Randomized Proof-of-Concept Trial to Evaluate the Safety and Explore the Effectiveness of Resveratrol, a Plant Polyphenol, for COVID-19: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomized Proof-of-Concept Trial to Evaluate the Safety and Explore the Effectiveness of Resveratrol, a Plant Polyphenol, for COVID-19 (NCT04400890), a randomized phase 2 study. The primary outcome is Hospitalization Rates for COVID-19.

2. Clinical Question

This framing is important: the posted comparison concerns the assigned regimens in this trial, not resveratrol in isolation from the shared Vitamin D3 regimen. The registry reports 50 participants in each group for the primary outcome. It does not report participant-level characteristics, adherence, or subgroup results, so those details cannot refine the interpretation of the comparison.

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group, placebo-controlled phase 2 trial. Its title identifies it as a proof-of-concept study of resveratrol for outpatient treatment of mild COVID-19, and its brief summary says the study was intended to assess safety and explore effectiveness. The sponsor is Marvin McCreary, MD.

The registered intervention was resveratrol 1000mg four times per day for 15 days, paired with Vitamin D3 100,000 IU on day 1. The comparator was placebo capsules 4 times per day for 15 days, also paired with Vitamin D3 100,000 IU on day 1. Because both groups received Vitamin D3, the direct randomized contrast is between the resveratrol-containing regimen and the placebo regimen, with that supplement common to both.

The registry lists enrollment as 105. The posted primary outcome and secondary outcome summaries each show 50 participants per group. The relationship between the enrollment figure and the denominators in those posted summaries is not explained in the registry record. The dates listed are a study start of 2020-09-13 and primary completion of 2021-03-01; the current status is terminated. The reason for termination is not reported in the registry record.

The primary endpoint was hospitalization for COVID-19 within 21 days of randomization. Listed secondary outcomes include ICU admission rates, invasive ventilation rates, pneumonia, pulmonary embolism, and death. The record identifies seven outcome measures, while the detailed posted results include the primary endpoint and results for pneumonia and pulmonary embolism. Details for the remaining outcome measures are not reported in the registry record. The original statistical analysis plan, allocation procedures, masking procedures, and reasons for the study’s termination are not reported in the registry record.

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.

Before assignment: One-hundred-five subjects were enrolled and randomized. Four participants withdrew before starting treatment. One participant withdrew after one treatment day citing "too many pills" as reason for withdrawal.

Overall Study

Reasons for not completing this period:

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.

Population: Between September 13, 2020 and December 11, 2020, 1,694 patients were telephoned within 24-h of testing positive for COVID-19 to be recruited into the clinical trial . One-hundred-five were enrolled and randomized. Five withdrew after receiving treatment packets (four withdrew before starting treatment and one withdrew after one treatment day citing "too many pills" as reason for withdrawal).

6. Primary Endpoint

The registry lists the primary outcome as Hospitalization Rates for COVID-19, measured over 21 days from study randomization.

The primary endpoint counts participants admitted to hospital within 21 days of study randomization. It is a binary outcome at the participant level: a participant either had a recorded hospitalization within the specified follow-up window or did not. The posted counts are 1 participant among 50 in the resveratrol-with-Vitamin-D3 group and 3 participants among 50 in the placebo-with-Vitamin-D3 group.

Hospitalization is a clinically consequential event and provides a direct way to summarize whether participants crossed a threshold of care during the defined follow-up period. For statistical comparison, the endpoint can be expressed as the proportion with the event in each group, as well as the difference between those proportions. The registry also posts relative measures and an unadjusted p-value. These are different descriptions of the same comparison, not separate outcomes.

General explanation: a prespecified follow-up window makes clear which events count toward an endpoint and when they are assessed. A binary endpoint is straightforward to interpret, but when events are infrequent, a small change in the event count can noticeably affect the estimated group difference. The registry record does not report the endpoint’s adjudication process, details of hospitalization classification, or how missing follow-up was handled. It also does not report participant characteristics that would help readers assess how representative the trial population was.

7. Results Posted in the Registry

• Resveratrol With Vitamin D3: 2.0% (1/50) versus 6.0% (3/50) on control; risk difference -4.0 percentage points (95% CI -11.6 to 3.6), risk ratio 0.33 (0.04–3.10); unadjusted two-proportion z-test p = 0.307.

