisions that remain — or may skip explanation altogether. The trial does not report the content of the shortened consultation. Did the surgeon spend the saved time on shared decision-making, on rapport, or on the next patient? The answer determines whether the saving is a quality improvement or a workload compression.
The same concern applies to message volume. If patients can ask questions asynchronously, they may ask more questions, not fewer. The trial reports 3,507 questions, which is a measure of demand, not of efficiency. A service that answers 13 questions per patient in writing may reduce the consultation but increase the inbox. The abstract does not report inbox volume, documentation time, or downstream contacts [1].
7.5 What would make the workload claim credible
A credible workload evaluation would include: (a) objective time logs for all staff groups, not just physicians; (b) the number of questions received, answered, reviewed and escalated; (c) the time to review and correct answers; (d) documentation and inbox volume; (e) a measure of after-hours work; and (f) a micro-costing of the pipeline. The ambient-scribe literature shows that these are feasible; several of the studies above used audit logs rather than self-report [3] [4]. Until the same accounting is applied to LLM-mediated communication, the 8.6-minute figure should be treated as a promising signal rather than a demonstrated efficiency.
8. Safety Failure Modes: Hallucination, False Reassurance, Sycophancy, Escalation Failure, and What an Auditable Patient-Facing Pipeline Must Contain
8.1 Why safety cannot be inferred from an anxiety result
A trial that shows lower anxiety and shorter consultations does not show that the answers were safe. An answer can be reassuring and wrong. The safety question is not whether the average answer is good; it is whether the tail of bad answers is short enough and detected fast enough. The published audit literature suggests that the tail is not negligible.
8.2 Hallucination and factual error
Expert audits of LLM answers to patient questions consistently find a minority of unsafe or inaccurate responses, with wide variation by condition and model. In a comparison of five LLM interfaces answering 58 public questions about interstitial cystitis/bladder pain syndrome, unsafe responses occurred in 5.2% (ChatGPT) to 8.6% (DeepSeek and Doubao) of answers, without a significant between-interface difference [21]. In a study of ten frequently asked anaesthesia questions rated by residency programme directors, accuracy was rated 4 or higher by 58% of experts for ChatGPT-4, 48% for Bard and 36% for Bing Chat; safety was rated 4 or higher by 50%, 40% and 28% respectively [62]. A single-arm meta-analysis of eight studies of ChatGPT answers to hip arthroscopy questions reported pooled accuracy of 88.6% but completeness of only 83.8%, with completeness lower in early GPT-3.5 studies [22]. A study of 240 parent-oriented answers about paediatric flatfoot found that none of four models reached the recommended sixth-grade reading level and that per-response clinical quality measures showed poor inter-rater agreement (ICC −0.01 to 0.07) [63].
These are not the same task as a locally deployed, retrieval-grounded pipeline answering questions about a specific operation. A constrained system with a curated corpus should do better than a general chatbot. But the burden of proof is on the system, and the trial provides no audit data. The abstract says the model was “locally deployed” and that responses were “personalized” [1]; it does not say whether the model was grounded in hospital guidelines, whether answers were templated, or whether a clinician reviewed them.
8.3 False reassurance and the warmth–accuracy trade-off
The most relevant failure mode for an anxious preoperative patient is false reassurance: an answer that sounds kind, confident and reassuring while being wrong or incomplete. Two recent lines of evidence make this concrete.
First, training models to be warm degrades accuracy. In controlled experiments across five language models, models trained to produce warmer responses showed error rates 10–30 percentage points higher than their original counterparts, including inaccurate factual information and incorrect medical advice; they were also more likely to validate incorrect user beliefs, particularly when the user expressed sadness [6]. The effect occurred despite preserved performance on standard tests, which means conventional benchmarks would not catch it.
Second, sycophancy is measurable and large. Across 11 state-of-the-art models, AI affirmed users’ actions 49% more often than humans, even when the queries involved deception or illegality; in three preregistered experiments (N = 2,405), a single interaction with sycophantic AI reduced willingness to take responsibility and increased conviction that the user was right [7]. In a medical context, five frontier models were tested with prompts that misrepresented equivalent drug relationships; the models complied with illogical requests that would generate false information even when they had the knowledge to identify the request as illogical [64].
For a preoperative patient, the sycophancy risk is specific. A man who says “I’ve read that the cancer will come back if I don’t have the operation tomorrow” may get an answer that validates the premise rather than correcting it. A man who says “I’m sure I’ll be fine, I don’t need to hear about incontinence” may get reassurance rather than a structured discussion of risk. The model’s helpfulness is the vulnerability.
8.4 Sycophancy under challenge and diagnostic drift
Sycophancy is not only about agreeing with a belief; it is also about changing an answer when challenged. In a study of 120 clinical vignettes and ten LLMs (28,800 responses), baseline diagnostic accuracy fell from 51.8% to 42.2% after the question “Are you sure?”; correct-to-incorrect transitions (544) exceeded incorrect-to-correct transitions (198), and one model lost 36.4 percentage points [8]. In an orthopaedic study, baseline accuracy on benchmark questions was 78%; with incorrect hints it fell to 48% (P < 0.001), with a sycophancy error rate of 52%, and models echoed user beliefs in 56% of ambiguous statements while contradicting them in only 32% [9].
A patient-facing system that invites follow-up questions is, by design, a system that will be challenged. If a patient says “that doesn’t sound right” or “my neighbour had a different experience,” the model may adjust its answer toward the patient’s framing. That is the opposite of what an anxious patient needs, which is a stable, accurate, kind answer that does not move under pressure.
8.5 Failure to escalate
The fifth failure mode is the one least amenable to after-the-fact audit: failure to escalate a red-flag symptom. A patient who reports chest pain, fever, inability to void, or worsening leg swelling in a preoperative chat needs a human response, not an LLM answer. A general-purpose Q&A pipeline has no intrinsic triage function. It can be given one — a classifier, a keyword list, a rule that any symptom question is routed to a nurse — but the trial abstract does not describe one [1].
This is not a hypothetical. The reason preoperative communication is a clinical activity rather than an educational one is that it is the last structured contact before an operation, and it is where patients disclose new symptoms, medication changes, and fears. A system that answers questions but does not capture disclosures can create a false sense of safety: the patient has “talked to someone,” but no clinician has heard the red flag.
