Safety and Efficacy of Andecaliximab in Participants With Moderately to Severely Active Crohn's Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Andecaliximab in Participants With Moderately to Severely Active Crohn's Disease (NCT02405442), a randomized phase 2 study. The primary outcome is Percentage of Participants Achieving Clinical Response (PRO2 Score ≤ 8) at Week 8 of the Double-Blind Phase.

2. Clinical Question

The study was randomized, double-blind, parallel-group, and placebo-controlled. The primary question is about the observed response proportions during the blinded phase, not about later treatment during the optional open-label and extended treatment phases. No causal conclusion should be drawn from percentages alone without considering uncertainty, the analysis population, and the conduct and analysis details recorded for the trial.

3. Trial Design

This was a Phase 2, randomized, double-blind, placebo-controlled, multicenter study of andecaliximab in participants with moderately to severely active Crohn’s disease. The registry record reports enrollment of 187 and lists the study status as terminated. The study started on 2015-04-30, and the primary completion date was 2016-11-30. The reason for termination is not reported in the registry record.

The double-blind phase was planned for 8 weeks, with four parallel groups: andecaliximab 150 mg every 2 weeks, andecaliximab 150 mg weekly, andecaliximab 300 mg weekly, and placebo. According to the arm descriptions, treatment was administered by prefilled syringe, with matching placebo used to maintain blinding. The primary Week 8 analysis group sizes were 53 for each andecaliximab regimen and 28 for placebo.

Participants completing the double-blind phase could be eligible for an optional open-label extension for an additional 44 weeks. Participants completing Week 52 assessments could be eligible to enter an extended treatment phase for an additional 156 weeks. These later phases differ from the randomized, placebo-controlled comparison; the Week 8 results discussed for the primary endpoint are from the double-blind phase.

The registry record does not report the original sample-size justification, the planned statistical analysis in sufficient detail to reproduce it, interim analyses, or the reason the study was terminated. Those absences limit interpretation of how the enrollment target and analysis strategy were chosen. The posted results describe outcomes, but they do not replace a full protocol or 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: 315 participants were screened.

Double-Blind Phase (up to Week 8)

Reasons for not completing this period:

Open-Label Phase (up to Week 52)

Reasons for not completing this period:

Extended Treatment Phase(up to Week 208)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set included all randomized participants who received at least 1 dose of study drug.

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: Safety Analysis Set included all participants who received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Clinical Response (PRO2 Score ≤ 8) at Week 8 of the Double-Blind Phase, measured over Week 8.

The primary endpoint was the percentage of participants achieving clinical response at Week 8 of the double-blind phase. Response was defined as a PRO2 score ≤ 8. PRO2 is the weighted average of two patient-reported measures: frequency of liquid or very soft stools and abdominal pain. The score draws on participant diary data over 7 days. A higher score indicates more frequent stools and more severe abdominal pain; the score has a minimum of 0 and no upper bound.

This endpoint captures symptoms reported by participants rather than an objective measure alone. It gives a defined threshold for classifying whether a participant met the response criterion during the Week 8 assessment window. That window was Day 43 to Day 70 and had to occur before the first open-label dose. Participants with a missing PRO2 value at the Week 8 analysis visit were counted as not achieving clinical response.

In general, a binary endpoint such as this makes the result straightforward to describe as a proportion meeting or not meeting a threshold. It also discards differences in score among participants on the same side of that threshold: a participant just meeting the criterion and one with a lower score both count as responders. The endpoint therefore answers a specific question about threshold achievement, not the full range or trajectory of PRO2 scores.

7. Results Posted in the Registry

• Andecaliximab 150 mg Every 2 Weeks: 17.0% (9/53) versus 14.3% (4/28) on control; risk difference 2.7 percentage points (95% CI -13.7 to 19.1), risk ratio 1.19 (0.40–3.52); unadjusted two-proportion z-test p = 0.753.
• Andecaliximab 150 mg Weekly: 13.2% (7/53) versus 14.3% (4/28) on control; risk difference -1.1 percentage points (95% CI -16.9 to 14.8), risk ratio 0.92 (0.30–2.89); unadjusted two-proportion z-test p = 0.893.
• Andecaliximab 300 mg Weekly: 11.3% (6/53) versus 14.3% (4/28) on control; risk difference -3.0 percentage points (95% CI -18.5 to 12.6), risk ratio 0.79 (0.24–2.58); unadjusted two-proportion z-test p = 0.700.