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.

Pneumonia

• 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:
  • Resveratrol With Vitamin D3: 8.0% (4/50) versus 16.0% (8/50) on control; risk difference -8.0 percentage points (95% CI -20.6 to 4.6), risk ratio 0.50 (0.16–1.55); unadjusted two-proportion z-test p = 0.218.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Resveratrol With Vitamin D3 and the control. The interval gives the range of effects that remain compatible with the data.

Pulmonary Embolism

• 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:
  • Resveratrol With Vitamin D3: 2.0% (1/50) versus 2.0% (1/50) on control; risk difference 0.0 percentage points (95% CI -5.5 to 5.5), risk ratio 1.00 (0.06–15.55); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Resveratrol With Vitamin D3 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results should be read as exploratory context around the primary hospitalization comparison. The registry lists several other clinical outcomes, including ICU admission, invasive ventilation, pneumonia, pulmonary embolism, and death. Detailed posted comparisons are available for pneumonia and pulmonary embolism; results for the other listed outcomes are not reported in the registry record. The secondary outcomes therefore do not form a complete set of evidence that can be compared uniformly with the primary result.

Across the secondary outcomes with posted comparisons, the point estimates do not all tell the same story: the pneumonia estimate is negative, while the pulmonary embolism estimate is zero. Their intervals are broad and include the null difference, and the posted unadjusted p-values do not give a basis for strong conclusions. These results do not resolve the uncertainty around the primary hospitalization estimate. Nor do they independently establish a consistent overall pattern across the full list of outcomes, because results for some listed outcomes are absent from the registry record.

General explanation: secondary outcomes can provide useful information about different aspects of a trial, but interpreting many outcomes creates a multiplicity problem. If many hypotheses are examined, some apparently notable results may arise by chance even when there is no underlying effect. An unadjusted secondary result does not account for that broader testing context. The registry record does not report a multiplicity adjustment, a hierarchy of outcomes, or a statistical analysis plan specifying how secondary outcomes were to be interpreted.

For these reasons, secondary findings carry less weight than a clearly prespecified primary comparison, particularly when the detailed analysis plan and complete results are not reported. They are most appropriately treated as descriptive and hypothesis-generating. The posted information does not support combining the outcomes into a single conclusion, and no composite result is reported in the registry record.

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

• ICU Admission Rates
• Invasive Ventilation Rates
• Pneumonia
• Pulmonary Embolism
• Death

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary, and the posted summaries count participants with hospitalization during the defined follow-up period. The main absolute comparison is the risk difference: the event proportion in the resveratrol-with-Vitamin-D3 group minus the event proportion in the placebo-with-Vitamin-D3 group. Its posted estimate is -0.04. A negative value in this direction means that the observed event proportion was lower in the resveratrol group. This is a descriptive direction for the posted data, not by itself evidence that the intervention caused a difference.

What does the risk difference tell readers?

General explanation: an absolute difference expresses how far apart two event proportions are on the probability scale. It can be useful because it retains the scale of the event itself and does not depend on choosing a reference group in the same way that a ratio does. The confidence interval for this difference describes uncertainty around the estimated contrast. In this trial, the interval runs from -0.116 to 0.036, crossing zero. The posted data therefore do not tightly determine whether the underlying difference is negative, close to zero, or positive.

How do relative measures differ?

The registry also reports a risk ratio and an odds ratio. The posted risk ratio is 0.333, and the posted odds ratio is 0.320. General explanation: a risk ratio compares the event proportions directly, while an odds ratio compares the odds of the event. Both are relative measures, so their interpretation depends on the reference group and on the scale used. When events are sparse, ratio estimates can be especially unstable. Here, their confidence intervals are wide: 0.036 to 3.097 for the risk ratio and 0.032 to 3.184 for the odds ratio. Each interval includes the value corresponding to no relative difference.

What does the p-value contribute?

The posted unadjusted p-value is 0.307. General explanation: a p-value measures how unusual data at least as discrepant as those observed would be under a null hypothesis and the test’s assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. An unadjusted p-value also does not account for a broader family of outcome comparisons. The registry record does not report the test specification or a multiplicity procedure, so the p-value should be read as the posted unadjusted result rather than as a fully documented analysis.

Why do the counts matter?