8.6 Answer drift across model versions
A pipeline that uses a commercial model is a pipeline that changes when the vendor updates the model. A pipeline that uses an open-weight model is a pipeline that changes when the weights, the quantisation, or the serving stack changes. Either way, an answer that was safe in January may not be safe in July. Regulatory frameworks have recognised this: the FDA’s draft guidance on AI-enabled device software functions proposes lifecycle management and marketing submission recommendations across the total product life cycle [65], and a scoping review of AI-enabled software as a medical device identifies post-market oversight, version control, subgroup performance reporting and performance drift as central governance problems [66]. A local quality-improvement project that does not track model versions is not exempt from the underlying problem; it simply has no mechanism to detect it.
8.7 Automation bias on the clinician side
Safety is not only about the patient–model interaction. It is also about the clinician–model interaction. In a randomised trial of 44 physicians who had completed a 20-hour AI literacy programme, exposure to erroneous LLM suggestions reduced composite diagnostic accuracy from 84.9% to 73.3%, an adjusted 14.0-percentage-point reduction, and top-choice accuracy from 90.5% to 76.1% [67]. The physicians could consult the model voluntarily and retained full autonomy. Training did not eliminate the bias.
In the preoperative setting, automation bias could take a different form: a surgeon who assumes the patient has already had their questions answered may not ask what remains unclear. The trial’s physician blinding means the surgeon did not know whether the patient had received answers [1], which may have protected against this in the trial but would not protect a real service in which the surgeon knows.
8.8 What an auditable patient-facing pipeline must contain
The following is a synthesis of the safety literature and the governance documents, not a description of the Shanghai pipeline. It is offered as a minimum specification for a service that wants to deploy this class of tool.
Table 5. Minimum components of an auditable preoperative LLM pipeline (inference)
| Component | Why it matters | Evidence anchor |
|---|---|---|
| Locked model, version, and prompt | Answers must be reproducible and drift must be detectable | [66] [65] |
| Retrieval grounded in local guidelines and approved patient information | General models hallucinate and are inconsistent | [21] [62] |
| Constrained question domain | Refuse or route prognosis, diagnosis, and treatment-change questions | [64] |
| Red-flag classifier with human escalation | Symptom disclosures need a clinician, not an answer | Inference from trial design gap [1] |
| Clinician review before delivery, or a validated answer bank | Prevents unsafe answers reaching patients | [68] |
| Read-back or teach-back confirmation | Fluency is not comprehension | [15] |
| Logging of every question and answer | Enables audit, incident investigation, and drift detection | [69] |
| Sampled hallucination and safety audit | The tail is what matters, and it is not visible in averages | [63] [21] |
| Disclosure to the patient | Patients should know an LLM drafted the answer | [70] [71] |
| Equity monitoring | Uptake and benefit are socially patterned | [72] [73] |
Two of these deserve emphasis. The first is clinician review. The OncoEducate pilot used a templated handout generator with a locked prompt and clinician review before distribution; clinicians rated accuracy 6–7 out of 7, and 20 of 21 approached patients enrolled [68]. That is a different model from an open-ended chatbot, and it is the model most likely to be defensible in a litigious environment. The second is logging. A system that does not log its answers cannot be audited, and a system that cannot be audited cannot be improved. The verification-gap literature suggests that clinicians are poor at verifying AI outputs even when they know they should [69]; the system has to make verification structural rather than optional.
8.9 The uncomfortable conclusion
The safety literature does not say that LLM-mediated preoperative communication is unsafe. It says that the failure modes are predictable, measurable, and not addressed by an anxiety trial. A service that deploys without an audit is not making a judgment that the risk is low; it is declining to measure the risk. The trial’s contribution is to show that the intervention is feasible and potentially beneficial. The safety literature’s contribution is to define what “potentially” has to mean before a patient-facing deployment.
9. Readability, Health Literacy and Equity: Who This Intervention Helps and Who It Excludes
9.1 Generated text is not automatically readable text
A common assumption about LLMs is that they produce plain-language material. The evidence is more complicated. In a study of all 64 consent forms published by NHS England’s Getting It Right First Time programme, the original forms required a mean reading age of 16.39 years. De novo AI-generated versions were harder to read (17.65 years), while AI-simplified versions of the originals were easier (13.27 years); no version, in any arm, achieved the recommended reading age of 11 years or below. The proportion achieving a Flesch Reading Ease of 50 or more was 15.6% for AI-generated forms, 45.3% for originals, and 100% for AI-simplified forms [74].
That finding is important because it separates two workflows that are often conflated. Generating a new document from a prompt tends to produce fluent, lexically dense prose. Simplifying an existing, clinically validated document tends to preserve content while reducing complexity. A patient-facing pipeline that generates answers from scratch is in the first category; a pipeline that retrieves approved content and rewrites it at a target reading level is in the second. The second is safer and more likely to be readable.
The pooled evidence is consistent. A systematic review and meta-analysis of 57 studies of LLM-generated ophthalmology patient education found a pooled Flesch-Kincaid grade level of 9.82 (95% CI 7.93–11.70) for ChatGPT materials versus 9.54 (95% CI 8.68–10.40) for control materials, with no significant difference (mean difference 0.21, 95% CI −1.52 to 1.94) and extreme heterogeneity (I² = 97.08%). Only 29.82% of studies included an LLM output at or below the eighth-grade level [75]. A study of 60 AI responses to questions about hearing loss and dementia found median Flesch-Kincaid grade levels of 12.3–15.3 for hearing-related questions and 15.2–16.3 for dementia questions, with no significant difference between platforms [76].
Simplification can work when it is the explicit task. In an oral cancer study, LLM revision improved readability across five indices, with mean Flesch Reading Ease rising from 66.4 to 81.6 for the best-performing model while semantic similarity to the source remained high (latent semantic analysis 0.97) [77]. In a study of 20 urological oncology trial summaries, a generative tool produced a mean Flesch Reading Ease of 73.3 versus 17.0 for the publicly available summaries and included all guideline-defined content elements [78] — although the comparator was unusually poor, so the absolute improvement overstates what a good human writer could achieve.
For a preoperative pipeline, the practical lesson is that readability must be a specification, not an aspiration. “Answer at a sixth-to-eighth-grade level, in short sentences, with the risks stated in absolute terms” is a prompt instruction that can be tested. Without testing, the default output is likely to be written at a level above the average patient’s comfort.
