PRE-VENT Study in Hospitalized Patients With Severe COVID-19 With or Without Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for PRE-VENT Study in Hospitalized Patients With Severe COVID-19 With or Without Cancer (NCT04404361), a randomized phase 2 study. The primary outcome is Percentage of Participants With Progression to IMV and/or ECMO or Death.

2. Clinical Question

The trial was randomized, double-blind, placebo-controlled, and multicenter. Those design features frame the comparison: the groups were assigned to different study treatments, and the masking and placebo were intended to support a controlled comparison. The posted primary results are event counts and a treatment-group comparison, not a direct demonstration that either regimen caused a particular outcome.

3. Trial Design

PRE-VENT was a Phase 2, randomized, double-blind, placebo-controlled, parallel-group, multicenter study of pacritinib plus standard of care versus placebo plus standard of care. The registry record lists enrollment as 200. It records a start date of 2020-05-22, a primary completion date of 2021-09-21, and a status of terminated. The reason for termination is not reported in the registry record.

The two study arms differed in the assigned study drug while both included standard of care. In the pacritinib arm, the listed regimen was 400 mg once daily on Day 1, followed by 200 mg twice daily from Day 2 to Day 14. In the placebo arm, the listed regimen was 4 capsules once daily on Day 1, followed by 2 capsules twice daily from Day 2 to Day 14. The registry record does not report further details about what standard of care comprised.

The primary endpoint covered baseline to Day 28 and was defined as the percentage of participants who progressed to invasive mechanical ventilation or extracorporeal membrane oxygenation, or died. The endpoint description specifies the intention-to-treat population as the denominator. The posted arm results list 99 participants and 26 events for pacritinib plus standard of care, and 101 participants and 25 events for placebo plus standard of care.

The registry record lists secondary outcomes that include ventilator-free days, mortality at Day 28 and Day 15, clinical-status measures, time to improvement on an ordinal scale, and use of immunomodulatory agents. The registry record does not report the original sample-size justification or the assumptions used to design the trial.

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

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.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Progression to IMV and/or ECMO or Death, measured over Baseline to Day 28.

The primary endpoint counts participants who experienced progression to invasive mechanical ventilation or extracorporeal membrane oxygenation, or death, from baseline to Day 28. Its stated measure is a percentage: the number of participants with one of these outcomes divided by the total number in the intention-to-treat population. The posted arm results also give the event counts and group sizes.

This is a composite endpoint. It treats the listed respiratory-support events and death as components of one outcome, allowing the analysis to compare the occurrence of any qualifying component rather than presenting only one component. The registry record does not report component-specific results for the primary endpoint, so the posted overall counts cannot show how many events were due to each component.

As a general statistical point, a binary endpoint reduces each participant’s follow-up to whether the defined event occurred within the specified period. This can make a between-group comparison straightforward to interpret, but the composite combines outcomes that may differ in clinical meaning. It also does not describe when an event occurred or the duration of respiratory support. Those questions require other outcome measures.

The primary outcome is a measure of clinical progression during a specified period, not a complete account of recovery or safety. Its interpretation depends on the endpoint definition, the analysis population, and how missing outcome information was handled. The registry record identifies the intention-to-treat population in the endpoint definition, but details of missing-data handling are not reported in the registry record.

7. Results Posted in the Registry

• Placebo and SOC: 24.8% (25/101) versus 26.3% (26/99) on control; risk difference -1.5 percentage points (95% CI -13.6 to 10.6), risk ratio 0.94 (0.59–1.51); unadjusted two-proportion z-test p = 0.806.

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.

The Number of Ventilator-Free Days

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Placebo and SOC: mean 22.60 versus 22.10 on control; difference 0.50 (95% CI -2.21 to 3.21), standardized effect d = 0.05; z-test p = 0.718.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo and SOC and the control. The interval gives the range of effects that remain compatible with the data.

The Time to Improvement by at Least 2 Points Relative to Baseline on the 7-point Ordinal Scale of Clinical Status

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Pacritinib and SOC vs Placebo and SOC: hazard ratio 1.09 (95% CI 0.79–1.53), reported p = 0.567 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Pacritinib and SOC vs Placebo and SOC and the control. The interval gives the range of effects that remain compatible with the data.

