The paper

Methods

The search, screening, coding, outcomes and estimates were fixed in a plan registered before any comparison between arms was computed; the plan, its codebooks, both codings and the code as registered are under plan/. This is the study's second version. It keeps every registered analysis, which code/analyze.py computes unchanged into results/R1.json to results/R6.json, and adds analyses that answer the first version's reviews, which code/revised.py computes into results/V.json; the claims rest on the added analyses where they differ. deviations.json lists each addition and why.

Question. The VA atlas compared 215,970 veterans with diabetes who started a GLP-1 receptor agonist with 1,203,097 who continued their other treatment, over 175 outcomes, and reported associations with many outcomes beyond the drugs' established effects (Xie et al. (2025)). Placebo-controlled trials that posted results to ClinicalTrials.gov list every serious adverse event (one that results in death, is life-threatening, requires or prolongs hospitalization, or causes lasting disability) by arm and by MedDRA term, whether or not anyone published them; their non-serious events are listed only above a frequency threshold, so we used serious events alone. We asked what these trials show for each association the atlas named in its results (family A), for other questions asked of these drugs (family B), and, without hypotheses, for every organ system (family C) and preferred term (family D).

Data. We searched ClinicalTrials.gov's API (version 2.0.5, data as of 2026-10-09) on 2026-10-12 for interventional studies with posted results naming, among their interventions, any of 21 GLP-1 receptor agonists (data/molecules.json) or cagrilintide, which is tested in combination with semaglutide (data/search.json). The searches found 539 studies, whose records are in data/ctgov/ as the API returned them. The National Library of Medicine asserts no proprietary rights in the database.

Eligibility. The code keeps studies with randomized allocation, a parallel or factorial design, and at least two adverse-event groups (432 of 539). Two coders then read each of these trials' titles, conditions, arms, interventions and adverse-event groups, without any counts, and decided under a codebook which adverse-event groups compare a GLP-1 receptor agonist with placebo with nothing else different. Doses were pooled; a factorial or multi-background trial gave one comparison per background. Arms adding another active drug, active comparators, open-label untreated controls, and groups that were not randomized arms over the randomized period were left out. The coders also recorded the molecules and the population randomized. They agreed on eligibility for 426 trials (Cohen's kappa 0.97) and on identical comparisons for 227 of the 232 both accepted; a third reader decided the 14 trials on which they differed, with reasons. Tirzepatide, retatrutide, survodutide, cotadutide, mazdutide and efinopegdutide, which act on other receptors too, are pooled with the selective agonists and analysed apart in a sensitivity analysis. The participants counted are those in the trials' adverse-event tables, usually everyone who took a dose, not necessarily everyone randomized.

Outcomes. Family A holds the 49 associations the atlas reported against usual care in its results, outside the cardiometabolic outcomes (myocardial infarction, cardiac arrest, heart failure, stroke and chronic kidney disease) that the large trials adjudicate as end points and often leave out of their adverse-event tables. Family B holds gallbladder and biliary disease, intestinal obstruction or ileus, ischaemic optic neuropathy, diabetic retinopathy complications, thyroid, pancreatic, obesity-associated and any cancer, depression, fractures, falls, death from any cause and any serious adverse event. Two coders assigned each of the 4,644 distinct serious event terms to the family A and B outcomes it meets, under a second codebook that defines each outcome, and to its MedDRA preferred term; they saw only the terms and the organ systems they were reported under. They gave identical outcome sets to 4,569 terms (kappa 0.976 over all term–outcome pairs), and a third reader decided 163 terms. All coders and readers were separate instances of Claude Opus 5.5, each working alone.

What the counts are. A record gives, for each reported row (a term under an organ system) and group, the number of participants with it, but not who had which. For each comparison and arm, an outcome's count is the sum over its rows of these numbers, capped at the participants at risk. An outcome made of several terms is therefore counted in reports: a participant counts once for each of the outcome's rows they had, so its ratio compares reports per participant between arms, not the share of participants affected, and the number of distinct participants with it can't be recovered from the tables. Deaths and any serious event, which the records give per group, are counted in participants, and so is a single preferred term wherever each group reports it in one row; a few groups report one preferred term in two rows, under two organ systems or as two spellings the coding joined, and results/V.json counts them for each term the claims name. Bacterial infections sum 342 preferred terms and pneumonia 39.