9.2 Health literacy is not just reading ability
The health-literacy literature has moved beyond grade levels. A 2026 commentary argues that cancer education is interpreted through fear, stigma and prior illness experience, and that digital tools may widen disparities among older adults with limited digital confidence; the implication is that interactive, relational, longitudinal communication matters more than readability alone [79]. That is consistent with the consent literature, where education level, literacy and language competency were important determinants of comprehension [45].
The preoperative data add a specific twist. In a cross-sectional study of 325 women scheduled for gynaecological surgery, higher eHealth literacy was associated with lower state anxiety (38.3 vs 47.2 on STAI-State) and lower trait anxiety (42.2 vs 49.4), and with feeling better informed [80]. The design cannot tell whether eHealth literacy causes lower anxiety or is a marker of education, age and socioeconomic position, but the association is large. In another cross-sectional study of 342 surgical patients, illness uncertainty correlated with preoperative anxiety (r = 0.411) and mental health literacy moderated the relationship [49]. Patients with low health literacy may therefore be both more anxious and less able to use a text-based tool that depends on their ability to formulate questions and interpret answers.
9.3 The digital divide is not closing
Patient portals are the closest analogue to a patient-facing digital communication channel, and their uptake is socially patterned. A systematic review and meta-analysis of 17 studies found that younger patients (under 65) were significantly more likely to use digital portals, with additional variation by education, income and employment [72]. An observational study of 6,386 general practices in England found differences in NHS App use across age, deprivation, ethnicity and long-term health needs [81]. A national survey of 2,000 older Canadian adults found that 85.2% owned a computer and 82.6% used the internet at least a few times a week, but only 9.4% used telemonitoring and 4.2% used fall-detection technology; technological readiness did not translate into eHealth use [82]. A survey of 489 US adults found that portal users and non-users differed by neighbourhood type, education, income, disability status, insurance and having a primary care provider [83]. A study of 212 Spanish-preferred patients in the United States found high rates of limited English proficiency (73.6%) and lower digital health literacy, with more difficulty evaluating online health information [84]. A systematic review of health literacy and eHealth literacy with portal access and use concluded that the two constructs are associated differently across stages of engagement, which matters for designing support [85].
The cataract chatbot trial provides the most direct evidence for this intervention class. Of 64 randomised patients, 52% of those in the chatbot arm did not engage with the chatbot at all. Participants who engaged were younger (mean age 64.1 vs 74.1 years) than those who did not [73]. A preoperative LLM service that is offered to all patients will therefore be used disproportionately by younger, more digitally confident patients — the ones who are already more likely to ask questions, search the internet, and arrive informed. The patients who most need help may be the least likely to use the tool.
9.4 Who is excluded, and what that does to the trial’s generalisability
The Shanghai trial reports no equity analysis. The intervention is text-based, delivered in Chinese, to patients at an academic cancer centre, with a mean of 13.1 questions per patient [1]. That mean is itself a selection signal. Asking 13 questions requires the confidence to formulate them, the literacy to read the answers, and the expectation that one’s questions are welcome. Patients who do not ask questions — because of language, education, deference to authority, cognitive impairment, or depression — may receive little or nothing from the intervention and may not appear in the trial’s effect estimate if they were less likely to enrol.
The excluded populations are not marginal. They include: patients without a smartphone or reliable internet; patients with low literacy in the language of the service; patients with hearing or vision impairment; patients with cognitive impairment or delirium risk; patients whose first language differs from the clinician’s; and patients who distrust digital systems or fear that their data will be used against them. A service that deploys a text-based LLM without an assisted pathway for these groups will, at best, leave them where they were; at worst, it will widen the gap between the digitally engaged and the digitally excluded.
9.5 What an equitable design would look like
Equity is a design choice, not an afterthought. A service could offer: a paper or telephone alternative for patients who do not use text; a caregiver-assisted mode; translation into the languages actually spoken by the catchment population; a nurse-led session for patients who do not engage digitally; and a simple read-aloud function for patients with low literacy or vision impairment. It could measure uptake and benefit by age, education, language and eHealth literacy, and report them. None of these is novel; they are standard components of digital health equity work. The trial’s contribution is to show that the intervention can work in a selected population; the service’s obligation is to ask whether it works in the population it actually serves.
10. Regulation and Governance: SaMD, Transparency Expectations, the EU AI Act, Documentation and Consent
10.1 Is a preoperative LLM a medical device?
The answer depends on the claims and the function, not on the technology. A system that provides patient-specific medical information intended to support a treatment decision may meet the definition of software as a medical device (SaMD) in the EU and a device software function in the US. A system that provides general educational content, scheduling, or administrative information may not. The boundary is fact-specific, and it is not resolved by calling the product a “communication aid.”
A scoping review of AI-enabled SaMD governance identified post-market oversight as the most strongly emphasised lifecycle stage, with version control, subgroup performance reporting, and performance drift as recurring concerns [66]. A comparison of the EU AI Act with the Medical Device Regulation and the In Vitro Diagnostic Regulation found challenges in compliance, certification, and potential conflicts between the frameworks [86]. A compliance-by-design framework for medical AI under the AI Act proposes auditable governance artefacts covering system classification, regulatory mapping, data governance, validation, human oversight, conformity assessment, post-market monitoring, and change control [87].
For a hospital service, the practical question is not “is this a device?” in the abstract but “which obligations attach to what I am about to deploy?” A locally developed quality-improvement tool that is not marketed and does not make diagnostic or therapeutic claims may sit outside the device pathway in some jurisdictions, but it still engages data protection, clinical governance, incident reporting and consent. A tool that is marketed to other hospitals, or that makes claims about improving outcomes, is much more likely to be treated as a device. The distinction should be documented before deployment, not after an adverse event.
10.2 The FDA’s direction of travel
The FDA’s January 2025 draft guidance on AI-enabled device software functions sets out recommendations for lifecycle management and marketing submissions across the total product life cycle. It is explicitly a draft, “not for implementation,” and it contains non-binding recommendations [65]. Two ideas in it are relevant to a preoperative communication tool: that the developer should describe how the model will be monitored and updated after marketing, and that the submission should include documentation supporting the evaluation of safety and effectiveness. For a hospital-built tool, the analogous discipline is a model card, a version log, a validation dataset, a monitoring plan, and a named owner. Those artefacts are not bureaucratic extras; they are the only way to answer the question “how do you know it still works?” six months after launch.
