AI peer review for epidemiology and population science

PerfectPaper reviews population science manuscripts with a standing team of specialist agents, and lets you add up to three custom agents for the conventions that team does not cover. This page contains five prebuilt agent briefs for cancer control and population sciences: health equity reporting, competing risks and time-related bias, registry and claims data validity, causal language discipline, and qualitative rigour.

Two of these fill gaps that are unusually wide. The standing team has no qualitative competence at all, since it was built for quantitative manuscripts. And nothing in a general review is briefed on how race, ethnicity and socioeconomic position should be reported — which is the single most consequential reporting question in disparities research.

The five agents

PerfectPaper’s five epidemiology briefs each target one convention the standing team does not check on its own, and a review uses at most three of the five at a time.

Health equity reporting — race and ethnicity treated as biological rather than social, category derivation unstated, area-level measures read as individual-level, disparities documented without mechanism.

Competing risks and time-related bias — Kaplan-Meier where a competing risks method is required, immortal time in registry and claims cohorts, lead-time and length-time bias in screening studies.

Registry and claims data validity — SEER, NCDB and Medicare coding limitations glossed over, missing stage or treatment detail, conclusions the data source cannot support.

Causal language discipline — observational findings written in causal verbs, adjustment sets unjustified, no DAG.

Qualitative and mixed-methods rigour — saturation claimed without evidence, coding reliability, reflexivity, member checking.

Each is a text brief you copy into the agent field. Manuscripts are reviewed as .docx; the briefs do not read LaTeX source.

How custom agents work

A PerfectPaper review accepts up to three custom agents. Each takes a name, instructions up to 6,000 characters, a work type, a skill level, and an optional tool selection — web search, scholarly search, code execution, and vision for reading figures. PerfectPaper supplies the review contract and output format, so the brief describes what to look for.

Tool choice matters more in population science than in most fields. Give the competing risks agent code execution, because the findings it produces are arithmetic: recomputing a cumulative incidence, summing cause-specific estimates to check they do not exceed the all-cause event probability, reconciling a number-at-risk row against a reported denominator. Give the registry agent web search only when you want it to read a data dictionary or a release note; without a tool it reads the manuscript alone, which is the more reliable mode for a checking task. Leave tools off the causal language agent entirely — its object is your own sentences, and a search tool pulls it toward the literature and away from the text. How to write a custom reviewer agent covers the brief structure that produces actionable findings, and custom AI reviewer agents covers how agents attach to a review across every field.

Common questions about using custom reviewer agents

Can AI actually peer review an epidemiology paper?

Yes, as a pre-submission specialist check rather than a substitute for a journal’s reviewers. PerfectPaper’s standing team reads statistical models, causal inference, tables and citations in every submission; five optional briefs add competing risks, registry validity, health equity reporting, causal-language discipline and qualitative rigor — conventions a general methodology review typically does not check.

How many custom reviewer agents can I run on one paper?

Up to three. PerfectPaper accepts three custom agents per manuscript, run alongside its standing specialist team, which already covers statistical models, causal inference, survey design, tables and citation checking. For population science, five prebuilt briefs — competing risks, registry validity, health equity reporting, causal language and qualitative rigor — compete for those three slots, prioritized by study design.

What the standing team already covers

PerfectPaper’s standing specialist team reads every manuscript for statistical models, causal inference and confounding, survey design, tables, figures and citation verification, alongside structure, numeric integrity, prior work, logic and journal fit. In an epidemiology submission it already questions a model specification, an unreported denominator, an abstract number that appears in no table, and a discussion that runs past the result.

What the standing team does not carry is what a specific data source contains, what a specific reporting standard requires in its own words, and which conventions a subfield’s reviewers treat as non-negotiable. A general methodology reviewer objects that a covariate is unjustified; the health equity agent objects that the ICMJE Recommendations require you to define how race was determined and justify its relevance, quotes your sentence, and proposes the replacement. That difference — a comment an editor can weigh versus a comment an author can act on — is the whole reason for a custom slot.

Choosing among the five

Choosing among PerfectPaper’s five epidemiology briefs comes down to study design, not subfield label: match the agent to how the manuscript could actually fail. For a survival analysis in a cancer cohort, competing risks earns a slot before anything else, because death from other causes is common in these populations and the wrong method biases every reported probability upward. For a disparities paper, health equity reporting comes first. For any observational study, causal language is a cheap and high-yield slot. Registry data validity suits secondary analyses of SEER, NCDB or claims. Qualitative rigour is essential for interview and focus group work and irrelevant elsewhere.

