CROWN CORONATION: COVID-19 Research Outcomes Worldwide Network for CORONAvirus prevenTION: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for CROWN CORONATION: COVID-19 Research Outcomes Worldwide Network for CORONAvirus prevenTION (NCT04333732), a randomized phase 3 study. The primary outcome is Number of Participants With Symptomatic COVID-19 at 60 Days.

2. Clinical Question

3. Trial Design

CROWN CORONATION is described in the registry as an international, multi-site, Bayesian platform adaptive, randomized, placebo-controlled trial. It is listed as Phase 3, with a parallel-group model and double masking. The registry identifies Washington University School of Medicine as the sponsor and reports an enrollment of 3411. The trial status is completed; the recorded start date is 2020-09-04 and primary completion date is 2021-08-10.

The posted primary comparison is M-M-R II® versus placebo. Both groups received education and surveillance; the active group received a single 0.5 mL subcutaneous injection of M-M-R II®, and the control group received a single 0.5 mL subcutaneous injection of 0.9% saline. The primary endpoint was symptomatic COVID-19 by 60 days after intervention. Listed secondary outcomes concern symptomatic COVID-19 at 150 days, COVID-19 severity at 60 and 150 days, and SARS-CoV-2 infection risk up to 150 days.

The official title characterizes the study as a Bayesian platform adaptive trial, but details of the adaptive procedures, Bayesian model, allocation ratio, or decision rules are not reported in the registry record. The original sample-size justification and the trial’s own planned statistical analysis are also not reported in the registry record. The registry lists five outcome measures and two posted analyses. Those record counts do not establish which analysis procedures were planned in advance or how the platform features were implemented.

Enrollment and endpoint-analysis counts are not identical: the primary endpoint lists 1607 participants for M-M-R II® and 1545 for placebo. The registry record does not explain the difference between the overall enrollment and these analysis denominators. Randomization and double masking describe key design features, but by themselves they do not specify the handling of missing outcomes, adherence, or exclusions from an analysis.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Symptomatic COVID-19 at 60 Days, measured over 60 days after receiving trial intervention.

The primary endpoint counts participants with symptomatic, laboratory test-confirmed COVID-19 by 60 days after receiving the trial intervention. The registry’s definition includes a set of symptoms: cough, shortness of breath or difficulty breathing, fever, chills, muscle pain, sore throat, new loss of taste or smell, nausea, vomiting, or diarrhea. A participant’s event therefore depends on both symptoms and laboratory confirmation, according to the endpoint description.

This is a binary outcome at the participant level: each person is counted as having or not having the endpoint during the specified follow-up period. For this kind of outcome, the number of events and the number of participants assessed in each group describe the observed event frequency. A risk difference expresses the contrast between the groups’ event risks on an absolute scale. It is useful because it relates the group difference directly to the probability of experiencing the specified event.

The endpoint focuses on symptomatic disease rather than all SARS-CoV-2 infections. The registry separately lists infection risk as a secondary outcome, underscoring that symptomatic, laboratory-confirmed disease and infection are distinct outcomes in the trial record. The primary endpoint is used to address the stated prevention objective, but it does not by itself describe disease severity, infection without symptoms, or outcomes beyond the specified follow-up.

7. Results Posted in the Registry

• M-M-R II ®: 1.5% (24/1607) versus 1.2% (19/1545) on control; risk difference 0.3 percentage points (95% CI -0.5 to 1.1), risk ratio 1.21 (0.67–2.21); unadjusted two-proportion z-test p = 0.523.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Participants With Symptomatic COVID-19 at 150 Days

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • M-M-R II ®: 4.1% (65/1585) versus 4.1% (64/1544) on control; risk difference -0.0 percentage points (95% CI -1.4 to 1.3), risk ratio 0.99 (0.71–1.39); unadjusted two-proportion z-test p = 0.951.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between M-M-R II ® and the control. The interval gives the range of effects that remain compatible with the data.

Severity of COVID-19 Measured at 60 Days After Intervention

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • M-M-R II ®: 0.2% (3/1607) versus 0.1% (1/1544) on control; risk difference 0.1 percentage points (95% CI -0.1 to 0.4), risk ratio 2.88 (0.30–27.68); unadjusted two-proportion z-test p = 0.337.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between M-M-R II ® and the control. The interval gives the range of effects that remain compatible with the data.