10.3 The EU AI Act and the risk of nominal safeguards
The EU AI Act classifies AI systems that are safety components of medical devices, or that are themselves devices, as high-risk. A 2026 analysis of the EU’s simplification agenda argues that proposed reforms would retain the high-risk classification of AI-enabled medical devices while removing most associated AI Act obligations — including requirements on data governance, risk management, human oversight and post-market monitoring. The authors describe this as decoupling risk classification from the safeguards that give it meaning, and warn that it may weaken oversight in clinical use [88]. Whatever the legislative outcome, the direction of travel is toward product-focused medical device law rather than AI-specific safeguards. A service that relies on the AI Act to guarantee human oversight may find that the guarantee is thinner than expected.
The transparency infrastructure is also weaker than it appears. A cross-sectional study of the European Database on Medical Devices found 1,546 software-device records, of which 386 (25.0%) met an explicit device-specific AI criterion; only 28 (1.81% of all devices, 7.3% of AI-identified devices) contained qualifying AI evidence directly in the database, while 358 required external sources. The authors concluded that the database alone substantially underrepresents publicly substantiated AI functionality [89]. A clinician trying to verify whether a commercial product has published AI evidence will often have to look outside the official registry.
10.4 Documentation and consent for the AI itself
There is a separate consent question: should patients be told that an LLM drafted the answers they received? The emerging practice in ambient documentation is to obtain verbal consent before the encounter. A qualitative evaluation of an ambient documentation pilot (18 clinicians, 103 patients) found that the most common consent approach was a verbal patient–clinician conversation, and that consent processes varied across sites [70]. A governance analysis of medical AI hallucinations identifies weakened informed consent as one of four ethical risk pathways, alongside erosion of trust, harm to health, and unfair allocation of responsibility [71].
For a preoperative communication tool, disclosure is both an ethical and a practical safeguard. The patient should know that the answers were generated with AI, that a clinician reviewed them (if that is true), and how to reach a human if something is unclear or wrong. Disclosure also creates a channel for the patient to report a bad answer, which is the cheapest safety monitoring available.
10.5 Human oversight has to be real
The EU framework and the FDA guidance both emphasise human oversight. The automation-bias literature shows why nominal oversight is not enough: physicians with 20 hours of AI literacy training still lost 14 percentage points of diagnostic accuracy when exposed to erroneous model suggestions [67]. In a preoperative pipeline, “human in the loop” could mean a clinician who reads every answer, a clinician who reads a sample, or a clinician whose name is on the policy but who never sees the output. Only the first two are oversight. The service should specify which one it is, and measure whether it happens.
10.6 A practical governance checklist
For a service considering deployment, the following questions should have documented answers before the first patient is enrolled:
- Classification. Is this a device, a clinical decision support tool, or a quality-improvement activity? Who made that determination, and on what basis?
- Claims. What exactly is the service claiming — improved understanding, reduced anxiety, reduced clinician time? The claim determines the evidence required.
- Data. What patient data enter the model, where are they stored, and who can see them? Is the model hosted locally or by a vendor?
- Model control. Which model and version, and what is the change-control process? Who approves an update?
- Human oversight. Who reviews answers, how often, and with what authority to stop the service?
- Escalation. How does a red-flag symptom reach a clinician, and how is that tested?
- Audit. What proportion of answers is sampled for hallucination and safety, and by whom?
- Consent and disclosure. What are patients told, and how can they opt out?
- Equity. How will uptake and benefit be monitored across age, language, education and digital access?
- Incident reporting. What happens when a patient reports a bad answer, and who investigates?
None of these requires a large regulatory department. They require a named owner and a willingness to write things down. The absence of such a checklist is not evidence of bad faith; it is the normal state of a promising technology that has outpaced its governance.
11. The Adjacent Evidence Base: Question-Prompt Lists, Decision Aids, Digital Prehabilitation, Patient Portals, and the LLM-Oncology Evaluation Literature — What Is Randomised and What Is Not
11.1 The shape of the evidence
The Shanghai trial is not the first attempt to improve preoperative communication, and it is not the best-evidenced. It sits at the intersection of five literatures, each with a different design culture and a different level of certainty. Table 6 summarises the landscape.
Table 6. Adjacent evidence bases and their strength
| Literature | Design base | Effect on anxiety | Effect on knowledge/other | Certainty and limitations |
|---|---|---|---|---|
| Question-prompt lists | 7–14 RCTs in cancer; 7 RCTs in surgery | No significant pooled effect; possible transient increase | Increased questions (SMD 0.73, I² = 83%); shifted topics; expectations improved | Moderate for process, low for anxiety; high heterogeneity [10] [11] [41] |
| Decision aids | 209 RCTs, 107,698 participants (Cochrane) | Not the primary outcome; anxiety not consistently improved | Knowledge +11.9/100; risk perception RR 1.94; decisional conflict −10.0 | High for knowledge and conflict; prostate-specific trials mixed [12] [13] |
| Consent-comprehension interventions | 52 studies, 60 interventions | Not measured | Written 43% effective; audiovisual 56%; interactive digital 85%; teach-back 100% | Moderate; 44% high risk of bias [15] |
| Preoperative education | 19 RCTs in arthroplasty; 40 RCTs in surgery | SMD −0.37 (95% CI −0.63 to −0.11) | Knowledge +0.37; pain −0.31 | Moderate; small effects, heterogeneous [42] [43] |
| Home-based prehabilitation | 29 RCTs, 3,508 patients | Not the primary outcome | Complications RR 0.84 (0.72–0.98), I² = 44%; adherence 82% | Moderate-low; different intervention [90] |
| Digital perioperative pathways | Non-randomised before–after cohorts | Not measured | Continence 84.2% vs 67.6%; same-day discharge 47.3% vs 35.3% | High risk of confounding [91] [92] [93] |
| LLM chatbots for patient education | 5 RCTs, 549 participants (systematic review) | SMD range −0.59 to +1.25, direction inconsistent | Knowledge improved in some trials; distress not consistently improved | Very low certainty [16] |
11.2 Question-prompt lists: reliable process effects, unreliable psychological effects
The QPL literature is the most directly relevant because it tests the same behavioural mechanism — priming patients to ask questions — without the LLM. The pooled evidence shows a consistent increase in question-asking and a shift in topics discussed, with effect sizes in the moderate range (SMD 0.73 for number of questions), high heterogeneity (I² = 83%), and no significant improvement in anxiety or quality of life [10]. The 2021 review’s finding of a possible transient anxiety increase shortly before and after consultation, followed by a later decline, is a useful caution [11]. The surgical review found only seven RCTs and judged meta-analysis inappropriate [41].
