Study to Assess Efficacy and Safety of Cx601, Adult Allogeneic Expanded Adipose-derived Stem Cells (eASC) for the Treatment of Complex Perianal Fistula(s) in Participants With Crohn's Disease (CD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess Efficacy and Safety of Cx601, Adult Allogeneic Expanded Adipose-derived Stem Cells (eASC) for the Treatment of Complex Perianal Fistula(s) in Participants With Crohn's Disease (CD) (NCT03279081), a randomized phase 3 study. The primary outcome is Percentage of Participants With Combined Remission at Week 24.

2. Clinical Question

The question concerns a combined clinical and imaging outcome rather than external-opening closure alone. Requiring both features makes the endpoint a stricter measure of remission than either feature by itself. The trial compared the observed proportions between randomized groups; it did not simply ask whether participants improved from their own baseline.

The registry describes a Phase 3, randomized, double-blind, parallel-group, placebo-controlled study conducted internationally at multiple centres. The trial’s stated purpose was to assess efficacy and safety over 24 weeks, with follow-up up to 52 weeks. The primary comparison therefore focuses on the Week 24 assessment, while the later follow-up and secondary outcomes address other time points and definitions.

3. Trial Design

This was a Phase 3 randomized, double-blind, parallel-group, placebo-controlled, international, multicentre trial of Cx601 in participants with Crohn’s disease and complex perianal fistula(s). The registry lists quadruple masking. Participants were assigned to a single local injection of Cx601 or placebo; the Cx601 description specifies 120 million cells, while the placebo description specifies saline 24 mL.

The registry records enrollment of 568. The primary completion date was 2023-01-23, and the study status is completed. The official title describes assessment over 24 weeks and follow-up up to 52 weeks. Week 24 was the time point for the primary combined-remission outcome. Secondary outcomes include clinical remission and response, combined remission at a later time point, and time-to-event measures.

The ITT Analysis Set included all randomized participants regardless of treatment receipt and regardless of whether postbaseline efficacy measurements were available. For the primary outcome, the posted group estimates use 285 participants in the placebo group and 283 in the Cx601 group. The registry’s primary endpoint description defines the outcome using clinical assessment and blinded central MRI assessment.

The registry record does not report the trial’s original sample-size assumptions or justification, the allocation procedure beyond randomization, or the identities of the masking roles. Details of the randomization strata, if any, are not reported in the registry record. The outcome results and design description support interpretation of the stated comparison, but do not fill in those protocol details.

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: A total of 568 participants with a diagnosis of Crohn's disease were enrolled in a 1:1 ratio to receive either Cx601 or matching placebo.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT Analysis Set included all randomized participants regardless of their being treated or not and regardless of their having any postbaseline efficacy measurements or not.

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 Intent-to-treat (ITT) Analysis Set included all randomized participants regardless of their being treated or not and regardless of their having any postbaseline efficacy measurements or not.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Combined Remission at Week 24, measured over Week 24.

The primary endpoint is the percentage of participants with combined remission at Week 24. A participant met the definition if all treated external openings that were draining at baseline were closed despite gentle finger compression, and MRI showed no collection >2 cm in at least 2 dimensions in the treated perianal fistula(s). The imaging assessment was made by a blinded central reviewer.

This endpoint combines a clinical sign with an imaging finding. External-opening closure alone may not capture whether a collection remains, while imaging alone would not establish that the draining openings have closed. Requiring both elements gives the outcome a more comprehensive definition of remission for the treated fistula(s). That is a general rationale for a combined endpoint; it does not establish that the measure captures every outcome important to participants.

The percentage is interpretable as the proportion meeting the definition in each randomized group. The registry specifies the ITT Analysis Set, including randomized participants whether treated or not and whether or not they had a postbaseline efficacy measurement. The record does not describe how missing Week 24 endpoint information was handled in the analysis. As a result, the endpoint definition is clear, but the precise missing-data procedure cannot be assessed from the registry record.

7. Results Posted in the Registry

• Cx601: 48.8% (138/283) versus 46.3% (132/285) on control; risk difference 2.4 percentage points (95% CI -5.8 to 10.7), risk ratio 1.05 (0.89–1.25); unadjusted two-proportion z-test p = 0.559.