Severity of COVID-19 at 150 Days After Intervention

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • M-M-R II ®: 0.2% (3/1585) versus 0.1% (1/1544) on control; risk difference 0.1 percentage points (95% CI -0.1 to 0.4), risk ratio 2.92 (0.30–28.06); unadjusted two-proportion z-test p = 0.330.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between M-M-R II ® and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover symptomatic COVID-19 at a later follow-up point, COVID-19 severity at two follow-up points, and SARS-CoV-2 infection risk up to 150 days. Taken together, the posted numerical comparisons do not present a clear, consistent separation between the randomized groups. The pattern is broadly in keeping with the primary comparison’s uncertainty, rather than providing a strong independent basis for a different overall interpretation.

Secondary outcomes help describe whether the primary pattern is accompanied by differences in related outcomes or over additional follow-up. They are not interchangeable with the primary endpoint: severity, symptomatic disease, and infection risk address different questions. The registry lists infection risk as a secondary outcome, but its detailed result is not reported in the registry record. Sponsor-reported analyses for the severity outcomes are also not reported in the registry record.

Unadjusted secondary results carry less weight when several outcomes are examined. In general, considering many outcomes increases the chance that at least one comparison may appear notable by chance, even when no underlying difference exists. A prespecified multiplicity strategy can address this issue, but such a strategy is not reported in the registry record. Accordingly, secondary estimates are best treated as supporting descriptive evidence, not as standalone confirmation of the primary finding.

The secondary results should be read in light of their event counts, denominators, follow-up periods, and uncertainty. Small event counts can make estimates unstable, and incomplete reporting limits comparisons across all outcomes named in the registry. These considerations mean the secondary pattern can add context without resolving the uncertainty around the primary endpoint.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Number of Participants With Symptomatic COVID-19 at 150 Days
• Severity of COVID-19 Measured at 60 Days After Intervention
• Severity of COVID-19 at 150 Days After Intervention
• Risk of SARS-CoV-2 Infection up to 150 Days After Trial Intervention

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is a count of participants with an event. For a binary endpoint, each participant either meets the event definition or does not. The event count is interpreted alongside the number of participants in the group, because the same number of events can represent different risks in groups of different sizes. The analysis denominators for the primary comparison are 1607 for M-M-R II® and 1545 for placebo.

What does a risk difference describe?

A risk difference subtracts the event risk in one group from the event risk in the other. It is an absolute contrast: a value of zero corresponds to equal event risks, while positive or negative values indicate the direction of the contrast according to the subtraction convention. The recalculated primary risk difference is 0.003. The displayed group risks are 0.012 for placebo and 0.015 for M-M-R II®. These are the posted risk values used in the recalculation. A risk difference is distinct from a relative measure such as a risk ratio or odds ratio, which compares risks or odds by division rather than subtraction.

What does the confidence interval add?

A confidence interval gives a range of values compatible with the data under the method used to construct it. It communicates uncertainty around an estimate rather than replacing the estimate. For the recalculated primary risk difference, the interval runs from -0.005 to 0.011. Since this includes zero, the data do not clearly distinguish the estimated contrast from no difference. The interval also includes values in both directions, so the estimate is not precise enough to settle the direction of the group difference.

The sponsor’s primary analysis is identified as logistic regression, with the reported parameter being risk difference. Its reported 95% confidence interval is -0.5 to 1.1 on the reported percentage-point scale. The registry record does not explain the exact regression specification, covariates, or method used to derive the risk difference from the logistic regression. Those details should not be inferred from the method label alone.

How should the p-value be read?

The sponsor reports p = 0.52 for the primary analysis; the simple recalculation gives an unadjusted p-value of 0.523. A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the assumptions of the test. It is not the probability that the null hypothesis is true, the probability that the result occurred by chance, or a measure of treatment effect size. A p-value should be read with the point estimate, confidence interval, design, and endpoint definition.

What is the role of the recalculation?

The recalculated comparison is an unadjusted calculation from the posted event counts and group sizes. It does not reproduce an adjusted regression model or any unreported protocol procedures. Its value is to provide a transparent summary contrast that can be checked against the group-level results. Because the registry’s reported analysis is available and there is no noted discrepancy, that sponsor analysis remains the primary reported inferential result.