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 Achieving CDAI Remission (CDAI ≤ 150) at Week 8 of the Double-Blind Phase

• 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:
  • Andecaliximab 150 mg Every 2 Weeks: 20.8% (11/53) versus 21.4% (6/28) on control; risk difference -0.7 percentage points (95% CI -19.4 to 18.0), risk ratio 0.97 (0.40–2.34); unadjusted two-proportion z-test p = 0.944.
  • Andecaliximab 150 mg Weekly: 17.0% (9/53) versus 21.4% (6/28) on control; risk difference -4.4 percentage points (95% CI -22.7 to 13.8), risk ratio 0.79 (0.31–2.00); unadjusted two-proportion z-test p = 0.624.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Andecaliximab 150 mg Every 2 Weeks and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Andecaliximab 150 mg Weekly and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Achieving Mucosal Healing (SES-CD Size-of-Ulcer Subscore = 0) at Week 8 of the Double-Blind Phase

• 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:
  • Andecaliximab 150 mg Every 2 Weeks: 5.7% (3/53) versus 7.1% (2/28) on control; risk difference -1.5 percentage points (95% CI -12.9 to 9.9), risk ratio 0.79 (0.14–4.47); unadjusted two-proportion z-test p = 0.792.
  • Andecaliximab 150 mg Weekly: 1.9% (1/53) versus 7.1% (2/28) on control; risk difference -5.3 percentage points (95% CI -15.5 to 5.0), risk ratio 0.26 (0.03–2.79); unadjusted two-proportion z-test p = 0.234.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Andecaliximab 150 mg Every 2 Weeks and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Andecaliximab 150 mg Weekly and the control. The interval gives the range of effects that remain compatible with the data.

The two posted secondary endpoints broaden the outcome picture beyond the patient-reported symptom threshold used for the primary endpoint. CDAI remission describes a clinical remission threshold, while mucosal healing uses an endoscopic ulcer-size subscore criterion. These outcomes assess different aspects of Crohn’s disease and should not be expected to match the primary endpoint exactly. Their overall pattern does not provide a consistent indication of a clear advantage across all andecaliximab regimens.

The secondary results should be read alongside, not as replacements for, the primary result. The primary outcome itself had no clear unadjusted separation from placebo, and the secondary endpoints do not remove the uncertainty surrounding that finding. Differences in endpoint definition, event frequency, and precision mean the secondary outcomes may tell a different descriptive story without establishing a different overall conclusion.

The registry record lists two secondary outcomes and reports no sponsor analyses for them. The unadjusted comparison results therefore have limited inferential weight. When multiple outcomes and treatment contrasts are examined, unadjusted testing can increase the chance of an apparently notable finding even when there is no underlying difference. A prespecified hierarchy, adjustment method, or other multiplicity strategy could clarify how such results should be interpreted, but none is reported in the registry record.

In general, secondary outcomes can be useful for exploring consistency and for understanding whether effects appear across different domains. Their value depends on their prespecification, measurement quality, completeness, and analysis plan. Since the registry record does not describe those details or a multiplicity strategy, these outcomes are best viewed as descriptive evidence that complements the primary endpoint rather than as confirmatory proof of a treatment difference.

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

• Percentage of Participants Achieving CDAI Remission (CDAI ≤ 150) at Week 8 of the Double-Blind Phase
• Percentage of Participants Achieving Mucosal Healing (SES-CD Size-of-Ulcer Subscore = 0) at Week 8 of the Double-Blind Phase

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary endpoint is binary: each participant is classified as having achieved clinical response or not achieved it. The group result is therefore a percentage of participants meeting the PRO2 threshold. A confidence interval around that percentage expresses statistical uncertainty about the underlying response proportion, given the observed data and the method used to calculate the interval. It does not account for every possible source of uncertainty, such as limitations in trial conduct or outcome measurement.

