A Study to Investigate the Pharmacokinetics, Efficacy and Safety of INM005 in Patients With COVID-19.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Investigate the Pharmacokinetics, Efficacy and Safety of INM005 in Patients With COVID-19. (NCT04494984), a randomized phase 2, phase 3 study. The primary outcome is Number of Participants With Improvement in at Least Two Categories in WHO 8-point Ordinal Clinical Scale at Day 28 or Discharge.

2. Clinical Question

3. Trial Design

This was a randomized, controlled Phase 2/3 trial of INM005 and placebo in patients with confirmed COVID-19. The registry record classifies the study as adaptive and sequential, and describes masking as quadruple. It lists enrollment of 243. The primary outcome analysis describes the population as modified intent-to-treat, with 118 participants in the active group and 123 in the placebo group.

The active regimen consisted of two intravenous doses of INM005, each 4 mg/kg, with 48 h (± 2 h) between doses. The placebo group received two intravenous placebo doses on the same stated interval. The study aim included efficacy and safety, as well as pharmacokinetics. Named pharmacokinetic outcomes included maximum concentration, clearance, area under the curve, elimination measures, and distribution volume. Numerical results for those pharmacokinetic outcomes are not reported in the registry record summarized by the posted outcome results.

The primary endpoint was assessed at discharge or up to Day 28. It counted participants who improved by at least two categories on the WHO ordinal clinical scale or were discharged. The scale runs from 0, no evidence of infection, to 8, death; higher scores represent worse status. This combines change in clinical status with discharge into a binary response measure.

The registry record gives a start date of 2020-07-27, a primary completion date of 2020-11-23, and completed status. Details of the adaptive or sequential conduct, including any interim analyses or adaptations, are not reported in the registry record. The original design’s sample-size assumptions and the rationale for the planned enrollment are also not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: These patients constituted the Modified intent-to-treat (mITT) population.

5. Baseline Characteristics

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

Population: Only patients included in the modified Intention-to-treat population are considered

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Improvement in at Least Two Categories in WHO 8-point Ordinal Clinical Scale at Day 28 or Discharge, measured over Discharge or up to Day 28.

The primary endpoint counts participants who met a response definition by discharge or up to Day 28. A response was either improvement by at least two categories on the WHO 8-point ordinal clinical scale or discharge. The scale describes clinical status from 0, no evidence of infection, through progressively greater illness severity to 8, death. Higher scores indicate worse status.

This endpoint converts a clinical course into a binary outcome: each participant either meets the response definition or does not. That makes the result interpretable as a comparison of the proportion of participants responding in each group. It also combines two routes to response—ordinal improvement and discharge—so the endpoint reflects either a specified change in scale categories or reaching discharge. The registry description says the endpoint concerns improvement 28 days after the first dose, while the stated timeframe is discharge or up to Day 28.

General: a binary endpoint can be straightforward to communicate, but it does not retain all the detail in an ordinal scale. Participants with different degrees of change may be grouped together if both satisfy the response rule; those who do not satisfy it are grouped together as nonresponders. The definition therefore determines what the count captures. The registry identifies the primary analysis population as modified intent-to-treat. Further details about how missing endpoint observations were handled are not reported in the registry record.

7. Results Posted in the Registry

• Active: 89.8% (106/118) versus 84.6% (104/123) on control; risk difference 5.3 percentage points (95% CI -3.1 to 13.7), risk ratio 1.06 (0.96–1.17); unadjusted two-proportion z-test p = 0.221.

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.

Patients Discharged at 28 Days

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active: 89.0% (105/118) versus 83.7% (103/123) on control; risk difference 5.2 percentage points (95% CI -3.4 to 13.9), risk ratio 1.06 (0.96–1.17); unadjusted two-proportion z-test p = 0.237.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active and the control. The interval gives the range of effects that remain compatible with the data.

Participants Who Require (ICU) Hospitalization

• 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:
  • Active: 12.7% (15/118) versus 18.7% (23/123) on control; risk difference -6.0 percentage points (95% CI -15.1 to 3.2), risk ratio 0.68 (0.37–1.24); unadjusted two-proportion z-test p = 0.202.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active and the control. The interval gives the range of effects that remain compatible with the data.

Participants Who Require Mechanical Ventilation Assistance (MVA)

• 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:
  • Active: 9.3% (11/118) versus 13.8% (17/123) on control; risk difference -4.5 percentage points (95% CI -12.5 to 3.5), risk ratio 0.67 (0.33–1.38); unadjusted two-proportion z-test p = 0.276.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover discharge by 28 days, ICU hospitalization, and mechanical ventilation assistance, with Cox regression results also reported for those outcomes. Their estimates do not form a uniformly precise pattern that resolves the uncertainty in the primary comparison. The confidence intervals for these time-to-event analyses include the no-relative-difference value. The endpoints are related to clinical course, but they are not identical to the primary responder definition, which combines ordinal improvement and discharge.

