Convalescent Plasma as Treatment for Subjects With Early COVID-19 Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Convalescent Plasma as Treatment for Subjects With Early COVID-19 Infection (NCT04456413), a randomized phase 2 study. The primary outcome is Hospitalization Rate.

2. Clinical Question

The study asked whether hospitalization within 10 days differed between non-immune people with early COVID-19 infection at high risk of complications who were assigned to convalescent plasma and those assigned to best supportive care. The primary endpoint was the number of participants hospitalized during that timeframe. The registry describes a phase II randomized study and says the hospitalization frequency was to be compared between the treatment and control arms.

3. Trial Design

The registry describes a phase II randomized study sponsored by Hackensack Meridian Health. The study started on 2020-11-06, and its primary completion date is recorded as 2021-04-29. Its current registry status is terminated; the reason for termination is not reported in the registry record. The recorded enrollment is 21.

Participants were assigned to convalescent plasma or best supportive care. The plasma arm received a one-time infusion of fresh or frozen plasma. The control arm received best supportive care, with the option to receive plasma if hospitalization was required for progression of COVID-19 disease. This allowed a change in treatment exposure for at least some participants assigned to supportive care, which matters when interpreting the contrast between assigned groups.

The registry lists the allocation as randomized, masking as none, and the model as crossover. These are registry classifications; the record does not explain how the crossover model classification relates to the specific treatment sequence or to the allowance for plasma after hospitalization. The posted arm results include 10 participants in the convalescent-plasma arm and 11 in the best-supportive-care arm.

The brief summary describes follow-up through a 2-month visit, with completion after 2 months (+/- 5) days unless consent withdrawal or death occurred first. It says final analysis would occur after the last participant completed that visit or withdrew. The registry record does not report the trial’s original sample-size justification, detailed protocol procedures, or the reason the study was terminated.

Eight secondary outcomes are listed, including symptom resolution, overall survival, virologic clearance, donor measures, and antibody titers. Their presence indicates that the study addressed questions beyond the primary hospitalization endpoint, but the registry record does not report results for every listed outcome in the registry record for this 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 Hospitalization Rate, measured over 10 Days.

The primary endpoint is hospitalization rate over 10 days, described as a count of participants. It asks whether participants assigned to convalescent plasma or best supportive care were hospitalized during the specified follow-up period. This is a binary outcome at the participant level: each participant either experienced hospitalization in that period or did not. The posted arm counts are 1 of 10 for convalescent plasma and 3 of 11 for best supportive care.

Hospitalization is used as a clinically important measure of disease progression in a study enrolling people described as being at high risk of complications. An endpoint with a defined timeframe makes the comparison specific: the result concerns hospitalization within 10 days, not hospitalization at any later point or a broader measure of health. The registry’s endpoint description says the frequencies would be compared using a Mantel-Haenszel test.

The endpoint should be read alongside the assigned-treatment rules. Participants in the supportive-care arm could receive plasma if hospitalization was required because of disease progression. That allowance is part of the treatment strategy recorded for the comparator arm and can affect how an assigned-group comparison represents treatment exposure. The record does not describe additional endpoint adjudication details or how hospitalizations were classified.

7. Results Posted in the Registry

• Convalescent Plasma: 10.0% (1/10) versus 27.3% (3/11) on control; risk difference -17.3 percentage points (95% CI -49.5 to 15.0), risk ratio 0.37 (0.05–2.98); unadjusted two-proportion z-test p = 0.314.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: hospitalization within the stated 10-day period is counted as an event. A frequency comparison summarizes how often that event occurred in each assigned arm. The posted counts are 1 of 10 in the convalescent-plasma arm and 3 of 11 in the best-supportive-care arm. The registry describes the planned comparison as a Mantel-Haenszel test. In general, the Mantel-Haenszel approach can combine information across strata when stratification is part of the analysis. The registry record does not report the strata, if any, used for this endpoint, so the precise implementation cannot be described.

The risk difference is an absolute contrast. It subtracts the comparator-arm risk from the intervention-arm risk, with negative values indicating a lower observed risk in the intervention arm under that direction of comparison. The posted estimate is -0.173. The corresponding confidence interval is -0.495 to 0.149. In general, an absolute measure is often easier to relate to the observed event frequencies than a relative measure, but its value depends on the underlying risks in the groups being compared.