The group summaries report 1 hospitalization among 50 participants in the resveratrol group and 3 among 50 in the placebo group. General explanation: when an outcome occurs infrequently, estimates can be sensitive to a small number of events, and intervals can be wide even when the group denominators are the same. The counts allow readers to understand the basis of the summaries and discourage treating the point estimate as more stable than the data support.

What is not documented?

The registry reports no analyses in its analysis listing. It does not report an analysis population, missing-data approach, covariate adjustment, prespecified testing hierarchy, or method for handling multiple outcomes. The calculations displayed for the primary outcome are unadjusted comparisons of the posted summaries; they do not substitute for a protocol-level account of the analysis. The record also does not describe whether outcome assessment was blinded or adjudicated, despite listing quadruple masking for the trial. Without those details, readers cannot verify the analysis decisions or determine whether the posted summaries follow a prespecified plan.

General explanation: randomization is intended to make treatment groups comparable on average, while masking can reduce some opportunities for expectations to influence care or assessment. Those design labels alone do not show how allocation was implemented or how masking was maintained. The registry gives the design descriptors but not those operational details. Accordingly, statistical interpretation should focus on the posted estimates, their uncertainty, and the limits of the available analysis record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.04, with a 95% confidence interval from -0.116 to 0.036. This interval is wide relative to the point estimate and includes zero. It therefore does not identify a single direction for the underlying group difference with much precision. The posted relative estimates also have broad intervals: the risk ratio is 0.333, with an interval from 0.036 to 3.097, and the odds ratio is 0.320, with an interval from 0.032 to 3.184. Each relative-effect interval includes the value associated with no difference.

General explanation: a confidence interval gives a range of effect estimates compatible with the observed data under the statistical method used. It reflects sampling uncertainty, not every possible source of uncertainty, such as missing outcome data, measurement problems, or bias. A confidence interval that includes the null value does not prove the absence of an effect; it indicates that the data are not precise enough to rule out that value under the method used. A wide interval signals that substantially different effect sizes remain compatible with the data.

The small number of observed primary events, alongside the posted group denominators, helps explain why the estimate is uncertain. The registry record does not provide a documented analysis method or missing-data account that would allow readers to assess other contributions to uncertainty. The point estimate should therefore not be read alone: the interval and raw event counts are essential context for judging how much the data resolve the comparison.

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 sample-size illustrations are planning calculations based on the observed effect, not the trial’s original design. The registry’s original sample-size assumptions and justification are not reported in the registry record. For the primary outcome, the illustrations report participants per arm. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect targeted is the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm in a hypothetical study designed to have an 80% chance of detecting the target effect under those assumptions, if that effect were the true effect and the model assumptions held. The 90% power column gives the corresponding planning figure for a higher chance of detecting that target effect. These are design illustrations, not observations from the trial. This is not observed power.

For example, the row for 100% of the observed effect lists 376 participants per arm for 80% power and 503 participants per arm for 90% power. The row for 75% of the observed effect lists 749 and 1,002 participants per arm, respectively. The row for 50% of the observed effect lists 1,863 and 2,494 participants per arm, respectively. The pattern reflects a general planning principle: smaller effects are harder to distinguish from random variation, so detecting them with the same planned power requires more participants.

These figures depend on using the observed effect as a planning reference. The primary estimate is imprecise, so the illustrations should not be treated as definitive requirements for a future study. They do not establish the design that would be appropriate for a different population, endpoint, or analysis plan. The registry’s sample-size assumptions identify the calculation approach, but the trial’s own design rationale is not reported in the registry record.

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 = 0.060; treatment proportion p₁ = 0.020; average p̄ = 0.040.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2771 = 0.5432.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2757 = 0.2320.
4. n = (0.5432 + 0.2320)² / (-0.0400)² = 375.6, rounded up to 376 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 <- 0.06                          # control proportion
p1 <- 0.02                          # 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(4400890)
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 = 376 (80% power), 503 (90% power)
 75% of observed effect: n per arm = 749 (80% power), 1,002 (90% power)
 50% of observed effect: n per arm = 1,863 (80% power), 2,494 (90% power)
power.prop.test: 375.6 
Simulated power at n = 376 per arm: 0.818 (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. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary hospitalization outcome and lists multiple secondary outcomes. It also reports seven outcome measures, but the record does not provide a complete statistical analysis plan or a testing hierarchy. The number of analyses reported is zero, and the detailed secondary results cover only some of the listed outcomes. Whether the analyses were prespecified, and how the investigators intended to handle multiple comparisons, is not reported in the registry record.