These secondary findings can provide context about outcomes beyond the primary measure, but they should be interpreted alongside the primary result rather than as independent confirmation. The primary endpoint was the designated central comparison in the registry outcome record. Secondary analyses ask additional questions, and each may use a different endpoint definition or statistical measure. For example, a hazard ratio from a time-to-event analysis is not directly interchangeable with a difference between response proportions.

Unadjusted secondary results carry less inferential weight when many outcomes are assessed, because examining multiple results increases the chance of finding an apparently notable result by chance. General: multiplicity procedures can control that risk, but the registry record does not report a strategy for adjusting or prioritizing the secondary analyses. The posted p-values should therefore not be treated as if they arose from a single isolated test with no other outcomes considered.

The registry lists 23 outcome measures and 28 analyses, and 15 secondary outcomes are posted. It names several pharmacokinetic measures, including concentration, clearance, area under the curve, elimination, and distribution-volume measures. Numerical results for those pharmacokinetic measures are not reported in the registry record. The available secondary results thus offer limited additional context and do not change the need to interpret the primary estimate with its confidence interval.

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

• Pharmacokinetics (PK) Evaluation of INM005 (Cmax)
• Pharmacokinetics (PK) Evaluation of INM005 (Clearance)
• Pharmacokinetics (PK) Evaluation of INM005 (Weight-adjusted Clearance)
• Pharmacokinetics (PK) Evaluation of INM005 (AUC0)
• Pharmacokinetics (PK) Evaluation of INM005 (Elimination Half-time)
• Pharmacokinetics (PK) Evaluation of INM005 (Elimination Rate)
• Pharmacokinetics (PK) Evaluation of INM005 (Distribution Volume)
• Pharmacokinetics (PK) Evaluation of INM005 (Weight-adjusted Distribution Volumen)

9. Statistical Interpretation

10. Statistical Methods Explained

How is the primary outcome compared?

The primary outcome is binary: participants either met the responder definition or did not. A risk, in this setting, is the proportion of participants in a group who experienced the event—in this case, meeting the endpoint definition. A risk difference compares those two proportions by subtracting the placebo-group risk from the active-group risk. A positive estimate indicates a greater response proportion in the active group; a negative estimate indicates a greater response proportion in the placebo group. The recalculated risk difference is 0.053.

General: a risk difference expresses an absolute contrast between groups. It keeps the comparison tied to the event proportions observed in the trial, rather than expressing the contrast as a relative multiple. Its interpretation depends on the event definition and the population being analyzed. Here, the event is the combined response criterion of improvement by at least two scale categories or discharge by the stated endpoint time.

What does the confidence interval add?

A confidence interval gives a range of estimates compatible with the observed data under the statistical method used. It communicates precision as well as direction: a narrower interval indicates greater precision, while a wider interval leaves more uncertainty about the size and direction of the difference. The recalculated 95% interval for the primary risk difference runs from -0.031 to 0.137. Since that range crosses zero, the data do not rule out no difference using this interval. The interval also contains values on either side of zero, so the estimate does not settle the direction of the underlying difference.

General: a confidence interval is not a guarantee that the true effect lies in the displayed range, nor does it assign a probability to each possible effect after observing the data. It is an interval generated by a method with a stated long-run coverage property when its assumptions hold. The registry’s reported interval and the simple recalculated interval differ because the registry reports a one-tailed Z test with continuity correction, while the recalculation is a simple unadjusted comparison from the posted summary counts. The registry’s reported analysis takes precedence as the sponsor’s own reported analysis; the recalculation is a supplementary description.

How should the p-values be read?

The recalculated unadjusted p-value for the primary comparison is 0.221. The sponsor-reported analysis gives a one-tailed p-value of 0.151. A p-value measures how unusual data at least as incompatible with a null hypothesis would be under that hypothesis and the chosen statistical model. It is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of a difference.

The one-tailed and unadjusted descriptions matter. A one-tailed test evaluates evidence in a specified direction, whereas a two-sided test considers deviations in either direction. The registry labels the reported test as one-tailed and specifies a continuity correction. The recalculation’s p-value is unadjusted, meaning it does not account for testing multiple outcomes. The registry record does not report a multiplicity adjustment for the primary or secondary results. A threshold for statistical significance or a complete prespecified statistical analysis plan is not reported in the registry record.