The record describes the trial as Bayesian and adaptive in its official title, but the posted primary result is presented as a regression analysis with a risk difference, confidence interval, and p-value. Bayesian platform methods can involve models that borrow information or adapt trial procedures, but those are general possibilities, not claims about this study’s implementation. The specific prior distributions, adaptation rules, interim decision procedures, and Bayesian estimates are not reported in the registry record.

For sparse binary outcomes, estimates can be sensitive to small changes in event counts, and relative measures can have wide uncertainty. General statistical reasoning therefore favors reading the event counts, absolute risk difference, and interval together rather than treating a single test statistic as decisive. The posted primary event counts are modest, which helps explain why uncertainty remains important even though the group denominators are substantial. No method can make the endpoint more informative than the information contained in the observed events and follow-up.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.003, with a 95% confidence interval from -0.005 to 0.011. The range crosses zero and extends to both negative and positive differences. Thus, the point estimate is not precise enough to establish which group had the lower event risk. The interval describes uncertainty around the risk-difference estimate; it is not a range in which individual participants’ outcomes fall.

The sponsor-reported primary risk difference is 0.3 on the reported percentage-point scale, with a 95% confidence interval from -0.5 to 1.1 and p = 0.52. The sponsor result likewise has an interval that includes zero. The reported and recalculated estimates use different displayed scales, but both communicate uncertainty about the direction and size of the primary contrast. There is no reported discrepancy between them.

Precision depends not only on the total number of participants but also on the number of observed events and the variability of the outcome. General statistical reasoning explains why binary outcomes with few events may have substantial uncertainty even when many participants are enrolled. The primary result should therefore be understood as an estimate with meaningful uncertainty, rather than as a definitive demonstration of equivalence or of a difference.

A confidence interval is not a guarantee that the true value lies within its endpoints, nor does it assign a probability to each value inside the range. Its interpretation relies on the statistical method and assumptions. The registry record does not report enough detail to independently assess every modeling assumption behind the sponsor’s interval. The displayed interval is most useful as a clear indication that the data allow a range of plausible group contrasts.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original design calculations. For the binary outcomes, the figures are participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm that would be needed, under those assumptions, for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses the same kind of interpretation with a higher target chance of detecting that effect. These are design-planning quantities. They do not tell how likely the trial’s observed result was to be true, and they do not show the trial’s achieved power.

Each planning row uses a different fraction of the observed effect: 100%, 75%, or 50%. A smaller effect is harder to distinguish from random variation, so it requires more participants per arm under the stated assumptions. The figures can therefore rise sharply as the target effect becomes smaller, particularly when the observed effect itself is close to zero. They should not be treated as a recommended target for a future study without an independently justified effect size and design.

The sample-size curve is another way to view how the planning requirement changes with the effect being targeted. It reflects the same stated assumptions and the observed estimate on which the illustration is based. When the observed effect is small or uncertain, the resulting planning figures can be very large and unstable as estimates of future study needs. This is not observed power; it is a planning illustration conditional on the stated assumptions.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.012; treatment proportion p₁ = 0.015; average p̄ = 0.014.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1639 = 0.3212.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1639 = 0.1379.
4. n = (0.3212 + 0.1379)² / (0.0026)² = 30,319.8, rounded up to 30,320 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.0122977346278317                          # control proportion
p1 <- 0.014934660858743                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(4333732)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 30,320 (80% power), 40,590 (90% power)
 75% of observed effect: n per arm = 52,616 (80% power), 70,437 (90% power)
 50% of observed effect: n per arm = 115,488 (80% power), 154,606 (90% power)
power.prop.test: 30319.8 
Simulated power at n = 30,320 per arm: 0.799 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis for the primary endpoint using logistic regression, with risk difference as the reported parameter. The reported estimate is 0.3, with a 95% confidence interval from -0.5 to 1.1 and p = 0.52. The registry also reports an analysis of symptomatic COVID-19 at 150 days. It does not provide sponsor-reported analyses for the severity outcomes.

