Trial of Imatinib for Hospitalized Adults With COVID-19: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trial of Imatinib for Hospitalized Adults With COVID-19 (NCT04394416), a randomized phase 3 study. The primary outcome is To Evaluate the Efficacy and Safety of Oral Administration of Imatinib Combined With BCC vs. Placebo Plus BCC in Hospitalized Patients With COVID-19.

2. Clinical Question

The question is framed around a count of participants who died by the specified follow-up point. It is therefore a binary endpoint for each participant: a participant either had the event during the defined period or did not. The posted arm counts are 2 deaths among 10 participants assigned to imatinib and 1 among 11 assigned to placebo. These observed counts describe this enrolled group; they do not by themselves establish a reliable estimate of what would occur in a larger population.

The registry describes a randomized, double-blind, placebo-controlled, parallel-group trial. Random allocation is intended to make treatment groups comparable on average, while masking is intended to limit the influence of treatment knowledge on care or outcome assessment. Neither design feature removes the uncertainty created by the small number of participants and events. The registry record does not report the eligibility criteria in detail, the rationale for the enrollment target, or the original statistical assumptions used to plan the trial.

The primary question should be kept distinct from the trial's other measures, which include later mortality, hospitalization, ICU stay, respiratory support, swab results, and serious adverse events. These outcomes provide additional descriptions but do not replace the specified Day 28 mortality endpoint.

3. Trial Design

The registry identifies this study as a Phase 3 randomized, double-blind, placebo-controlled trial with a parallel design. Participants were assigned to imatinib or an oral placebo. The registered imatinib regimen was 400 mg orally each day for 14 days; placebo was also described as oral and given for 14 days. The primary objective refers to treatment combined with BCC, but the expansion of that abbreviation and further details about background care are not reported in the registry record.

The trial enrolled 21 participants. The posted outcome groups include 10 participants in the imatinib arm and 11 in the placebo arm. The study status is terminated. Its recorded start date is 2020-06-02, and the primary completion date is 2024-06-30. The reason for termination, the date of termination, and whether the recorded primary completion date represents the completion of planned follow-up are not reported in the registry record. No conclusions about why enrollment ended should be drawn from the status alone.

Double masking means the registry identifies the study as masked to two parties, but it does not specify in the posted record exactly who was masked or how masking was maintained. The record also does not report detailed allocation procedures, concealment methods, eligibility criteria, site information, or the intended recruitment target. These omissions limit how fully readers can assess implementation from the registry information alone.

The registered primary endpoint is all-cause mortality at Day 28 after starting imatinib or placebo. The secondary outcome list includes mortality during a later period, hospitalization, time to clinical change on an ordinal scale, duration of ECMO or invasive mechanical ventilation, ICU stay, negative respiratory swab results, and serious adverse events. Although the registry lists these measures, the posted numeric secondary results cover only a subset. Results for the other named outcomes are not reported in the registry record.

The record reports no analyses. It does not describe an analysis population, missing-data approach, covariate adjustment, interim monitoring, or a prespecified strategy for handling multiple outcomes. Those design and analysis details should not be inferred from the randomized and masked labels.

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 To Evaluate the Efficacy and Safety of Oral Administration of Imatinib Combined With BCC vs. Placebo Plus BCC in Hospitalized Patients With COVID-19, measured over Day 28 after the start of imatinib/placebo..

The primary endpoint counts participants who died from any cause by Day 28 after the start of imatinib or placebo. The registry describes the endpoint as all-cause mortality at Day 28. “All-cause” means the endpoint is not limited to deaths attributed to COVID-19 or to a particular mechanism; the record does not provide a cause-specific breakdown.

Mortality is a clinically important outcome because it records whether a participant experienced death during the defined follow-up period, rather than relying on a symptom score or a laboratory measure alone. A binary endpoint makes each participant's outcome an event or a non-event for the specified time window. That definition is useful for comparing the proportions of participants with an event in each randomized group, provided the timing and ascertainment are applied consistently.

The posted primary counts are 2 participants with the event in the imatinib arm and 1 in the placebo arm. The denominators are 10 and 11, respectively. These counts are the observed endpoint data, not a precise estimate of a general treatment effect. With so few participants and events, the comparison is uncertain, as reflected in the reported p value and the broad interval around the risk-ratio estimate.

The endpoint's timeframe matters: it concerns mortality through Day 28 after treatment begins. It does not describe mortality at all later times. The registry separately lists all-cause mortality from Day 29 to Day 60 as a secondary outcome. That later period is distinct from the primary endpoint, and its results should not be combined with the Day 28 counts unless a prespecified analysis says to do so. Such a combined analysis is not reported in the registry record.