What do the secondary hazard ratios represent?

The posted secondary analyses for discharge, ICU hospitalization, and mechanical ventilation use Cox regression and report hazard ratios with 95% confidence intervals. General: a hazard ratio compares the instantaneous event rates between groups over time, among participants who have not yet experienced the event, under the model’s assumptions. It is not the same quantity as a risk difference or a ratio of the proportions with an event. Interpretation depends on how the event and time origin were defined and on modeling assumptions.

The registry gives the method as Cox regression but does not report the model details, covariate adjustments, or checks of assumptions in the record. The confidence intervals for these analyses include the value corresponding to no relative difference. Consequently, the estimates should be read with their uncertainty rather than as precise evidence of a group difference. The endpoint counts are also useful descriptive information, but the hazard ratios and the counts answer different statistical questions.

What is not established by the methods record?

The study is classified as adaptive and sequential, but the specific adaptations, interim looks, stopping criteria, and any adjustments related to sequential monitoring are not reported in the registry record. The original sample-size justification and planned detectable effect are not reported either. The methods information therefore does not support a reconstruction of the trial’s complete design rationale or a claim that a particular statistical adjustment was or was not applied beyond what is stated for each posted analysis.

General: with binary outcomes, the amount of information depends on the number of participants and the frequency of events, as well as the balance between groups. Estimates based on finite counts remain subject to sampling variability. For time-to-event outcomes, event timing and censoring contribute to the analysis, so counts alone do not reproduce a Cox model. These general principles explain why the posted estimates and their intervals are more informative than a point estimate or p-value viewed alone.

11. Confidence Intervals and Precision

The primary recalculation estimates a risk difference of 0.053, with a 95% confidence interval from -0.031 to 0.137. This interval is wide enough to include negative values, zero, and positive values. It therefore conveys substantial uncertainty about the direction and size of the group difference. The point estimate is only one possible value in a range that remains compatible with the data under the recalculation method.

The registry’s reported primary analysis gives an estimate of 5.28 and a 95% confidence interval from -3.95 to 14.5. It reports a one-tailed Z test with continuity correction. The simple recalculation uses the posted summary counts and reports the risk difference in a different numeric representation. Because the methods differ, the two intervals should not be treated as identical. The registry’s reported analysis is the sponsor’s analysis; the recalculation is an unadjusted check based on summary statistics.

General: precision concerns how narrowly an analysis estimates a quantity, not whether the result is important. A confidence interval crossing the no-difference value indicates that the data are compatible with no difference under the analysis, but it does not prove there is no effect. Conversely, a point estimate in one direction does not by itself establish that direction. The posted primary interval leaves room for both a response advantage in either group and for a range of effect sizes.

The secondary Cox results also have confidence intervals that include the no-relative-difference value. Their precision should be considered separately from the primary risk-difference interval because hazard ratios are different measures and arise from time-to-event analyses. The number of participants and event counts are finite, and the registry record does not provide additional precision measures or detailed model diagnostics. The results are therefore best read as estimates with material uncertainty, not as exact measurements of an underlying 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 figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For the posted binary-outcome planning rows, the figures are participants per arm. The general assumptions stated for the illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation indicates would be needed for an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one and the model assumptions held. The 90% power column gives the corresponding planning count for a 90% chance. These are conditional planning targets, not guarantees that a future study will reach a particular result. The sample-size illustrations do not show the probability that the completed study’s findings are true.

Rows that plan for 75% or 50% of the observed effect ask what would be needed to detect a smaller effect than the observed estimate. Smaller effects require more participants to distinguish them from random variation at the same significance and power settings. The stated fractions therefore let readers see how the planning requirement changes when the target effect is made more modest. They should not be interpreted as claims about what effect a future trial will observe.

General: a curve, when read alongside a planning table, usually illustrates how the required sample size varies as the target effect changes. The exact values to use are those stated for the relevant endpoint and planning assumptions. These figures are planning illustrations, not observed power. Observed power is not a useful substitute for interpreting the estimated effect and its confidence interval; the completed trial’s data are better understood through those estimates and their uncertainty.

