Cx611-0204 SEPCELL Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cx611-0204 SEPCELL Study (NCT03158727), a randomized phase 1, phase 2 study. The primary outcome is Number of Participants Reporting One or More Treatment-emergent Adverse Events (TEAEs).

2. Clinical Question

This is principally a safety question, although the study also explored efficacy-related outcomes. Treatment-emergent adverse events describe events arising during the specified follow-up period; the endpoint does not, by itself, establish that an event was caused by the assigned infusion. The comparison is between groups receiving standard care plus their assigned infusion, rather than between Cx611 and no care.

The registry record describes the study as phase Ib/IIa, randomized, double blind, parallel group, placebo controlled, and multicentre. Its stated aim was to assess safety, tolerability, and efficacy of Cx611 for severe community-acquired bacterial pneumonia. The posted primary measure is a participant count, not an event count: a participant reporting one or more events contributes to the count, without conveying how many events that participant experienced or their severity.

3. Trial Design

SEPCELL (NCT03158727) is recorded as a completed phase Ib/IIa randomized, double-blind, placebo-controlled, parallel-group, multicentre study sponsored by Tigenix S.A.U. The registry record lists an enrollment of 84 and identifies bacterial pneumonia as the condition. The recorded study start is 2017-01-30, and primary completion is listed as 2020-07-07.

Both groups received standard-of-care therapy according to local guidelines. The experimental group received Cx611 in two intravenous central-line infusions; the arm description specifies a fixed dose of 160 million expanded allogeneic adipose-derived stem cells. The placebo group received two intravenous central-line infusions of Ringer Lactate. The comparison therefore concerns the addition of the assigned infusion to standard care.

The registry identifies quadruple masking. The record does not explain which roles were masked or describe how masking was maintained. It also does not report the randomization sequence method, allocation concealment procedure, treatment-adherence measures, or site count. These details should not be inferred from the labels for allocation, masking, and study model.

For the primary endpoint, the stated timeframe is baseline up to Day 90. Its population is the safety population: randomized participants who received at least one dose of study treatment. The posted group sizes for this endpoint are 41.0 for placebo and 42.0 for Cx611. These are endpoint-specific safety-population counts; they should not be confused with the registry enrollment entry.

The registry lists mechanical ventilation and vasopressor outcomes among its secondary measures, including treatment-free days and status at Day 29. It records 34 outcome measures and 27 posted secondary outcomes. The registry record does not report the original protocol’s sample-size justification or the trial’s original statistical analysis plan.

4. Participant Flow and Accounting

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

Before assignment: Adult participants with severe community-acquired bacterial pneumonia (sCABP) and admitted to the intensive care unit (ICU) were enrolled in 1 of the 2 treatment groups to receive Cx611 or placebo on Days 1 and 3.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The safety population included all randomized participants who received at least one dose of the study treatment.

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: The safety population included all randomized participants who received at least one dose of the study treatment.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Reporting One or More Treatment-emergent Adverse Events (TEAEs), measured over Baseline up to Day 90.

The primary endpoint is the number of participants reporting one or more treatment-emergent adverse events (TEAEs) from baseline up to Day 90. Its stated population includes randomized participants who received at least one dose of study treatment. The measure counts people with at least one event, rather than counting every event. A participant with several events still contributes to the participant count as someone reporting one or more TEAEs.

This kind of endpoint is used to describe the frequency of participants experiencing events during follow-up and to compare that frequency between assigned groups. The count alone does not describe the types, duration, severity, or recurrence of all events. Nor does the term treatment-emergent establish that study treatment caused an event: events occurring during follow-up can have multiple possible causes, particularly in a seriously ill population receiving standard care.

The posted results report 37.0 of 41.0 participants with at least one TEAE in the placebo group and 40.0 of 42.0 in the Cx611 group. The unadjusted risk-difference estimate is 0.050, with a confidence interval from -0.061 to 0.161 and an unadjusted p-value of 0.38. The interval crosses zero, so the posted summary does not precisely distinguish a group difference from no difference. The endpoint is a safety summary, not a stand-alone test of efficacy or a complete accounting of clinical benefit and harm.

7. Results Posted in the Registry

• Cx611 160 mL: 95.2% (40/42) versus 90.2% (37/41) on control; risk difference 5.0 percentage points (95% CI -6.1 to 16.1), risk ratio 1.06 (0.93–1.19); unadjusted two-proportion z-test p = 0.380.

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.

