A custom AI reviewer for registry and claims data validity

PerfectPaper’s registry data agent reads a secondary analysis of cancer registry or administrative claims data for the gap between what the data source records and what the manuscript concludes. The agent checks coding validity, missing treatment and recurrence detail, how the cohort was selected into the source, and whether conclusions stay inside what the source can support.

Copy the brief below into a custom agent slot. A review takes up to three custom agents, and they run alongside the standing specialist team rather than replacing any part of it.

Large registries produce large sample sizes, and large sample sizes produce narrow confidence intervals around estimates whose main source of error is not random. That mismatch is the recurring problem in this literature. The SEER 21 registry grouping covers 45.8% of the United States population against the 2020 Census, and the National Cancer Database is sourced, in the American College of Surgeons’ own words, from “hospital registry data collected in more than 1,500 Commission on Cancer-accredited facilities”. Those denominators buy statistical power and buy nothing else: neither source was assembled to answer the question a given manuscript asks of it.

When to use this agent

Run this agent whenever a manuscript’s exposure, outcome or cohort is defined by a cancer registry or an administrative claims database, because at least one of the conditions below usually applies once that is true.

• Your manuscript analyses SEER, SEER-Medicare, NCDB, or an administrative claims database
• Treatment exposure is identified from billing or registry codes
• Your outcome is recurrence, which most registries do not capture
• The cohort is very large and the effect size is small
• The discussion draws conclusions about care quality or effectiveness
• Your study period crosses a coding-system change, such as the United States move from ICD-9-CM to ICD-10-CM on 1 October 2015
• You compare two treatment strategies that a clinician chose between for reasons the database never recorded
• A reviewer has asked whether your cohort is population-based, or has asked what the codes actually mean
• You use a claims-derived comorbidity index, such as the Charlson index or the NCI comorbidity index, as a covariate or as an eligibility criterion

One condition is enough, and the last one is the most commonly overlooked, because a comorbidity index looks like a measured variable and is in fact a summary of how intensively a patient’s encounters were coded.

Common questions about registry and claims data limitations

What are the limitations of registry and claims data in research?

Registry and claims data were collected for cancer surveillance and for billing, not for the study being written, so they record what those purposes required. Recurrence, treatment intent, performance status, dose, duration and the clinician’s reason for choosing a treatment are absent, and treatment recorded from codes reflects what was billed.

Does the ICD-9-to-ICD-10 switch actually break a registry trend analysis?

Only if the variable in question is an ICD code. The United States moved from ICD-9-CM to ICD-10-CM diagnosis coding on 1 October 2015, and inpatient procedure coding moved from ICD-9-CM Volume 3 to ICD-10-PCS, so both of those break at that date. CPT and HCPCS Level II codes did not change with it, and those are what physician and outpatient claims use to record services, so a chemotherapy or radiotherapy exposure built from them has no break there. State which coding system each variable comes from before assuming one.

Why do reviewers flag a Charlson or NCI comorbidity index as a confounder instead of just a covariate?

Because a claims-derived comorbidity index measures how often a patient generated billable encounters, not directly how sick they were. The NCI index of Klabunde, Potosky, Legler and Warren counts conditions from the year before diagnosis, excluding the diagnosis month, and requires a condition to appear in physician claims more than once over 30 days apart. A patient seen rarely scores low partly because they were coded rarely.

The agent brief

Paste this into a custom agent. Suggested settings: work type domain_review, skill level graduate, no tools required.

Name: Registry and claims data validity

You are reviewing a secondary analysis of cancer registry or administrative
claims data. Your task is to determine whether the conclusions stay within
what the data source can support.

Determine and report:

1. Source and version. Determine which database was used, which years, and
   which release. Report where this is unstated, since registry contents and
   coding change between releases.

2. Cohort selection. Determine how patients entered the database, not only how
   they entered the study. Report where the manuscript does not address who is
   represented: a hospital-based registry is not population-based, and a
   claims database covers only the insured population it draws from. State
   what the resulting cohort can and cannot generalise to.