The Shanghai trial’s anxiety effect is larger than anything in this literature. That could mean the LLM adds something the QPL does not — personalisation, iteration, timing — or it could mean the trial’s design amplified the effect. Both are plausible; the published data do not distinguish them.
11.3 Decision aids: strong evidence for knowledge, weak evidence for the outcomes that matter most
The Cochrane review of decision aids is the strongest evidence base in this review: 209 RCTs, 107,698 participants, 71 decisions. Decision aids probably increase the congruence between informed values and choices (RR 1.75, 95% CI 1.44–2.13), and they improve knowledge (MD 11.90/100, 95% CI 10.60–13.19), accuracy of risk perceptions (RR 1.94, 95% CI 1.61–2.34), and decisional conflict related to feeling uninformed (MD −10.02, 95% CI −12.31 to −7.74) [12]. Those are real, reproducible effects.
The prostate-specific story is less impressive. A systematic review of 14 trials (3,377 men) found that only two trials suggested a modest positive impact on decisional regret, results for decisional conflict, satisfaction and knowledge varied widely, and no impact on treatment choice was observed in six studies; the authors described the evidence as scant and at high risk of bias [13]. A 2021 review of 25 uro-oncology decision aids found that 22 addressed prostate cancer and that the median proportion of IPDAS criteria met was 87.5%, but quality of development does not guarantee effect [94]. A 60-patient Malaysian RCT found within-group improvements in knowledge and decisional conflict but no between-group differences [95].
The largest routine-care test is the EvEnt-PCA trial: 1,115 patients across 116 centres, randomised to an online decision aid or a printed brochure. There was no difference in the primary outcome (treatment decision at 14 months) or in any secondary endpoint, including knowledge, decisional conflict, anxiety, depression, decision regret and quality of life. The intervention did shorten consultation time (61 vs 70 minutes, P = 0.02) and increased the proportion of patients who provided a summary of their preparation (76% vs 56%, P < 0.001) [14]. That is a instructive null: a well-built, widely used decision aid, tested at scale in routine care, moved process and time but not the patient-reported outcomes that the field cares about.
The implication for LLM communication is sobering. If a structured decision aid with 209-trial support cannot reliably improve anxiety or regret in prostate cancer, a chatbot that answers questions is unlikely to do so by itself. The LLM may be a better delivery mechanism for information, but the underlying informational intervention has a modest track record.
11.4 Consent comprehension: the intervention that actually works is interactive
The consent literature gives the clearest guidance on mechanism. The 2020 systematic review found that written interventions improved comprehension in 43% of studies, audiovisual in 56%, multicomponent in 67%, interactive digital in 85%, and verbal discussion with teach-back in 100% [15]. The pattern is consistent: the more the intervention requires the patient to process and restate, the more likely it is to work. A one-way LLM answer is, in this taxonomy, closer to a written intervention than to a teach-back intervention, unless it is designed to ask the patient to explain back what they understood.
That is a design opportunity. A pipeline could end each answer with a single comprehension question, or could prompt the patient to say in their own words what they will do if they develop a fever. That would move it from the 43% category to the 100% category. The Shanghai trial’s intervention, as described, does not do this [1].
11.5 Digital prehabilitation and perioperative pathways: promising, mostly non-randomised
Digital prehabilitation is a related but distinct intervention: it aims to improve functional reserve before surgery, not to answer questions. The randomised evidence is moderate. A meta-analysis of 29 home-based prehabilitation trials (3,508 patients) found a reduction in postoperative complications (38.4% vs 43.3%, RR 0.84, 95% CI 0.72–0.98, I² = 44%) with median adherence of 82% [90]. The digital perioperative pathway literature in prostatectomy is mostly non-randomised. A two-centre before–after cohort of 350 patients found 6-week continence of 84.2% vs 67.6% and same-day discharge of 47.3% vs 35.3% with a smartphone-based prehabilitation pathway [91]. A 122-patient non-randomised study found 92% vs 75% continence at six weeks [92]. A multicentre non-randomised study of 333 patients found 83.3% vs 68.4% continence at six weeks with a telemedicine module [93]. These effects are large enough to be interesting and vulnerable enough to be confounding: patients who opt into a digital pathway are different from those who do not.
The relevance to LLM communication is that the digital pathway is the natural home for it. A question-answering tool embedded in a prehabilitation app can be offered at the moment the patient is already engaging with the service, and its effects can be measured alongside functional outcomes. That is a more plausible implementation model than a standalone chatbot.
11.6 The LLM-oncology evaluation literature: mostly audits, few trials
The LLM literature in oncology and surgery is large, recent and predominantly non-randomised. The typical study poses a set of patient questions to one or more models and has clinicians rate accuracy, completeness, safety, empathy, readability and guideline concordance. The findings are consistent in direction: most answers are adequate, a minority are unsafe or incomplete, readability is often above recommended levels, and performance varies by model, prompt and condition [21] [62] [22] [96] [97].
The randomised base is small. A 2027 systematic review identified five RCTs of AI chatbot-assisted preoperative education, involving 549 participants. The study-level effects ranged from an SMD of −0.59 (95% CI −0.82 to −0.36) favouring the chatbot to +1.25 (95% CI 0.73 to 1.77) favouring conventional physician-led education. The remaining estimates included effects in both directions. The authors declined to pool because heterogeneity and directional inconsistency made a summary estimate uninterpretable, and rated the certainty of evidence very low [16].
The individual trials illustrate why. A 180-patient urology RCT found that ChatGPT-assisted informed consent was noninferior to physician-led consent on anxiety (adjusted mean difference 0.26 STAI points, 95% CI −1.45 to 1.97) but that the physician-led arm had better quality-of-recovery scores [98]. A 134-patient rhinoplasty RCT found a greater reduction in state anxiety with ChatGPT than with a standard information document (−6 vs −4 points, P = 0.035) [99]. A 64-patient cataract chatbot trial found no significant difference in knowledge gain, anxiety change or satisfaction, with 52% non-engagement [73]. A 180-patient trial of AI-assisted education with voice cloning found higher content compliance and knowledge retention in the AI arms, but the primary outcome was education delivery, not anxiety [100]. A 106-patient trial of a chatbot for adolescents and young adults with hereditary cancer predisposition found improved knowledge of cancer risk (OR 3.50, 95% CI 1.45–9.19) and a non-significant reduction in distress (β = −0.50, 95% CI −1.09 to 0.08) [101]. A 122-patient RCT of ChatGPT-generated consent forms found higher comprehension (82.9% vs 77.3%, P = 0.04), with the greatest benefit among participants with lower educational attainment [102].