The recalculated primary risk difference is 0.003, with a 95% confidence interval from -0.005 to 0.011 and unadjusted p-value 0.523. This recalculation uses only the posted group counts and denominators; it is not a recreation of the logistic regression. The sponsor’s analysis is the relevant reported inferential analysis, while the recalculation offers an unadjusted comparison that can be understood directly from the group summaries.

The registry does not flag a discrepancy between the primary recalculation and the sponsor result. Both analyses place the estimate near zero and have confidence intervals that include zero. Their broad interpretation is therefore aligned, though the methods and displayed scales differ. Details needed to reproduce the sponsor model, including covariates and model specification, are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The record lists a primary outcome and several secondary outcomes, and it identifies two posted analyses. It does not report a multiplicity adjustment strategy, such as a prespecified hierarchy or another method for controlling the chance of false-positive findings across multiple comparisons. Without that information, unadjusted secondary p-values, where available, should be interpreted cautiously. The registry record does not state whether an adjustment was planned in the protocol.

Information about missing outcome data is not reported in the registry record. The primary analysis denominators are smaller than overall enrollment, but the record does not explain why, whether outcomes were unavailable, whether participants were excluded, or how missing observations were handled. The endpoint-specific analysis populations and the rules used to determine inclusion are also not reported in the registry record. Therefore, the posted denominators alone cannot establish the extent or cause of missing data.

The registry identifies a logistic-regression method for the primary sponsor analysis and a reported risk difference, but it does not give the model specification, covariates, or analysis population definition. Details of any sensitivity analyses for missing data are not reported in the registry record. These omissions limit independent assessment of whether the analytic choices could affect the estimate.

The official title describes a Bayesian platform adaptive trial, but the registry record does not report the Bayesian model, prior distributions, interim analyses, adaptation rules, stopping criteria, or decision thresholds. These details should not be inferred from the title. The record also does not provide the trial’s original statistical analysis plan or sample-size justification. Consequently, the posted results can be described and compared, but the full planned inferential framework cannot be reconstructed from the registry record alone.

These reporting gaps do not demonstrate that the trial lacked procedures for multiplicity, missing data, or adaptive decisions. They mean only that those procedures are not reported in the registry record. Clear documentation of such choices is important because they affect how estimates, uncertainty, and multiple outcome findings should be interpreted.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: covid-19 (0.2%), pre-eclampsia (0.1%), headache (0.1%), seizure (0.1%), tuberculous meningitis (0.1%).

The registry reports serious adverse events for groups of 1722 participants in the M-M-R II® group and 1689 in the placebo group. Serious adverse events affected 11 participants in the M-M-R II® group and 5 in the placebo group. No other adverse events were reported in either group under the record’s other-adverse-event field, and deaths were recorded as 0 in both groups.

The listed serious-event terms include COVID-19 at 0.2%, and Pre-eclampsia, Headache, seizure, Tuberculous meningitis, and Ovarian infection at 0.1% each. These are registry-reported event terms and percentages; they do not establish that an event was caused by the assigned intervention. The event-group denominators differ from the primary endpoint analysis denominators, and the registry record does not explain the distinction.

Serious adverse event summaries are descriptive safety information. They do not, on their own, estimate comparative risk with adjustment for follow-up or establish a causal relationship. The registry record does not provide additional detail on event timing, attribution, or the criteria applied to each event. The figures should therefore be read as posted counts and terms rather than as a complete causal assessment of safety.

17. What the Result Does, and Does Not, Mean

The primary result describes symptomatic, laboratory-confirmed COVID-19 by 60 days after intervention among adults with repeated exposures to SARS-CoV-2. The observed counts were 24 participants in the M-M-R II® group and 19 in the placebo group. The recalculated risk difference is 0.003, and its 95% confidence interval includes zero. The sponsor-reported analysis has the same broad uncertainty: its interval also includes zero.

These results do not establish a clear difference between the randomized groups for this endpoint and follow-up period. They also do not prove that the groups are identical. The interval permits differences in either direction, and the posted counts alone do not determine the probability of any particular true effect. The p-value should not be interpreted as the probability that the intervention has no effect.

The primary endpoint is not a measure of all infections, asymptomatic infection, disease severity, or outcomes beyond the specified follow-up. The record lists those as separate or related outcomes, and some detailed results are not reported in the registry record. The primary result cannot substitute for those missing or distinct outcome comparisons.