3. Variable validity. For every key variable, determine whether it is directly
   recorded or inferred from codes. Report treatment exposure inferred from
   billing codes without acknowledging that codes capture billing rather than
   delivery. Report comorbidity indices computed from claims without
   acknowledging their dependence on coding intensity, which varies by
   institution and by insurance type.

4. Missing detail. Determine whether the analysis requires detail the source
   does not carry. Registries generally lack recurrence, dose, duration,
   performance status, and reasons for treatment choice. Report every
   conclusion that depends on a variable the source does not record, and name
   the variable.

5. Missing data. Determine how missing values were handled, particularly for
   stage and grade, which are frequently incomplete. Report complete case
   analysis presented without assessment of whether missingness relates to the
   outcome.

6. Confounding by indication. Where treatments are compared, determine whether
   the manuscript addresses that treatment was chosen for reasons recorded
   nowhere in the data. Report comparative effectiveness conclusions that do
   not address this, and state that statistical adjustment cannot resolve
   confounding by unrecorded indication.

7. Precision versus accuracy. Where the sample is very large, determine
   whether the manuscript distinguishes statistical significance from
   meaningful difference. Report narrow confidence intervals presented as
   precision when the dominant error is systematic rather than random.

8. Limitations. Determine whether the limitations section names the specific
   limitations of this source rather than generic ones. Report a limitations
   paragraph that would apply unchanged to any study.

9. Codes and algorithms. Determine whether the manuscript gives the codes or
   the algorithm used to define each exposure, outcome and covariate, and
   whether any validation of those codes is cited. Report a definition given
   only in words, such as "patients who received chemotherapy", with no code
   list and no validation reference.

10. Linkage and coding-system change. Where two or more databases were linked,
    determine whether the linkage method and the number linked at each stage
    are reported. Determine whether the study period spans a change in coding
    system or registry practice. Report a trend or a before-after comparison
    that crosses such a change without addressing it.

For each finding, state what the source cannot support and propose a narrower
claim that it can.

Settings, and why this brief takes no tools

The work type domain_review and skill level graduate fit this brief because every item is a comparison between two documents the agent already has: the manuscript, and the documented contents of the named data source. Leave web search off. An available tool is a tool that gets used, and the failure mode here is an agent that retrieves a registry’s marketing page instead of reading your methods section for the variable you assumed was recorded. Add code execution only if you want the agent to reconcile reported denominators across the abstract, the flow diagram and the models. Keep the brief inside the 6,000-character limit that applies to every custom agent; the version above runs to roughly 3,400 characters, which leaves room to name your specific release — “SEER-Medicare, diagnoses 2007–2019, 2023 linkage” — so the agent checks against the release you used. The general case for tool selection is in how to write a custom AI reviewer agent, and the slot mechanics in custom AI reviewer agents.

What this agent catches

PerfectPaper’s registry data agent catches ten specific manuscript patterns, each paired below with the concrete reason the named data source cannot support it.

Every row names the variable rather than the concept, and that is deliberate. A finding that says “registry data have limitations” is dismissed in one line of a response letter. A finding that says the manuscript’s cancer-specific survival endpoint requires a cause-of-death field the named file does not contain, and that the same analysis run on all-cause mortality would answer a question the source can support, is a finding an author has to act on.

What each source records, and what it does not

Each named source has a different boundary, and the boundary is the thing manuscripts get wrong.

The chemotherapy and radiotherapy sensitivities come from Noone, Lund, Mariotto, Cronin, McNeel, Deapen and Warren, “Comparison of SEER Treatment Data With Medicare Claims” (Medical Care 2016;54(9):e55–e64). SEER states the consequence itself: “Because we cannot accurately distinguish between ‘no treatment’ and ‘unknown if patients received treatment,’ the variables that are released upon request are classified as ‘yes’ or ‘no/unknown’.” A manuscript that reports “32% of patients did not receive chemotherapy” from a SEER field has reported a category that means something else, and the correction is a sentence, not a reanalysis.