Percentage of Participants Alive and Free of Both Mechanical Ventilation and Vasopressors at Day 29

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cx611 160 mL: 64.3% (27/42) versus 78.0% (32/41) on control; risk difference -13.8 percentage points (95% CI -33.0 to 5.5), risk ratio 0.82 (0.62–1.09); unadjusted two-proportion z-test p = 0.167.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cx611 160 mL and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Alive and Free of Mechanical Ventilation at Day 29

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cx611 160 mL: 66.7% (28/42) versus 78.0% (32/41) on control; risk difference -11.4 percentage points (95% CI -30.5 to 7.7), risk ratio 0.85 (0.65–1.12); unadjusted two-proportion z-test p = 0.247.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cx611 160 mL and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Alive and Free of Vasopressors at Day 29

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cx611 160 mL: 76.2% (32/42) versus 85.4% (35/41) on control; risk difference -9.2 percentage points (95% CI -26.0 to 7.6), risk ratio 0.89 (0.72–1.10); unadjusted two-proportion z-test p = 0.289.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cx611 160 mL and the control. The interval gives the range of effects that remain compatible with the data.

The three detailed Day 29 secondary comparisons concern whether participants were alive and free of both mechanical ventilation and vasopressors, free of mechanical ventilation, or free of vasopressors. Across these posted outcomes, the unadjusted estimates are below zero for Cx611 relative to placebo, and every confidence interval crosses zero. This describes the direction of the estimates, but the uncertainty prevents a firm conclusion about the direction or size of a group difference.

These secondary measures complement rather than replace the primary safety endpoint. They address short-term status at Day 29, whereas the primary endpoint counts participants reporting one or more TEAEs from baseline up to Day 90. An adverse-event count and a survival or treatment-support status measure capture different aspects of the trial. A pattern in one domain does not resolve uncertainty in the other.

The registry lists additional secondary outcomes, including treatment-free days and times to the end of forms of mechanical ventilation. The three detailed comparisons should not be taken as a complete account of the listed secondary outcome family. The record reports no sponsor analyses for these detailed outcomes, and the original statistical analysis plan is not reported. It is therefore unclear whether the reported comparisons correspond to a prespecified testing hierarchy or which outcomes, if any, were intended to be confirmatory.

Unadjusted secondary results carry less weight because assessing many endpoints can produce apparently notable results by chance, even when no clear underlying difference exists. Without a reported multiplicity plan, these comparisons are best viewed as exploratory descriptions. Their non-significant p-values do not prove the groups are identical, and their point estimates should not be treated as precise estimates of treatment effect. The overall pattern is a set of uncertain secondary estimates, not a definitive efficacy conclusion.

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

• Mechanical Ventilation and Vasopressors Treatment-free Days
• Percentage of Participants Alive and Free of Both Mechanical Ventilation and Vasopressors at Day 29
• Percentage of Participants Alive and Free of Mechanical Ventilation at Day 29
• Number of Ventilator Free Days (VeFD)
• Percentage of Participants Alive and Free of Vasopressors at Day 29
• Number of Vasopressor Treatment-free Days (VaFD)
• Time to End of Invasive Mechanical Ventilation
• Time to End of Invasive and/or Non-invasive Mechanical Ventilation

9. Statistical Interpretation

10. Statistical Methods Explained

Randomized parallel-group trials assign participants to one of the study groups and compare outcomes between those groups. Random assignment is intended to make groups comparable on average, including with respect to factors that are measured and factors that are not measured. It does not guarantee balance in every characteristic, particularly in a study with relatively limited group sizes. The registry calls SEPCELL randomized and parallel group but does not report the randomization procedure or allocation concealment details.

What does a risk difference express?

A risk difference subtracts the event proportion in one group from the event proportion in the other, using the direction defined for the comparison. It expresses an absolute difference in the probability of an outcome, rather than a relative comparison. A value of zero represents no difference in the two proportions. For the primary endpoint, the posted risk-difference estimate is 0.050. Its confidence interval crosses zero, so the estimate is compatible with differences in either direction. Risk differences are often easier to relate to absolute frequencies than relative measures, but they remain uncertain estimates when based on limited data.

What does the confidence interval contribute?

A confidence interval describes the precision of an estimate under the statistical method used. In general, it gives a range of values that are reasonably compatible with the observed data and method, rather than a guarantee that the true effect lies within that specific interval. Wider intervals indicate less precision. For the primary comparison, the interval runs from -0.061 to 0.161. Because it includes zero, the data do not sharply distinguish a positive difference from a negative difference. It also includes values that could represent more than a negligible difference; the record does not define a threshold for clinical importance.