What is the comparison measuring?

Each reported comparison places one andecaliximab group against placebo for the Week 8 response outcome. The risk difference is a contrast between the two response proportions, expressed on the probability scale. A value of zero would mean equal proportions in the two groups. The posted comparison intervals span zero for all three primary contrasts, so the data do not distinguish clearly between a positive and negative difference. The reported unadjusted p-values likewise do not indicate a clear difference.

Risk differences are often useful because they retain an absolute scale: they describe how much the response proportion differs between groups, rather than expressing it as a relative multiplier. Relative measures such as a risk ratio or odds ratio answer different questions and can appear numerically large or small depending on the baseline event frequency. The registry record includes those measures as calculated comparisons, but the interpretation emphasizes the observed proportions and their uncertainty.

What does unadjusted mean?

An unadjusted comparison is not corrected for testing multiple outcomes or multiple treatment contrasts. In general, when many statistical comparisons are examined, the chance of at least one apparently notable result can increase. Adjustment methods and prespecified testing hierarchies can address this issue, but the registry record does not report a multiplicity strategy. The posted primary comparison p-values are therefore described as unadjusted, and they should not be treated as if a broader testing plan had been documented.

The registry record reports no sponsor analyses for the posted primary or secondary outcomes. The comparison statistics available alongside the arm-level results are unadjusted comparisons based on the posted summary data. They may be informative for reading the observed pattern, but they are not a substitute for a prespecified analysis with full participant-level data and documented handling of covariates, missingness, and multiplicity.

How does the endpoint definition affect the analysis?

The endpoint classifies participants using a PRO2 threshold at a defined Week 8 window. Participants missing a PRO2 value at the analysis visit were counted as nonresponders. In general, this approach preserves a binary outcome for every participant in the analysis population, but it makes the result depend on the missing-data rule. If missingness is related to symptoms, treatment, or other factors, treating all missing observations as nonresponse may affect the estimated response proportion. The registry record does not report further sensitivity analyses for missing primary endpoint data.

The Full Analysis Set included randomized participants who received at least 1 dose of study drug. This population is not necessarily identical to every participant enrolled or randomized, because the stated definition excludes randomized participants who did not receive any dose. The primary endpoint group sizes are given for the four treatment groups, but the registry record does not provide a participant flow explanation for the difference between enrollment and these group counts.

Why do wide intervals matter?

In general, an interval estimate is more informative than a point estimate alone because it conveys how much uncertainty surrounds the observed result. With relatively small analysis groups, and especially with a smaller comparator group, a percentage based on only a few outcome events can vary substantially from one sample to another. The primary comparison intervals are wide and include no difference. This limits precision: the observed percentages are not estimates that should be treated as exact underlying response rates.

Failure to show a clear difference is not a formal test of equivalence or noninferiority. Such conclusions require specific margins and a design and analysis intended to assess them. Those margins and plans are not reported in the registry record. A non-significant unadjusted p-value alone cannot establish that two regimens have the same effect.

What can be said about the planning calculations?

Separate planning illustrations use the observed effect as a starting point and consider fractions of that effect. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The original trial design assumptions, including its own sample-size justification, are not reported in the registry record. These planning figures are not observed power and should not be confused with the trial’s actual enrollment or its achieved precision.

More generally, planning calculations depend on the effect one wishes to detect, the variability or event frequency, the chosen error rates, and the design. Smaller effects require more participants to distinguish them from no difference with the same planned power, all else being equal. The illustrations are based on observed effects in relatively small groups, so they are sensitive to the observed estimates and are not evidence that a future study of those sizes would necessarily reproduce the effects.