On the National Cancer Database, Boffa, Rosen, Mallin and colleagues wrote in their review that “several potentially important patient and treatment attributes are not collected in the NCDB, which may affect the extent to which comparisons can be adjusted”, and that the database “has undergone several significant changes during the past decade that may affect its completeness and the types of available data” (JAMA Oncology 2017;3(12):1722–1728). That second clause is why item 1 of the brief asks for the release, not just the years.

Questions about SEER, NCDB and claims data specifically

Is NCDB population-based?

No. The NCDB is a hospital-based registry drawing from more than 1,500 Commission on Cancer-accredited facilities, so it covers a large share of cases but is not a population sample. Conclusions about population incidence or population-level disparities need that limitation stated, not just conclusions about treated patients.

Can I study cancer recurrence using SEER?

Generally not directly: SEER records vital status and cause of death, not recurrence. Analyses needing recurrence usually require linked claims run through a validated algorithm, such as the breast-cancer methods of Chubak et al. (2012), and the manuscript should state which operating point — sensitivity, specificity, and positive predictive value — was used.

Can claims data tell me which treatment a patient actually received?

Claims record what was billed to a payer, which is close to but not identical with what was delivered, and they carry no record of intent or of treatments considered and declined. Report the codes used, cite any validation of that definition, and describe the exposure as billed rather than as administered.

Precision is not accuracy, and here is the arithmetic

A larger registry sample narrows the confidence interval around a biased estimate without changing the bias, and the size of that gap can be computed rather than asserted.

Take a registry cohort of 210,000 patients reporting an adjusted hazard ratio of 0.94 for mortality, 95% CI 0.92 to 0.96, p < 0.001. The E-value of VanderWeele and Ding is the minimum strength of association, on the risk ratio scale, that an unmeasured confounder would need with both the treatment and the outcome, above and beyond the measured covariates, to explain the result away (Annals of Internal Medicine 2017;167(4):268–274). For a point estimate of 0.94 that E-value is 1.32, and for the confidence limit nearest the null, 0.96, it is 1.25. An unrecorded frailty, performance status or physician preference associated with treatment and with death by a risk ratio of about 1.3 each is enough to erase the finding entirely — and unrecorded frailty is precisely what a claims file lacks.

Doubling the cohort to 420,000 narrows the interval by roughly a factor of the square root of two and leaves the E-value of the point estimate at 1.32, because the E-value is a function of the estimate, not of the sample size. That single sentence is the cleanest available answer to “our sample was very large”. Compare an estimate of 0.70, whose E-value is 2.21: the same design, a much stronger signal, and a much harder confounder to postulate. Implementations are in the R package EValue; where the outcome is common enough that a hazard ratio is a poor approximation to a risk ratio, VanderWeele and Ding give the conversion, and the manuscript should say which was used. State the E-value beside the estimate rather than beside the confidence interval, and treat statistical significance and effect size as separate reports.

One caveat belongs beside every E-value the agent asks for. The standard formulation bounds a single unmeasured confounder that alone fully explains the association. Several weaker, correlated unmeasured factors — treatment-seeking behaviour, frailty and access to care moving together, for instance — can jointly reach the same threshold even though none alone does. Extensions for multiple and correlated confounders exist in the causal-inference literature, but the routine single-number E-value reported in a manuscript is a lower bound on vulnerability, not a certificate that the result survives every plausible unmeasured factor at once.

Questions about sample size and precision in registry studies

Does a large sample make an observational estimate reliable?

A large sample makes an estimate precise, not accurate. With hundreds of thousands of patients the confidence interval narrows toward the point estimate while confounding by indication and coding error remain completely unchanged, and those systematic errors — not sampling variability — become the dominant source of doubt in the result.

My confidence interval is razor-thin with 200,000 patients in my registry cohort — why do reviewers still say the result could be biased?