The Rate of Use of Immunomodulatory Agents as Treatment for COVID-19

• 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:
  • Placebo and SOC: 95.0% (96/101) versus 98.0% (97/99) on control; risk difference -2.9 percentage points (95% CI -8.0 to 2.1), risk ratio 0.97 (0.92–1.02); unadjusted two-proportion z-test p = 0.260.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo and SOC and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several aspects of clinical course: ventilator-free days, mortality at two follow-up points, clinical status on an ordinal scale, time to improvement, and use of immunomodulatory agents. The posted secondary results include a mean comparison, a time-to-event comparison, and a binary comparison. Taken together, the estimates and reported tests do not present a consistent, precise pattern of between-group separation across the outcomes with numerical results posted.

The reported tests for ventilator-free days, time to improvement, and immunomodulatory-agent use have p-values of 0.749, 0.567, and 0.272, respectively. Those p-values do not establish a difference. They also do not show that the groups are equivalent or that a difference is impossible. The registry record lists mortality and ordinal clinical status among the secondary outcomes, but numerical results for those endpoints are not included in the registry entries used for this interpretation. Their results are not reported in the registry record in the information summarized by these registry entries.

Secondary outcomes can add context to the primary result by examining different dimensions of illness and recovery. They do not independently confirm or overturn the primary finding. Each outcome has its own definition, measurement scale, follow-up, and uncertainty, so the results should be interpreted on their own terms rather than combined informally into a single conclusion.

Unadjusted secondary results carry less weight when many outcomes or comparisons are examined because the chance of finding at least one apparently unusual result can rise with repeated testing. A multiplicity adjustment, hierarchical testing plan, or other prespecified approach can address that issue, but such a plan is not reported in the registry record. This is a general statistical concern, not a claim that any particular secondary result is false. The secondary findings are best treated as supportive or exploratory unless the registry’s analysis plan establishes otherwise.

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

• The Number of Ventilator-Free Days
• The Mortality Rate at Day 28
• The Mortality Rate at Day 15
• The Time to Improvement by at Least 2 Points Relative to Baseline on the 7-point Ordinal Scale of Clinical Status
• The Clinical Status as Assessed by the 7-point Ordinal Scale of Clinical Status at Days 8, 15, 22, and 28
• The Rate of Use of Immunomodulatory Agents as Treatment for COVID-19

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the composite endpoint during baseline to Day 28 or did not. The posted event counts and group sizes form the basis for comparing the observed proportions. A risk difference expresses the difference between two event proportions. A value of zero corresponds to equal proportions under the chosen subtraction order; a negative or positive value indicates which group has the larger observed proportion under that convention.

For the unadjusted recalculation, the stated direction is placebo and standard of care minus pacritinib and standard of care. Its estimate is -0.015. The 95% confidence interval is -0.136 to 0.106. The calculation is unadjusted, meaning it is based on the posted summary counts rather than a model that controls for other factors. The registry-reported primary analysis instead used the Cochran-Mantel-Haenszel method. The registry record does not report enough detail in the registry entries to describe any stratification variables used in that analysis.

The Cochran-Mantel-Haenszel method is generally used to estimate a treatment comparison across strata, combining information while accounting for the stratification structure. That general description does not establish which strata, if any, were used in this trial. The registry lists a risk difference, confidence interval, and p-value for its reported analysis. The point estimate is 1.51, the 95% confidence interval is -10.55 to 13.53, and p = 0.852. The recalculation and the registry analysis do not use the same stated method or reporting convention, so the registry’s own analysis should be understood as the sponsor-reported result, while the recalculation is a separate unadjusted summary-statistic calculation.

A confidence interval describes a range of estimates compatible with the data under the method’s assumptions. It conveys uncertainty around the point estimate; it is not a range in which the true effect is guaranteed to lie. When an interval for a difference includes zero, the data do not rule out no difference at the confidence level used. This does not demonstrate equivalence. Establishing equivalence would require a defined equivalence margin and an analysis designed for that question, which are not reported in the registry record.

The primary endpoint description refers to the intention-to-treat population. In general, an intention-to-treat analysis aims to compare participants according to their assigned groups, whether or not they followed the assigned treatment exactly. The registry record does not report further details about the analysis population actually used for each result, deviations from assigned treatment, or missing-data handling. The definition should therefore not be taken as a complete description of all analysis procedures.

Several secondary outcomes use different statistical forms. Ventilator-free days are reported as means and standard deviations, with an unadjusted mean-difference recalculation. A mean difference compares the average outcome between groups; its interpretation depends on the outcome definition and distribution. As a general statistical point, unusually skewed data or influential observations can make a mean sensitive to a small part of the distribution. The registry’s listed analysis for this endpoint is Wilcoxon (Mann-Whitney), a rank-based method that compares the distributions of observations rather than directly testing a difference between means under a normal model. The posted p-value for that analysis is 0.749.

