ECOSPOR III - SER-109 Versus Placebo in the Treatment of Adults With Recurrent Clostridium Difficile Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for ECOSPOR III - SER-109 Versus Placebo in the Treatment of Adults With Recurrent Clostridium Difficile Infection (NCT03183128), a randomized phase 3 study. The primary outcome is Recurrence of CDI up to 8 Weeks.

2. Clinical Question

The registry describes the study as a Phase 3 evaluation of safety, tolerability, and efficacy. For statistical interpretation, the central comparison is the number of participants with a recurrence in each assigned group. The posted outcome reports 11 participants with recurrence in the SER-109 group and 37 in the placebo group. The registry’s specified analysis population preserves randomized assignment, including for participants who received no study drug. This matters because the primary comparison is based on assigned groups rather than on a comparison restricted to people who completed treatment.

3. Trial Design

ECOSPOR III was a Phase 3, randomized, double-blind, placebo-controlled, parallel-group study of SER-109 in adults with recurrent Clostridium difficile infection. The registry records an enrollment of 182. Participants were assigned to SER-109 or matching placebo. The study start date was 2017-07-10, the primary completion date was 2020-07-03, and the record lists the study status as completed. Seres Therapeutics, Inc. is named as the sponsor.

The intervention description specifies an oral dose of SER-109 in 4 capsules once daily for 3 consecutive days. The placebo group received matching placebo once daily for 3 consecutive days. Double masking and randomization are recorded, while the registry description does not identify which specific roles were masked or provide further details about the randomization process. Those details are not reported in the registry record.

The primary outcome was recurrence of CDI through Week 8 after initiation of treatment, with recurrence determined by a stool Clostridioides difficile toxin assay. The primary analysis population comprised all randomly assigned participants, including those not exposed to study drug, analyzed according to assigned treatment. This stated population is important when reading the group counts: the analysis follows assignment rather than exposure.

The registry also identifies recurrence through 4, 12, and 24 weeks as a secondary outcome. Numerical results for those additional time points are not reported in the registry record. The original sample-size justification, allocation ratio rationale, detailed randomization procedures, and prespecified analysis plan are not reported in the registry record. The planning illustrations associated with the observed result should therefore not be read as a reconstruction of the trial’s original design.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All participants who were randomly assigned, including those who were not exposed to any study drug, were analyzed based on the treatment to which they were randomly assigned.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Recurrence of CDI up to 8 Weeks, measured over Up to Week 8.

The primary endpoint is the number of participants with CDI recurrence through 8 weeks after treatment initiation. A recurrence was determined using a stool Clostridioides difficile toxin assay. The endpoint is binary at the participant level: each participant is classified according to whether a qualifying recurrence occurred during the stated timeframe. The posted group results are counts of participants, not event rates calculated over person-time.

This endpoint is used to represent recurrence after an initial treatment episode in the population under study. A defined assay and follow-up window make the comparison operational: the groups are compared using the same stated criterion and timeframe. The measure answers a focused question about recurrence identified by the assay; it does not capture every aspect of illness, symptom burden, safety, or longer-term outcome.

The registry specifies that all randomized participants were included in the primary analysis, even if they were not exposed to study drug, and were analyzed according to their assigned group. This approach retains the randomized assignment in the comparison. It also means that the reported endpoint counts should be interpreted under the registry’s assigned-group analysis definition, rather than as counts only among participants who completed the dosing schedule.

The endpoint’s timeframe is a key part of its meaning. Recurrence through Week 8 is not interchangeable with recurrence at another follow-up point. Although the registry names secondary recurrence assessments through 4, 12, and 24 weeks, their numerical results are not reported in the registry record. The primary result therefore supports interpretation only for the stated assay-based endpoint and Week 8 timeframe.

7. Results Posted in the Registry

• SER-109: 12.4% (11/89) versus 39.8% (37/93) on control; risk difference -27.4 percentage points (95% CI -39.5 to -15.4), risk ratio 0.31 (0.17–0.57); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant either had a recurrence meeting the assay-based definition through Week 8 or did not. The posted counts are therefore interpreted as participants with an event out of the participants in each assigned group. Such outcomes can be compared using measures including a risk difference, a risk ratio, or an odds ratio. These measures express the contrast in different ways and should not be treated as interchangeable.