7. Results Posted in the Registry

• Imatinib: 20.0% (2/10) versus 9.1% (1/11) on control; risk difference 10.9 percentage points (95% CI -19.1 to 41.0), risk ratio 2.20 (0.23–20.72); unadjusted two-proportion z-test p = 0.476.

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.

All-Cause Mortality

• 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:
  • Imatinib: 0.0% (0/10) versus 9.1% (1/11) on control; risk difference -9.1 percentage points (95% CI -26.1 to 7.9); unadjusted two-proportion z-test p = 0.329.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Imatinib and the control. The interval gives the range of effects that remain compatible with the data.

Hospitalization

• 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:
  • Imatinib: mean 19.30 versus 17.30 on control; difference 2.00 (95% CI -7.51 to 11.51), standardized effect d = 0.18; z-test p = 0.680.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Imatinib and the control. The interval gives the range of effects that remain compatible with the data.

Duration of ICU Stay

• 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:
  • Imatinib: mean 14.00 versus 9.26 on control; difference 4.74 (95% CI 0.64 to 8.84), standardized effect d = 1.00; z-test p = 0.023.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Imatinib than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the description beyond mortality at Day 28. They cover later all-cause mortality, duration of hospitalization and ICU stay, clinical change on an ordinal scale, respiratory support, respiratory swab results, and serious adverse events. The posted numerical secondary results include only a subset of these listed outcomes. Results for the other named measures are not reported in the registry record, so their direction or magnitude cannot be assessed.

Across the reported secondary outcomes, estimates do not form a consistent pattern that independently resolves the primary uncertainty. Later mortality is based on very few events. Hospitalization is reported as a mean duration, while ICU stay is another continuous measure; these outcomes have different definitions and should not be treated as substitutes for mortality. The registry also lists measures such as clinical change and respiratory support, but listing an outcome does not provide evidence about its result when numeric results are absent.

Secondary outcomes are useful for describing possible effects across different aspects of the course of illness, but they are usually less decisive than a prespecified primary endpoint. If many outcomes are examined, some may appear unusual by chance even when there is no consistent underlying effect. The registry record does not report a multiplicity adjustment, an outcome hierarchy, or a confirmatory analysis plan. Accordingly, the unadjusted secondary results warrant cautious interpretation and should not be used alone to settle the primary question.

The primary result remains the registered Day 28 mortality comparison. Secondary results may add context, but they cannot compensate for the very small number of primary events or establish a treatment effect without a suitable analysis plan. The absence of posted results for several named secondary outcomes further limits any overall synthesis. No combined or composite analysis of these outcomes is reported in the registry record.

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

• All-Cause Mortality
• Time to a 2-point Clinical Change Using the 8-category Ordinal Scale.
• Hospitalization
• Duration of ECMO or Invasive Mechanical Ventilation
• Duration of ICU Stay
• Negative Oropharyngeal or Nasopharyngeal Swab
• Negative Oropharyngeal or Nasopharyngeal Swab
• Serious Adverse Events (SAEs)

9. Statistical Interpretation

10. Statistical Methods Explained

The main comparison concerns a binary outcome: whether each participant died by Day 28. For a binary endpoint, the arm-level event count is interpreted alongside the number of participants in that arm. The posted data give the counts and denominators, and the comparison includes a risk difference, a risk ratio, an odds ratio, and an unadjusted p value. These summaries answer related but different questions. A risk difference expresses the difference in event probabilities, a risk ratio compares those probabilities as a ratio, and an odds ratio compares the odds. Each can be difficult to estimate precisely when there are very few events.

What does a confidence interval add?

A confidence interval describes the range of values reasonably compatible with the observed data under the method used to calculate it. It is not a list of outcomes that will occur, and it does not give the probability that the true effect lies inside the particular interval. For a difference, an interval that includes zero is compatible with no difference as well as with effects in either direction. For a ratio, the corresponding no-effect value is one. The primary risk-ratio interval is broad and includes values below and above one, so it does not pin down the direction or size of the underlying relative effect.

How should the p value be read?

A p value measures how incompatible the observed data are with a specified null model, assuming that model and the calculation's conditions hold. It is not a measure of effect size, a probability that the null hypothesis is true, or a direct measure of clinical importance. The primary p value is 0.476. This value does not show that the groups are equivalent; the small event count means that meaningful differences in either direction remain compatible with the data. The secondary p value for ICU stay is 0.023, but it is unadjusted and belongs to a group of multiple outcomes.