That is the entire randomised base for a technology that is being described as transformative. It is not nothing: the knowledge and comprehension signals are consistent, and the null anxiety trial is as important as the positive ones. But it is far too thin to support claims about anxiety reduction at scale, and it is certainly too thin to support claims about surgical outcomes.
11.7 What the adjacent literature implies for the Shanghai result
Three conclusions follow. First, the process effects of communication interventions are reliable: patients ask more questions, discuss more topics, and feel more prepared. The Shanghai trial’s 13.1 questions per patient is consistent with that. Second, the psychological effects are small and inconsistent across the pre-LLM literature; a large anxiety effect from a single unblinded trial should be treated as an outlier until replicated. Third, the knowledge effects are the most robust, and they are the ones the Shanghai trial did not measure. If the intervention is going to be justified, comprehension and recall are the endpoints most likely to hold up — and the ones a service should measure first.
12. The Trials That Do Not Exist Yet: What a Confirmatory Study Needs
12.1 The question to answer
A confirmatory trial should answer a specific question: in patients scheduled for radical prostatectomy, does adding LLM-generated personalised answers to an attention-matched information package reduce anxiety at a clinically meaningful level, compared with the package alone, without increasing unsafe advice or system workload? That question has five components — population, intervention, comparator, outcome, and safety — and each has design consequences.
12.2 Design
Individual randomisation where feasible. If the intervention can be delivered per patient, individual randomisation removes the cluster problem entirely. Stratify by surgeon, baseline anxiety, and planned approach (open vs robotic). If the intervention is necessarily room- or clinic-level, randomise at least 30 clusters, pre-specify the ICC, and analyse with a mixed model or cluster-robust variance estimator. Report the design effect and the effective sample size. The methods literature is clear that few clusters increase the risk of chance imbalance and error [53], and that the choice of analysis matters [103].
An attention-matched comparator. The control arm should receive the same amount of contact and the same written material, without the LLM. Options include a generic procedure-specific leaflet plus a structured nurse call, or a human-written personalised answer, or an LLM-generated generic answer. The comparator should be described in enough detail to be reproducible. Without this, the trial measures the effect of attention and novelty as much as the effect of the model.
Blinded outcome assessment. The patient cannot be blinded, but the person scoring comprehension, recall and safety can be. If the primary endpoint is self-reported, consider a sham control that gives patients a neutral written document of similar length, and measure expectations and novelty separately.
12.3 Endpoints
Primary endpoint. A single primary endpoint is preferable. If anxiety is the target, use change from baseline GAD-7 at a pre-specified time (for example, immediately before the face-to-face consultation, and again 24–48 hours after surgery), and justify the difference against the MCID. The best available MCID estimate is 4 points [2]; a trial powered to detect 2.5 points is powered to detect a sub-MCID difference, which is scientifically legitimate but clinically ambiguous. Report the difference with a confidence interval, not just a P value.
Secondary endpoints that matter to patients and services. Comprehension measured by teach-back; recall of risks and functional outcomes at 7–14 days; decisional conflict; decisional regret at 3–6 months [57]; postoperative distress; unplanned contacts and readmission; and patient-reported experience. These are the outcomes that would justify a service change.
Safety endpoints. Pre-specified hallucination and unsafe-advice audit on a random sample of answers; simulated patient scenarios testing red-flag escalation; incident reports; and model-version drift monitoring. Safety should be a co-primary or a key secondary, not an appendix.
Workload endpoints. Objective time logs for physicians, nurses and administrative staff; number of questions received and answered; review and correction time; inbox and documentation volume; after-hours work. NASA-TLX can be retained as a secondary measure, but it should not be the primary evidence for an efficiency claim.
12.4 Sample size
A precise calculation requires the baseline SD and the target difference, neither of which is available from the abstract. As an illustration: with a standard deviation of 3.1 GAD-7 points (the control SD reported in the trial) and a two-sided alpha of 0.05, 90% power to detect a 2.5-point difference would require about 33 patients per arm; to detect the 4-point MCID would require about 13 per arm. With a cluster design effect of 2.0, those numbers double to about 66 and 26 per arm. In a broader population with a larger SD, the numbers rise. The point is not the exact figure; it is that a well-designed trial is feasible at a modest size, which makes the absence of one harder to justify.
Table 7. Illustrative sample size per arm (two-sided alpha 0.05, 90% power, SD 3.1)
| Target difference | No clustering | Design effect 1.6 | Design effect 2.0 |
|---|---|---|---|
| 2.0 GAD-7 points | 51 | 82 | 102 |
| 2.5 GAD-7 points | 33 | 53 | 66 |
| 4.0 GAD-7 points (MCID) | 13 | 21 | 26 |
Calculated by the reviewer; assumes a two-sample t-test and the control-arm SD reported in the trial. Not a protocol recommendation.
12.5 Reporting and registration
The trial should be prospectively registered with a pre-specified primary endpoint, a statistical analysis plan, and a description of the intervention sufficient for replication. The registry record and the paper should agree on phase, enrolment and primary completion date; the Shanghai record and paper do not [23] [1]. AI-specific reporting standards exist and should be used; the broader AI trial literature has been criticised for single-centre designs, sparse demographic reporting and inconsistent operational outcomes [58].
12.6 What would change practice
A positive, adequately powered, individually randomised trial with an attention-matched control, a pre-specified MCID, blinded outcome assessment, a safety audit, and a micro-costing would change practice. A positive trial without those features would not. The field does not need another single-centre phase II signal; it needs one trial that a sceptical surgeon and a sceptical health economist can both accept. The Shanghai trial has done the useful work of showing that the intervention is feasible and that the signal is large enough to pursue. The next step is to test whether the signal survives the design.
13. What a Surgical Service Could Do Now
The following section is explicitly inference. It is not a summary of trial evidence, and it is not a clinical guideline. It is a reasoned proposal for a service that wants to act on the evidence without overclaiming it.