What does the risk ratio express?

A risk ratio compares the event risk in one group with the event risk in another group. A ratio of 1 corresponds to equal risks; a ratio below 1 means a lower observed risk in the numerator group, and a ratio above 1 means a higher observed risk. The sponsor reported a risk ratio of 0.32 for SER-109 relative to placebo. Its 95% confidence interval is 0.18 to 0.58. In this context, the estimate is a relative comparison for the specified Week 8 recurrence outcome, not an absolute count or a measure of time until recurrence.

A risk difference instead expresses the contrast as a difference between the groups’ event risks. A negative risk difference for SER-109 relative to placebo indicates fewer observed recurrences in the SER-109 group. The recalculation uses the posted group summaries and is unadjusted. The registry record also reports an unadjusted p-value of <0.001 for the comparison. The risk difference and risk ratio answer related but distinct questions: one is an absolute contrast, and the other is a relative contrast.

What does the Cochran-Mantel-Haenszel method do?

The sponsor’s posted analysis is identified as Cochran-Mantel-Haenszel and reports a risk ratio. In general, this method combines information across strata to estimate an overall association while accounting for the strata used in the analysis. The registry record does not report the strata or the detailed computation, so it is not possible to describe which factors were controlled or to reproduce the sponsor’s calculation from the record alone. The reported result should therefore be read as the sponsor’s stated analysis, not as a fully documented adjusted model.

The recalculated comparison is different in scope: it is an unadjusted calculation from the posted summary counts. It does not incorporate unreported covariates or strata. Because the registry record does not indicate a discrepancy between the sponsor result and the recalculation, they are directionally consistent; the sponsor’s reported analysis is still the analysis to cite when describing the registry’s formal result.

How should the p-value be read?

In general, a p-value measures how unusual results at least as extreme as the observed result would be under a specified null hypothesis and the assumptions of the test. The reported p-value of <0.001 indicates that the observed comparison is not readily compatible with equal group outcomes under that framework. It is not the probability that the null hypothesis is true, and it does not measure the probability of a particular result in a future study. Nor does it establish that the analysis assumptions, endpoint definition, or handling of missing data are correct.

Statistical significance also does not directly communicate clinical importance. For that, the estimate’s scale, uncertainty, endpoint meaning, and clinical context matter. The risk ratio is relative; the group counts and an absolute risk contrast can help contextualize the observed difference. The registry record’s primary outcome is limited to assay-defined recurrence through Week 8.

What is a confidence interval?

In general, a confidence interval gives a range of estimates compatible with the observed data under the method used. It communicates uncertainty in the estimated effect and is more informative about precision than a p-value alone. The sponsor’s 95% interval for the risk ratio runs from 0.18 to 0.58. Because the interval does not include 1, it is consistent with a lower relative risk in the SER-109 group under the sponsor’s analysis. The interval does not cover every uncertainty, including limitations from study conduct, unreported analysis choices, or missing outcome information.

For a binary outcome, the assumptions and definitions behind the analysis matter. The registry specifies the assigned-group population and assay-based recurrence criterion, but it does not report detailed missing-data procedures, the sponsor’s strata, or a complete statistical analysis plan. These gaps limit independent verification of all analytic choices. The posted result is best understood as the estimate for the defined endpoint and analysis, with those documentation limits in mind.

10. Confidence Intervals and Precision

The sponsor’s risk ratio estimate is 0.32, with a 95% confidence interval from 0.18 to 0.58. The interval lies below 1, the value corresponding to equal relative risks, and thus supports a lower recurrence risk in the SER-109 group under the sponsor’s analysis. The estimate gives the central summary of the comparison; the interval shows that the exact relative effect is uncertain even though the direction is consistent across the interval.