Time to improvement is reported using medians, a hazard ratio, and a log-rank analysis. A median time describes the midpoint of the observed time distribution under the endpoint’s definitions. A hazard ratio compares event rates over time under the assumptions of a time-to-event analysis; it is not the same quantity as a difference in median days. The registry reports a hazard ratio of 1.09, with a 95% confidence interval from 0.79 to 1.53, and p = 0.567. The registry record does not provide further detail about censoring or the handling of participants who did not improve during follow-up.

The immunomodulatory-agent outcome and the primary endpoint are binary. Their recalculated risk differences are unadjusted comparisons of observed proportions. The registry’s listed analysis for immunomodulatory-agent use is a chi-squared analysis reporting an odds ratio. An odds ratio compares odds rather than probabilities, so it should not be interpreted as a risk difference. The registry-reported odds ratio is 2.46, with a 95% confidence interval from 0.47 to 12.93 and p = 0.272.

As a general statistical point, over-dispersion occurs when the variability in data is greater than a model assumes. It can make standard errors too small and intervals too narrow if the model does not account for the extra variability. The registry entries do not identify a count model or an over-dispersion assessment for the primary endpoint, so over-dispersion should not be assumed to have affected this analysis.

Each method answers a particular statistical question and relies on assumptions. The posted summary does not report the full analysis plan, prespecified adjustment factors, diagnostics, or sensitivity analyses. Those details are not reported in the registry record and cannot be inferred from the method labels or the numerical results alone.

11. Confidence Intervals and Precision

The primary unadjusted risk-difference estimate is -0.015, with a 95% confidence interval from -0.136 to 0.106. The interval crosses zero and extends in both directions. Thus, the estimate does not precisely distinguish a lower event proportion in one group from a lower event proportion in the other. The registry-reported primary analysis also has an interval spanning zero: its risk difference is 1.51, with a 95% confidence interval from -10.55 to 13.53.

A confidence interval is an uncertainty summary under a particular statistical method. In repeated use of the same method under its assumptions, intervals at the stated confidence level would cover the underlying value at that rate. For an individual trial, the interval does not assign a probability to the true effect, and it does not mean every value in the interval is equally plausible. It indicates that the point estimate alone should not be treated as exact.

The primary confidence intervals are compatible with effects on either side of zero. That means the results do not rule out no difference, but neither do they exclude all potentially important differences. The registry record does not report a threshold for what would count as a clinically important difference, so statistical precision cannot by itself determine whether the range is clinically acceptable.

Other posted outcomes also have uncertainty. The ventilator-free-days mean-difference interval runs from -2.213 to 3.213. The time-to-improvement hazard-ratio interval runs from 0.79 to 1.53. The immunomodulatory-agent odds-ratio interval runs from 0.47 to 12.93. These intervals differ in the effect measure and scale they describe; they should not be compared as though they were the same quantity. Their breadth is a reminder that point estimates and p-values alone do not convey the full uncertainty in the posted results.

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 effects, not the original design assumptions for the trial. The assumptions listed for these calculations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect. The registry record does not report the trial’s original sample-size justification or design assumptions.

For binary and continuous outcomes, the planning figures are participants per arm. For time-to-event outcomes, the figures are total events, not participants per arm. This distinction matters: an event target is not interchangeable with a participant target, because not every participant necessarily experiences the event during follow-up.

The 80% power column describes the number of participants per arm, or total events for a time-to-event calculation, that the planning illustration estimates would be needed to detect the stated effect under its assumptions with 80% power. The 90% power column gives the corresponding target for 90% power. In general, power is the chance of detecting an effect of the specified size under the assumed model if that effect is present; it is not a measure of the probability that a finding is true.

Rows using a smaller fraction of the observed effect require more participants or events than rows using a larger fraction. Smaller effects are harder to distinguish from random variation, so detecting them generally calls for more information. These figures are not observed power. They are forward-looking planning illustrations, not a retrospective score for the trial or an explanation of why it was stopped.