11. Confidence Intervals and Precision

The primary response proportions have 95% confidence intervals of 8.1% to 29.8% for andecaliximab 150 mg every 2 weeks, 5.5% to 25.3% for andecaliximab 150 mg weekly, 4.3% to 23.0% for andecaliximab 300 mg weekly, and 4.0% to 32.7% for placebo. These intervals show substantial uncertainty around each estimated proportion. The placebo interval is particularly broad, consistent with its smaller group size of 28 participants compared with 53 in each andecaliximab group.

For the comparison of andecaliximab 150 mg every 2 weeks with placebo, the reported 95% interval for the risk difference is -0.137 to 0.191. For andecaliximab 150 mg weekly, it is -0.169 to 0.148; for andecaliximab 300 mg weekly, it is -0.185 to 0.126. Each interval spans zero, the point representing no difference in response proportions. The range of compatible values includes differences in both directions, so the point estimates should not be interpreted as precise estimates of the size or direction of a true effect.

In general, a 95% confidence interval describes the uncertainty of an estimate under the statistical method used; it is not a guarantee that the true value lies in a particular interval. The intervals do not include uncertainty about unreported design details, possible biases, or whether the analysis method matches the trial’s original plan. Nor does overlap of separate group intervals alone constitute a formal test of the difference. The comparison intervals are the relevant direct uncertainty estimates for contrasts with placebo.

The secondary endpoint intervals are also broad. In particular, mucosal-healing outcomes were uncommon in all groups, and the reported intervals extend across a wide range of plausible proportions. Taken together, the precision of the posted outcomes is limited; the registry results do not narrowly determine what the underlying response or secondary outcome differences might be.

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 report participants per arm for 80% power and participants per arm for 90% power. They are not total sample sizes and are not total event counts. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each illustration, the effect to detect is set to 100%, 75%, or 50% of the observed effect. The registry record does not report the original trial’s sample-size justification or design assumptions.

In general, the 80% power column represents a planned chance of detecting the specified effect under the calculation’s assumptions if that effect is real. The 90% power column uses a higher target chance of detection, which generally requires a larger planned group size. These are design concepts, not probabilities that the observed trial result is correct. The displayed figures are not observed power.

For example, the primary comparison using 100% of the observed effect gives 2,849 participants per arm for 80% power and 3,813 participants per arm for 90% power for andecaliximab 150 mg every 2 weeks versus placebo. The corresponding figures for andecaliximab 150 mg weekly are 16,011 and 21,434; for andecaliximab 300 mg weekly they are 1,993 and 2,667. The much larger planning figures for the weekly 150 mg comparison reflect that its observed difference from placebo was close to zero, making that observed effect difficult to distinguish under the stated calculation framework.

Across the illustrations, smaller effects require more participants than larger effects, all else being equal. This is why the 75% and 50% effect scenarios generally produce larger figures than the full observed-effect scenario. These calculations are planning examples based on unstable observed estimates from small groups; they should not be treated as recommended sample sizes or as a reconstruction of the trial’s original plan.

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 = 0.143; treatment proportion p₁ = 0.170; average p̄ = 0.156.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5136 = 1.0066.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5132 = 0.4320.
4. n = (1.0066 + 0.4320)² / (0.0270)² = 2,848.6, rounded up to 2,849 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 <- 0.142857142857143                          # control proportion
p1 <- 0.169811320754717                          # 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(2405442)
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 = 2,849 (80% power), 3,813 (90% power)
 75% of observed effect: n per arm = 4,976 (80% power), 6,661 (90% power)
 50% of observed effect: n per arm = 10,994 (80% power), 14,717 (90% power)
power.prop.test: 2848.6 
Simulated power at n = 2,849 per arm: 0.803 (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 record lists four outcome measures and two secondary outcomes, but it reports no sponsor analyses for the outcomes. It does not report a multiplicity adjustment, a testing hierarchy, or a strategy defining which comparisons were intended to support confirmatory conclusions. The unadjusted comparison p-values should therefore be read as individual comparisons without an indicated correction for examining multiple outcomes or regimens.