Nor does the result establish that the intervention works or does not work in other populations, settings, or circumstances. The registry describes a particular randomized comparison of M-M-R II® and placebo, with education and surveillance in both arms. The interpretation should remain within that study’s intervention, endpoint definition, enrolled population, and recorded follow-up. It is a statistical description of the posted evidence, not medical advice.

18. Why This Trial Matters Statistically

This trial illustrates why randomized design and transparent outcome definitions matter in clinical research. Randomization creates a structured comparison between intervention and placebo groups, while double masking can help reduce some sources of bias. These design labels do not eliminate uncertainty, but they clarify the context in which event counts and estimated differences should be read.

The primary comparison also demonstrates why an estimate, confidence interval, and event counts should be considered together. A point estimate near zero does not by itself show equivalence, and a confidence interval crossing zero does not prove there is no difference. The interval communicates that the posted data remain compatible with a range of possible contrasts. That distinction is central to interpreting a result that is not statistically clear.

The record’s official title identifies a Bayesian platform adaptive design, while its posted primary analysis is described as logistic regression with a risk-difference result. This makes documentation particularly relevant: adaptive and Bayesian features can shape how evidence is accumulated and interpreted, but their specific procedures are not reported in the registry record. Readers should distinguish the design label from the detailed statistical methods that would be needed to reproduce the trial’s decision process.

Finally, the trial shows the limits of interpreting secondary outcomes and safety summaries without full methods and population details. Secondary outcomes broaden the clinical questions, but multiple comparisons and incomplete reporting can reduce the weight placed on isolated findings. A careful statistical reading identifies what the posted evidence supports while keeping unresolved questions visible.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves important design and analysis details unresolved. Although the official title describes a Bayesian platform adaptive trial, the adaptive procedures, interim analyses, Bayesian model, prior distributions, and decision rules are not reported in the registry record. The protocol’s original sample-size justification and the trial’s planned statistical analysis are also not reported.

The primary analysis denominator differs from overall enrollment, and the record does not explain the difference. Missing outcome counts, reasons for unavailable data, analysis population definitions, and methods for handling missing observations are not reported in the registry record. The sponsor analysis is identified as logistic regression, but its specification, covariates, and exact estimation procedures are not described.

Reporting of secondary outcomes is incomplete. The record names infection risk up to 150 days, but its detailed result is not reported in the registry record. Sponsor-reported analyses for severity outcomes are also not reported. The registry does not state how multiplicity was addressed, if at all. This limits the strength of conclusions drawn from a collection of secondary comparisons.

The primary endpoint is defined around symptomatic, laboratory-confirmed COVID-19 through 60 days. It does not capture all infections or outcomes outside that timeframe. The safety summaries provide serious-event counts and terms, but the record does not report event attribution, timing, or additional detail needed for a causal assessment. These limitations concern what can be established from the registry record; they do not show that the trial lacked additional procedures or documentation elsewhere.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: CROWN CORONATION: COVID-19 Research Outcomes Worldwide Network for CORONAvirus prevenTION — NCT04333732.
• Registry record last updated 2024-03-26; status last verified 2024-01.
• Results first posted 2024-03-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

CROWN CORONATION is a completed, Phase 3, randomized, double-masked, parallel, placebo-controlled trial sponsored by Washington University School of Medicine. The registry reports enrollment of 3411 and describes the study as international, multi-site, Bayesian, and platform adaptive. The primary comparison evaluated education and surveillance plus a single dose of M-M-R II® against education and surveillance plus saline placebo.

The primary endpoint was symptomatic, laboratory-confirmed COVID-19 by 60 days after intervention. The sponsor-reported risk difference was 0.3, with a 95% confidence interval from -0.5 to 1.1 and p = 0.52. The unadjusted recalculation is 0.003, with a 95% confidence interval from -0.005 to 0.011. Both results include no difference within their intervals and leave uncertainty about the direction and size of the contrast.

The registry lists secondary outcomes addressing later symptomatic disease, severity, and infection risk. Some secondary analyses and important design details are not reported in the registry record, so interpretation remains centered on the posted primary comparison and its limitations.