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 With Clinical Remission at Week 24

• 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:
  • Cx601: 49.8% (141/283) versus 47.0% (134/285) on control; risk difference 2.8 percentage points (95% CI -5.4 to 11.0), risk ratio 1.06 (0.89–1.26); unadjusted two-proportion z-test p = 0.503.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cx601 and the control. The interval gives the range of effects that remain compatible with the data.

Time to Clinical Remission at Week 24

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Placebo vs Cx601: hazard ratio 1.09 (95% CI 0.90–1.32), reported p = =0.374 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo vs Cx601 and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Combined Remission at Week 52

• 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:
  • Cx601: 41.0% (116/283) versus 39.6% (113/285) on control; risk difference 1.3 percentage points (95% CI -6.7 to 9.4), risk ratio 1.03 (0.85–1.26); unadjusted two-proportion z-test p = 0.745.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cx601 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question in several directions: they include clinical remission and response, outcomes assessed at Week 52, and time to remission or response. These measures are related to the primary endpoint, but they are not interchangeable. Clinical remission does not include the same combined clinical-and-MRI definition, and a time-to-event measure asks when an outcome occurs rather than only whether it is met at a fixed assessment.

Across the secondary results with estimates recorded, the overall pattern is of group estimates that are relatively close, with uncertainty that does not establish a clear separation. This broad pattern is consistent with the primary comparison. It should not be taken as proof that all outcomes are the same between groups, nor does it settle outcomes for which the record does not give corresponding estimates.

Secondary analyses generally carry less confirmatory weight than a prespecified primary analysis, particularly when multiple outcomes or time points are examined. Testing many outcomes increases the opportunity to find an apparently notable result by chance. A multiplicity adjustment can address that issue, but the registry record does not report whether an adjustment was planned or applied. Secondary p-values should therefore be interpreted cautiously, and isolated findings should not be treated as conclusive without the full testing plan.

The secondary outcomes are useful as supporting context because they explore different aspects and time points of the condition. Their value depends on the quality of measurement, completeness of follow-up, and analysis choices, including how missing observations and multiple comparisons were handled. Those details are not all reported in the registry record.

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

• Percentage of Participants With Clinical Remission at Week 24
• Time to Clinical Remission at Week 24
• Percentage of Participants With Combined Remission at Week 52
• Percentage of Participants With Clinical Remission at Week 52
• Percentage of Participants With Clinical Response at Week 24
• Percentage of Participants With Clinical Response at Week 52
• Time to Clinical Remission at Week 52
• Time to Clinical Response at Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either met the combined-remission definition at Week 24 or did not. A group percentage expresses the number meeting the definition relative to the group’s analysis denominator. Comparing these percentages addresses the difference in outcome probability between the randomized groups.

What does the risk difference represent?

The risk difference subtracts the outcome proportion in the comparator group from the outcome proportion in the intervention group. A value of zero represents equal proportions; a positive value indicates a higher observed proportion in the intervention group, and a negative value indicates a lower one. The re-calculated estimate is 0.025, with a 95% confidence interval from -0.058 to 0.107. The interval crosses zero, so the data are compatible with either direction of difference.

The posted unadjusted comparison also gives a risk ratio and an odds ratio. In general, a risk ratio compares the outcome probabilities between groups, while an odds ratio compares the odds. These measures describe relative rather than absolute contrasts and can be harder to interpret without the group percentages. The registry’s sponsor analysis is instead reported as a difference in combined-remission rate using the Cochran-Mantel-Haenszel method.

Why are there two reported comparisons?

The registry reports its own Cochran-Mantel-Haenszel analysis and the posted results include a simple unadjusted recalculation from the group summary statistics. A Cochran-Mantel-Haenszel procedure is generally used to estimate or test a group association while accounting for strata. Which strata were used is not reported in the registry record. The unadjusted calculation compares the displayed group summaries without such adjustment. These analyses can differ because their calculation methods and inputs differ. The registry analysis is the sponsor’s reported analysis; the recalculation is a supplementary description of the posted summaries.

A p-value describes how unusual data at least as inconsistent with a specified null model would be, if that model and its assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The p-values for the primary comparison are close to one another, and neither indicates a clear separation of the groups under conventional interpretation. The registry’s planned significance threshold and complete testing procedure are not reported in the registry record.

What does the confidence interval add?