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 = 0.846; treatment proportion p₁ = 0.898; average p̄ = 0.872.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4726 = 0.9263.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4711 = 0.3965.
4. n = (0.9263 + 0.3965)² / (0.0528)² = 628.2, rounded up to 629 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 <- 0.845528455284553                          # control proportion
p1 <- 0.898305084745763                          # 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(4494984)
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 = 629 (80% power), 841 (90% power)
 75% of observed effect: n per arm = 1,167 (80% power), 1,562 (90% power)
 50% of observed effect: n per arm = 2,734 (80% power), 3,660 (90% power)
power.prop.test: 628.2 
Simulated power at n = 629 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 reports the sponsor’s primary comparison as a one-tailed Z test with a continuity correction. Its risk-difference estimate is 5.28, with a 95% confidence interval from -3.95 to 14.5 and p = 0.151. This is the trial’s reported analysis and should be distinguished from a simple unadjusted recalculation from the posted response counts.

The unadjusted recalculation gives a risk difference of 0.053, a 95% confidence interval from -0.031 to 0.137, and p = 0.221. It uses the group counts and denominators and does not reproduce every feature of the sponsor’s stated method. The two results are not identical analyses: the sponsor describes a one-tailed test with continuity correction, while the recalculation is a simple unadjusted comparison. The numerical risk-difference presentations also use different scales.

The registry record does not include sufficient analysis detail to reconstruct the sponsor’s full procedure beyond the method description. The recalculation is therefore a supplementary check of the posted summary statistics, not a replacement for the sponsor’s reported result. Both presentations indicate uncertainty: the sponsor-reported confidence interval and the recalculated interval include the no-difference value. Neither the p-value nor the point estimate alone gives a complete account of precision or establishes a causal conclusion.

15. Multiplicity, Missing Data and Analysis Populations

The trial is described as adaptive and sequential, but the registry record does not report the details needed to assess how those design features were implemented statistically. Specific interim analyses, the timing or number of any looks at accumulating data, stopping rules, and any adjustment to account for sequential monitoring are not reported in the registry record. The classification alone does not establish that a particular interim procedure was used.

The record lists multiple outcome measures and analyses, while a multiplicity strategy for the primary and secondary comparisons is not reported in the registry record. General: when many hypotheses are tested, the chance of at least one result appearing unusual under its null hypothesis can increase. Prespecifying a hierarchy, adjusting testing thresholds, or treating secondary analyses as exploratory are possible approaches, but the record does not state which approach governed interpretation. The posted secondary p-values should be read with this limitation in mind.

The primary endpoint identifies the analyzed population as modified intent-to-treat. The registry does not report further detail in this record about the precise inclusion rules for that population, handling of missing primary outcomes, or sensitivity analyses for missing data. Missing-data procedures can affect an estimate when outcome availability differs between groups or is related to participants’ clinical status. Without those details, it is not possible to determine the impact of missing observations from the registry record alone.

The group denominators and event counts are posted for the outcomes discussed, but information about protocol deviations, exclusions after randomization, and analysis-population handling beyond the mITT designation is not reported in the registry record. The original sample-size rationale, anticipated effect, and any design-specific inflation for adaptive or sequential features are likewise not reported. These absences limit assessment of the complete prespecified analysis plan; they do not by themselves establish that a particular procedure was omitted.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: multiorganic failure (2.5%), septic shock (2.5%), ventilator-associated pneumonia (2.5%), hypoxemia (1.7%), pneumotorax (1.7%).

The posted safety counts list serious adverse events in 16 of 119 participants at risk in the active group and 25 of 124 at risk in the placebo group. Other adverse events are listed for 22 of 119 and 24 of 124, respectively. Deaths are reported as 11 in the active group and 16 in the placebo group. These are descriptive counts and denominators; they do not by themselves establish that an event was caused by the study intervention.

The registry also lists serious-event terms with percentages, including multiorganic failure, septic shock, ventilator-associated pneumonia, hypoxemia, pneumotorax, and cardiac arrest. The record’s listed terms should be read as a selection of serious events, not as a complete account of every safety outcome. The registry excerpt does not establish how the listed term percentages map to each randomized group, so they should not be assigned to a group without further reporting detail.

Safety counts can differ in their denominators from efficacy analyses, and the posted safety denominators are 119 and 124. Serious events and deaths may also overlap conceptually in a safety record; the registry summary does not provide participant-level overlap. These figures support descriptive comparison only and should be interpreted with the study’s population, event definitions, and reporting limitations in mind.

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

The posted primary outcome counts show that 106 participants in the active group and 104 in the placebo group met the defined response criterion. The simple unadjusted estimate favors a higher response proportion in the active group, but its 95% confidence interval crosses the no-difference value and extends in both directions. The sponsor’s reported result is also uncertain, with a confidence interval spanning values on either side of no difference.