Because interval width and bias are unrelated: width shrinks with sample size, but bias comes from confounding by indication, misclassified exposure, or selection into the source, none of which more patients corrects. At 210,000 patients an adjusted hazard ratio of 0.94 has an E-value of 1.32 — an unmeasured confounder only that strong, on both treatment and outcome, would erase the finding.

How strong would an unmeasured confounder have to be to explain away my result?

Exactly as strong as the E-value of VanderWeele and Ding: the minimum risk-ratio association an unmeasured confounder would need with both treatment and outcome, beyond the measured covariates, to fully explain the estimate. A hazard ratio of 0.94 has an E-value of 1.32; one of 0.70 has an E-value of 2.21. Report the E-value beside the estimate, not beside the confidence interval.

Confounding by indication, and what adjustment can reach

Confounding by indication is the failure that adjustment does not fix in registry comparative effectiveness, because the variable that drives it — the clinician’s reason for choosing the treatment — is not in the file. NCI states this plainly for SEER-Medicare: “There are no diagnoses or procedures contained in Medicare files that can signal either treatment intent or whether specific treatments were considered and not given.”

That is different from ordinary confounding by a measured covariate, which regression, stratification, matching or weighting removes. It is also different in kind from selection bias, which arises from who entered the analysed sample. A manuscript that answers a confounding-by-indication comment by adding covariates has answered a different objection, and reviewers notice.

Three responses are available and each has a stated limit. High-dimensional propensity scores use hundreds of empirically selected claims-derived proxies rather than a predefined covariate list; Schneeweiss, Rassen, Glynn, Avorn, Mogun and Brookhart tested the method in 49,653 new users of Cox-2 inhibitors or non-selective NSAIDs, where a crude relative risk of 1.09 (95% CI 0.91–1.30) became 0.94 (0.78–1.12) after 15 predefined covariates and 0.88 (0.73–1.06) after a further 500 algorithm-derived covariates (Epidemiology 2009;20(4):512–522). The method improves proxy adjustment; it does not observe the indication. Negative control outcomes, in the sense of Lipsitch, Tchetgen Tchetgen and Cohen (Epidemiology 2010;21(3):383–388), detect residual confounding by testing the exposure against an outcome it cannot plausibly cause; a non-null association there is evidence the adjustment failed. The check only works when the candidate control shares the same confounding structure as the outcome of interest but genuinely cannot be caused by the exposure — a control that is itself downstream of treatment, such as a claims-based healthcare-utilisation marker, fails silently rather than flagging anything, so the choice of control needs its own justification in the manuscript. An E-value or other bound states how strong the unmeasured confounder would have to be. None of the three converts an observational contrast into a causal one, which is why the discussion section still has to obey causal language discipline and why the objection often arrives as the finding is correlative, not causal. Where adding covariates made your effect vanish, the diagnostic question is a different one — see my effect disappeared after adjusting — and a propensity score balances only the variables you fed it.

Frequently asked questions

Why can’t statistical adjustment fix a registry treatment comparison?

Because the variable that drives the comparison — the clinician’s reason for choosing one treatment over another, which tracks prognosis — is not recorded in the data. Adjustment can only handle variables the file contains, so confounding by an unrecorded indication survives it, and that limit is a property of the source rather than of the model.

Reviewer 2 says my chemo-versus-no-chemo comparison is confounded by indication in a registry study — what do I actually write back?

Concede the mechanism rather than defend the covariate list: state that treatment choice depended on factors — frailty, performance status, patient preference — that the source does not record, so no adjustment removes that confounding. Then add a quantitative bound, such as an E-value, or a high-dimensional propensity score using claims-derived proxies, and narrow the conclusion to the population actually compared.

How do I write the limitations section of a registry study?

Name the source, the release and the years; name each variable the source does not record that your conclusion depends on; state the direction each limitation would push the estimate; and give a bound where one is computable. A limitations paragraph that would apply unchanged to any observational study is the one reviewers reject.

How the cohort entered the source

Patients enter a registry or a claims file through a process the study did not design, and that process is a selection gate operating before the first eligibility criterion.