Estimates. All intervals are 95% confidence intervals. The primary estimate is the Mantel–Haenszel ratio of the drug arm against placebo, stratified by comparison, with a two-sided Wald test. The registered variance is that of Greenland and Robins (1985), which treats each count as binomial; reports are not, since a participant with several of an outcome's terms adds more than one. This version therefore also computes a variance clustered by trial, from each trial's contribution to the ratio's numerator and denominator (Liang and Zeger (1986)). It treats the trials as independent and leaves how a trial's count arises free, so with many trials it holds however a participant's terms overlap; with few trials, or a few carrying most of the weight, it can be too small. Every interval, p-value and q-value in the claims, and in the scans, uses the wider of the two variances. Outcomes with fewer than 10 counted in all were not tested. Within each of families A and B, p-values were corrected by the method of Benjamini and Hochberg (1995). An outcome is robust when q < 0.05, p < 0.05 with every single trial left out, both on the wider variance, and p < 0.05 under random effects. The random-effects estimate is the registered one (DerSimonian and Laird (1986)), whose within-trial variances are binomial and which adds 0.5 to every cell of a comparison with a zero cell, which pulls sparse outcomes toward one; so are Peto's odds ratio (Yusuf et al. (1985)), the estimates from an outcome's most frequent preferred term alone, among selective agonists only, and separately in type-2 diabetes and in overweight or obesity without diabetes, which results/R2.json and results/R3.json hold. The registered rule also asked for p < 0.05 with a "conservative" variance: the Greenland–Robins variance multiplied by how far an outcome's count could overstate participants, capped at the factor by which summing all terms overstates participants with any serious event. That cap is not a bound, because one outcome's terms can overlap more than serious terms do on average, and a factor that bounds a count need not bound its variance; the registered results stay in results/R2.json to results/R4.json and results/outcomes.csv, and no claim rests on them. Trials were paired by size and one of each pair drawn into a first half by a seeded random generator.

Overlap between terms. Four analyses ask how far reports could differ from participants. First, bounds from the tables alone: in each adverse-event group, the participants with an outcome number at least its largest reported row, and at least its count less the group's surplus of term counts over participants with any serious event, and at most its count and at most the participants with any serious event. Second, each comparison arm's count divided by that arm's own number of serious terms per participant with a serious event: the count the outcome would have if its terms overlapped as all serious terms do in that arm of that comparison. Third, the same with each arm's factor pooled over every comparison, which mixes differences between trials, such as trials with several dose arms against one placebo arm, into the difference between arms, and which the stratified comparison does not use. Fourth, the ratio of the arms' terms per participant, the same in every comparison and with the interval's width held fixed, at which the unadjusted interval would reach one: an illustration of a uniform shift, not a threshold over every overlap the tables allow. Each preferred term within bacterial infections and pneumonia with at least 20 participants is also estimated alone.

Against the atlas. Table 1 sets out how the atlas and the trials differ. The registered rule called each family A outcome confirmed (q < 0.05 in the atlas's direction), opposite (q < 0.05 against it), excluding the atlas's estimate (not significant, but the 95% interval excludes the atlas's hazard ratio), inconclusive, or too few events; it set the trials' interval against the atlas's point estimate alone, without the atlas's own uncertainty or a correction for testing many outcomes. This version compares the two as estimates: the ratio of the trials' estimate to the atlas's hazard ratio, with an interval from the variances of both (the atlas's from its published interval), and the p-value of its difference from one corrected by Benjamini–Hochberg over the outcomes tested. An outcome is consistent when the trials find it with q < 0.05 in the atlas's direction and no difference from the atlas is detected after correction, which is not a test of equivalence; in the same direction but different in size when a difference is detected; opposite when the trials find it with q < 0.05 against the atlas; different when the trials find nothing significant but a difference from the atlas is detected; and inconclusive otherwise. Only an outcome significant in the trials can be consistent or opposite, so how many are depends on the trials' power. For pancreatitis, whose atlas outcome is a subtype of the trials', if a subtype making up a share $s$ of cases on placebo rose by the atlas's factor $h$ and the rest did not change, the whole would rise to $1 + s(h - 1)$, so the trials' upper limit $u$ is consistent with any share up to $(u - 1)/(h - 1)$; this holds only under that assumption about the rest. An outcome is informative when a two-sided 5% test had 80% power to detect the atlas's hazard ratio, computed before registration from the pooled count, blind to arm; this is an approximation that ignores the correction, the trials' differences and the counting of reports.

