A Study of MORAb-202 Versus Investigator's Choice Chemotherapy in Female Participants With Platinum-resistant High-grade Serous (HGS) Ovarian, Primary Peritoneal, or Fallopian Tube Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of MORAb-202 Versus Investigator's Choice Chemotherapy in Female Participants With Platinum-resistant High-grade Serous (HGS) Ovarian, Primary Peritoneal, or Fallopian Tube Cancer (NCT05613088), a randomized phase 2 study. The primary outcome is Objective Response Rate (ORR) by Response Evaluation Criteria in Solid Tumors (RECIST) v1.1 Per Investigator Assessment.

2. Clinical Question

3. Trial Design

This was a phase 2, randomized, open-label, parallel-group study sponsored by Bristol-Myers Squibb. The registry record lists 106 participants enrolled. It gives a study start date of 2023-02-01 and a primary completion date of 2024-06-17, and lists the study status as terminated. The reason for termination is not reported in the registry record.

Participants were assigned to MORAb-202 or investigator’s choice chemotherapy. The primary endpoint results include 70 participants in the MORAb-202 group and 36 in the chemotherapy group. The chemotherapy options named in the registry are paclitaxel, pegylated liposomal doxorubicin, and topotecan. The arm descriptions do not give further details about treatment selection, dose, schedule, or treatment modifications.

Open-label means that treatment assignment was not masked from participants and study personnel, according to the registry’s masking classification. The primary endpoint relies on investigator assessment, so the absence of masking is relevant when considering how response assessments may have been influenced. The registry record does not describe independent central review or other safeguards for assessment.

The primary outcome is objective response rate under RECIST v1.1, with a stated timeframe from randomization until objectively documented progression or subsequent therapy, up to approximately 70 weeks. The registry also lists safety outcomes, including adverse events, serious adverse events, treatment-related events, and deaths. Their listed observation periods differ from the primary endpoint timeframe. The registry record does not report the original statistical design assumptions, the planned allocation ratio, or a sample-size justification. Nor does it explain why the study was terminated. Those details should not be inferred from the observed group sizes or results.

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: Enrollment was stopped and no participants were enrolled into Arm A (MORAb-202 at 33 mg/m\^2)

Pre-Treatment

Treatment

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants

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 Objective Response Rate (ORR) by Response Evaluation Criteria in Solid Tumors (RECIST) v1.1 Per Investigator Assessment, measured over From the date of randomization to the date of first objectively-documented progression or the date of subsequent therapy (Up to approximately 70 weeks).

The primary endpoint is objective response rate, or ORR, by investigator assessment using RECIST v1.1. It is the proportion of all randomized participants whose best overall response was a confirmed complete response or confirmed partial response. A complete response requires disappearance of target lesions, with pathological lymph nodes reduced to a short axis <10 mm. A partial response requires at least a 30% decrease in the sum of target-lesion diameters from baseline.

ORR is used as a measure of tumor response: it records whether a participant met a defined response threshold during the assessment period. It differs from a time-to-event endpoint, which concerns how long participants remain without an event, and it does not directly measure response duration. The timeframe in the registry extends from randomization to documented progression or subsequent therapy, up to approximately 70 weeks.

The posted ORR is 20.0% among 70 participants assigned to MORAb-202 and 13.9% among 36 assigned to investigator’s choice chemotherapy. The confidence intervals are 11.4% to 31.3% and 4.7% to 29.5%, respectively. These intervals describe uncertainty around each group’s response rate. Because response is assessed by investigators in an open-label study, the assessment context also matters when interpreting the endpoint. The registry record does not report a separate independent review result.

7. Results Posted in the Registry

• Investigator's Choice (IC) Chemotherapy: 13.9% (5/36) versus 20.0% (14/70) on control; risk difference -6.1 percentage points (95% CI -20.8 to 8.6), risk ratio 0.69 (0.27–1.78); unadjusted two-proportion z-test p = 0.437.

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.