In general, a confidence interval represents the range of values reasonably compatible with the data and the method used. A narrower interval indicates greater statistical precision than a wider interval, but precision is not the same as freedom from bias. The interval does not account for every source of uncertainty, such as outcome misclassification, unreported analytic decisions, or missing-data handling. Those matters depend on study conduct and reporting, not only on the formula used to calculate an interval.

The posted counts provide the basis for an unadjusted recalculation, while the sponsor reports a Cochran-Mantel-Haenszel risk ratio. The registry does not document the sponsor’s strata or all analysis details. Consequently, the interval should be attributed to the sponsor’s reported analysis rather than treated as a fully reproducible adjusted estimate based solely on the registry description.

The interval is specific to the Week 8 assay-defined recurrence endpoint. It does not establish the precision of estimates at the secondary follow-up times, for which numerical results are not reported in the registry record. Nor does it predict the range of effects that would necessarily appear in a future study. It quantifies uncertainty in the estimate from this analysis, subject to its assumptions.

11. 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 figures are participants per arm for 80% power and participants per arm for 90% power. They are planning illustrations based on the observed effect, not the original trial’s sample-size calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect.

For planning around 100% of the observed effect, the illustration gives 40 participants per arm for 80% power and 52 participants per arm for 90% power. For 75% of the observed effect, it gives 76 participants per arm for 80% power and 102 participants per arm for 90% power. For 50% of the observed effect, it gives 184 participants per arm for 80% power and 245 participants per arm for 90% power.

In plain language, the 80% power column describes the planned number per arm under which the assumed effect would be detected at the specified significance level in 80% of repetitions of the statistical process, if the planning assumptions held. The 90% column describes the corresponding planning target for 90% power. These are design concepts, not guarantees about a particular study result. The illustrations concern participants per arm, not total events.

Smaller effects require more participants to detect under the same planning assumptions. That pattern is reflected in the increasing per-arm requirements as the assumed effect fraction becomes smaller. The original trial’s design assumptions and sample-size justification are not reported in the registry record. These figures are not observed power: they are hypothetical planning calculations based on the observed effect, not a measure of what the completed trial achieved.

12. 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 = 0.398; treatment proportion p₁ = 0.124; average p̄ = 0.261.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6209 = 1.2169.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5898 = 0.4964.
4. n = (1.2169 + 0.4964)² / (-0.2743)² = 39.0, rounded up to 40 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 <- 0.397849462365591                          # control proportion
p1 <- 0.123595505617978                          # 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(3183128)
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 = 40 (80% power), 52 (90% power)
 75% of observed effect: n per arm = 76 (80% power), 102 (90% power)
 50% of observed effect: n per arm = 184 (80% power), 245 (90% power)
power.prop.test: 39 
Simulated power at n = 40 per arm: 0.824 (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.

13. Analyses Reported by the Sponsor

The sponsor’s reported analysis is a Cochran-Mantel-Haenszel comparison expressed as a risk ratio. It gives a risk ratio of 0.32, a 95% confidence interval from 0.18 to 0.58, and p < 0.001. This is the sponsor’s stated inferential result for the comparison. The registry record does not describe the strata or all details needed to reproduce the analysis independently.

The recalculation uses the posted group counts and is unadjusted. It is a simple comparison from the summary data, not a replacement for the sponsor’s analysis and not an attempt to reproduce its Cochran-Mantel-Haenszel method. The two approaches are directionally consistent: each indicates fewer observed recurrences in the SER-109 group. The registry’s discrepancy indicator is false, so the record does not flag a disagreement requiring a different reading of the sponsor’s result.

When describing the formal reported analysis, the sponsor’s estimate and confidence interval should be used. The unadjusted recalculation is useful as a transparent check based on the group summaries, but it may differ in method from the sponsor’s analysis. The record does not report enough detail to determine precisely how the sponsor’s strata or other implementation choices affect the estimate. Neither result should be interpreted beyond the defined population, assay-based endpoint, and Week 8 follow-up.