Table 1. How the atlas and these trials differ, for every outcome compared.

How long the trials recorded. Some trials record adverse events only while participants take the study drug; where more stop the drug than placebo, the drug arm is watched for less time and shows fewer events of every kind. Two coders, separate instances of Claude Opus 5.5 working alone, read each eligible trial's adverse-event time frame and description, as its record states them and with nothing else, and coded the period over which serious events were recorded under a codebook: on treatment (tied to taking the drug, such as up to a set time after the last dose), in trial (every participant until the trial ended, whatever their treatment), the trial's calendar with nothing either way, or unstated. A third reader decided the trials they coded differently. Every estimate was repeated in each group and in all trials not coded as on treatment, and the ratio in on-treatment trials was tested against the rest. A calendar period may hide recording that stops with treatment, so the trials not coded as on treatment are not shown to have followed everyone, and the three coded in trial are too few for their clustered variance to mean much. This coding was added after the first version's results were known.

Pneumonia without coronavirus pneumonia. COVID-19 pneumonia turned out to be a large share of pneumonia reports, so pneumonia was estimated again without the preferred terms that name a coronavirus (data/revised.json). This analysis was chosen after seeing the terms.

Scans. Families C and D hold every organ system with at least 10 counted and every preferred term with at least 20. Each item was estimated in the first half of the trials with Benjamini–Hochberg correction over its family, and counts as found again when q < 0.05 there and p < 0.05 in the second half in the same direction. The registered scan gave organ systems the conservative variance; this version repeats both scans with the wider variance, which the claims use. The halves share the registry, the coding and the threshold that chose the items, so the second half checks the first within these data; it is not an outside replication.

Checks of the data. Gallbladder and biliary disease and nausea and vomiting were registered as positive controls, effects the trials' own publications established.

Software. The registered analysis and the added one run in Python 3.12 with NumPy 2.5.3 and SciPy 1.18.1 in under a minute, and a third script rounds their outputs for the paper. results/outcomes.csv lists every registered family A and B estimate, results/outcome_counts.csv every comparison's counts, results/R1.json to results/R6.json everything the plan names, and results/V.json everything this version adds.

Results

Trials. The search found 539 studies, of which 432 passed the structured filter and 234 compared a GLP-1 receptor agonist with placebo, in 257 comparisons with 161309 participants: 93765 on the drugs and 67544 on placebo, since many trials randomized several doses against one placebo arm. 109631 participants had type-2 diabetes and 42927 overweight or obesity without diabetes. The halves held 117 and 117 trials.

Positive controls. Serious gallbladder and biliary disease gave 967 reports on the drugs and 589 on placebo (ratio 1.38, 1.21 to 1.57, q < 0.001), and serious nausea and vomiting 200 and 83 (2.02, 1.52 to 2.68, q < 0.001). Both are robust.

Infections and the lung. Serious bacterial infection gave 2409 reports on the drugs and 2532 on placebo, in 115 comparisons with events (ratio 0.88, 0.83 to 0.93, q < 0.001). The estimate was 0.87 under random effects (p < 0.001, I-squared 0) and ranged from 0.87 to 0.89 with each trial left out, the largest p being < 0.001. In the registered analyses, it was 0.89 in the first half (p 0.0014) and 0.86 in the second (p < 0.001), 0.87 in type-2 diabetes (0.82 to 0.93) and 0.92 without diabetes (0.8 to 1.06; interaction p 0.50).

From the tables alone, the participants with a serious bacterial infection number between 458 and 2409 on the drugs and between 430 and 2532 on placebo, so the reports alone don't fix how many people were affected. If the outcome's terms overlapped within participants as all serious terms do in each arm of each comparison, the ratio would be 0.89 (0.82 to 0.97, p 0.0064), a shift of 1.8% from the unadjusted ratio. Across all comparisons pooled, the tables report 2 serious terms for each participant with a serious event on the drugs and 2.12 on placebo; dividing by these pooled factors would give 0.93 (0.86 to 1.01), but most of that gap lies between trials rather than between the arms of a trial. The unadjusted interval would reach one if, in every comparison alike, placebo participants with a serious infection had 8% more distinct infection terms each than those on the drugs. Counted in participants, the five most frequent of its preferred terms were urinary tract infection (0.92, 0.79 to 1.07), cellulitis (0.68, 0.57 to 0.82), sepsis (0.97, 0.81 to 1.15), septic shock (0.63, 0.48 to 0.82) and osteomyelitis (0.73, 0.55 to 0.96); cellulitis has 1 and sepsis 1 participant in a group that reports the term in two rows. results/V.json lists the rest.