Number of Participants With Treatment-Related AEs

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Investigator's Choice (IC) Chemotherapy: 85.3% (29/34) versus 75.7% (53/70) on control; risk difference 9.6 percentage points (95% CI -6.0 to 25.2), risk ratio 1.13 (0.93–1.37); unadjusted two-proportion z-test p = 0.262.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Investigator's Choice (IC) Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Treatment-Related SAEs

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Investigator's Choice (IC) Chemotherapy: 5.9% (2/34) versus 1.4% (1/70) on control; risk difference 4.5 percentage points (95% CI -3.9 to 12.8), risk ratio 4.12 (0.39–43.84); unadjusted two-proportion z-test p = 0.203.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Investigator's Choice (IC) Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Who Died

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Investigator's Choice (IC) Chemotherapy: 58.8% (20/34) versus 51.4% (36/70) on control; risk difference 7.4 percentage points (95% CI -12.9 to 27.7), risk ratio 1.14 (0.80–1.64); unadjusted two-proportion z-test p = 0.478.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Investigator's Choice (IC) Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a range of secondary outcomes, including adverse events, serious adverse events, events leading to discontinuation, treatment-related events, deaths, and grade 3-4 laboratory abnormalities. The posted secondary results include event counts for treatment-related adverse events, treatment-related serious adverse events, and deaths. These outcomes concern safety and follow-up as well as treatment exposure, so they address different questions from the primary response endpoint.

The overall pattern should be read as descriptive rather than as a second confirmatory test of the primary finding. The primary endpoint concerns confirmed tumor response; adverse-event outcomes concern harms and tolerability, and death counts are not a substitute for a time-to-event survival analysis. The registry does not provide a single integrated analysis that weighs response, safety, response duration, and survival together. Nor does the available record establish that secondary outcomes were ranked in a prespecified hierarchy.

The posted secondary comparisons are unadjusted, and their confidence intervals often span no difference. For example, the unadjusted p-values listed for the secondary comparisons are 0.262, 0.203, and 0.478. These results do not establish a clear between-group difference for those outcomes. They should not be interpreted as proof of equal safety, especially because the group sizes and available safety denominators differ and follow-up may not be identical. The registry record does not report exposure-adjusted rates or a full account of follow-up by group.

General statistical explanation: when many endpoints are examined, the chance of at least one apparently unusual result can increase even if there is no underlying difference. Multiplicity procedures can address this issue, but the registry record does not report a correction strategy for the secondary analyses. Unadjusted secondary results therefore carry less weight than a prespecified primary analysis, and isolated secondary findings should be considered exploratory unless the analysis plan says otherwise. The primary response result remains the principal comparative result in the posted record, while the secondary outcomes provide context rather than a decisive reinterpretation of it.

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

• Number of Participants With Adverse Events (AEs)
• Number of Participants With Serious Adverse Events (SAEs)
• Number of Participants With AEs Leading to Discontinuation
• Number of Participants With Treatment-Related AEs
• Number of Participants With Treatment-Related SAEs
• Number of Participants With AEs of Special Interest (AESIs)
• Number of Participants Who Died
• Number of Participants With Grade 3-4 Laboratory Abnormalities

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is a binary participant-level result: each randomized participant either met the confirmed response definition or did not. General statistical explanation: a response proportion estimates the fraction of a group with the event of interest. Its uncertainty depends partly on the number of participants and the number of observed responses. Here, the posted group sizes are 70 and 36, and the response percentages are accompanied by 95% confidence intervals.

What does a confidence interval describe?

General statistical explanation: a confidence interval gives a range of values compatible with the data under the method used to calculate it. It is not a guarantee that the true value lies in that particular interval, and it does not mean that every value within the range is equally likely. For MORAb-202, the interval for ORR is 11.4% to 31.3%; for investigator’s choice chemotherapy, it is 4.7% to 29.5%. The intervals show that each response-rate estimate remains uncertain.

How should the comparison be read?

The registry posts an unadjusted comparison and a p-value of 0.437. General statistical explanation: a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions are appropriate. It is not the probability that the null hypothesis is true, nor the probability that the result occurred by chance. A p-value above a conventional threshold does not prove no effect. It indicates that this analysis did not provide strong evidence against its null model. The registry record does not report a prespecified threshold or a detailed analysis plan, so the result should be interpreted as an unadjusted comparison rather than as a fully documented confirmatory analysis.