A hospital-based registry enrols cases through accredited treating facilities, so patients treated at non-accredited facilities, treated outside the system, or never treated at all are absent by construction. A claims database contains people enrolled with that payer for the period observed, so a cohort requiring twelve months of continuous enrolment before diagnosis has selected on having been insured and having stayed insured — a filter correlated with employment, income and health. This is the same structure as collider bias whenever both the exposure and the outcome influence whether a patient appears.

The sharpest current instance is fee-for-service restriction. SEER-Medicare analyses commonly require continuous Medicare Parts A and B with no managed-care enrolment, because, as NCI states, claims for services delivered to HMO enrollees do not appear in the Medicare data unless they were submitted to Medicare for payment. KFF reported that in 2026, 35.2 million of 64.2 million Medicare beneficiaries with Parts A and B — 55% — were enrolled in Medicare Advantage, up from 19% of the eligible population in 2007. A design requirement that once excluded a minority now excludes the majority, and it excludes them non-randomly. A manuscript using that restriction should report the number excluded for managed-care enrolment as a line in its flow diagram and should say what the remaining cohort represents, which is also the substance of health equity reporting when managed-care penetration differs by region and by group.

Worked example: adjuvant chemotherapy in a registry cohort

Consider a registry analysis of 38,000 patients with resected stage III colon cancer, comparing overall survival between patients coded as receiving adjuvant chemotherapy and those coded as not, and concluding that chemotherapy is underused and that increasing its use would improve survival.

The agent reports four separate defects in that one sentence. First, the exposure is a code, and in SEER the “no” arm is a “no/unknown” arm with a documented chemotherapy sensitivity of 68% against Medicare claims, so an unknown fraction of the comparison group was in fact treated — a misclassification that pulls the contrast toward the null and is not symmetric. Second, the exposure is defined by an event occurring after the time origin: a patient who died eight weeks after resection could not be coded as treated, so the treated group is partly defined by having survived to treatment. Bach, Schrag and Begg named this design problem directly in “Resurrecting treatment histories of dead patients: a study design that should be laid to rest” (JAMA 2004;292(22):2765–2770); the remedies are a time-varying exposure or a pre-specified landmark, set out in immortal time bias and checked by the competing risks and time-related bias agent. A landmark date cannot be picked arbitrarily: one set too early still misclassifies patients who go on to receive treatment shortly afterward as untreated, and one set too late discards everyone who died before reaching it, shrinking the treated group toward its healthiest survivors — the date needs justification against the cohort’s own observed time-to-treatment distribution, not a round number of weeks picked in advance. Third, the untreated group was untreated for reasons — frailty, performance status, patient refusal, comorbidity — that the file does not record, which is confounding by indication in its purest form. Fourth, the conclusion is an intervention claim built on all three.

The narrower claim the source can support is worth writing out, because it is what survives review: among patients in this registry coded as receiving adjuvant chemotherapy, observed overall survival was higher than among patients coded “no/unknown”, a difference consistent with a treatment effect, with selection of healthier patients into treatment, and with the immortal span between resection and first cycle. That sentence loses the headline and keeps the paper.

Recurrence, and what to do when the source does not record it

Recurrence is the single most common conclusion that registry data cannot support, and NCI states the position for the largest linked file without qualification: “Neither SEER nor Medicare collect information about recurrence. Medicare claims can be used to identify recurrences indirectly only if the patient receives treatment for the recurrence.”

The remedy is a published, validated claims algorithm, reported with its performance. Chubak, Yu, Pocobelli and colleagues built such algorithms for second breast cancer events in 3,152 women with stage I or II breast cancer diagnosed 1993–2006, using medical record review as the gold standard, and published two operating points: a high-specificity algorithm with 89% sensitivity (95% CI 84–92%), 99% specificity (98–99%) and 90% positive predictive value (86–94%), and a high-sensitivity algorithm with 96% sensitivity (93–98%), 95% specificity (94–96%) and 74% positive predictive value (68–78%) (Journal of the National Cancer Institute 2012;104(12):931–940). Name the algorithm, name the operating point, and state that positive predictive value depends on how common the event is in your cohort, so a value measured in an integrated health system in early-stage breast cancer does not transfer unexamined to a different cancer, a different payer or a different decade.