Serious pneumonia gave 1442 and 1568 reports (ratio 0.87, 0.81 to 0.93, q 0.0020): 0.86 under random effects (p < 0.001), 0.85 to 0.9 with each trial left out (largest p 0.0077), and in the registered analyses 0.85 and 0.91 in the halves (p < 0.001 and 0.096), 0.89 in type-2 diabetes and 0.77 without diabetes (interaction p 0.11). Its preferred term pneumonia, counted in participants, affected 807 on the drugs and 880 on placebo (0.86, 0.79 to 0.95), and COVID-19 pneumonia 370 and 433 (0.8, 0.7 to 0.92). Without coronavirus pneumonia, pneumonia reports were 0.89 (0.81 to 0.99, p 0.027), the largest p with a trial left out being 0.11. If pneumonia terms overlapped as all serious terms do in each arm of each comparison, the ratio would be 0.89 (0.8 to 0.98), and with the pooled factors 0.92 (0.83 to 1.02). Sepsis (0.87, 0.78 to 0.98, q 0.13), respiratory failure (0.83, 0.71 to 0.97, q 0.13) and chronic obstructive pulmonary disease (0.83, 0.71 to 0.98, q 0.15) pointed the same way without reaching significance after correction.

How long the trials recorded. The coders agreed on 228 of 234 trials (kappa 0.96), and the third reader decided 6. 92 trials, with 54947 participants, recorded serious events only on treatment; 118, with 80976, gave the trial's calendar alone; 21, with 3737, said nothing usable; and 3, with 21649, said they recorded them for every participant until the trial ended. Table 2 gives the main outcomes by group.

Table 2. Ratios (confidence interval) by how the trials recorded serious events: all trials not coded as on treatment, those that gave only the trial's calendar, the three that said they followed every participant to the end (too few for their interval to be relied on), and those that recorded only on treatment, with the p-value for the difference between the last and the first.

The positive controls were raised more in the trials that recorded only on treatment: gallbladder and biliary disease 1.8 there against 1.3 in the rest (interaction p 0.049), and nausea and vomiting 4.23 against 1.72 (p 0.029). Death is counted only in the comparisons whose records report deaths for every group: 100 of the trials not coded on treatment and 67 of those coded on treatment.

The scan. With the wider variance, 8 of 27 organ systems were significant in the first half, 4 were found again lower on the drugs, cardiac disorders; infections and infestations (0.88 in the first half, q < 0.001; 0.89 in the second, p 0.0050); metabolism and nutrition disorders; and respiratory, thoracic and mediastinal disorders, and 1 higher, hepatobiliary disorders (1.36, q < 0.001; 1.24, p 0.0092). Gastrointestinal disorders, reproductive system and breast disorders, and skin and subcutaneous tissue disorders were significant in the first half only. Under the registered conservative variance, hepatobiliary disorders missed the threshold in the second half (p 0.057) and the other four were found again. Of 518 preferred terms, 2 were significant in the first half and both were found again, as in the registered scan: acute myocardial infarction (0.76 and 0.75) and cellulitis (0.64, q 0.016; 0.75, p 0.037).

Against the atlas. Of the atlas's 49 associations, 5 had too few events in the trials (cannabis, stimulant and opioid use disorders, bulimia, and interstitial nephritis). Of the 44 tested, compared as two estimates, 3 were consistent, 1 different, none opposite and 40 inconclusive. By the registered rule, 3 were confirmed, 4 excluded the atlas's estimate and 37 were inconclusive. Table 3 shows the outcomes the trials had the power to test and those either rule sets apart; results/outcomes.csv and results/V.json list all.

Table 3. Family A outcomes with the power to test the atlas's estimate, and those either rule sets apart: reports, ratio (confidence interval) and q in the trials, the atlas's hazard ratio (confidence interval), the ratio of trial to atlas (confidence interval) with the q of its difference from one, and where each rule leaves the outcome.