How should the p-value be read?

A p-value measures how unusual data at least as extreme as those observed would be under a specified null model and its assumptions. It is not the chance that the null hypothesis is true, and it is not a measure of the size or importance of an effect. The primary comparison has an unadjusted p-value of 0.38. This value does not show that the groups are equivalent; equivalence requires a prespecified margin and an analysis designed to assess it. No equivalence margin is reported in the registry record.

The registry includes unadjusted comparisons based on posted group summaries. An unadjusted result is not the same as a multivariable-adjusted trial analysis, and it may not account for stratification factors, repeated measures, site effects, or other features of a prespecified analysis. The registry record does not report the original statistical analysis plan or the sponsor’s analysis methods for the primary endpoint. The reported safety population is defined by receipt of at least one dose, which is not necessarily identical to every possible randomized analysis population.

Why do participant counts differ from event counts?

The primary endpoint is a count of participants with one or more TEAEs. It does not count the total number of TEAEs. This distinction matters because one participant may experience multiple events, while another may experience none. The group counts therefore describe how many participants were affected at least once, not the total burden or pattern of events. The adverse-event summaries separately report participants affected by serious and other events; those categories should not be combined by addition, because the record does not state that they are mutually exclusive.

Why does multiplicity matter?

When a study examines multiple outcomes, multiple timepoints, or multiple comparisons, the chance of finding at least one apparently unusual result can increase. A multiplicity strategy may control that risk through a prespecified testing hierarchy or another adjustment. The registry record does not report such a strategy. The secondary results therefore warrant cautious interpretation, particularly when considered individually. Their unadjusted p-values are descriptive evidence, not a basis for treating one isolated finding as confirmatory.

General statistical considerations also apply to missing outcome data. If outcome availability differs between groups or is related to participants’ health status, a comparison among observed cases may be biased. Methods such as imputation or sensitivity analyses can address some missing-data concerns, but their appropriateness depends on assumptions. The registry record does not report missing-data counts or methods for these comparisons, so the extent and handling of missingness cannot be assessed.

For safety outcomes, participants may contribute to more than one category, and an adverse event can be serious without being caused by the study treatment. A group-level count is useful for describing what was reported but does not replace examination of event definitions, timing, severity, relatedness assessments, and participant-level clinical context. Those details are not reported in the registry record beyond the listed summaries and terms.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.050, with a confidence interval from -0.061 to 0.161. This interval crosses zero and extends in both directions. It therefore reflects uncertainty not only about the magnitude of a possible group difference but also about its direction. The unadjusted p-value is 0.38. Neither the point estimate nor the p-value should be read in isolation from the interval and the small group counts.

In general, confidence intervals convey the precision of estimates: a narrower interval indicates greater precision, while a wider interval leaves more possible values consistent with the data and method. They are not a guarantee about the true value, and they do not determine whether a difference matters clinically. The registry record does not report a threshold for a clinically meaningful difference in TEAEs.

Each of the three posted Day 29 risk-difference intervals also crosses zero. Their unadjusted p-values are 0.167, 0.247, and 0.289. This pattern means the estimates are uncertain and does not establish equivalence or absence of an effect. The secondary intervals are broad in relation to their point estimates, so the posted summaries allow a range of plausible differences.

Precision depends on the amount of information in the data, the outcome frequency, and the method used. The registry record’s group counts are limited, and the outcomes are participant-level binary measures. The confidence intervals are recalculated, unadjusted intervals from the posted summaries rather than reported adjusted intervals from a trial model. The record does not report the methods used for any sponsor-adjusted intervals or the original analysis plan. Accordingly, these intervals are best read as transparent summaries of uncertainty around the posted group comparisons, not as a substitute for a full trial analysis.

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 original trial design. For these binary outcomes, the listed figures are participants per arm. The assumptions stated for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column indicates the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under the illustration’s assumptions, if that effect were the true effect and the model assumptions held. The 90% power column uses a higher target probability of detecting the same specified effect. These are design-planning quantities, not forecasts of what a future study will find. The figures are not observed power.

Rows for 100%, 75%, and 50% of the observed effect consider progressively smaller effects than the full observed estimate. Smaller effects are harder to distinguish from random variation, so the planning figures require more participants per arm. For example, the primary endpoint illustration lists 423 participants per arm for 80% power and 566 for 90% power when planning for 100% of the observed effect. For 75% of that effect, the figures are 812 and 1,086; for 50%, they are 1,959 and 2,622.