Where no validated algorithm exists for your setting, the honest move is to change the endpoint rather than to approximate the one you wanted. Overall survival is recorded. Cancer-specific survival requires a cause-of-death field, which SEER carries and which a hospital registry file may not, so item 4 of the brief asks which file the cause came from before it asks anything about the model.

Missing stage and grade

Stage and grade are the fields most often incomplete in registry files, and how a manuscript handles them changes both the cohort and the estimate.

An “unknown” stage code is a recorded value, not an absent one. Dropping those patients is a selection decision, and it belongs in the flow diagram with its N and in the results with a comparison of the dropped and retained groups on age, comorbidity and facility type. Complete-case analysis is defensible when missingness is unrelated to the outcome and indefensible when it is not, and the manuscript rather than the reader should make that argument. Multiple imputation is available and carries its own requirement: state the imputation model, the number of imputations, and which variables were included, because an imputation model that omits the outcome is misspecified. Imputation still assumes the missingness is random once the model’s variables are accounted for; if patients with unknown stage differ in ways nothing in the file captures — an undocumented refusal of staging workup, say — imputation reproduces that same gap with a false appearance of completeness rather than removing it, which is why the agent asks what the dropped and retained groups looked like before treating imputation as sufficient. Where the proportion unknown differs across the exposure groups being compared, report it by group; a single overall percentage hides the pattern that matters. The agent reports a stage distribution that omits the unknown category entirely, because that omission usually means the denominators in the abstract and in Table 1 no longer match.

What reviewers say when registry limitations are mishandled

Reviewers rarely write “registry limitations”. They write the specific version, and these are the comments that decide papers.

“The authors describe the NCDB cohort as population-based; it is hospital-based and this should be corrected throughout.” “Chemotherapy is coded ‘no/unknown’ in this source; the manuscript treats it as ‘not administered’.” “Please provide the complete list of codes used to define the exposure, and cite any validation of that definition.” “Recurrence is not recorded in this registry; on what basis is the recurrence endpoint reported?” “The comparison is between patients whose clinicians chose different treatments for reasons absent from the data; adjustment for the listed covariates does not address this.” “With this sample size the confidence interval is narrow, but the dominant source of error is systematic; please provide a quantitative bias analysis.” “The limitations paragraph would apply unchanged to any observational study and does not name a limitation of this data source.” “The study period spans the ICD-9-CM to ICD-10-CM transition and the apparent trend coincides with it.”

The last two are the ones a generic limitations paragraph provokes rather than prevents, which is why how to write a limitations section matters more here than in most designs, and why a response to reviewers that concedes the boundary and narrows the claim outperforms one that defends the original wording.

What reporting guidance already requires

Three published requirements turn several of these items into compliance checks rather than a referee’s preference, and an editor can act on a compliance failure without a methodological referee.

The RECORD statement — REporting of studies Conducted using Observational Routinely-collected health Data, an extension of STROBE published by Benchimol, Smeeth, Guttmann, Harron, Moher, Petersen, Sørensen, von Elm and Langan (PLoS Medicine 2015;12(10):e1001885) — states at item 6.1 that “the methods of study population selection (such as codes or algorithms used to identify subjects) should be listed in detail”, at item 6.2 that “any validation studies of the codes or algorithms used to select the population should be referenced”, and at item 7.1 that “a complete list of codes and algorithms used to classify exposures, outcomes, confounders, and effect modifiers should be provided”. Item 12.3 requires authors to “state whether the study included person-level, institutional-level, or other data linkage across two or more databases”. Item 13.1 requires them to “describe in detail the selection of the persons included in the study (i.e., study population selection), including filtering based on data quality, data availability and linkage”. Item 19.1 requires the discussion to “discuss the implications of using data that were not created or collected to answer the specific research question(s)”.