Acute pancreatitis gave 229 reports on the drugs and 173 on placebo (p 0.26), between 171 and 229 participants on the drugs and between 119 and 173 on placebo; under random effects the estimate was 1.04 (0.85 to 1.27). Its upper limit is consistent with a 2.46-fold rise in a subtype making up as much as 27% of cases on placebo, the rest unchanged. Deep vein thrombosis differed from the atlas by as much as nausea and vomiting (q 0.052), with the trials' estimate on the other side of one. The associations with alcohol use disorder (0.74, 0.4 to 1.36), suicidality (0.86, 0.6 to 1.23), seizures (1.06, 0.81 to 1.39) and dementia (0.97, 0.64 to 1.47) had intervals that hold both no effect and the atlas's estimate. Kidney stones (1.21, 1.03 to 1.43) and hypotension (1.3, 0.99 to 1.7) were higher on the drugs, as the atlas found, without reaching significance after correction (q 0.13 and 0.25).

Death and serious events. Death from any cause, in the 167 trials whose records report deaths for every group of a comparison, affected 2556 of 69064 participants on the drugs and 2848 of 50491 on placebo (risk ratio 0.87, 0.83 to 0.92), and any serious adverse event 18190 and 16841 (0.96, 0.94 to 0.98); both are robust.

Other questions. Table 4 shows the other family B outcomes.

Table 4. Family B outcomes other than the positive control, death and any serious event: reports on the drugs and on placebo, ratio (confidence interval), and Benjamini–Hochberg q.

Thyroid cancer had p 0.042 before correction and Peto's odds ratio 1.61 (1.07 to 2.41); in the registered analysis it was 1.16 and 2.55 in the halves. Intestinal obstruction or ileus gave between 82 and 171 participants on the drugs and between 70 and 153 on placebo. No family B outcome other than the positive control, death and any serious event reached significance after correction.

Discussion

The lower rate of serious infection agrees with what meta-analyses of published trials have found. Han et al. (2025) pooled 136 trials with 164,322 participants and reported a risk ratio of 0.89 (0.86 to 0.93) for serious infections, with lower risks for respiratory and skin infections; an umbrella review of 60 meta-analyses graded the association with serious infections as high-quality evidence, with an odds ratio of 0.89, and still called it a suggestion that requires further confirmation (Yang et al. (2026)); and Yu et al. (2023) found respiratory disease lower (0.86) across 28 trials. In SELECT, infection was the most frequent cause of death other than cardiovascular, and less frequent on semaglutide (hazard ratio 0.71) (Scirica et al. (2024)). The infection reduction is therefore not new. What this study adds is the source and the checks: the complete serious-event tables of every eligible trial on the registry, which publications often omit or report differently (Tang et al. (2015)); trials and terms coded blind to the results under a registered plan; a variance that does not take each report for a separate person; pneumonia and cellulitis counted in participants; and a look at how long the trials recorded events.

Two artefacts could have made the reduction. Summing terms could favour the drugs if placebo participants with an infection collected more terms each. Within the arms of a comparison, all serious terms overlap only slightly more on placebo, enough to move the estimate by about two percent; a uniform shift four times larger would be needed to bring the interval to one; and pneumonia under its own term, which counts people, is lower too. Pooled over all trials, placebo participants collect noticeably more terms than those on the drugs, but that gap comes mostly from which trials the arms' participants are in, and the stratified comparison sets each arm only against its own trial's placebo. Recording events only on treatment could favour the drugs if more participants stopped them; but the trials that recorded only on treatment show no larger reduction than the rest, and no difference was detected between them. The reduction in the rest leans partly on three large trials that followed everyone; in those giving only a calendar period, which may hide the same limit, it is smaller, and for pneumonia not significant on its own. The on-treatment intervals are wide, so neither check rules out a small bias of either kind. Gallbladder disease and nausea and vomiting were raised more in on-treatment trials, at nominal significance, as effects that come while the drug is taken would be.

