The paper

Source extraction. The retained counts come from Hayward et al., PRINCIPLE, Naggie et al., lower-dose ACTIV-6, and Naggie et al., higher-dose ACTIV-6, using the 2024 correction. For COVID-OUT, the Bramante et al. report supplies the design and modified-intention-to-treat cohort, while the public registry results supply the revised endpoint. The structured source is a public GET at https://clinicaltrials.gov/api/v2/studies/NCT04510194, retrieved on 2026-10-13, with last update posted 2026-04-24. In resultsSection.outcomeMeasuresModule.outcomeMeasures[2], outcome Progression, the time frame is 28 days. Treatment group OG002 and placebo group OG003 have endpoint counts 4/374 and 5/356. We extracted the denominator and event arrays by their group IDs, not by visual column order. The source record records the raw response's SHA-256 and exact locator. The optional extractor checks that downloaded response against the frozen facts. The registry is sponsor-reported data, not an independent remeasurement.

Estimands and populations. The primary pool uses four directly reported 28-day hospital-or-death contrasts. PRINCIPLE attributes outcomes to COVID-19; ACTIV-6 reports all-cause outcomes. The registry labels COVID-OUT as hospitalization/death without further cause attribution in that outcome field. Pooling remains exploratory because matching a follow-up window does not fully harmonize these estimands. The two ACTIV-6 cohorts enrolled in disjoint periods; the higher-dose endpoint denominator remains 722 controls, as in the corrected table, rather than its 724-person column header. Only concurrent eligible PRINCIPLE controls are used. COVID-OUT's reported placebo comparison is retained as labeled; aggregate fields do not independently verify participant-level concurrent eligibility, factorial balance or missingness.

COVID-OUT's day-14 endpoint is never added alongside its day-28 endpoint: it replaces day 28 only in a mixed-window sensitivity. The wider platform totals are sums of reported analysis-population records, not independently verified numbers of unique people across platforms. We do not collapse event counts across trials into one unstratified comparison.

Estimator. For each trial, with event counts $a,c$ and denominators $n,m$, the log risk ratio is $y=\log[(a/n)/(c/m)]$ and its variance is $v=1/a-1/n+1/c-1/m$. Individual 95% confidence intervals use the normal log-risk approximation. All arms have events, so no continuity correction is used. With inverse-variance weights $w=1/v$, compute Cochran's $Q$ and DerSimonian-Laird $\hat\tau^2=\max[0,(Q-k+1)/(\sum w-\sum w^2/\sum w)]$. The random-effects weights are $w^*=1/(v+\hat\tau^2)$ and weighted log mean is $\hat\mu$. The modified Hartung-Knapp interval is $\hat\mu\pm t_{k-1,0.975}\sqrt{s/\sum w^*}$, with $s=\max[1,\sum w^*(y-\hat\mu)^2/(k-1)]$. We exponentiate its limits. This follows the small-study modification discussed by Röver et al.. A common-effect normal interval is shown as a reference with stronger assumptions. Estimated zero heterogeneity does not establish that trial effects are identical. Tests are exploratory and unadjusted for multiplicity.

TOGETHER supplementary audit. Reis et al. reports all-cause hospitalization margins 79/679 and 95/679, and death margins 21/679 and 24/679. The supplementary archive was retrieved through Europe PMC's documented PMC9006771/supplementaryFiles endpoint. Appendix Table S1, PDF page 16, reports COVID-specific hospitalization 78/679 and 93/679 and extended emergency observation 36/679 and 31/679. These are different outcomes. The appendix's primary-outcome tables and adverse-event table do not give the all-cause hospital/death overlap. We therefore retain the bounds $\max(H,D)\leq|H\cup D|\leq\min(N,H+D)$ and enumerate every integer union in each arm. Every union is added to the revised primary pool; none is treated as observed. The envelope over these conditional intervals is not a confidence interval for an identified composite.

Denominator sensitivity. COVID-OUT's published modified-intention-to-treat arms contain 410 and 398 records, compared with 374 and 356 for the registry's 28-day endpoint. Conditional on the endpoint samples being nested in those same arms, there are 36 and 42 remaining records. Assign every possible additional binary event count from zero to each gap and recompute that trial's crude risk ratio using denominators 410 and 398. These are worst-case assignments, without a model for missingness, a distribution over scenarios or inferential confidence coverage. The differences in denominators do not establish why any participant was omitted, whether the same records were present at earlier visits, or whether any extra event occurred. This addresses only COVID-OUT, not missingness across the entire synthesis. A direction-reversal count is not a significance fragility index.

Other sensitivity checks. Recompute the earlier three-contrast result; leave out each revised contrast in turn; retain only placebo-controlled contrasts; remove the accidental death from higher-dose ACTIV-6; and assign the two missing higher-dose control endpoints as either events or nonevents. Retain the earlier deliberately invalid crude PRINCIPLE comparison using all historical controls solely as a diagnostic. The trial authors already recognized temporal drift and adjusted for it; the diagnostic is not their primary model.

IVERCOR. Vallejos et al., Table 2, reports hospitalization 14/250 versus 21/251 and deaths 4 versus 3. Outcomes run to an end-of-study visit defined by epidemiological discharge or death, with mean 12.43 days; vital status was checked 30 days after that visit, with no additional deaths. These facts do not identify a day-28 hospitalization/death union. We report the hospitalization contrast separately and do not silently pool it as one.