In general, testing multiple hypotheses increases the chance of at least one result appearing noteworthy by chance. A prespecified approach can control or describe that risk, but its details are necessary to interpret p-values across a collection of endpoints. Since no such approach is reported in the registry record, the secondary findings warrant particular caution, and the primary p-values should not be assumed to represent a complete family-wise analysis.

The primary endpoint description specifies that participants with a missing PRO2 value at the Week 8 analysis visit were imputed as not achieving clinical response. This is a nonresponder-imputation rule for that endpoint. The record does not report additional sensitivity analyses to show how alternative assumptions about missing outcomes might change the result. Missing-data handling for the secondary endpoints is not reported in the registry record.

The Full Analysis Set included all randomized participants who received at least 1 dose of study drug. The record does not provide enough participant-flow information to explain all exclusions from the enrolled population or to reconcile enrollment with each endpoint’s analysis group. It also does not report details of an intention-to-treat analysis, per-protocol analysis, covariate adjustment, interim analyses, or the original statistical analysis plan. These omissions make it difficult to determine whether the posted comparisons match the trial’s prespecified analysis and how robust the estimates are to alternative analysis choices.

These details matter because the strength of an inference depends not only on the observed percentages but also on which participants were analyzed, how missing outcomes were handled, and how the set of statistical tests was managed. The registry record permits a descriptive reading of the posted results, but does not establish a full confirmatory analysis framework.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: crohn's disease (11.5%), small intestinal obstruction (4.3%), anaemia (3.8%), appendicitis (3.8%), bacterial pyelonephritis (3.8%).

During the double-blind phase, serious adverse events were reported for 1 of 53 participants assigned to andecaliximab 150 mg every 2 weeks, 6 of 53 assigned to andecaliximab 150 mg weekly, 8 of 53 assigned to andecaliximab 300 mg weekly, and 3 of 28 assigned to placebo. The registry record reports 0 deaths in each of these listed double-blind groups. These counts describe participants with serious adverse events; they do not indicate how many total events occurred in a participant or how long each person was followed.

The record also lists serious adverse events during the open-label phase, organized by participants’ earlier assignment. The counts were 9 of 52, 10 of 48, 7 of 47, and 6 of 26 across the four listed groups, with 0 deaths in each. Since these groups were receiving open-label treatment, they are not a continuation of a blinded placebo comparison in the same sense as the double-blind results.

The leading serious adverse event terms include Crohn’s disease at 11.5%, small intestinal obstruction at 4.3%, and anaemia, appendicitis, bacterial pyelonephritis, and nephrolithiasis at 3.8% each. Serious-event counts alone do not establish whether an event was caused by a study drug or whether the groups differ reliably in safety. The registry record does not report further adjudication or a causal assessment in these data.

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

The posted Week 8 results show that the proportion meeting the PRO2 clinical-response threshold was 17.0% with andecaliximab 150 mg every 2 weeks, 13.2% with andecaliximab 150 mg weekly, 11.3% with andecaliximab 300 mg weekly, and 14.3% with placebo. The unadjusted comparisons and their broad intervals do not establish a clear difference between any andecaliximab regimen and placebo for this endpoint. The estimates are imprecise, so the results also do not establish that the groups have equal response proportions.

The secondary endpoints describe CDAI remission and mucosal healing, which are distinct from symptom response. Their posted results are also uncertain and their unadjusted comparisons have no reported multiplicity strategy. They add descriptive information but cannot, on their own, confirm an effect that is not clearly separated in the primary comparison.

In general, a randomized, double-blind, placebo-controlled design can support a fair comparison when allocation, follow-up, measurement, and analysis are conducted as planned. The registry record identifies this design but does not report all details needed to assess those elements fully. It also does not report the original sample-size justification, the full statistical analysis plan, or the reason for termination. The results therefore need to be interpreted in the context of both the design strengths and the missing information.

These data do not show that andecaliximab works or does not work as a clinical treatment. They report observed outcomes in this particular study and leave substantial statistical uncertainty about the underlying differences. The record’s terminated status is a study-status fact, not an explanation for the outcome pattern; the reason is not reported in the registry record. No medical decision should be based on these registry statistics alone.