The risk ratio compares the event risk in one arm with the event risk in the other. The posted risk ratio is 0.367, with a confidence interval from 0.045 to 2.979. A ratio of 1 represents equal risks. The odds ratio compares event odds rather than risks; the posted odds ratio is 0.296, with a confidence interval from 0.025 to 3.452. An odds ratio of 1 represents equal odds. In general, odds and risks are different quantities, even when both describe a binary outcome. The wide intervals for both relative measures indicate that the observed event counts provide limited precision for estimating a relative contrast.

The registry reports an unadjusted p-value of 0.314. In general, a p-value measures how unusual data at least as incompatible with a null hypothesis would be under that hypothesis and the analysis assumptions. It does not measure the size or importance of an effect, and it does not indicate the probability that the null is correct. The record does not report a separate adjusted p-value or a detailed account of covariate adjustment. The comparison is therefore best described using the posted estimate, its interval, and the reported unadjusted p-value, rather than relying on a threshold interpretation alone.

Random assignment aims to make treatment groups comparable on average with respect to factors that could influence outcomes. In a small trial, however, chance imbalances can remain, and the posted information does not permit an assessment of baseline comparability. Masking is listed as none. In general, lack of masking can affect behavior, care decisions, or outcome assessment, depending on the endpoint and study procedures. The hospitalization endpoint is a concrete event, but the registry record does not describe how hospitalization decisions were made or verified.

The model is listed as crossover, while the arm descriptions state that people assigned to best supportive care may receive plasma if they require hospitalization for progression. These details make it important to distinguish the assigned-arm comparison from a comparison based on treatment actually received. The posted arm counts are presented by assigned intervention; the record does not report the extent of crossover, a treatment-received analysis, or procedures for handling treatment changes. No conclusion about those details should be inferred from the model label alone.

In general, over-dispersion concerns variation greater than a model expects and is relevant to some count-data analyses. This endpoint is recorded as participants with an event, rather than as a repeated count of events per participant, and the registry lists no dispersion parameter. The record does not report an over-dispersion assessment or a model requiring such a parameter. Statistical methods should therefore be described from the endpoint and analysis information that is actually recorded, without attributing unreported modeling choices to the investigators.

The registry lists eight secondary outcomes, including time to symptom resolution, overall survival, virologic clearance at stated follow-up points, donor measures, and antibody titers. Considering several outcomes can raise a multiplicity question: when many hypotheses are tested, the chance of at least one apparently notable result may increase if each is assessed separately. In general, prespecified outcome hierarchies or multiplicity adjustments can address that issue. The registry record does not report an adjustment strategy, a hierarchy among outcomes, or analyses for the secondary outcomes in the information used.

10. Confidence Intervals and Precision

The confidence interval for the risk difference ranges from -0.495 to 0.149 around the estimate of -0.173. In general, a confidence interval describes a range of values reasonably compatible with the observed data under the method’s assumptions. It is not a guarantee that the true value lies within the particular interval, and it is not a direct measure of the probability that any one value is correct.

For this comparison, the interval includes zero, the value corresponding to no absolute difference. It also extends to negative and positive values, so the data are compatible with the direction of the observed estimate as well as with a contrast in the other direction. The interval is broad relative to the estimate, indicating low precision. The posted risk-ratio interval, 0.045 to 2.979, and odds-ratio interval, 0.025 to 3.452, likewise include the no-difference value for those measures.

The small number of participants and the few observed hospitalization events are important context for this imprecision. Binary outcomes with few events often yield substantial uncertainty because each event has considerable influence on the observed frequency. This is a general statistical point, not a claim about any unreported analysis choice in this study.

The interval quantifies sampling uncertainty under its calculation method; it does not account automatically for every possible limitation, such as unreported missing outcomes, changes in treatment exposure, or selection into the study. The registry record does not report the confidence-interval method, details of missing-data handling, or a sensitivity analysis. The interval should therefore be read as a measure of statistical precision for the posted comparison, not as a complete summary of all uncertainty about the trial.

11. 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 participants per arm, not total participants and not total events. They illustrate sample sizes under the stated planning assumptions using the observed effect as a reference. For 100% of the observed effect, the figures are 79 participants per arm for 80% power and 105 participants per arm for 90% power. For 75% of the observed effect, they are 153 participants per arm for 80% power and 205 participants per arm for 90% power. For 50% of the observed effect, they are 372 participants per arm for 80% power and 497 participants per arm for 90% power.