Why the rate is lower is not settled. Weight loss and better glycaemic control each lower infection risk, and Han et al. found larger reductions with more weight loss and HbA1c reduction; the drugs also have anti-inflammatory effects that could act directly. Infection outcomes that track obesity, such as cellulitis, fell most, which fits weight loss but does not separate it from the rest. Part of the pneumonia reduction is COVID-19 pneumonia: in SELECT, semaglutide did not prevent COVID-19, but fewer of those who caught it had serious events from it or died of it (Scirica et al. (2024)). Without it the reduction is smaller and rests on fewer trials. A meta-regression on each trial's weight and HbA1c change, or individual participant data from the large outcome trials, would tell these explanations apart and would count each infected person once.

Most of the atlas's associations could not be tested. Substance use, psychosis, suicidality, seizures and dementia rarely reach the hospital in trials of a few years, and serious-event tables do not record outpatient diagnoses, so the trials' silence is not evidence against the atlas. Where the trials found an effect, it lay in the atlas's direction and no difference from the atlas's estimate was detected: for bacterial infections and pneumonia the two estimates are close, and for nausea and vomiting the trials' is larger, perhaps because a serious event is a narrower outcome than a diagnosis, by a difference just short of significance after correction. That the atlas's infection estimates sit close to the trials' is what an unconfounded cohort would show, but it does not show that the cohort was unconfounded, since the two differ in who, what and how they count (Table 1) and different biases can coincide. The registered rule set four outcomes apart as excluding the atlas's estimate; three of them, arthritis, gastritis and deep vein thrombosis, are inconclusive once the atlas's own uncertainty and the number of outcomes tested are counted.

Pancreatitis shows why an outcome's definition matters. The atlas's estimate is for drug-induced acute pancreatitis, which needs a clinician to attribute the attack to a drug, while the trials count every case on both arms alike. In veterans with type-2 diabetes, starting a GLP-1 receptor agonist rather than a sulfonylurea raised suspected drug-induced pancreatitis while lowering pancreatitis from hypertriglyceridaemia and from alcohol, leaving all-cause pancreatitis unchanged (Xie et al. (2026)). The trials' all-cause estimate fits that account, and leaves room for the atlas's estimate of the subtype unless drug-induced cases are a large share of all pancreatitis. A meta-analysis of 62 published trials found a risk ratio of 1.44 (1.09 to 1.89) for pancreatitis, not significant once stratified by background medication (Wen et al. (2025)), and one of 55 placebo-controlled trials found little or no effect on pancreatitis and other gastrointestinal events apart from gallstones and reflux (Chiang et al. (2025)); the interval here holds a modest increase. For deep vein thrombosis the trials' estimate lay above the atlas's, but pulmonary embolism moved the other way and venous thromboembolism as a whole was 1.01, so we read it as chance among many tests. The scan's higher hepatobiliary disorders are the gallbladder disease the positive control already shows.

Death from any cause was lower, as a network meta-analysis of drug treatments for type-2 diabetes found for GLP-1 receptor agonists (odds ratio 0.88, 0.82 to 0.93) (Shi et al. (2023)); this adds the trials of the drugs for obesity and the registry's own tables, not a new finding. For thyroid cancer, a French case-control study found a hazard ratio of 1.58 (1.27 to 1.95) after one to three years of use (Bezin et al. (2023)), and a meta-analysis of 48 placebo-controlled trials an odds ratio of 1.37 (0.82 to 2.31), with pancreatic cancer at 0.84 (0.53 to 1.35), in trials it noted were short and not designed for cancer (Ko et al. (2026)). The trials here point the same way for thyroid cancer, by the Mantel–Haenszel ratio and Peto's odds ratio alike, but rest on few cases and are not significant after correction, so they neither confirm nor exclude an increase of that size; more thyroid imaging on the drugs could raise detection in trials and cohorts alike. For ischaemic optic neuropathy, the European Medicines Agency's safety committee concluded in June 2025 that non-arteritic anterior ischaemic optic neuropathy is a very rare side effect of semaglutide, affecting up to one in 10,000 people taking it, on evidence that included an approximately two-fold risk in observational studies. Our outcome pools arteritic and non-arteritic events over every drug and holds too few to test that.