There is deliberate overlap with the standing team on causal inference; the causal language agent is scoped to the claims-and-wording layer for that reason.

Competing risks is the default failure in a cancer cohort

Competing risks is routinely missed in oncology and geriatric population research, and treating a competing event as censoring biases cumulative incidence in one direction only: upward. Koller, Raatz, Steyerberg and Wolbers reviewed 50 clinical studies performed in individuals susceptible to competing risks and published in high-impact clinical journals, and found competing risks issues in 70% of the articles (Statistics in Medicine 2012;31(11–12):1089–1097).

The arithmetic is fixed rather than approximate. With a cause-specific hazard of 0.05 per year for cancer death and 0.10 per year for other-cause death, one minus Kaplan-Meier gives 39.3% at ten years where the Aalen-Johansen cumulative incidence function gives 25.9% — a 13.5 point gap that widens with follow-up. The agent also runs the sum check: naive estimates for cancer death and other-cause death in that cohort sum to 102.6% against an all-cause event probability of 77.7%, an arithmetic contradiction a reader can verify from the published figures alone.

The consequence lands at the decision threshold. Wolbers, Koller, Witteman and Steyerberg predicted 10-year coronary heart disease risk in women aged 55 to 90 in the Rotterdam Study and found a standard Cox model ignoring the competing risk classified 18% of women as high risk, above a 20% threshold, against 8% under the Fine and Gray model (Epidemiology 2009;20(4):555–561). Any nomogram built on Kaplan-Meier in an older population inherits that inflation, and inherits it where it changes who is treated.

A regression model raises the same distinction the two curves above already show, and it is not optional once the reviewer asks for adjusted estimates. A cause-specific Cox model removes a patient from the risk set the moment the competing event occurs, asking what drives the outcome among those with no event yet; a Fine-Gray subdistribution hazard model keeps that patient in the risk set indefinitely, which is the mechanism that lets its hazard ratio map directly onto cumulative incidence. A covariate that raises the cause-specific hazard for the outcome can show a null or even opposite-signed Fine-Gray hazard ratio if it also strongly raises the competing risk. Austin, Lee and Fine’s worked cardiac example shows the mechanism plainly: a history of cancer had essentially no association with the cause-specific hazard of cardiac death (hazard ratio 0.96) yet a subdistribution hazard ratio of 0.82, because cancer raised the cause-specific hazard of non-cardiac death by 85% (Circulation 2016;133(6):601–609). Neither number is computed wrong, and a manuscript that reports only one owes the reader a sentence saying which question it answers.

Time-related bias enters through follow-up, not through the model

Time-related bias in a registry or claims cohort comes from how person-time is allocated relative to when exposure is defined, and it survives every covariate adjustment. Immortal time bias is the standard instance: a patient must survive long enough to receive the treatment that defines their group, and that guaranteed survival is credited to the treated arm.

Suissa’s reanalysis of inhaled corticosteroids after a chronic obstructive pulmonary disease hospitalisation moved the adjusted rate ratio from 0.69 (95% CI 0.55–0.86) to 1.00 (95% CI 0.79–1.26) by changing one thing: whether the person-time before the first prescription was analysed as time-fixed or time-dependent exposure (American Journal of Respiratory and Critical Care Medicine 2003;168(1):49–53). No covariate was added and no patient was removed — the fix is one of two standard designs: a time-varying exposure model, the reallocation Suissa applied above, or a landmark analysis that fixes eligibility at a point after which every patient’s exposure status is already known, discarding the ambiguous person-time rather than reallocating it. The oncology dialect is the responder-versus-non-responder comparison, where a patient must survive to the first scheduled response assessment before they can be classified as a responder at all, so the responder group is guaranteed the person-time between randomisation and that assessment.

Screening studies carry a different version, in which survival is not a valid endpoint at all. Marcus and colleagues’ long-term follow-up of the Mayo Lung Project reported median survival among participants with resected early-stage lung cancer of 16.0 years in the intervention arm and 5.0 years in usual care, while lung cancer mortality was 4.4 deaths per 1,000 person-years in the intervention arm (95% CI 3.9–4.9) against 3.9 in usual care (95% CI 3.5–4.4) (Journal of the National Cancer Institute 2000;92(16):1308–1316). Survival and mortality pointed in opposite directions in the same trial, and the authors read that gap as overdiagnosis — some detected lesions had limited clinical relevance — which is lead time bias and length bias made visible.