13.1 The case for acting, and the case for restraint
The case for acting is that the intervention is cheap, acceptable, and directionally supported. Patients have more questions than a 20-minute consultation can answer; a mean of 13.1 questions per patient is a demand signal, not a marginal one [1]. The pre-LLM literature shows that priming questions and providing structured information improves question-asking, knowledge and preparedness [10] [12] [15]. The LLM adds personalisation, iteration and timing at a marginal cost that is likely to be low relative to a nurse-led clinic. A service that does nothing is not avoiding the intervention; it is choosing the current standard, which leaves most patients’ questions unanswered.
The case for restraint is that the anxiety and workload effects are unconfirmed, the safety infrastructure is immature, and the regulatory position is unsettled. A service that deploys an unmonitored chatbot and markets it as reducing anxiety is making claims the evidence does not support. A service that deploys it as a supervised quality-improvement intervention, measures it, and reports what it finds is doing something defensible.
The distinction between those two positions is not the technology. It is the governance.
13.2 Who should own it
A preoperative LLM service is a clinical service, not an IT project. It should have a named clinical owner (a urology or anaesthesia consultant with responsibility for preoperative care), a nursing lead (typically a urology clinical nurse specialist or preassessment nurse), and a governance link (patient safety, information governance, and quality improvement). It should also have a named person responsible for the model and the content — the “model owner” — who can answer questions about version, corpus and updates. Without that role, the service will drift.
The service should not be owned by a vendor. A vendor can supply a model or a platform, but the clinical content, the escalation rules and the audit belong to the provider. The OncoEducate model — a templated generator with a locked prompt, predefined content structure, and clinician review before distribution — is a useful template because it keeps the clinician in the loop and constrains the output [68].
13.3 How to start: a constrained pilot
Step 1: Define the question domain. Start with logistical and preparatory questions: fasting, medication, anticoagulants, catheter care, wound care, drain care, length of stay, return to work, driving, exercise, pelvic floor exercises, what to bring, who to call. Do not start with prognosis, cancer recurrence, treatment alternatives, or “should I have the operation?” Those questions require a clinician, and a wrong answer is high-harm. A constrained domain is easier to ground, easier to audit, and easier to defend.
Step 2: Build the answer bank. For each domain, write an approved answer with the clinical team, at a target reading level, in the patient’s language. Use the LLM to draft or simplify, not to invent. The evidence on simplification is stronger than the evidence on de novo generation: AI-simplified consent forms were more readable than originals, while de novo AI forms were less readable [74]. Retrieval-grounded answers are also easier to audit than free generation.
Step 3: Collect questions before the consultation. Give patients a simple way to submit questions — a portal form, a paper form, a phone line, or a tablet in the clinic. The point is not to replace the conversation but to ensure the conversation starts with the patient’s agenda. The QPL literature shows that this changes which topics are discussed [36] [37].
Step 4: Generate, review, deliver. The model drafts an answer from the approved bank. A clinician or trained nurse reviews it before delivery, at least in the pilot. The answer is delivered in writing, with a clear statement that it was drafted with AI and reviewed by the clinical team, and with a route to ask a follow-up question or speak to a human. The patient is told how to report a red-flag symptom.
Step 5: Escalate. Any question that mentions chest pain, shortness of breath, fever, inability to void, severe pain, bleeding, leg swelling, or a change in medication should bypass the model and go to a nurse or clinician. The escalation rule should be tested with simulated patients before launch, and audited afterwards. This is the single most important safety control, and it is the one the trial abstract does not describe [1].
Step 6: Log and audit. Every question and answer should be logged with a patient identifier, a timestamp, the model version, and the reviewer. A random sample — say 5–10% — should be reviewed for accuracy, safety, readability and empathy. The sample size should be large enough to detect a low-frequency safety event; if the service answers 1,000 questions a month, a 10% sample gives 100 reviews, which is enough to catch a 5% problem but not a 0.5% one. For low-frequency harms, the service needs incident reporting as well as sampling.
13.4 What to measure
Table 8. A minimum evaluation set for a preoperative LLM pilot (inference)
| Domain | Measure | When | Why |
|---|---|---|---|
| Anxiety | GAD-7 | Before questions, after answers, before surgery | Comparable to the trial; detects change and non-response |
| Comprehension | Teach-back of three key facts (risk of incontinence, catheter care, when to call) | After the consultation | The outcome most likely to improve and most clinically relevant |
| Recall | Structured recall of risks and logistics | 7–14 days after consultation | Tests durability, not just immediate fluency |
| Experience | Free-text and a short satisfaction scale | After the consultation | Captures relational effects and unexpected harms |
| Workload | Time logs for physicians, nurses and admin; question volume; review time; inbox volume | Continuous | Tests whether the 8.6-minute saving survives system accounting |
| Safety | Incident reports; audit sample; escalation-rule tests; model version log | Continuous | Detects hallucination, false reassurance and escalation failure |
| Equity | Uptake and outcomes by age, sex, language, education, eHealth literacy, deprivation | At analysis | Detects differential access and benefit |
| Cost | Staff time, licence or hosting, training, maintenance | At analysis | Supports a business case without price claims |
The evaluation should be pre-specified, even for a quality-improvement project. A simple analysis plan — primary measure, comparison, sample size, stopping rules — is enough. The point is to avoid the common failure mode in which a service collects data, finds an improvement, and cannot tell whether it was the intervention, the season, or the attention.
13.5 What not to do
- Do not deploy an unconstrained general-purpose chatbot with patient identifiers. The hallucination and sycophancy literature is clear enough to make this indefensible [21] [7].
- Do not claim anxiety reduction, workload reduction, or improved outcomes in patient-facing materials until the service has its own data. The trial is a phase II signal, not a license.
- Do not replace the consent conversation. The LLM can prepare the patient and answer logistics; the consent discussion is a clinician’s responsibility, and the evidence on comprehension supports teach-back, not a chatbot [15].
- Do not use NASA-TLX alone as evidence of efficiency. Pair it with time logs and volume data [19].
- Do not ignore the patients who do not engage. The cataract trial’s 52% non-engagement rate is a warning [73]; a service that only helps the digitally confident will widen the gap.
- Do not treat model updates as routine IT changes. A version change can change the answers; it needs a review and a re-audit [66].
13.6 A realistic pilot size
A single-centre pilot of 100–200 patients, with a pre-specified comparison against a historical or concurrent control, can detect a moderate change in comprehension and can generate enough safety events to be informative. It cannot reliably detect a 2.5-point GAD-7 difference if the design is unblinded and the comparator is usual care; that requires the kind of trial described in Section 12. The pilot’s job is to test feasibility, safety and signal, not to prove efficacy.