A confidence interval gives a range of values compatible with the observed data under the method’s assumptions. In general, a 95% confidence procedure would cover the target quantity in 95% of repeated samples under those assumptions. It is not a statement that there is a 95% probability that this particular interval contains the true effect. The interval is especially useful because it shows that the point estimate should not be treated as precise evidence of a single effect value.

Confidence intervals for the individual group percentages describe uncertainty in each group estimate. The interval for the group contrast directly addresses the comparative question. Those intervals answer different questions, so comparing whether the separate group intervals overlap is not a substitute for examining the interval for the difference.

How is time to an outcome analysed?

For a time-to-event outcome, the event is the occurrence of the defined outcome, and the method considers when it occurs. The registry reports a log-rank comparison and a hazard ratio for time to clinical remission. In general, the log-rank method compares event timing across groups while accounting for the time participants remain under observation. A hazard ratio describes the relative event rate over time under the model’s conditions; it is not the same quantity as a difference in percentages. The registry does not provide enough detail to assess every time-to-event assumption or the handling of censoring.

Median time is a separate summary: it identifies the time by which half of the relevant observed event-time distribution has occurred, subject to the analysis definition. It should not be read as a comparison of the proportion meeting remission at a fixed time point. The two kinds of endpoint address related but distinct questions.

What information is missing for a full statistical audit?

The registry record identifies the ITT population and names the primary analysis method, but it does not report the trial’s full statistical analysis plan, the handling of missing primary outcome data, any prespecified covariates or strata, or the complete multiplicity procedure. It also does not report whether interim analyses were conducted. These omissions limit independent assessment of the exact analysis decisions. They do not change the arithmetic meaning of the posted group summaries, but they matter when judging how fully the reported tests reflect the original plan.

11. Confidence Intervals and Precision

The primary group estimates are 46.32% for placebo, with a 95% confidence interval from 40.53% to 52.1%, and 48.76% for Cx601, with a 95% confidence interval from 42.94% to 54.59%. These intervals show uncertainty in each group’s percentage. The comparative estimate is more directly relevant to whether the groups differ: the re-calculated risk difference is 0.025, with a 95% confidence interval from -0.058 to 0.107.

Because the comparative interval includes zero, the data do not pin down the direction of the difference. Its width also indicates that the estimate is not precise enough to distinguish confidently among a range of possible effects. The point estimate alone would give an incomplete account; it should be read together with the interval and the group estimates.

The sponsor’s reported 95% confidence interval for the difference in combined-remission rate runs from -5.82 to 10.55. It also includes zero. This interval comes from the reported Cochran-Mantel-Haenszel analysis, whereas the other interval is an unadjusted recalculation. The methods should not be silently treated as identical, even though they lead to a broadly similar interpretation.

In general, a confidence interval reflects both the observed information and the method used to analyse it. It does not account for every possible source of uncertainty, such as uncertainty about endpoint definitions, missing-data assumptions, or selective reporting. Those issues require information about the analysis plan and conduct, some of which is not reported in the registry record.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations are based on the observed effect, not on the trial’s original design assumptions. For binary outcomes, the figures are participants per arm. For time-to-event outcomes, the figures are total events. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They show planning for 100%, 75%, and 50% of the observed effect.

The 80% power column describes an illustrative design that, under those assumptions, would have an 80% chance of detecting the stated effect if that effect were the true one. The 90% power column uses the same idea with a higher chance of detection under the assumed effect. These are design calculations, not guarantees: actual results depend on the true effect, variability, follow-up, missingness, and whether the assumptions hold.

The illustrations show the general planning relationship: smaller effects require more participants per arm for binary outcomes, or more total events for time-to-event outcomes, to achieve the same target power under the stated assumptions. This relationship is why planning for a fraction of the observed effect produces larger figures than planning for the full observed effect.

These figures are not observed power. They are hypothetical planning illustrations based on the observed effect and specified assumptions. The trial’s own original sample-size justification and design assumptions are not reported in the registry record. They should therefore not be used to infer what the investigators planned or whether the completed trial met its original design target.