Questions about competing risks and immortal time bias

My reviewer says I should have used competing risks instead of Kaplan-Meier — is that really a big deal?

Yes, whenever a competing event is common in the cohort. Kaplan-Meier treats a competing death as though the patient could still die of the outcome later, which is false. Koller and colleagues found competing-risks handling was wrong in 70% of 50 reviewed clinical studies (Statistics in Medicine 2012). The error only runs one direction: cumulative incidence is overestimated, never underestimated.

What is immortal time bias, in plain terms?

It is a period during which a patient could not yet have had the outcome, misclassified as exposed time, which makes the treated group look artificially protected. Suissa’s reanalysis of inhaled corticosteroids after a COPD hospitalization moved the adjusted rate ratio from 0.69 to 1.00 purely by reclassifying that person-time as time-dependent rather than time-fixed (American Journal of Respiratory and Critical Care Medicine 2003).

Why does my hazard ratio change so much when I switch from Kaplan-Meier’s complement to a Fine-Gray model?

Because the two estimate different things, not the same thing measured two ways. A cause-specific model removes a patient from the risk set at the competing event; Fine-Gray keeps that patient in the risk set indefinitely so its hazard ratio maps onto cumulative incidence directly. A covariate can legitimately flip sign between the two without either model being computed wrong — report which question each answers.

What a race, ethnicity or deprivation variable owes the reader

A manuscript reporting race, ethnicity or socioeconomic position owes its reader three things that are already written down in publishable sentences: how the category was determined, why it is relevant, and how the result should be interpreted. The ICMJE Recommendations state it directly, under “Selection and Description of Participants”: “Authors should define how they determined race or ethnicity and justify their relevance… Race and ethnicity are social and not biological constructs; authors should interpret results associated with race and ethnicity in that context.”

Two supporting facts decide most findings. Administrative race codes are measurably wrong, and the error concentrates in the groups a disparities paper is about: Eicheldinger and Bonito reported that the Medicare administrative race and ethnicity code, compared with self-report, had a sensitivity of 29.5% for Hispanic beneficiaries and 54.7% for Asian and Pacific Islander beneficiaries (Health Care Financing Review 2008;29(3):27–42). And area-level indices are not the multidimensional summaries their names imply: Petterson recalculated the Area Deprivation Index and found it “reducible to a weighted average of just 2 measures — income and home values”, with the published unstandardised index matching his reconstruction at r > 0.9999 while a properly standardised version correlated with it at only r = 0.7245 (Health Affairs Scholar 2023;1(5):qxad063).

The category vocabulary itself is moving. The US Office of Management and Budget published revisions to Statistical Policy Directive No. 15 in March 2024, moving federal collection to a single combined race and ethnicity question allowing multiple responses and adding Middle Eastern or North African as a minimum reporting category, with agencies given five years to come into full compliance. A dataset collected in the 2010s and a manuscript submitted in 2026 use different systems, and the paper has to say which — the combined, multiple-response format changes case counts for multiracial respondents on its own, before any underlying population has shifted, which is a discontinuity a supplementary table can show and a paragraph cannot. STROBE item 7 additionally asks you to clearly define every exposure, predictor and potential confounder, which is exactly the question an unexplained “other” category fails.

What a registry records and what a manuscript concludes

A registry analysis fails at the point where the conclusion needs a variable the source never recorded, and the most common instance is recurrence. Most cancer registries record vital status and cause of death rather than recurrence; an analysis of recurrence generally requires linked claims and a validated algorithm whose performance is stated. Treatment exposure identified from billing codes captures billing rather than delivery. Comorbidity indices computed from claims depend on coding intensity, which varies by institution and by insurance type. A hospital-based registry is not population-based, and a claims database covers only the insured population it draws from.