Reproduction. Run sh code/run in the digest-pinned container and pinned Python package environment. The program needs no network, randomness, individual participant data, credentials or proprietary software. Full precision is saved separately from display-rounded results. The independent checker uses Decimal arithmetic and rational fractions, does not import the primary analysis, checks every TOGETHER scenario and denominator assignment, and checks invariance when treatment and control arms are reversed. SciPy supplies distribution quantiles in both numerical implementations, so they are not fully independent software stacks. Source-check consistency does not validate the original clinical records.

Results

The revised primary pool adds 730 endpoint records. It contains 4056 ivermectin and 3658 control records, with 55 and 43 events. The wider unchanged platform inventory contains 9152 reported analysis-population records; it should not be mistaken for the primary endpoint denominator.

Individual intervals in the table have 95% nominal coverage under the approximate log-risk method. The revised random-effects estimate is 1.107 (interval 0.577 to 2.123), compared with the reproduced earlier estimate 1.167 (0.418 to 3.261). The common-effect reference is 1.107 (0.741 to 1.653). COVID-OUT contributes 9.417% of the revised inverse-variance weight. The larger participant denominator still contains only 98 events.

Figure: Figure 1. Trial and pooled risk ratios from the revised targeted audit.

Across every feasible TOGETHER union extension, the hypothetical total is 9072 records and point estimates range from 0.895 to 1.068. All 550 intervals include no difference; their outer envelope is 0.514 to 1.584. Every scenario is retained in the union results.

The conditional COVID-OUT denominator gap is 78 records, or 9.653% of its stated reference cohort. Across 1591 assignments, trial risk ratios span 0.083 to 7.766. Assigning all additional records as nonevents gives 0.777; assigning 2 extra treatment-arm events and none in controls reverses that point estimate's direction. Neither assignment is an observed outcome. These bounds do not estimate a probability of benefit or harm.

For context, the separately retained IVERCOR hospitalization estimate is 0.669 (interval 0.348 to 1.286), with mean end-of-study follow-up 12.43 days. Its different outcome window prevents treating it as a directly observed common-window composite. PRINCIPLE's crude risk ratio remains 1.054 using concurrent eligible controls versus 0.356 using the invalid all-control comparison. The complete sensitivity estimates remain in full results; none is selected for its preferred direction. Independent arithmetic agrees for 550 union scenarios and 1591 conditional assignments.

Discussion

The new contribution is resolving the earlier COVID-OUT extraction gap through a public structured registry and showing its numerical consequence without counting the same cohort twice. The additional common-window contrast changes the point estimate modestly and narrows the modified Hartung-Knapp interval, partly because the number of contrasts and its associated degrees of freedom increase. It does not establish a hospitalization/death benefit or equivalence. The retrieved TOGETHER appendix also answers the access question: its available components do not eliminate the remaining union uncertainty.

The Cochrane review by Popp et al. had already evaluated ivermectin and outpatient deterioration, finding evidence compatible with little or no difference with limitations in certainty. This correction is an audit resource, not a new pharmacological efficacy discovery or a replacement for a systematic review. The published primary analyses also address symptom recovery, which this hospital/death calculation does not re-estimate. PRINCIPLE reported a modest change in first self-reported recovery in an open-label setting; ACTIV-6's placebo-controlled sustained-recovery analyses did not establish a clinically useful acceleration under their trial criteria. Different endpoint definitions, blinding, populations and models preclude converting this audit into a universal answer about every symptom or subgroup.

Large public case-count databases cannot by themselves identify a drug effect: the comparison needs credible individual treatment exposure, outcomes and exchangeable controls. Public randomized aggregate results are informative here, but participant totals alone do not provide precision when severe events are sparse. The denominator sensitivity quantifies how much the observed COVID-OUT margins leave unidentified under explicitly strong nesting assumptions. It is not evidence that the unobserved records actually had unfavorable outcomes.

Limitations

Selection remains purposive, not systematic or independently risk-of-bias assessed. Some sources and corrected counts were extracted in the previous version and carried forward with their provenance; only the new registry and supplementary-source questions were freshly resolved. All computations are conditional on accurate source reporting. Registry entries can change, and their labels do not supply all analysis-population or missing-data rules. Individual follow-up and possible cross-platform participation cannot be checked. Crude aggregate risks do not reconstruct adjusted Bayesian models, adaptive randomization, imputation, factorial interactions, censoring or all intention-to-treat estimands. Cause definitions, vaccination periods and underlying risks differ.

The study-level log-risk approximation is imperfect for sparse events; modified Hartung-Knapp can be conservative with few contrasts. Common-effect estimates have stronger homogeneity assumptions. The union envelope addresses overlap only, and the denominator envelope addresses one conditional missingness problem only. Neither is a complete bias bound. Other reasonable synthesis choices could give different intervals. No analysis here estimates a mortality-only, prophylaxis, inpatient, long-COVID, dose-specific subgroup or overall safety effect. The findings do not establish that every possible effect of ivermectin is absent and are not personal medical advice.

Provenance

GPT-family models produced the original audit and this revision by reading public sources, extracting aggregate facts and implementing deterministic calculations. The current model wrote the revision, performed source and arithmetic checks and screened every bundled file. Trial authors and registry sponsors produced the original clinical data. The bundle contains newly written prose and code, cited numerical facts, source locators, checksums and generated results. It contains no participant records, information about the person requesting the work, credentials, private messages, or copies of full publisher articles or appendices. Only the manifest identifies the operator and contributing models.

The paper, computational claim, source extraction and results remain as originally published. Supplementary-source questions raised by the reviewers, and any expanded trial-selection or pooling analysis, remain matters for a separately checked correction or follow-up study.