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 = 0.463; treatment proportion p₁ = 0.488; average p̄ = 0.475.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7063 = 1.3842.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7060 = 0.5942.
4. n = (1.3842 + 0.5942)² / (0.0245)² = 6,534.5, rounded up to 6,535 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 <- 0.463157894736842                          # control proportion
p1 <- 0.487632508833922                          # 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(3279081)
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 = 6,535 (80% power), 8,748 (90% power)
 75% of observed effect: n per arm = 11,611 (80% power), 15,543 (90% power)
 50% of observed effect: n per arm = 26,107 (80% power), 34,949 (90% power)
power.prop.test: 6534.5 
Simulated power at n = 6,535 per arm: 0.802 (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 sponsor’s reported primary analysis is a Cochran-Mantel-Haenszel comparison. It gives a difference in combined-remission rate of 2.37, with a 95% confidence interval from -5.82 to 10.55 and p=0.571. The supplementary unadjusted recalculation from the posted group summaries gives a risk difference of 0.025, with a 95% confidence interval from -0.058 to 0.107 and an unadjusted p-value of 0.559.

The estimates are not identical because the reported analysis and the unadjusted recalculation use different methods. Both intervals include zero, and both p-values support a similar broad reading: the estimates do not show a clear between-group separation. The registry record does not identify the strata used for the sponsor’s analysis, so the source of the numerical difference cannot be examined further from the available details.

The recalculation is a descriptive check based on posted summaries; it does not replace the prespecified sponsor analysis. In this case the discrepancy flag is false, so there is no indicated discrepancy requiring the sponsor’s result to take precedence over a conflicting recalculation.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and lists multiple secondary outcomes. The posted record also reports 14 outcome measures, 11 analyses, and 13 secondary outcomes with results posted. When many outcomes, time points, or analyses are examined, the chance of at least one apparently unusual result can increase even if no true effect exists. This is the general multiplicity problem.

One common response is to define a testing hierarchy or adjust significance thresholds across a family of comparisons. Another is to describe secondary analyses as exploratory and interpret them as supportive rather than definitive. The registry record does not report a multiplicity adjustment, testing hierarchy, or complete prespecified plan, so it is not possible to determine whether the reported secondary tests were protected against multiplicity.

The primary endpoint is defined for the ITT Analysis Set, which includes all randomized participants regardless of treatment receipt and regardless of having postbaseline efficacy measurements. This is an important population description. However, the method used to handle missing endpoint data is not reported in the registry record. The record also does not say whether missing outcomes were imputed, treated as failures, excluded from a particular analysis, or addressed through sensitivity analyses. Those details can affect the interpretation of an ITT result when outcome measurements are incomplete.

The registry names the Cochran-Mantel-Haenszel method for the primary comparison, but does not provide the full statistical analysis plan, including any covariate specifications or strata. Interim analyses are not reported in the registry record. These omissions mean the posted results can be described and their numerical uncertainty interpreted, but the extent to which every analysis followed a prespecified plan cannot be independently assessed from the registry record alone.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anal abscess (4.4%), proctalgia (1.8%), anal fistula (1.5%), covid-19 (1.1%), female genital tract fistula (0.8%).

The serious adverse event summaries report 35 participants affected among 274 at risk in the placebo group and 41 among 278 at risk in the Cx601 group. These are counts with their stated denominators; they should not be confused with the efficacy analysis denominators. The registry also reports 67 participants with other adverse events among 274 at risk for placebo, and 66 among 278 at risk for Cx601.

The most frequently listed serious adverse event terms include anal abscess at 4.4%, proctalgia at 1.8%, anal fistula at 1.5%, COVID-19 at 1.1%, female genital tract fistula at 0.8%, and fallopian tube cancer at 0.8%. The record reports 0 deaths in the placebo group and 1 in the Cx601 group.

These summaries describe reported events during the trial; they do not establish that an event was caused by the assigned intervention. The registry record does not provide event-level timing, severity grades, exposure-adjusted rates, or enough detail to assess overlap among event terms. Counts should therefore be read as a descriptive safety summary, not as a causal comparison or a complete account of individual risk.

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

The primary result describes the proportion of randomized participants meeting a specific combined-remission definition at Week 24. The observed percentages were 46.32% with placebo and 48.76% with Cx601. The estimated comparative difference is imprecise: its 95% confidence interval includes zero, and the sponsor’s reported analysis also gives an interval spanning zero. The result does not provide clear statistical evidence of a between-group difference under the reported analyses.

This is not the same as demonstrating that the groups are equivalent. Equivalence or noninferiority requires a prespecified margin and an analysis designed to answer that question; such a margin is not reported in the registry record. Nor does the result show that the intervention has no possible effect. The interval remains compatible with a range of comparative effects, including effects in either direction.