Why does the endpoint type matter?

Binary outcomes and continuous outcomes are summarized differently. The mortality endpoint is a count of participants with an event. Hospitalization and ICU stay are reported as means with standard deviations, in days. A mean describes the center of the observed values, while a standard deviation describes their spread around that mean. A mean difference compares the group averages, but it may not convey the full distribution, especially in a small sample where a few long stays can influence the mean. The registry record does not report a distributional analysis or an adjusted model for these outcomes.

Confidence intervals for mean differences show the range of values compatible with the observed difference under the calculation used. The hospitalization interval runs from -7.506 to 11.51 days, crossing zero. The posted means are 19.3 days for imatinib and 17.3 days for placebo. The ICU means are 14.0 and 9.26 days, respectively. The registry reports an ICU mean difference of 4.74 days and an interval above zero. These are unadjusted comparisons, and the record does not report the analysis details needed to evaluate whether assumptions such as the suitability of a mean-based comparison were assessed.

What does over-dispersion mean in general?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors and confidence intervals too optimistic if the model assumes less variability than the data contain. This is a general statistical concern, not a finding reported for this trial. The registry record does not describe an over-dispersion assessment, a model for count outcomes beyond the posted endpoint summaries, or a variance adjustment. Readers should not infer that such checks were carried out.

What does “unadjusted” mean?

In general, an unadjusted comparison is calculated without accounting for other variables or for the number of hypotheses examined. It can be a useful descriptive comparison, but it does not control for baseline characteristics or multiplicity. The registry labels the posted p values as unadjusted and reports zero analyses. The exact test or model used for each p value, any covariate adjustment plan, and the method for confidence-interval construction are not reported in the registry record. The estimates should therefore be read as posted summary comparisons rather than as a fully described inferential analysis.

The registry's planning illustrations use the observed effect as a starting point and show hypothetical sample sizes under stated assumptions. They are not estimates of what the trial actually enrolled or of the probability that the trial detected an effect. The planning assumptions are described separately with those illustrations. The original trial design's sample-size assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

Precision is limited by the small number of participants and primary events. The primary endpoint includes 2 deaths in the imatinib group and 1 in the placebo group. The posted risk-ratio interval extends from 0.234 to 20.72, spanning a very wide range and including the no-effect value of one. The risk-difference interval also crosses zero. This means the data are compatible with effects in different directions, as well as with little or no difference; the point estimate alone should not be treated as a stable measure of the underlying effect.

The unadjusted primary p value is 0.476. It does not quantify the probability that the treatments are the same, and it does not establish equivalence. The interval is more informative about the range of effects compatible with the data, but its breadth shows that the trial gives little precision for the primary comparison. No adjusted or sponsor-reported analysis is available in the registry record to add a different estimate or account for additional variables.

Precision also varies by outcome and measure. The hospitalization mean difference is 2.0 days, with a confidence interval from -7.506 to 11.51 days. Since this interval crosses zero, it is compatible with shorter or longer mean stays in the imatinib group. The ICU estimate has an interval on the positive side of zero, but it is a secondary unadjusted comparison in a very small cohort. Its apparent separation from zero does not remove the uncertainty arising from the small sample or the number of outcomes considered.

Confidence intervals are not guarantees about the range of individual participant outcomes. They describe uncertainty in an estimated group contrast under the method used. The registry record does not report the detailed interval methods, missing-data handling, or analysis populations. Those omissions limit further assessment of precision. The posted intervals should be read as estimates with substantial uncertainty, not as proof for or against a particular effect.

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 examples based on fractions of the observed effect, rather than the trial's original design calculations. For the displayed binary and continuous comparisons, the entries are participants per arm. The registry's general assumption note says that time-to-event planning rows, when present, are total numbers of events; the displayed planning rows concern non-time-to-event outcomes and are stated per arm.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect. The rows planning for 100% of the observed effect use the full observed estimate; rows planning for 75% or 50% use smaller effects. Smaller effects require more participants to distinguish them from random variation under the same assumptions, which is why the illustrative participant counts rise as the target effect becomes smaller.

The 80% power column represents a planning target under which a study with the stated sample size would have an 80% chance of detecting the specified effect at the stated significance level, if the assumptions hold. The 90% power column uses a higher detection-probability target and therefore generally requires more participants. These are prospective planning concepts, not a statement about what happened in this trial. The sample-size figures are not observed power.