Large registries also invert the usual relationship between sample size and confidence. A cohort of 400,000 patients produces confidence intervals narrow enough to make a fraction of a percentage point statistically significant, while the dominant source of error in that estimate is systematic — miscoding, unmeasured indication, differential ascertainment — and does not shrink with n. The registry agent reports narrow intervals presented as precision, and reports confounding by indication wherever two treatments are compared, because the reasons a clinician chose one over the other are recorded nowhere in the data and no adjustment set recovers them. Propensity score matching does not settle this by itself: a propensity score balances the measured confounders entered into it, but confounding by indication is defined by the clinical reasoning behind a treatment choice, which is by construction not in the data to match on. Bosco and colleagues tested this head-on in a cohort of older women with breast cancer, where adjuvant chemotherapy appeared to increase recurrence (crude hazard ratio 2.6, 95% CI 1.9–3.5) because the patients at highest risk were the ones treated. Restriction with multivariable regression moved the estimate to 1.1 (95% CI 0.7–1.6) and propensity score adjustment to 1.3 (95% CI 0.8–2.0); neither recovered the protective effect the authors expected, and they concluded that neither propensity scores nor an instrumental-variable method adequately controlled confounding by indication (Journal of Clinical Epidemiology 2010;63(1):64–74). The paper is titled “A most stubborn bias” for that reason. An E-value bounding the unmeasured confounder is the honest complement to matching, not a substitute analysis to run once matching is done.

The related problem is who entered the database in the first place, which is selection bias rather than confounding, and is therefore not fixed by a longer covariate list.

Questions about SEER, NCDB and claims data limits

Does SEER track cancer recurrence?

No. Most cancer registries, including SEER, record vital status and cause of death but not recurrence. An analysis that reports recurrence from SEER alone is describing progression the registry never captured; a recurrence outcome generally needs linked claims data and a validated detection algorithm with its own stated sensitivity and specificity, named in the methods.

Reviewer 2 says my SEER cohort is too small to see this effect, but I have 400,000 patients — what do I say?

Sample size and precision are not the objection here. A cohort of 400,000 can make a fraction-of-a-percentage-point difference statistically significant, while the dominant error source in registry data — miscoding, unmeasured indication, differential ascertainment — is systematic and does not shrink as n grows. State the interval’s width and name the systematic risk as a separate limitation, rather than treating narrowness as proof.

Can I trust the race variable in a SEER-Medicare or claims file?

Only with a stated caveat, not as ground truth. Eicheldinger and Bonito found the Medicare administrative race code, checked against self-report, had a sensitivity of just 29.5% for Hispanic beneficiaries and 54.7% for Asian and Pacific Islander beneficiaries (Health Care Financing Review 2008). Report the field as administratively derived, name its known error pattern, and say which direction it likely biases the comparison.

Causal language is where an observational paper commits itself

Causal language outruns the design most reliably in the abstract’s linking verb and in the closing recommendation, and both have been measured. Haber and colleagues screened 1,170 articles from 18 high-profile medical, public health and epidemiology journals published from 2010 to 2019, and three reviewers rated the causal implication of the abstract’s exposure–outcome linking language as strong in 18.7% of abstracts, moderate in 33.2%, weak in 34.2% and absent in 13.8% (American Journal of Epidemiology 2022;191(12):2084–2097). In the same sample, the implied causality of the action recommendation was higher than that of the linking sentence in 44.5% of articles — the advice is more causal than the finding in nearly half of published observational work.

Softening the verb is not the remedy. “Associate” was the most common linking word at 45.7%, and over half of that study’s reviewers rated “association” as carrying at least some causal implication. Miguel Hernán’s argument in “The C-Word: Scientific Euphemisms Do Not Improve Causal Inference From Observational Data” (American Journal of Public Health 2018;108(5):616–619) is the primary source to cite instead: being explicit about the causal objective reduces ambiguity in the question, errors in the analysis, and excesses in the interpretation.

Two structural moves answer the objection rather than dodging it. State the target trial the analysis emulates — eligibility, treatment strategies, assignment procedure, start of follow-up — which forecloses immortal time on the way. And bound residual confounding with a number: the E-value of VanderWeele and Ding (Annals of Internal Medicine 2017;167(4):268–274) is 2.37 for an observed risk ratio of 1.5 and 3.41 for 2.0, and the informative version is the E-value for the confidence limit nearest the null. The usual objection to it is backwards. Ding and VanderWeele’s bounding factor imposes no requirement that the unmeasured confounder be binary, that exposure and confounder not interact, or that there be only one confounder — those were assumptions of the earlier sensitivity analyses it replaced, which is why the paper deriving it is called “Sensitivity Analysis Without Assumptions” (Epidemiology 2016;27(3):368–377). “There could be several confounders acting together” is therefore not a defect in the number. The genuine limits are different ones, and the agent states them: the E-value is conditional on the covariates already adjusted for, it speaks to unmeasured confounding rather than to selection bias or measurement error, and it says how strong confounding would have to be, not that none is present. The agent reports the number as a bound, never as proof the finding is unconfounded. A directed acyclic graph makes the adjustment set reviewable; presenting every coefficient in that model as its own effect estimate is the Table 2 fallacy.