Item 19.1 is the clause that decides most of these arguments. A limitations paragraph that names generic threats does not discuss the implications of using data collected for billing and cancer surveillance to answer a comparative effectiveness question, and saying which RECORD item is unmet converts a reviewer’s opinion into a revision instruction.

That instruction still depends on someone reading the manuscript against the checklist line by line, which most journals do not do. RECORD, like STROBE, is typically completed by the authors themselves and filed with the submission rather than audited by the editorial office against the actual methods section, so a manuscript can claim compliance without meeting a specific item and no automated system will catch it. Naming the unmet item in a review carries weight precisely because that check would otherwise not happen.

When the obvious remedy is unavailable

Re-running the analysis in a better data source is the correct answer to most of these findings, and it is usually not available. Four situations recur, and the brief asks for the remedy that fits each.

The source cannot be changed. Narrow the estimand instead. An association measured among patients treated at accredited facilities, or among continuously enrolled fee-for-service beneficiaries, is a valid estimate for those people; what fails is the sentence that generalises it. Rewrite the abstract’s conclusion to name the population, and keep the adjusted coefficients out of the causal register — the Table 2 fallacy is the standard way a registry table acquires eleven causal claims it cannot support.

No validated algorithm exists for your endpoint. Report the endpoint the source does record, state the one you wanted, and say why the substitution is not equivalent. A surrogate endpoint substituted silently is a finding; substituted explicitly, with its validation status stated, it is a design choice a reviewer can accept.

Confounding by indication with no instrument and no negative control. Give a bound. An E-value, a quantitative bias analysis with stated parameters, or an explicit statement of how strong the unmeasured indication would have to be makes a far stronger limitations paragraph than an acknowledgement, and it is the difference between a paper that concedes a weakness and a paper that measures it.

The paper is already published or already in a meta-analysis. The errors here are directional: exposure misclassification from “no/unknown” coding attenuates a contrast, immortal time inflates apparent benefit, and selection into an accredited-facility registry favours treated patients. A meta-analyst can therefore stratify the pooled estimate by whether treatment was ascertained from codes or from linked claims, and report the strata separately rather than pooling across them.

How this differs from the built-in review

The standing team includes methodology, causal inference and conclusion validity specialists that assess a design on its own terms. What they do not carry is knowledge of what a specific data source contains — that most cancer registries do not record recurrence, that claims-derived comorbidity depends on coding intensity, or that a hospital-based registry is not population-based. Those facts are what turn a general methodological reading into a specific, actionable objection.

The difference shows most clearly on the comorbidity index. A general methods reviewer reads “adjusted for Charlson comorbidity index” and moves on. This agent asks which adaptation was used — the Deyo ICD-9-CM adaptation, or the NCI comorbidity index of Klabunde, Potosky, Legler and Warren (Journal of Clinical Epidemiology 2000;53(12):1258–1267) — and over what window, since the NCI index is built from claims in the year before diagnosis, excluding the month of diagnosis, and requires a condition to appear in physician claims more than once in a period greater than 30 days to count. A patient with few encounters has a low index because they were coded rarely, not necessarily because they were well, and in a comparison where one treatment arm has systematically more contact with the health system that index is a confounder dressed as an adjustment.

PerfectPaper reads a registry or claims manuscript against what the named source actually records, and reports each conclusion that depends on a variable the source does not carry.

Pairs naturally with competing risks and time-related bias, since registry survival analyses commonly need both. Full set: AI peer review for epidemiology.

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Related agents

The other epidemiology agents share a review with this one; you can run three at a time. See AI peer review for epidemiology for the full set of five population-science agents.

• Health equity reporting — use it for how race, ethnicity and socioeconomic position are measured and interpreted.
• Competing risks and time-related bias — use it when death from other causes is common, or exposure is defined after follow-up starts.
• Causal language discipline — use it when an observational finding is written with causal verbs.
• Qualitative and mixed-methods rigour — use it for interview and focus group work, which the standing team does not cover.