The calculations use effects estimated from this small trial, so those inputs are themselves uncertain. The figures should not be read as a recommendation or as evidence that the original study was designed to enroll those numbers. The original sample-size justification and its assumptions are not reported in the registry record. No conclusion about the trial's planned enrollment or stopping decisions can be drawn from these illustrations.

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 = 0.091; treatment proportion p₁ = 0.200; average p̄ = 0.145.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4986 = 0.9772.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4926 = 0.4146.
4. n = (0.9772 + 0.4146)² / (0.1091)² = 162.8, rounded up to 163 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 <- 0.0909090909090909                          # control proportion
p1 <- 0.2                          # 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(4394416)
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 = 163 (80% power), 218 (90% power)
 75% of observed effect: n per arm = 268 (80% power), 358 (90% power)
 50% of observed effect: n per arm = 549 (80% power), 735 (90% power)
power.prop.test: 162.8 
Simulated power at n = 163 per arm: 0.811 (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 lists a primary endpoint and multiple secondary outcomes. When investigators examine several endpoints, the chance of seeing at least one apparently notable result by chance can increase. Statistical methods can address this issue through a prespecified hierarchy, adjustment, or other strategy. The registry record does not report a multiplicity plan, an adjustment for multiple comparisons, or a hierarchy defining which secondary outcomes were confirmatory. The posted secondary p values are unadjusted.

This matters when interpreting an isolated secondary result. The ICU-stay comparison has an unadjusted p value of 0.023, but it is one of several listed outcomes. Without a reported plan for multiplicity, that value should be viewed as exploratory rather than as an independent confirmation of the primary endpoint. The registry does not report whether a different analysis plan existed outside the record.

Missing-data procedures are also not reported in the registry record. The posted arm denominators are 10 and 11 for the primary endpoint, but the record does not describe whether every randomized participant had complete endpoint ascertainment, how any missing measurements were handled, or whether follow-up differed between groups. No assumptions about missing outcomes should be made from the posted counts alone.

The analysis population is not specified. The record does not say whether the primary analysis was intended to include all randomized participants, only participants who received treatment, or another defined group. It also does not report an intention-to-treat analysis, a per-protocol analysis, or a safety-population definition. The arm-level results can be described as posted, but their relationship to an intended analysis population is unclear.

No interim analyses, stopping boundaries, or interim monitoring procedures are reported. The study status is terminated, but the reason and decision process are not reported in the registry record. Termination alone does not establish that an interim analysis occurred or that the trial stopped for benefit, harm, futility, or any other particular reason. These omissions limit assessment of how the reported comparisons relate to the full planned analysis.

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: intracranial hemorrhage (10.0%), organ failure (10.0%), splenomegaly (9.1%), atrial fibrillation (9.1%).

The adverse-event summary reports serious events in 2 of 10 participants in the imatinib group and 2 of 11 in the placebo group. The other reported adverse-event category affected 8 of 10 participants assigned to imatinib and 6 of 11 assigned to placebo. The record lists 2 deaths in each group in the adverse-event summary. These counts describe the registry's safety reporting; they should not be assumed to have the same definition or timeframe as the primary Day 28 mortality endpoint.

The listed serious-event terms include intracranial hemorrhage and organ failure, each reported as 10.0%, and splenomegaly and atrial fibrillation, each reported as 9.1%. The registry does not provide enough detail in the posted summary to determine whether participants could contribute more than one event term, how events were attributed, or the timing and duration of each event. The percentages should therefore be read as registry-reported descriptions, not as proof that an event was caused by a treatment.

With 21 participants, these safety counts are highly limited for comparing uncommon events. Similar counts in the two groups do not establish equivalent safety, and differences in other-event counts do not establish a causal relationship. The registry record does not report detailed event narratives, exposure-adjusted rates, or a formal comparative safety analysis.

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

The posted results establish what was recorded for this small cohort: the primary Day 28 mortality counts were 2 in the imatinib group and 1 in the placebo group, and the corresponding unadjusted comparison is imprecise. The broad confidence interval and small number of events leave substantial uncertainty about the size and direction of any underlying difference. The result should not be described as proof that the groups are equivalent, nor as proof of a difference.

The trial's randomized, double-blind, placebo-controlled design is relevant because these methods are intended to reduce systematic differences in treatment assignment and outcome assessment. However, the design labels do not remove random variation, guarantee complete follow-up, or address missing details in the registry record. The study enrolled 21 participants and is listed as terminated. Its reason for termination and original sample-size assumptions are not reported.