The qualitative gap in a quantitative review

Qualitative and mixed-methods manuscripts are the clearest case for a custom slot, because PerfectPaper’s standing team was built for quantitative work and carries no qualitative competence at all. The gap is not a matter of taste: COREQ contains 32 items in three domains of 8, 15 and 9 (Tong, Sainsbury and Craig, International Journal for Quality in Health Care 2007;19(6):349–357), and SRQR contains 21 items covering the full range of qualitative approaches (O’Brien and colleagues, Academic Medicine 2014;89(9):1245–1251).

Saturation is where most claims fail. Hennink and Kaiser reviewed 23 articles that tested saturation on real data (17 studies) or by statistical modelling (6), and the studies using empirical data reached saturation within 9 to 17 interviews, or 4 to 8 focus group discussions, particularly those with relatively homogeneous populations and narrowly defined objectives (Social Science & Medicine 2022;292:114523). Hennink, Kaiser and Marconi found code saturation at nine interviews and meaning saturation at 16 to 24 in the same 25-interview dataset (Qualitative Health Research 2017;27(4):591–608), which is why “saturation was reached” without saying which saturation is an unfinished sentence.

Reflexivity is the domain a health-sciences manuscript most often leaves blank, and it is blank in a way a checklist can see. COREQ’s first domain asks eight concrete questions about the person who conducted the interviews — who they were, their credentials, their occupation, their gender, their experience and training, what relationship they had with participants before the study began, what participants knew about the interviewer, and what the interviewer brought to the topic. A methods section that says only “semi-structured interviews were conducted” answers none of the eight, and the agent lists the ones the text does not answer rather than asking for reflexivity in the abstract.

Coding reliability is the other reporting decision that has to match the approach rather than the convention. A kappa or percentage agreement belongs to a coding framework that treats codes as reliably applied categories; reporting one under reflexive thematic analysis, where coding is an evolving interpretive act and a second coder is not a reliability check, describes an operation that was not performed. The agent reports the mismatch in either direction — a reliability statistic with no stated approach behind it, and a codebook approach with no account of how disagreements were resolved.

Frequently asked questions about causal language and qualitative rigor

Is it safer to say “associated with” instead of “causes” in my discussion section?

Softening the verb does not remove the objection, it just hides it. Haber and colleagues rated the causal implication of the exposure–outcome language in 1,170 abstracts across 18 journals and found “association” was the most common linking word at 45.7%, yet most reviewers still rated it as carrying some causal implication (American Journal of Epidemiology 2022). State the causal objective explicitly, or say plainly that the design cannot support one.

I only managed 9 interviews before I ran out of funding — is that enough to claim saturation?

Possibly, if your sample is fairly homogeneous and the research question is narrowly defined. Hennink and Kaiser’s review of empirical saturation studies found it was reached within 9 to 17 interviews under those conditions (Social Science & Medicine 2022), though a companion study found code saturation at nine interviews and meaning saturation only by 16 to 24 — say which kind you are claiming.

Do I need a second coder and a kappa statistic for my qualitative paper?

Only if your coding framework treats codes as fixed categories applied by a rule, which is what a kappa statistic checks. Under reflexive thematic analysis, coding is an evolving interpretive act and a second coder is not a reliability check at all, so reporting kappa there describes an operation that was not performed — report instead how coding disagreements were discussed and resolved.

Is a causal language agent worth a slot when the standing team already covers causal inference?

For an observational paper, usually yes, because the overlap is deliberate rather than redundant. The custom agent is scoped to how claims are worded in the abstract and the closing recommendation, while PerfectPaper’s standing specialist reads the identification strategy and confounding structure underneath those sentences.

Worked example: three slots for a SEER disparities paper

Consider a manuscript analysing 4,000 patients with localised prostate cancer in SEER-Medicare, median age 73, reporting “10-year cancer-specific mortality of 39%, Kaplan-Meier method, log-rank p < 0.001” for a comparison between two treatment strategies, with a secondary analysis by race showing a higher rate in Black patients and a discussion attributing it to tumour biology.