General explanation: when investigators examine multiple outcomes or conduct several analyses, the chance of at least one apparently unusual result can increase. A prespecified hierarchy, adjustment procedure, or other clear strategy can help readers understand how findings should be interpreted. Without such information, unadjusted p-values for secondary outcomes should not be read as if each were the sole confirmatory test. This concern does not change the values of the posted estimates; it affects the strength of claims readers can reasonably attach to them.

The record also does not report how missing data were handled, whether all randomized participants were included in the outcome analyses, or which analysis population was used. The enrollment figure is 105, whereas the posted primary and detailed secondary summaries show 50 participants in each group. The record does not explain the relationship between these figures. It does not report reasons for exclusion, loss to follow-up, or imputation procedures.

General explanation: the analysis population and missing-data approach can affect estimates if participants with unavailable outcomes differ from those with observed outcomes. Without the relevant details, readers cannot assess whether the posted denominators represent all randomized participants or a subset, or how missing outcomes may have influenced the comparison. These reporting gaps do not establish that bias occurred; they mean its possibility and extent cannot be evaluated from the registry record.

The status is terminated, but the reason for termination is not reported in the registry record. The record also does not report interim analyses, stopping rules, or whether early termination affected the planned analyses. No assumption should be made about those design or analysis decisions in the absence of documentation.

15. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (16.0%), pulmonary embolism (2.0%), pancreatitis (2.0%).

The registry reports serious adverse events affecting 4 participants in the resveratrol-with-Vitamin-D3 group and 8 participants in the placebo-with-Vitamin-D3 group; each group lists 50 participants at risk. Deaths are listed as 0 in both groups. Other adverse events are listed for 50 participants in each group. The record’s serious adverse event terms include pneumonia at 16.0%, pulmonary embolism at 2.0%, and pancreatitis at 2.0%. The registry does not provide a denominator for these term percentages or specify their group allocation in the listed summary.

These figures are safety summaries, not proof that an event was caused by a study regimen. The registry does not report the event-level details, timing, severity criteria, attribution assessments, or participant-level overlap among events. It also does not describe the procedures used to collect or classify adverse events. Consequently, the counts are useful as a record of reported events but do not by themselves establish comparative safety or explain the clinical context of each event.

General explanation: safety comparisons can be uncertain when event counts are limited, and interpretation depends on consistent definitions and complete follow-up. The posted figures should be read descriptively, alongside the limits of the available reporting, rather than as a definitive estimate of risk.

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

The posted primary data show 1 hospitalization among 50 participants assigned to resveratrol with Vitamin D3 and 3 among 50 assigned to placebo with Vitamin D3 within 21 days of randomization. The risk-difference estimate is -0.04, but its confidence interval extends from -0.116 to 0.036. The interval includes zero, and the relative-effect intervals are also broad. The most defensible statistical reading is that the posted comparison is uncertain and does not precisely establish the direction or size of a difference.

This result does not show that the regimens are equivalent. A non-significant or imprecise comparison cannot establish that any true difference is absent. It also does not show that resveratrol caused the numerical difference in the observed counts. The estimates are compatible with a range of possibilities, and the posted counts are limited. The trial was described as proof-of-concept and intended to explore effectiveness, but the registry record does not report an analysis plan or enough detail to assess all sources of uncertainty.

The result concerns resveratrol with Vitamin D3 compared with placebo with Vitamin D3. It does not isolate a resveratrol effect independent of the shared supplement, nor does it determine the effect of Vitamin D3. The record describes outpatient treatment of mild COVID-19, so the findings should not be generalized to populations or settings not described by that trial context. Detailed eligibility criteria and participant characteristics are not reported in the registry record.

The safety summaries likewise do not establish a causal safety profile. They provide reported counts and event terms, but the registry does not report event-level details, attribution, or the denominator for the listed serious-event term percentages. In addition, the reason for termination, missing-data handling, and the relationship between the registry enrollment figure and outcome denominators are not reported. These gaps restrict the conclusions that can be drawn from the posted results.