Secondary outcomes provide additional descriptions, but they have limitations of their own. Some outcomes listed in the registry do not have posted numeric results. The posted comparisons are unadjusted, and the record does not report a strategy for multiple testing or a hierarchy of outcomes. An isolated secondary result should not be treated as a substitute for the primary endpoint or as a definitive finding.

The safety summary records serious and other adverse-event counts, but the small cohort is not sufficient to characterize uncommon harms precisely. The registry's adverse-event counts also should not be conflated with the primary mortality count, because their definitions and timeframes may differ and are not fully detailed in the summary.

Overall, the data support a cautious statistical description, not medical advice or a general conclusion about treatment. They do not establish that imatinib does or does not change mortality, length of stay, or safety in a broader population. The posted estimates are specific to the enrolled participants and are accompanied by substantial uncertainty. Further conclusions would require information and analyses not reported in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically informative as an example of the difference between a carefully described design and a precise estimate. Randomization, double masking, a placebo comparator, and a defined primary endpoint are important features. Yet only 21 participants were enrolled, and the primary endpoint includes only three recorded events. Those details sharply limit how precisely a between-group contrast can be estimated.

The record also illustrates why confidence intervals matter alongside point estimates and p values. The primary risk-ratio estimate is 2.2, but its interval is broad and includes values on either side of no effect. A single estimate can appear definitive if read without its uncertainty; the interval makes clear that multiple underlying effects remain compatible with the observed data. The unadjusted p value likewise does not establish equivalence or settle the clinical question.

Another statistical lesson concerns secondary outcomes. A trial can report several outcomes that measure different parts of a disease course, but multiple unadjusted comparisons increase the risk of chance findings. The registry record does not describe a multiplicity strategy, while some named secondary outcomes lack posted numeric results. This makes it important to distinguish the primary endpoint from exploratory context.

Finally, planning illustrations based on an observed effect should not be confused with the trial's original sample-size justification or with observed power. They demonstrate how target effect size and power targets affect hypothetical sample requirements under stated assumptions. The original design assumptions are not reported. Separating those planning examples from the enrolled trial helps prevent an illustrative calculation from being mistaken for a description of what the study was designed to achieve.

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.

The cohort is small: the posted primary groups contain 10 and 11 participants. This limits precision, particularly for mortality and safety events that occur infrequently. The trial is marked terminated, but the reason, timing, and decision process are not reported in the registry record. It is therefore not possible to determine from the record whether the enrolled group reflects the planned study population or why recruitment ended.

Important design and analysis details are absent. The original sample-size rationale, eligibility criteria in detail, allocation procedure, identities of masked parties, analysis population, missing-data methods, and any covariate-adjustment plan are not reported. Interim analyses and stopping rules are also not reported. These details would help assess how the posted estimates were produced and whether they reflect the intended analysis.

The registry lists multiple secondary outcomes, but numeric results are posted for only a subset. The record does not report a strategy for multiplicity or a hierarchy among secondary endpoints. Consequently, an isolated unadjusted secondary comparison has limited confirmatory value, and the unreported outcomes cannot be evaluated. The registry also does not report detailed event-level information for the adverse-event summary or a formal comparative safety analysis.

The meaning of BCC in the primary objective is not explained in the record. Further details about background care and treatment adherence are not reported. These limitations do not invalidate the descriptive counts, but they restrict interpretation and generalization. The findings should be treated as observations from this enrolled cohort rather than as a precise estimate applicable to a broader population.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Trial of Imatinib for Hospitalized Adults With COVID-19 — NCT04394416.
• Registry record last updated 2026-03-25; status last verified 2026-03.
• Results first posted 2026-03-25.
• 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

The registry describes a Phase 3 randomized, double-blind, placebo-controlled parallel trial of oral imatinib versus oral placebo in hospitalized adults with COVID-19. Imatinib was listed at 400 mg daily for 14 days, and placebo was listed for 14 days. The primary endpoint was all-cause mortality at Day 28 after treatment began.

The record reports 21 participants: 10 assigned to imatinib and 11 to placebo. Primary deaths were 2 and 1, respectively, with an unadjusted p value of 0.476 and a broad interval around the relative estimate. The trial status is terminated. Secondary results and safety counts are available for selected measures, while some listed outcomes have no numeric results reported in the registry record.

The record reports no analyses and does not describe the original sample-size justification, missing-data procedures, analysis populations, interim monitoring, or multiplicity strategy. The posted findings are therefore best read as descriptive results from a small trial with substantial uncertainty, rather than as a definitive estimate of treatment effects.