17. Why This Trial Matters Statistically

This trial illustrates why a numerical difference between group percentages is not enough to determine whether a treatment effect is established. The primary response percentages range from 11.3% to 17.0% in the andecaliximab groups, compared with 14.3% for placebo, but the groups are small and their confidence intervals are broad. The direct comparisons also include no difference. Looking at uncertainty changes the interpretation from a simple ranking of point estimates to a more cautious account of what the data can distinguish.

The trial also shows the importance of separating endpoints. A patient-reported symptom threshold, a CDAI remission threshold, and an endoscopic mucosal-healing criterion measure different outcomes. They may provide complementary evidence, but they are not interchangeable, and multiple unadjusted comparisons should not be read as independent confirmations.

The registry record contains a useful endpoint definition and a stated missing-data rule for the primary outcome. At the same time, it does not report the original sample-size justification, multiplicity plan, sponsor analyses, or the reason for termination. Such omissions make it harder to connect the posted findings to the trial’s intended inferential framework. The planning illustrations also demonstrate how sample-size requirements can change sharply when the target effect is smaller or when the observed estimate is near no difference.

For biostatistical interpretation, the central lesson is to distinguish observed proportions, uncertainty intervals, unadjusted hypothesis tests, and design-planning calculations. Each answers a different question. This distinction is especially important when the outcome groups are modest in size and the registry record leaves key analysis details unreported.

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

The primary outcome is based on a threshold applied to PRO2, a patient-reported measure. Threshold classification provides a clear response definition but does not retain all information about how scores differ within responder and nonresponder groups. The outcome also relies on participant diary data, and the registry record does not report further information on diary completion or measurement reliability.

The primary endpoint analysis counts participants with missing Week 8 PRO2 values as nonresponders. That rule is explicit, but the record does not report sensitivity analyses using other missing-data assumptions. Missing-data methods for the secondary outcomes are not reported in the registry record. If missingness differed across groups or was related to clinical status, this could affect the observed proportions.

The placebo group was smaller than each andecaliximab group for the primary endpoint, and all groups had limited numbers of participants. The confidence intervals are consequently broad, limiting precision. The record does not provide participant-flow details sufficient to explain the relationship between total enrollment and each endpoint analysis group.

The registry lists the trial as terminated, but the reason is not reported in the registry record. It also does not report the original sample-size justification, the complete statistical analysis plan, an adjustment for multiple testing, sponsor analyses, or interim analyses. These gaps limit assessment of whether the posted analyses follow prespecified methods and how the trial’s termination relates, if at all, to the reported outcomes. No causal explanation for termination can be inferred from the status alone.

Finally, the open-label extension and extended treatment phase do not provide the same blinded placebo comparison as the primary Week 8 analysis. Later safety counts should therefore be distinguished from the randomized double-blind results, and should not be interpreted as equivalent head-to-head evidence.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy of Andecaliximab in Participants With Moderately to Severely Active Crohn's Disease — NCT02405442.
• Registry record last updated 2019-04-23; status last verified 2019-04.
• Results first posted 2019-03-28.
• 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

NCT02405442 was a Phase 2 randomized, double-blind, placebo-controlled, parallel-group study of andecaliximab in participants with moderately to severely active Crohn’s disease. The registry reports enrollment of 187, a start date of 2015-04-30, primary completion on 2016-11-30, and status as terminated. The reason for termination is not reported in the registry record.

The primary Week 8 endpoint was clinical response, defined as PRO2 ≤ 8, with missing Week 8 PRO2 values counted as nonresponse. Recorded response proportions were 17.0%, 13.2%, and 11.3% across the three andecaliximab regimens and 14.3% with placebo. The unadjusted comparisons do not establish a clear difference, and the confidence intervals indicate substantial uncertainty. Secondary outcomes covered CDAI remission and mucosal healing. The registry record does not report the original sample-size justification, multiplicity strategy, complete analysis plan, sponsor analyses, or reason for termination.