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 = 0.263; treatment proportion p₁ = 0.248; average p̄ = 0.255.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6165 = 1.2082.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6164 = 0.5187.
4. n = (1.2082 + 0.5187)² / (-0.0151)² = 13,077.9, rounded up to 13,078 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 <- 0.262626262626263                          # control proportion
p1 <- 0.247524752475248                          # 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(4404361)
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 = 13,078 (80% power), 17,508 (90% power)
 75% of observed effect: n per arm = 23,364 (80% power), 31,277 (90% power)
 50% of observed effect: n per arm = 52,821 (80% power), 70,712 (90% power)
power.prop.test: 13077.9 
Simulated power at n = 13,078 per arm: 0.805 (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-reported primary analysis used the Cochran-Mantel-Haenszel method. It reports a risk difference of 1.51, with a 95% confidence interval from -10.55 to 13.53 and p = 0.852. The recalculated comparison uses an unadjusted approach based on the posted summary counts and expresses the difference as placebo and standard of care minus pacritinib and standard of care. Its estimate is -0.015, with a 95% confidence interval from -0.136 to 0.106 and an unadjusted p-value of 0.806.

These are not identical presentations: the registry analysis has a named stratified method, while the recalculation is unadjusted, and the displayed effect estimates use different numerical scales and subtraction directions. The registry record does not give further detail in the registry entries that would allow the reported calculation to be reconstructed fully. The registry-reported result is therefore the appropriate description of the sponsor’s own analysis; the recalculation is a separate summary-statistic check, not a replacement for that analysis.

Both reported confidence intervals include zero, and both p-values are large. Neither analysis establishes a clear difference on the primary endpoint. Because the discrepancy flag is false, no discrepancy requiring precedence is identified in the posted results. The distinct methods and conventions should still be kept visible when interpreting or quoting the estimates.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple secondary outcomes and reports several kinds of comparisons. When many hypotheses are tested, the overall chance of at least one false-positive result can increase if each test is judged separately at the same threshold. This is the general multiplicity problem. It matters especially when results are selected for emphasis after looking at the data, or when outcomes are not arranged in a prespecified testing sequence.

The registry record does not report a multiplicity adjustment, a hierarchy for testing outcomes, or another procedure controlling the family-wise error rate. It also does not report whether secondary analyses were designated confirmatory or exploratory. Without those details, individual secondary p-values should not be read as if they were protected from the consequences of multiple testing. This does not mean the results are invalid; it limits the strength of conclusions drawn from them.

The primary endpoint description names the intention-to-treat population, but the registry entries do not describe the full analysis-population definitions for all endpoints. Details about exclusions, protocol deviations, missing outcome data, or the analysis population actually used are not reported in the registry record. Missing-data handling can matter if outcome availability differs between groups or is related to clinical status. The registry record’s lack of detail does not establish that data were missing or that the groups differed in missingness.

The record also does not report sensitivity analyses testing alternative assumptions about missing outcomes, nor does it provide enough information to assess the robustness of the results to such assumptions. The endpoint’s follow-up window is specified, but the registry entries do not explain how incomplete follow-up or outcome status at the end of the period was handled.

These reporting gaps constrain interpretation rather than demonstrate a flaw. A complete statistical assessment would use the prespecified analysis plan and detail about analysis populations, multiplicity, and missing-data procedures. Those details are not reported in the registry record.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: respiratory failure (14.9%), acute respiratory failure (7.9%), hypoxia (5.9%), septic shock (5.9%), acute kidney injury (3.1%).

The posted safety figures list serious adverse events in the groups with 96 participants at risk in the pacritinib and standard-of-care group and 101 at risk in the placebo and standard-of-care group. The serious-event counts are 20 and 33, respectively. The listed counts for other adverse events are 74 and 79, and the death counts are 12 in each group. These are descriptive counts; they do not by themselves establish that a treatment caused or prevented an event.

The registry also lists serious adverse-event terms with percentages: respiratory failure, 14.9%; acute respiratory failure, 7.9%; hypoxia, 5.9%; septic shock, 5.9%; acute kidney injury, 3.1%; and acute respiratory distress syndrome, 3.1%. The registry entries do not specify the denominator or group attribution for each of these term percentages. They should therefore be read as listed terms and percentages, not as a basis for making unreported between-group comparisons.

Safety interpretation also depends on how events were defined, collected, and attributed. Those details are not reported in the registry record. Counts may not capture severity, duration, timing, or clinical context, and a comparison of observed counts is not proof of causation.

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

The primary results describe a randomized comparison of pacritinib plus standard of care with placebo plus standard of care for a composite outcome through Day 28. The observed event counts were 26 among 99 participants in the pacritinib group and 25 among 101 participants in the placebo group. The unadjusted risk-difference interval crosses zero, as does the interval from the registry-reported primary analysis. The posted results therefore do not establish a clear between-group difference in this endpoint.