This means the observed data do not provide a precise estimate of the direction or size of the underlying difference. They do not establish that INM005 caused better or worse outcomes, and they do not establish that the groups are equivalent. A conclusion of equivalence would require a prespecified margin and an analysis designed for that purpose; such information is not reported in the registry record. A non-significant p-value should not be read as proof of no effect.

The endpoint itself is specific: it combines improvement by at least two categories on the WHO ordinal scale with discharge by the stated time. It is not a measure of every aspect of illness, and a binary responder count does not preserve the full detail of each participant’s clinical course. The result applies to the analyzed population and outcome definition recorded for this trial.

The secondary outcomes and safety counts add descriptive context but do not remove uncertainty in the primary estimate. The secondary Cox intervals include the no-relative-difference value, and a multiplicity strategy is not reported. Safety counts are not causal estimates. The registry record also does not provide detailed information about missing-data handling, interim analyses, or the full analysis plan. These limitations argue for interpreting the posted results as estimates with uncertainty rather than as a definitive answer about treatment effect.

18. Why This Trial Matters Statistically

This trial is statistically informative because its primary result illustrates why a point estimate and a test result are not enough. The observed response counts are close in absolute terms, and the estimated risk difference is positive, but the confidence interval spans zero and includes values in either direction. The interval makes the uncertainty visible in a way that a single p-value cannot.

The endpoint also highlights how an analysis definition shapes its conclusion. Improvement by at least two categories on the WHO scale and discharge are combined into one binary response. That creates a clear event count for comparison, while compressing the differences among participants’ clinical courses. Readers need to understand the responder rule before interpreting the estimated contrast.

The record’s classification as adaptive and sequential raises an important design question, but the registry does not report the operational details needed to evaluate interim monitoring or adaptation. This is a useful reminder that a design label is not a substitute for a statistical analysis plan. The posted sponsor method is described, and a simple recalculation can be placed beside it, but the available registry entries do not reconstruct every design or analysis decision.

Finally, the secondary outcomes and safety counts demonstrate the importance of keeping different statistical measures distinct. A risk difference, a hazard ratio, and an adverse-event count answer different questions. Their uncertainty, outcome definitions, and multiplicity context matter. The trial is therefore a practical example of careful interpretation: report the estimate, inspect its interval, distinguish the primary question from secondary analyses, and identify what the registry record does not document.

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.

Several trial-specific details that would help interpret the results are not reported in the registry record. Although the study is classified as adaptive and sequential, the record does not describe the adaptations, interim analyses, stopping rules, or any sequential adjustment. The original sample-size justification and the effect size used in the trial’s own planning are also not reported. Planning illustrations based on the observed effect cannot fill that gap.

The primary analysis is identified as modified intent-to-treat, but the record does not explain the population’s exact inclusion rules or how missing primary outcomes were handled. It does not provide sensitivity analyses for missing data or additional details on exclusions and protocol deviations. Those omissions limit assessment of whether the posted analysis represents all randomized participants in the same way.

The endpoint combines ordinal improvement and discharge, so the resulting responder count does not show the full distribution of changes on the WHO scale. The record supplies the scale definition but not a complete participant-level trajectory. Numerical results for the named pharmacokinetic outcomes are not reported in the posted outcome results. The record also does not report a multiplicity plan for the multiple outcomes and analyses.

The safety summary provides counts and selected serious-event terms, but not participant-level overlap or enough information to assign the listed term percentages to treatment groups. These limitations affect the detail with which safety and clinical outcomes can be assessed. They do not imply a specific direction of bias, but they constrain what can be concluded from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Investigate the Pharmacokinetics, Efficacy and Safety of INM005 in Patients With COVID-19. — NCT04494984.
• Registry record last updated 2026-04-20; status last verified 2024-04.
• Results first posted 2026-04-20.
• 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

The registry record describes a completed, randomized, controlled Phase 2/3 study of INM005 versus placebo in adults with confirmed COVID-19. The study is classified as adaptive, sequential, and quadruple-masked. Total enrollment was 243. The primary endpoint was response by discharge or up to Day 28, defined as improvement by at least two categories on the WHO 8-point ordinal clinical scale or discharge.

The mITT primary outcome counts were 106 of 118 in the active group and 104 of 123 in the placebo group. The sponsor reported a one-tailed Z test with continuity correction; a simple unadjusted recalculation gives a risk difference of 0.053 with a 95% confidence interval from -0.031 to 0.137. The estimate is uncertain, and its interval includes no difference.

Secondary outcome and safety counts provide additional descriptive information, but do not resolve the primary uncertainty. Details of the adaptive and sequential procedures, the original sample-size rationale, multiplicity handling, and missing-data methods are not reported in the registry record.