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies the Week 8 recurrence outcome as primary and lists recurrence through 4, 12, and 24 weeks as a secondary outcome. Considering multiple outcomes or follow-up times raises a multiplicity question: when several hypotheses are tested, the chance of at least one small p-value can increase if no adjustment or testing strategy is used. In general, a prespecified hierarchy or multiplicity adjustment can help control that issue. The registry record does not report whether such a strategy was specified or used.

The posted sponsor analysis reports a result for the primary outcome. Numerical results for the secondary recurrence time points are not reported in the registry record. The record also does not report a complete statistical analysis plan, details of interim analyses, or a multiplicity adjustment. Therefore, it is not possible to determine from the registry record how secondary comparisons were handled or whether the primary result was interpreted within a larger testing framework.

The primary analysis population is explicitly described: all randomly assigned participants were included, including those not exposed to study drug, and analyzed according to assigned treatment. This supports an assigned-group interpretation of the primary comparison. The record does not report whether outcome data were missing, how missing outcomes were handled, or whether any sensitivity analyses assessed their effect. Those details matter because the observed group counts alone cannot show whether missingness could have changed the comparison.

The registry does not state whether analyses were additionally adjusted for baseline characteristics or identify any strata used in the sponsor’s Cochran-Mantel-Haenszel analysis. It also does not provide subgroup results or detailed methods for the secondary outcomes. These omissions do not negate the posted result, but they constrain assessment of robustness and independent reproducibility. The result is most directly interpreted as the stated sponsor analysis for the primary Week 8 endpoint, with analysis-plan, multiplicity, and missing-data details not reported in the registry record.

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: clostridioides difficile colitis (7.6%), urinary tract infection (3.3%), gastroenteritis (2.2%), cellulitis (2.2%), abdominal wall abscess (1.1%).

The registry’s serious adverse event figures list 15 participants affected in the SER-109 group, with 90 at risk, and 19 affected in the placebo group, with 92 at risk. These are group-level counts from the safety record and should be read separately from the primary recurrence outcome, which uses a different stated analysis population. The registry also lists 3 deaths in the SER-109 group and 0 in the placebo group.

The listed serious adverse event terms include Clostridioides difficile colitis at 7.6%, urinary tract infection at 3.3%, gastroenteritis at 2.2%, cellulitis at 2.2%, abdominal wall abscess at 1.1%, and bacteremia at 1.1%. These entries describe terms and percentages in the registry record; they do not establish that a treatment caused an event. The record does not provide enough detail in these figures to characterize timing, severity within each term, or individual participant histories.

Safety counts are descriptive and should not be treated as a stand-alone causal comparison. They do not replace review of the full safety record, and the small number of events represented by individual terms limits how much can be inferred from their percentages. Serious adverse events and deaths are distinct listings; the figures should not be combined or interpreted as a single outcome. The registry data describe what was recorded in each group, not a recommendation about treatment.

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

The result shows that, in this randomized study, fewer participants assigned to SER-109 had assay-defined CDI recurrence through Week 8 than participants assigned to placebo. The group counts are 11 of 89 for SER-109 and 37 of 93 for placebo. The sponsor’s reported risk ratio is 0.32, with a 95% confidence interval from 0.18 to 0.58 and p < 0.001. Taken together, the reported estimate and interval indicate a lower observed relative recurrence risk in the SER-109 group for this endpoint and follow-up period.

The result does not mean that every participant assigned to SER-109 avoided recurrence, or that the observed group difference will be identical in another study or population. The confidence interval communicates statistical uncertainty in the relative effect, while the endpoint definition limits what is being measured: recurrence identified by a stool toxin assay through Week 8. It does not answer questions about other symptoms, other clinical outcomes, or longer follow-up.

The study was randomized, double blind, and placebo controlled, and the primary analysis followed assigned treatment, including participants not exposed to study drug. Those design features provide context for the comparison, but the registry record does not report all operational details, missing-data methods, or the complete statistical analysis plan. The record also does not provide numerical results for the secondary recurrence time points through 4, 12, and 24 weeks.

Statistical evidence for a group difference is not the same as proof of a specific biological mechanism, and the record does not establish that the result generalizes to people outside the enrolled population. The interpretation should remain tied to the studied adults with recurrent CDI, the assigned-group comparison, the assay-based definition, and the stated follow-up. The results are a description of the trial evidence, not medical advice or a guarantee of an individual outcome.