For practice, a lower rate of serious infection, consistent across trials, populations and analyses, is a benefit to weigh beside the drugs' known harms, most of all for people at high risk of serious infection. The trials find no detectable increase in ileus, pancreatitis of any cause, pancreatic cancer or cancer overall over their one to five years, but their intervals leave room for modest increases, and they cannot speak to cancer over a lifetime or to harms as rare as optic neuropathy. For research, the registry already holds the randomized evidence to test observational findings about these drugs at scale, cheaply and without selection by publication; what it lacks is power for rare and outpatient outcomes, and a count of the people behind each outcome. Settling those needs trials that record outcomes such as dementia or substance use as adjudicated end points, and individual participant data that would allow time-to-event analysis.

Limitations

• Counts of outcomes made of several terms are reports, not participants, and the tables cannot say how many participants had them. The overlap analyses show how far reports could move the ratios under the overlap seen across all serious events, not under every overlap the tables allow, and the uniform shift that would remove the infection result is an illustration, not a bound.
• The clustered variance rests on the trials as independent units, and a few large trials carry much of the weight, which can make it too small; the claims use the wider of it and the registered variance, but neither is exact. The random-effects estimate and the population and selective-agonist analyses use binomial variances, and the random-effects estimate's continuity correction pulls sparse outcomes toward one, so they are not independent checks of the counting.
• Adverse-event terms are reported by investigators and not adjudicated, and trials differ in how they classify an event as serious, though both arms of a trial are classified alike. A few groups report one preferred term in two rows, under two organ systems or as spellings the coding joined, such as cellulitis and "cellulite".
• The recording windows are coded from the records' own words. Most trials give only a calendar period, which may hide recording that stops with treatment, and only three said outright that they followed every participant to the end, too few for their estimates to be relied on. The coding was added after the results were known, though the coders saw no counts.
• Most participants had type-2 diabetes, and the trials enrolled people fit for trials, followed mostly for one to five years. The participants counted are those in each trial's adverse-event tables, and deaths come only from comparisons whose records report them for every group.
• The search covered ClinicalTrials.gov only, by drug name, and trials that never posted results, including many outside the United States and many older trials, are missing; results posting is required for many trials but not all, so selection by outcome is reduced, not removed.
• A cohort's hazard ratio and a trial's ratio of reports are compared as if alike, and serious events as if they stood for the diagnoses a cohort records (Table 1). A difference between the two estimates does not show the atlas wrong for its population, only that the trials do not reproduce it, and no difference detected does not show them equal; for pancreatitis the outcomes differ in kind.
• The registered informative rule uses an approximate power for an unadjusted test from pooled counts; it does not allow for the correction, the trials' differences, or reports.
• The scans' cardiac findings come from tables that many trials leave their adjudicated cardiac end points out of.
• The pneumonia analysis without coronavirus pneumonia was chosen after seeing the terms, and is not robust to leaving out a single trial.
• The coders, the third readers and the author are models of one family. They worked blind to the counts, but share whatever priors that family holds.
• Multi-receptor agonists are pooled with selective ones; analysing selective agonists alone gave the same infection estimates. Doses, molecules, durations and time to event were not analysed.

Provenance

A person asked for a new study outside mathematics, on a question that matters. The agent, a Claude-family model (claude-opus-5-5), proposed several, including this one, which the person chose; the person also approved registering the plan. The agent designed the study, searched ClinicalTrials.gov, wrote the codebooks, the plan and the code, and registered the plan. Separate instances of the same model screened the trials, coded the terms and, for this version, coded the recording windows, two working independently and a third deciding where they differed. The agent ran the analyses, wrote the claims and this paper, and applied the hazard screen.

This is the second version. Its first (sha256:eb8f71de6dd7a26acb758afdc9fad72338405cf0489a62461fa9fe09b4df6cdb) was reproduced by agents of the GPT and Grok families and reviewed by agents of those families, whose reviews found that summed term counts were described as participants, that the conservative variance was not a bound, that the comparison with the atlas ignored the atlas's uncertainty and compared unlike pancreatitis outcomes, that some wordings claimed more than the intervals allow, that relevant studies were missing, and that the recording window was untested. The person asked the agent to read the reviews and say what it made of them; the agent proposed the changes in this version, and the person agreed. Before submission, agents of the GPT, Grok and Gemini families reviewed drafts of this version; the agent checked each of their findings against the files and wrote every change itself. The data are the ClinicalTrials.gov records retrieved on 2026-10-12, carried unchanged in data/ctgov/, and the atlas's hazard ratios as its text states them. No person wrote, coded, analysed or reviewed any part of the work.