In general, power is the probability that a study will detect an effect of a specified size under the assumed model and analysis, if that effect is truly present. The 80% power column means the planning calculation targets an 80% chance of detecting the stated effect under those assumptions; the 90% column targets a higher chance. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

Smaller effects require more participants to detect with the same target power, which is why the planning figures rise as the assumed fraction of the observed effect decreases. These are planning illustrations, not observed power for the completed study. They do not show that the trial had a particular probability of success, and they should not be read as a retrospective measure of the evidence.

12. 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 = 0.273; treatment proportion p₁ = 0.100; average p̄ = 0.186.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5507 = 1.0793.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5370 = 0.4519.
4. n = (1.0793 + 0.4519)² / (-0.1727)² = 78.6, rounded up to 79 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 <- 0.272727272727273                          # control proportion
p1 <- 0.1                          # 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(4456413)
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 = 79 (80% power), 105 (90% power)
 75% of observed effect: n per arm = 153 (80% power), 205 (90% power)
 50% of observed effect: n per arm = 372 (80% power), 497 (90% power)
power.prop.test: 78.6 
Simulated power at n = 79 per arm: 0.821 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary hospitalization endpoint and eight secondary outcomes. The secondary questions span symptom resolution, overall survival, virologic clearance, donor swab positivity and titer levels, the relationship between donor titers and efficacy, and participants’ antibody titer assessments. Each outcome can address a different aspect of the study, but testing multiple outcomes raises the general issue of multiplicity: the more separate comparisons are made, the greater the possibility of finding a nominally notable result by chance.

The registry record does not report a multiplicity adjustment, a prespecified testing hierarchy, or a statistical plan describing how primary and secondary tests were to be interpreted together. It also does not report a protocol-level account of interim analyses. These matters are therefore unknown; they should not be inferred from the presence of posted primary endpoint results or from the list of secondary outcomes.

Missing-data methods and analysis populations are also not reported in the registry record. The brief summary says participants were considered to have completed the study after the 2-month visit, with consent withdrawal or death as exceptions, and that final analysis would occur after the last participant completed the visit or withdrew. It does not state how missing outcome measurements, withdrawals, or deaths were handled in the hospitalization analysis. The posted arm denominators are 10 and 11, but the record does not explain whether these represent all randomized participants, all participants with endpoint data, or another analysis population.

In general, intention-to-treat analysis compares participants according to randomized assignment, while per-protocol or treatment-received analyses use different inclusion or exposure rules. The registry record does not identify the analysis population used for the posted comparison, so it should not be labeled as one of these approaches. The allowance for plasma after hospitalization makes this distinction especially relevant, but the record does not report a separate analysis accounting for crossover or treatment changes.

14. 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

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: worsening covid symptoms (27.3%).

The serious adverse event figures record 1 participant affected in the convalescent-plasma arm, among 10 at risk, and 3 participants affected in the best-supportive-care arm, among 11 at risk. No deaths are recorded in either arm. The leading serious event term listed is “Worsening Covid Symptoms,” with 27.3%. These figures describe the registry’s posted safety record; they do not establish that an event was caused by an assigned intervention.

The other adverse event figures record 1 participant affected among 10 at risk in the convalescent-plasma arm and 0 among 11 at risk in the best-supportive-care arm. The registry record does not provide further detail about event severity for these other events, timing, duration, attribution, or how event collection was conducted. Small arm counts also mean that the observed numbers provide limited precision for comparing safety outcomes.

Adverse event counts should be interpreted separately from the hospitalization endpoint. A serious adverse event is a safety classification, while hospitalization is the primary efficacy endpoint in this study; the record does not state that all hospitalizations were counted as serious adverse events or that the categories are interchangeable. The available figures support a description of events recorded, not a causal safety conclusion.

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

The posted results show fewer recorded hospitalizations in the convalescent-plasma arm than in the best-supportive-care arm over the 10-day endpoint period: 1 of 10 compared with 3 of 11. The estimated risk difference is -0.173, with a confidence interval from -0.495 to 0.149 and an unadjusted p-value of 0.314. The estimate favors a lower observed frequency in the plasma arm, but the interval includes no difference and extends in both directions. The comparison is therefore uncertain rather than conclusive.

That uncertainty is important. A result that does not clearly separate the arms is not evidence that the treatments are equivalent, and the point estimate alone is not enough to establish a dependable effect. The small participant counts and few observed events leave substantial room for sampling variation. The confidence interval communicates that uncertainty more directly than a single p-value.