That conclusion is narrower than saying the treatments are the same. A non-significant comparison does not prove equivalence, rule out a meaningful difference, or show that an effect is absent. The confidence intervals remain compatible with differences in either direction. The registry record does not report a clinically important-difference threshold or an equivalence design, so those questions cannot be resolved from these results.

The primary outcome combines progression to invasive mechanical ventilation or extracorporeal membrane oxygenation with death. The posted overall count does not show the contribution of each component. The result also does not describe all aspects of clinical recovery, the timing of events, or treatment safety. Those topics require separate outcomes and fuller reporting.

The secondary outcomes provide additional measures, but the numerical results available in the registry entries do not establish a consistent, precise treatment-group difference. Multiple secondary comparisons and the absence of reported multiplicity procedures make isolated secondary findings less conclusive. Safety counts are descriptive and should not be interpreted as proof of treatment-related harm or protection.

The trial is listed as terminated, but the reason is not reported in the registry record. That fact does not, by itself, explain the results or indicate whether termination was related to efficacy, safety, recruitment, or another issue. The registry record also does not report the original design assumptions, detailed missing-data procedures, or a full analysis plan. Interpretation should remain limited to the outcomes, methods, and uncertainty that are reported.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate and a p-value are not enough to characterize a clinical comparison. The primary endpoint counts were close, but the main statistical question is not whether the observed counts look similar. It is how much uncertainty surrounds the estimated difference and which range of effects remains compatible with the data. Both the recalculated and registry-reported confidence intervals cross zero, and each extends in both directions.

It also illustrates why analysis conventions matter. A risk difference depends on which group is subtracted from which, and the registry-reported method differs from the unadjusted recalculation. Naming the analysis and preserving its scale and direction are necessary for accurate interpretation. The sponsor’s reported result and a recalculation from summary counts can both be described without treating them as interchangeable.

The composite endpoint raises a further interpretive issue. Combining respiratory-support escalation and death can give a broad measure of clinical progression, while obscuring whether one component accounts for the observed pattern. Without component-specific results, the overall endpoint cannot answer that question.

Finally, the registry lists a range of secondary outcomes, but multiplicity and incomplete reporting affect how much weight those results can carry. This is a practical lesson in distinguishing the primary result from secondary evidence, statistical uncertainty from proof of no effect, and descriptive safety counts from causal conclusions. The posted record supports a cautious account of what was measured, what was estimated, and what remains uncertain.

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 primary outcome is composite, and the posted primary results do not separate progression to invasive mechanical ventilation, extracorporeal membrane oxygenation, and death. That limits understanding of which component contributed to the group counts. The record also does not report additional detail about endpoint adjudication or the handling of events occurring close to the end of the follow-up window.

The trial status is terminated, but the reason for termination is not reported in the registry record. Enrollment is listed as 200; the registry record does not report the original sample-size justification or design assumptions. As a result, the record does not explain whether the planned information target was reached or whether termination altered the intended analysis.

The primary analysis is described as Cochran-Mantel-Haenszel, but the registry entries do not give the strata or other implementation details. The full statistical analysis plan, prespecified covariates, multiplicity procedure, analysis populations for every endpoint, and missing-data methods are not reported in the registry record. These omissions limit independent reconstruction of the reported analyses and assessment of their assumptions.

Numerical results for all the listed secondary outcomes are not included in the registry entries. The available secondary comparisons also span different effect measures, which should not be combined as though they represented a single quantity. In addition, the posted serious-adverse-event term percentages lack group attribution and denominator detail in the registry record. The safety summaries therefore support descriptive reading but not a complete comparative safety assessment.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: PRE-VENT Study in Hospitalized Patients With Severe COVID-19 With or Without Cancer — NCT04404361.
• Registry record last updated 2024-06-05; status last verified 2024-05.
• Results first posted 2024-06-05.
• 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

PRE-VENT was a Phase 2 randomized, double-blind, placebo-controlled, multicenter study of pacritinib plus standard of care versus placebo plus standard of care in hospitalized patients with severe COVID-19, with or without cancer. The registry lists enrollment as 200 and the study status as terminated.

The primary endpoint was the percentage of participants with progression to invasive mechanical ventilation or extracorporeal membrane oxygenation, or death, from baseline to Day 28. Posted counts were 26 among 99 participants in the pacritinib group and 25 among 101 in the placebo group. The registry-reported primary analysis and the unadjusted recalculation both have confidence intervals that include zero; neither establishes a clear difference.

The record lists secondary efficacy outcomes and descriptive safety results. The reason for termination, original sample-size justification, multiplicity procedure, and detailed missing-data handling are not reported in the registry record.