17. Why This Trial Matters Statistically

This trial illustrates how the meaning of a clinical comparison depends on a clearly defined population, endpoint, follow-up window, and analysis population. Here, recurrence was determined using a stool toxin assay through Week 8, and all randomly assigned participants were analyzed according to assignment, including those not exposed to study drug. These details help readers understand exactly what the primary comparison represents.

The posted results also show why effect measures and uncertainty should be read together. The group counts describe observed events, while the sponsor’s risk ratio expresses a relative comparison. Its confidence interval communicates uncertainty around that estimate, and the p-value addresses compatibility with a null comparison under the analysis assumptions. None of these summaries alone captures every issue relevant to interpretation.

The comparison between an unadjusted recalculation and the sponsor’s Cochran-Mantel-Haenszel result is a useful reminder that analyses can use different methods even when based on the same trial. The registry identifies the sponsor’s method but does not report its strata or all implementation details. Transparent reporting of those details helps readers understand how estimates relate and whether they can be reproduced.

Finally, the trial highlights the distinction between observed results and planning illustrations. Sample-size scenarios based on a fraction of the observed effect can show how planning requirements change for smaller assumed effects. They do not describe the original design unless the original assumptions are documented, and they are not observed power. Keeping those categories separate avoids treating a retrospective illustration as part of the trial’s prospective plan.

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 gives the primary endpoint definition and assigned-group population, but it does not report the complete statistical analysis plan. Details of the randomization procedure, allocation concealment, the roles covered by double masking, and the original sample-size justification are not reported in the registry record. This limits assessment of design and analysis decisions beyond the summary description.

The sponsor’s Cochran-Mantel-Haenszel analysis is reported without the strata or other details needed for full independent reproduction. Missing-data methods and the extent of missing primary outcome information are not reported in the registry record. It is therefore not possible to assess from the posted information whether missing observations or analytic choices could affect the estimate.

The registry lists secondary recurrence follow-up through 4, 12, and 24 weeks, but numerical results for those time points are not reported in the registry record. Multiplicity procedures and interim analyses are also not reported. Consequently, the primary result cannot be placed in a documented hierarchy of all planned tests, and longer-term recurrence estimates cannot be evaluated from these posted results.

The primary endpoint is assay-defined recurrence through Week 8. It does not represent every clinical dimension of CDI or outcomes beyond that window. The registry record does not provide subgroup estimates or enough participant characteristics to assess how the result may vary across patient groups. Safety entries are summarized as counts and selected terms, without the detailed information needed to evaluate individual event timing or causal attribution. These reporting limits call for a focused interpretation of the posted primary comparison rather than broad conclusions beyond its endpoint and population.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: ECOSPOR III - SER-109 Versus Placebo in the Treatment of Adults With Recurrent Clostridium Difficile Infection — NCT03183128.
• Registry record last updated 2023-04-27; status last verified 2021-06.
• Results first posted 2023-04-27.
• 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

ECOSPOR III (NCT03183128) is recorded as a completed Phase 3, randomized, double-blind, parallel-group study sponsored by Seres Therapeutics, Inc. It enrolled 182 adults with recurrent Clostridium difficile infection and compared oral SER-109 with matching placebo. SER-109 was administered as 4 capsules once daily for 3 consecutive days; placebo was given once daily for 3 consecutive days.

The primary outcome was CDI recurrence through Week 8, determined by a stool Clostridioides difficile toxin assay. The primary analysis included all randomly assigned participants, including those not exposed to study drug, analyzed according to assigned treatment. Recurrence was recorded for 11 of 89 participants assigned to SER-109 and 37 of 93 assigned to placebo.

The sponsor reported a Cochran-Mantel-Haenszel risk ratio of 0.32, with a 95% confidence interval from 0.18 to 0.58 and p < 0.001. Secondary recurrence time points are listed, but their numerical results and several analysis details are not reported in the registry record.