The result applies to the recorded comparison, endpoint, and timeframe in this trial. It concerns participants with early COVID-19 infection described as non-immune and at high risk of complications; it does not automatically apply to populations with different characteristics, settings, or care practices. The registry record also does not provide enough detail to assess all eligibility criteria or the degree to which participants assigned to supportive care later received plasma.

The trial considered additional outcomes, including symptoms, survival, viral clearance, and donor-related measures, but the primary result should not be treated as a result for those other questions. The record’s status is terminated, and the reason is not reported in the registry record. Neither the status nor the posted hospitalization comparison alone explains why the study ended. Overall, the available statistics describe an imprecise comparison from a small randomized study; they do not provide a definitive answer about broader outcomes or treatment effects.

16. Why This Trial Matters Statistically

This study illustrates why an effect estimate, its confidence interval, and the observed event counts should be read together. The raw hospitalization counts are small, the estimated risk difference is -0.173, and its interval extends from -0.495 to 0.149. The direction of the point estimate is not enough to convey the uncertainty: the interval includes no difference and values on either side. The reported p-value, 0.314, cannot replace that interpretation.

It also highlights the distinction between randomized assignment and actual treatment exposure. Participants were randomized to plasma or best supportive care, but the latter group could receive plasma after hospitalization for disease progression. That crossover allowance is relevant both to what contrast the trial represents and to how analyses might be interpreted. The registry record does not quantify how often treatment changed, so the potential effect on the comparison cannot be measured from the registry entries.

Multiplicity is another statistical consideration because the registry lists eight secondary outcomes in addition to the primary endpoint. Without a reported adjustment or hierarchy, readers cannot tell how the investigators planned to manage the chance of findings arising across multiple outcome tests. The record also does not report missing-data methods or analysis-population definitions, further limiting assessment of how the posted estimates were produced.

Finally, the sample-size illustrations show how much planning requirements can depend on the effect size targeted. They are based on the observed effect and stated planning assumptions, not on the trial’s own design rationale. Together, these features make the study useful for understanding the interpretation challenges of a small randomized trial with a binary endpoint, multiple outcomes, and permitted treatment crossover—without turning a statistically uncertain result into a claim of benefit, no effect, or equivalence.

17. 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 participant counts are small, and the primary endpoint has few observed hospitalization events. This limits precision, as reflected by the broad confidence interval for the risk difference. The registry also records the study as terminated but does not report why it ended. It is not possible from the registry record to determine whether termination affected recruitment, follow-up, or the availability of outcomes.

The masking field is recorded as none. The registry record does not explain whether outcome assessment was independently verified or how hospitalization decisions were made. Since participants and care teams were not masked according to the record, the possibility of differences in care or assessment cannot be evaluated from the posted details. This is a general concern, not evidence that such differences occurred.

The comparator arm could receive plasma if hospitalization was required for progression of COVID-19 disease, and the model is listed as crossover. The record does not describe how many participants received plasma after assignment, when treatment changes occurred, or how they were handled in analysis. Consequently, the assigned-arm comparison cannot be translated into a precise contrast of actual plasma exposure from the information recorded.

Other important details are not reported in the registry record, including baseline characteristics, the exact analysis population, missing-data handling, confidence-interval method, a multiplicity plan, the original sample-size justification, and results for all listed secondary outcomes. The endpoint information also does not detail outcome adjudication. These omissions constrain reproducibility and make it difficult to assess whether other analyses would change interpretation. They do not invalidate the posted figures, but they limit how much can be concluded from them.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Convalescent Plasma as Treatment for Subjects With Early COVID-19 Infection — NCT04456413.
• Registry record last updated 2023-10-10; status last verified 2023-09.
• Results first posted 2023-02-10.
• 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.

21. Record Summary

The registry record describes a phase II randomized study of convalescent plasma for people with early COVID-19 infection who were considered non-immune and at high risk of complications. The study compared a one-time plasma infusion with best supportive care; participants assigned to supportive care could receive plasma if hospitalized for disease progression. Masking is listed as none, and the model is listed as crossover.

The primary endpoint was hospitalization within 10 days. The posted counts were 1 of 10 in the convalescent-plasma arm and 3 of 11 in the best-supportive-care arm. The risk difference was -0.173, with a confidence interval from -0.495 to 0.149; the unadjusted p-value was 0.314. These results are imprecise and do not establish a clear difference between assigned arms.

Enrollment is recorded as 21, and the registry status is terminated. The reason for termination and several analysis details are not reported in the registry record.