The competing risks agent takes the first slot. It reports that other-cause death occurs more often than the event of interest at that median age, that Kaplan-Meier treats those deaths as censored — that is, as patients who could still die of prostate cancer later, which is false — that the correct 10-year cumulative incidence is closer to 26% than 39% under an other-cause hazard twice the cancer-specific hazard, and that the group comparison belongs to Gray’s test rather than the log-rank test.

The health equity agent takes the second. It reports that the SEER race field was not collected by the authors, that the manuscript does not say how it was derived, and that the discussion converts a descriptive difference into a biological explanation without a mechanism — the point at which race stops being a social variable in the analysis and becomes a biological one in the prose.

The registry agent takes the third. It reports which SEER-Medicare release and years were used or that they are unstated, that treatment was identified from billing codes, that reasons for treatment choice are recorded nowhere in the data, and that the limitations paragraph would apply unchanged to any registry study. Three narrow agents produce three separately actionable findings; one broad agent asked to check all of it produces a summary.

When the obvious remedy is unavailable

The remedy a reviewer names is sometimes unavailable, and the correct response is a different estimand stated plainly, not a caveat. Each brief is written to reach for the substitute rather than stop at the objection.

Cause of death is unknown or untrustworthy. Relative survival methods estimate excess mortality against a matched general-population life table without using cause of death at all; the Pohar Perme estimator is the consistent net-survival estimator in that framework (Perme, Stare and Estève, Biometrics 2012;68:113–120). Say the estimand is excess mortality, because it is not interchangeable with cause-specific mortality in the discussion.

Too few events for a subdistribution model. Report nonparametric cumulative incidence functions with Gray’s test, state why the regression was not fitted, and give the event count that drove the decision rather than presenting an unstable model.

Race came from an administrative field you did not collect. Report the source and the known validity of that field rather than describing it as self-reported, and where an imputation algorithm was applied, name it and give its performance.

No DAG is feasible because the causal structure is contested. Apply VanderWeele’s modified disjunctive cause criterion — adjust for each covariate that is a cause of the exposure, of the outcome, or of both; exclude known instrumental variables; include proxies for unmeasured common causes (European Journal of Epidemiology 2019;34(3):211–219). It requires a judgement per covariate, not a complete diagram.

Saturation does not apply to your approach. Under reflexive thematic analysis, “saturation was not sought, because the analytic approach does not use the concept, and the sample size rationale was X” is the correct answer rather than an omission.

What a population-science reviewer writes

Reviewers in this literature rarely name the bias first; they name the number that contradicts the method, and those comments decide papers. “Cumulative incidence has been estimated by one minus Kaplan-Meier in a cohort with substantial non-cancer mortality; please re-estimate with a cumulative incidence function and update the abstract.” “Exposure is defined by receipt of treatment, so members of the treated group were required to survive until treatment; please align start of follow-up with eligibility.” “The registry does not record recurrence; the recurrence analysis should be removed or its algorithm validated and reported.”

On the equity side: “The race variable is registry-derived and its ascertainment is not described.” “The neighbourhood deprivation index is interpreted as individual poverty.” “The discussion offers a biological explanation for a difference the design cannot attribute to biology.” And on wording: “The conclusion recommends a clinical action that the observational design does not support” — the comment the 44.5% figure above predicts.

Anticipating these in a limitations section works only when the limitation is quantified. A limitations paragraph that names the direction of the bias and gives a bound reads as analysis; one that says results should be interpreted with caution reads as an admission without one.

What this set does not cover

The five briefs on this page check reporting, method choice and claim discipline in original research articles. They do not adjudicate whether the research question was worth asking, whether the cohort was the right one to assemble, or whether a contested substantive literature favours your interpretation. They do not verify a registry release against its data dictionary unless the agent is given web search, and they do not confirm that a cited paper says what you say it says — citation verification belongs to the standing team.

Trial-specific conventions live elsewhere: response criteria, dose-escalation safety and endpoint pre-specification are covered by the clinical trials set, and approval statements, consent scope and de-identification by the ethics and data sharing agent. PerfectPaper is an AI peer reviewer an author runs before submission; it does not replace a journal’s reviewers, and nothing it reports is an editorial decision.

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