In short, the record documents a randomized comparison and an observed numerical difference in hospitalization counts, accompanied by substantial statistical uncertainty. It does not establish a definitive benefit, lack of benefit, equivalence, or causal explanation.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate should be interpreted together with its confidence interval and the underlying event counts. The primary comparison has a negative risk-difference point estimate, but the interval includes zero and spans values in both directions. Looking only at the point estimate would overstate what the data can establish; the interval makes the uncertainty visible.

The study also shows the value of distinguishing absolute and relative measures. The risk difference communicates the absolute contrast between group event proportions, while the risk ratio and odds ratio describe relative contrasts. In this record, all these estimates are imprecise. Considering them together helps readers avoid treating a single scale as a complete account of the evidence, especially when the outcome is uncommon and the event counts are limited.

There is also a design-interpretation lesson: the randomized comparison is resveratrol with Vitamin D3 versus placebo with Vitamin D3. Accurately naming the comparator is essential to avoid attributing the result to a contrast that the trial did not make. The record’s proof-of-concept framing is consistent with an exploratory question, but a complete account of the original design rationale and analysis plan is not reported.

Finally, the registry record demonstrates how missing reporting details affect statistical interpretation. The enrollment figure and outcome denominators are not reconciled, the termination reason is not given, and analysis populations, missing-data methods, and multiplicity handling are not reported. These omissions do not determine the direction of the results, but they limit reproducibility and the strength of conclusions. A careful reading keeps the observed summaries, their uncertainty, and the limits of the record in view at the same time.

18. 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.

Several limitations specific to this record constrain interpretation. The trial status is terminated, but the reason for termination is not reported in the registry record. The registry lists enrollment as 105, while the primary and detailed secondary summaries each report 50 participants per group; the relationship between these figures is not explained. The analysis population, reasons for any exclusions, and handling of missing outcomes are not reported.

The primary outcome has few observed events in the posted summaries, and its confidence interval is broad. This makes the effect estimate imprecise. The record does not report the original sample-size justification, the trial’s statistical analysis plan, the method used for the posted comparison, interim analyses, or stopping rules. It therefore is not possible to determine from the registry whether the analyses followed a prespecified plan or how the study’s termination related to its statistical objectives.

The registry lists several secondary outcomes, but detailed posted comparisons are available only for pneumonia and pulmonary embolism among those described in the record. Results for the other listed outcomes are not reported in the registry record. Multiplicity handling and a testing hierarchy are also not reported, reducing the confirmatory weight of unadjusted secondary findings.

Participant characteristics and detailed eligibility criteria are not reported, limiting assessment of generalizability. The record does not describe adherence, outcome adjudication, event attribution, or the operational procedures for masking. Serious adverse event terms are listed, but their denominator and group allocation are not specified in the summary. The available safety information is therefore descriptive rather than a complete comparative safety analysis.

These are limits of what the registry record documents. They do not establish that the trial was conducted improperly or that any particular bias occurred, but they prevent readers from resolving those possibilities from the posted information.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Randomized Proof-of-Concept Trial to Evaluate the Safety and Explore the Effectiveness of Resveratrol, a Plant Polyphenol, for COVID-19 — NCT04400890.
• Registry record last updated 2023-02-24; status last verified 2023-02.
• Results first posted 2023-02-24.
• 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.

22. Record Summary

NCT04400890 is a randomized, quadruple-masked, parallel-group, placebo-controlled phase 2 proof-of-concept trial of resveratrol for outpatient treatment of mild COVID-19. The resveratrol group received resveratrol 1000mg four times per day for 15 days and Vitamin D3 100,000 IU on day 1; the placebo group received placebo capsules 4 times per day for 15 days and the same Vitamin D3 regimen.

The primary outcome was hospitalization within 21 days of randomization. The posted counts were 1 of 50 in the resveratrol group and 3 of 50 in the placebo group. The risk difference was -0.04, with a 95% confidence interval from -0.116 to 0.036 and an unadjusted p-value of 0.307. These estimates are imprecise and do not establish a definitive difference.

The registry lists the study as terminated. The reason for termination, the analysis population, missing-data approach, and original sample-size justification are not reported in the registry record. The posted results are best interpreted as descriptive evidence with substantial uncertainty and reporting limitations.