These illustrations are sensitive to the estimated effect used as their starting point. Because the trial’s observed comparisons are imprecise, planning directly from them may produce unstable estimates of future requirements. The figures also do not incorporate any assumptions beyond those stated for the illustration, such as potential loss to follow-up or a chosen multiplicity strategy. They should be read as conditional design examples, not as the enrollment target the trial used or evidence about the trial’s power.

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 = 0.902; treatment proportion p₁ = 0.952; average p̄ = 0.927.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3669 = 0.7192.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3652 = 0.3074.
4. n = (0.7192 + 0.3074)² / (0.0499)² = 422.5, rounded up to 423 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 <- 0.902439024390244                          # control proportion
p1 <- 0.952380952380952                          # 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(3158727)
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 = 423 (80% power), 566 (90% power)
 75% of observed effect: n per arm = 812 (80% power), 1,086 (90% power)
 50% of observed effect: n per arm = 1,959 (80% power), 2,622 (90% power)
power.prop.test: 422.5 
Simulated power at n = 423 per arm: 0.815 (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 broad set of outcome measures, including several secondary measures related to ventilation, vasopressors, and Day 29 status. Testing multiple outcomes can increase the chance of at least one apparently positive result arising by chance. Trials commonly address this through a prespecified hierarchy, adjustment of significance thresholds, or other procedures. The registry record does not report whether any such multiplicity strategy was planned or used. The unadjusted secondary comparisons should therefore be interpreted as exploratory, rather than as independent confirmatory tests.

The registry record reports no sponsor analyses for the detailed secondary results. It does not provide the original statistical analysis plan, specify which outcomes were primary or key secondary for inferential testing beyond the posted primary measure, or explain whether any analyses were adjusted for baseline factors. Those details are not reported in the registry record. As a result, it is not possible to determine from these summaries whether the analyses were prespecified in their reported form or how they relate to the full trial analysis.

Missing data can also affect interpretation. The registry summaries do not report missing-outcome counts, reasons for missingness, or methods used to handle missing observations for the endpoint comparisons. In general, missingness can bias a comparison if the probability of an outcome being observed is related to group assignment or participant health. Complete-case comparisons, imputation, and sensitivity analyses rely on different assumptions; without the underlying reporting, none can be attributed to this trial.

The primary endpoint population is defined as randomized participants who received at least one dose. This is a safety population definition and differs conceptually from an analysis that includes all randomized participants regardless of treatment received. The registry record does not report the full analysis-population strategy or how participants without a dose were handled in other outcomes. These gaps limit assessment of the influence of exclusions, missing follow-up, and analytic choices on the results.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: multiple organ dysfunction syndrome (9.8%), respiratory failure (7.3%), acute kidney injury (7.1%), atrioventricular block complete (4.9%), hypoxia (4.9%).

The adverse-event summary reports serious adverse events in 20 of 41 participants in the placebo group and 24 of 42 in the Cx611 group. It reports other adverse events in 41 of 41 and 42 of 42 participants, respectively. The registry separately lists deaths as 12 for placebo and 13 for Cx611. These are group-level counts; they do not indicate that events were caused by the assigned infusion.

The listed serious-event terms include multiple organ dysfunction syndrome at 9.8%, respiratory failure at 7.3%, acute kidney injury at 7.1%, atrioventricular block complete at 4.9%, hypoxia at 4.9%, and cardiac arrest at 4.8%. The record does not provide enough detail in these summaries to infer event timing, severity distribution, relatedness assessments, or whether one participant could contribute to more than one term. The listed percentages should be read as registry-reported values, not as a complete description of individual clinical courses.

Serious-event counts, other-event counts, and deaths are different summaries and should not be added together. These figures describe what was reported in the registry record and do not establish comparative causality or a full benefit-harm balance.

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

The posted results show that treatment-emergent adverse events were reported by 37.0 of 41.0 participants in the placebo group and 40.0 of 42.0 in the Cx611 group. The unadjusted comparison is imprecise: its confidence interval crosses zero and its p-value is 0.38. The result does not establish a clear between-group difference, but it also does not establish that the groups are equivalent or that an important difference is absent.

The secondary Day 29 status comparisons are also uncertain. Their estimates are in one direction, but each confidence interval crosses zero. These results do not establish a benefit or harm on those outcomes. Because the record does not report a multiplicity strategy or the full analysis plan, the secondary comparisons should not be interpreted as definitive tests of efficacy.