The endpoint is specific: it requires both closure of treated external openings and no qualifying collection on central MRI assessment. It does not represent every symptom, complication, quality-of-life measure, or longer-term outcome that might matter to participants. The secondary outcomes add other measures, but the results do not justify broad conclusions about outcomes not included in the posted record.

Trial averages also do not determine what will happen to an individual participant. The results apply to the studied population and the trial’s intervention, comparator, measurement definitions, and follow-up. Differences in those features can limit how directly the findings apply in other settings. The information is a statistical description of trial results, not medical advice or a recommendation about treatment.

Finally, confidence intervals and p-values are conditional on the analysis methods and data being appropriate. The registry does not report all details needed to assess missing-data handling, multiplicity, or the full analysis plan. Those uncertainties should remain part of any interpretation rather than being filled in by assumptions.

18. Why This Trial Matters Statistically

This trial illustrates why the point estimate alone is not enough to interpret a binary clinical outcome. The two group percentages are close, and the primary comparative interval crosses zero. Reporting the interval alongside the estimate makes clear that the data do not identify a narrow, certain effect.

It also highlights the distinction between a sponsor-reported analysis and a simple unadjusted recalculation. The sponsor used a Cochran-Mantel-Haenszel method, while the recalculation uses the posted group summaries. Their results are broadly similar in interpretation, but their methods and numerical estimates are not interchangeable. Clear reporting of the analysis method is essential for understanding what a comparison represents.

The combined-remission endpoint brings clinical assessment and central imaging together. That can make the measure more specific than a single component, while also making interpretation depend on consistent clinical assessment and imaging review. Endpoint definitions are therefore central to understanding what the reported percentage means.

Finally, the record illustrates how uncertainty extends beyond the effect estimate. The details of missing-data handling, multiplicity, and the trial’s original sample-size assumptions are not reported in the registry record. These gaps do not erase the posted results, but they limit how fully readers can assess the analysis plan and the strength of conclusions drawn from multiple outcomes.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The interpretation is limited by the details available in the registry record. The method for handling missing Week 24 outcome data is not reported, even though the ITT population includes randomized participants regardless of whether postbaseline efficacy measurements were available. Without that information, the effect of missing outcome data on the primary estimate cannot be assessed.

The record does not report the trial’s original sample-size justification, the planned significance threshold for the primary analysis, a complete multiplicity strategy, or whether interim analyses were conducted. It names a Cochran-Mantel-Haenszel method but does not identify the strata or other analysis specifications. These omissions make it harder to compare the reported analyses with the full prespecified plan.

The primary outcome uses a particular clinical and MRI definition at Week 24. Different endpoint definitions or assessment times could yield different summaries, so conclusions should remain tied to this measure. Although follow-up was planned up to 52 weeks and secondary measures include later outcomes, those do not substitute for the primary assessment.

The registry describes an international multicentre trial in participants with Crohn’s disease and complex perianal fistula(s). Results may not apply directly to populations or care settings with different characteristics, and the record does not provide subgroup results sufficient to assess variation across participant groups. The safety summary is also limited: it gives counts and selected serious event terms, but not detailed timing, severity, exposure-adjusted rates, or causal assessments.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess Efficacy and Safety of Cx601, Adult Allogeneic Expanded Adipose-derived Stem Cells (eASC) for the Treatment of Complex Perianal Fistula(s) in Participants With Crohn's Disease (CD) — NCT03279081.
• Registry record last updated 2024-09-19; status last verified 2024-08.
• Results first posted 2024-09-19.
• 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

NCT03279081 is a completed Phase 3 randomized, quadruple-masked, parallel-group, placebo-controlled, international, multicentre study sponsored by Tigenix S.A.U. It enrolled 568 participants with Crohn’s disease and complex perianal fistula(s). The primary completion date was 2023-01-23.

The trial compared a single local injection of Cx601, 120 million expanded adipose-derived stem cells, with a single local injection of placebo saline, 24 mL. The primary outcome was combined remission at Week 24, defined using closure of treated draining external openings and central MRI assessment for qualifying collections.

The Week 24 group percentages were 46.32% with placebo and 48.76% with Cx601. The sponsor’s reported comparison and the unadjusted recalculation both have confidence intervals that include zero. The posted record also contains secondary outcome and safety information, while key details of the missing-data procedure, multiplicity plan, and original sample-size assumptions are not reported in the registry record.