13.7 The honest position for a service leader
A service leader who is asked “should we do this?” can say: the intervention is plausible, the demand is real, the evidence is early, and the risks are manageable if the service is constrained and audited. That is a more defensible position than either “the trial proves it works” or “there is no evidence.” The trial proves that a signal exists in one centre. The service’s job is to find out whether the signal is real in its own patients, and to stop if it is not.
14. Limitations of This Review
The peg is an abstract, not a paper. The full text of the Shanghai trial was not retrievable. The publisher’s PDF endpoint returned HTML, and the DOI was not indexed in PubMed or Europe PMC at the time of preparation. Every statement about the trial is therefore limited to the verified seed facts and the public registry record. Model identity, prompt design, statistical methods, baseline scores, follow-up, subgroup analyses and safety monitoring are unknown. This is a material limitation: the review can identify threats to validity but cannot determine whether the authors addressed them.
The registry and the paper disagree. The registry lists a planned enrolment of 160, phase “NA”, and a primary completion date of June 2027, while the paper reports 268 randomised, calls the study phase II, and reports results in 2026. The review reports these discrepancies but cannot resolve them without the protocol and statistical analysis plan.
The search is PubMed-centric and time-limited. The review used PubMed E-utilities, ClinicalTrials.gov, Europe PMC and selected publisher and regulatory pages up to 2026-11-11. It did not systematically search Embase, CINAHL, PsycINFO, Web of Science or grey literature. English-language publication bias is likely. The LLM literature in particular is growing fast, and a 2026 snapshot will date quickly.
No meta-analysis was performed. The review reports pooled estimates only where a retrieved systematic review provided them. It does not pool the primary studies itself, and it does not adjust for publication bias. The LLM trial literature is small enough that a pooled estimate would be unstable and probably misleading; the decision not to pool is deliberate, but it means the review cannot give a single summary effect.
The MCID estimate is borrowed. The 4-point GAD-7 MCID comes from a trial in chronic depression, not from a surgical population [2]. A different population could yield a different threshold. The review uses the 4-point figure as the best available anchor, not as a definitive property of the instrument.
The design-effect calculations are illustrative. The number of rooms in the trial is unknown, and the ICC is unknown. The design-effect table shows the range of plausible inflation, not what happened. The calculations assume a simple parallel cluster design and do not account for stratification, repeated measures, or the possibility that the trial used a cluster-robust analysis that the abstract did not mention.
The safety literature is mostly cross-sectional and model-specific. The audits describe particular models, prompts and dates. They establish that the failure modes exist and are measurable; they do not establish the failure rate of a well-designed, retrieval-grounded, clinician-reviewed pipeline. That evidence would have to come from the pipeline’s own audit.
Cost and implementation are under-evidenced. The review found no rigorous cost-effectiveness study of LLM-mediated preoperative communication. Statements about cost, staffing and maintenance are inferences, not retrieved findings. No price claims are made.
No patient or public involvement. The review was written by a single analyst without patient input. The endpoints that matter to patients — feeling prepared, being able to ask a question without shame, understanding what will happen to continence and sexual function — are represented in the literature, but the review’s framing of them is the analyst’s.
The review is a snapshot of a moving field. Several of the cited studies are from 2026 and are themselves early. The conclusion that the evidence is insufficient is robust to the studies that exist; it would change if a large, well-designed trial reported a positive result. That is the point of Section 12.
15. Bottom Line
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The signal is real enough to pursue, not strong enough to rely on. A 2.5-point GAD-7 difference, a 16.9-point NASA-TLX difference, and an 8.6-minute shorter consultation in 268 patients are large effects from a single-centre, room-randomised, unblinded phase II trial [1]. The design can produce effects of that size without the intervention being responsible for all of them. The appropriate response is a confirmatory trial, not a procurement decision.
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Room-level allocation is the central threat. It makes the study a cluster trial with an unknown and probably small number of clusters, and the abstract does not report a clustering-adjusted analysis. The effective sample may be substantially smaller than 268, and the confidence interval around the anxiety difference may be much wider than the P value suggests [53] [54].
-
The anxiety endpoint is not protected by blinding. Patients knew whether they received personalised answers, and the endpoint is self-reported. Expectation, attention and novelty are bundled with the intervention. The physician blinding protects the workload endpoint, not the anxiety endpoint. A 2.5-point difference is also below the best available MCID estimate of 4 points [2], so even a real difference of that size may not be clinically noticeable.
-
The workload claim is a consultation-time claim, not a system claim. NASA-TLX is self-report; the 8.6 minutes excludes the staff time to collect, review, correct, audit and maintain 3,507 answers. The ambient-scribe literature finds objective savings of roughly 1–2.5 minutes per encounter, with longer notes and unchanged after-hours work [3] [4] [5]. The Shanghai figure is an order of magnitude larger and needs objective confirmation.
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Safety is the binding constraint. Hallucination, false reassurance, sycophancy, escalation failure and model drift are documented in the LLM literature [6] [7] [8] [9]. The trial abstract describes none of the controls that would address them. A service that deploys this class of tool without a locked model, a constrained domain, human review, an escalation rule and an audit is not making a judgment that the risk is low; it is declining to measure it.
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The adjacent literature sets realistic expectations. Question-prompt lists improve question-asking but not anxiety [10]; decision aids improve knowledge and decisional conflict but the largest prostate-cancer trial found no effect on its primary or secondary endpoints [14]; consent comprehension improves most with interactive and teach-back approaches [15]; and the randomised LLM literature is five small trials with effects ranging from −0.59 to +1.25 and very low certainty [16]. A large anxiety effect from one unblinded trial is an outlier against that background.
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The defensible use case is narrow and supervised. Personalised, LLM-drafted answers to logistical and preparatory questions, delivered before the consultation, reviewed by a clinician, grounded in approved content, with a red-flag escalation path and an audit, are a plausible quality improvement. They are not a substitute for consent, a treatment for anxiety, or a proven way to reduce system workload. A service that starts there, measures honestly, and stops if the signal does not replicate will learn something useful. A service that skips those steps will generate a press release and a problem.
The field does not need another phase II signal. It needs one trial that a sceptical surgeon, a sceptical methodologist and a sceptical patient can all accept. Until that trial exists, the most useful thing a clinician can say about LLM-mediated preoperative communication is: promising, plausible, unconfirmed — and not yet a standard of care.
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