These data cannot determine whether an individual adverse event was caused by Cx611. Treatment-emergent describes timing in relation to the study period, not causation. The registry summaries also do not give the detail needed to assess event severity, clinical course, or relatedness comprehensively. The death counts are descriptive and do not establish a treatment-related difference.

The study is described as an assessment of safety, tolerability, and efficacy, but the results available in the record support only cautious interpretation of the posted outcomes. They do not show that Cx611 works or does not work, and they do not provide medical guidance. The results are limited by the imprecision of the comparisons, the absence of reported sponsor analyses for the detailed secondary outcomes, and unreported details about missing data and analysis methods. Further conclusions would require the complete trial report and its prespecified analyses, which are not reported in the registry record.

17. Why This Trial Matters Statistically

SEPCELL illustrates a central statistical challenge in early-phase clinical research: a randomized comparison can produce useful safety and outcome summaries while still leaving substantial uncertainty about between-group effects. The primary endpoint is clinically relevant as a count of participants experiencing one or more treatment-emergent adverse events, but a participant count does not capture event frequency, severity, or attribution. Those distinctions matter when interpreting safety evidence.

The confidence interval around the primary comparison is informative because it makes the uncertainty visible rather than reducing interpretation to a single p-value. It crosses zero and includes estimates in both directions. The secondary comparisons likewise have intervals crossing zero. This means the data do not establish a clear effect on these outcomes, but neither do they prove equivalence. Understanding what remains uncertain is an important part of reading a clinical trial accurately.

The registry also lists multiple secondary measures. Without a reported multiplicity plan, individual secondary p-values have limited confirmatory force. The distinction between an exploratory signal and a prespecified confirmatory analysis is essential for avoiding overinterpretation. Similarly, a future sample-size illustration based on an observed estimate is not evidence of the original trial’s design assumptions or of observed power.

For biostatisticians and clinical researchers, the record highlights why endpoint definitions, analysis populations, missing-data methods, and prespecified plans are necessary to interpret results. The posted summaries are useful for describing what was recorded, but their limitations should remain visible alongside the estimates. Statistical restraint is especially important when interpreting a safety-focused early-phase study with imprecise comparisons.

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 registry record leaves important details unavailable for assessing the results. It does not report the original sample-size justification, the original statistical analysis plan, or the methods used for any sponsor-adjusted analysis. It also does not describe the randomization sequence, allocation concealment, the masking procedures in practice, or the identities of the roles covered by quadruple masking.

The primary comparison is based on the stated safety population of participants who received at least one dose. The record does not report how this population relates to other possible analysis populations or how participants who did not receive treatment were handled in other analyses. Missing-outcome counts, reasons for missingness, and missing-data methods are not reported for the posted comparisons.

The detailed secondary results are limited to three Day 29 status outcomes, despite additional secondary measures being listed in the registry. The record reports no sponsor analyses for these detailed results and does not explain any hierarchy or adjustment for multiple outcomes. Therefore, the secondary results are difficult to place within a complete inferential plan.

The primary endpoint counts participants with at least one TEAE, which does not describe the total number of events, event severity, or the causal relationship to treatment. The adverse-event summaries similarly do not provide participant-level patterns, event timing, or relatedness assessments in the information reported. The registry enrollment entry and endpoint population counts are different record fields and should not be conflated. These limitations constrain interpretation of both safety and efficacy-related findings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Cx611-0204 SEPCELL Study — NCT03158727.
• Registry record last updated 2022-04-06; status last verified 2022-02.
• Results first posted 2022-04-06.
• 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

NCT03158727, the Cx611-0204 SEPCELL Study, is recorded as a completed phase Ib/IIa randomized, double-blind, placebo-controlled, parallel-group, multicentre study. It assessed Cx611 added to standard care against placebo infusions added to standard care in adults with severe community-acquired bacterial pneumonia admitted to intensive care.

The primary endpoint was the number of participants reporting one or more treatment-emergent adverse events from baseline up to Day 90. The registry reports 37.0 of 41.0 participants in the placebo group and 40.0 of 42.0 in the Cx611 group. The unadjusted risk-difference estimate is 0.050, with a confidence interval crossing zero and an unadjusted p-value of 0.38.

Three detailed Day 29 secondary comparisons are also reported; each has an unadjusted confidence interval crossing zero. The registry record does not report the original sample-size justification, analysis plan, multiplicity approach, or missing-data methods. The posted summaries therefore describe the recorded outcomes but leave considerable uncertainty about comparative effects.