For the primary endpoint, the comparison is based on the posted ORR values for the two randomized groups. The registry’s comparison information gives the direction as investigator’s choice chemotherapy relative to MORAb-202. The corresponding interval includes values on either side of no difference. General statistical explanation: when a confidence interval for a difference includes zero, the data do not rule out no difference at the confidence level used. That does not show that the groups are the same; it reflects the range of uncertainty around the estimate.

What does randomization contribute?

General statistical explanation: random assignment is intended to make treatment groups comparable on average with respect to factors measured and unmeasured before assignment. It does not guarantee identical groups in a particular trial, and it cannot remove uncertainty from a small or imbalanced set of observed results. The registry identifies the study as randomized, with 70 participants in the MORAb-202 primary analysis group and 36 in the chemotherapy group. The reasons for this observed group-size pattern and details of the allocation procedure are not reported in the registry record.

The study is listed as open-label, and the endpoint is based on investigator assessment. General statistical explanation: knowledge of treatment assignment can matter for an outcome involving judgment, even when the response criteria are defined in advance. A protocol may use measures such as independent review to address this concern, but such a process is not reported in the registry record and should not be assumed.

Why does the analysis population matter?

The primary outcome description specifies all randomized participants as the population. This is useful because retaining randomized participants in the comparison generally preserves the advantages of random assignment. However, the registry does not provide a participant-level accounting of assessment availability, exclusions, or missing response data. It is therefore not possible to determine from this record how missing observations were handled or whether every randomized participant contributed an observed response classification.

The registry also lists secondary outcomes and associated event counts. General statistical explanation: secondary endpoints may give additional information about safety or other aspects of a trial, but they are usually less persuasive as stand-alone evidence when many outcomes are examined and no multiplicity strategy is reported. A chance finding becomes more likely across a broad set of tests. The registry record does not report a multiplicity adjustment or a hierarchy that would define which secondary comparisons should be treated as confirmatory.

Why does the open-label design matter for safety?

General statistical explanation: adverse events are often collected from clinical reports and participant accounts, so awareness of treatment assignment may affect reporting, attribution, or decisions to stop treatment. Treatment-related adverse events also involve judgments about whether an event is related to therapy. Differences in observation time and the number of participants with safety follow-up can affect counts. The registry provides adverse-event denominators for safety outcomes, but does not provide enough detail to assess exposure-adjusted event rates or the completeness of follow-up.

The record posts an analysis for the primary endpoint comparison but does not give a detailed statistical analysis plan. In particular, original sample-size assumptions, handling of missing data, covariate adjustment, and sensitivity analyses are not reported in the registry record. The posted estimates can therefore be described and interpreted with their stated uncertainty, but the missing analysis details limit assessment of how closely the results follow the trial’s original plan.

11. Confidence Intervals and Precision

The confidence intervals are central to assessing precision. For MORAb-202, the ORR estimate is 20.0%, with a 95% confidence interval from 11.4% to 31.3%. For investigator’s choice chemotherapy, the estimate is 13.9%, with a 95% confidence interval from 4.7% to 29.5%. Each interval spans a meaningful range of possible response rates, so neither point estimate should be treated as exact.

General statistical explanation: confidence intervals become narrower when data contain more information and broader when estimates are less precise. The width depends on factors such as the number of participants and the amount of variation or uncertainty in the outcome. The smaller chemotherapy group has 36 participants in the primary endpoint result, compared with 70 for MORAb-202. That difference in group size is part of the context for the uncertainty, though the registry does not provide a precision target or original sample-size rationale.

The reported comparison p-value is 0.437. A p-value alone does not describe the range of plausible group differences, and it should be read alongside the confidence intervals and the underlying rates. The posted comparison interval includes the no-difference value, so the data do not rule out no difference; it also allows for differences in either direction. A wide interval is not evidence that the treatments are equivalent. Equivalence requires a design and margin intended to test that question, which are not reported in the registry record.

The registry does not report interval estimates for all secondary outcomes. Their counts are therefore less informative about precision than a complete presentation of estimates with intervals would be. Taken together, the primary endpoint intervals indicate that the response-rate results are uncertain and should be interpreted cautiously rather than as precise estimates of the rates in a broader population.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not a description of the original trial’s design. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect defined as the stated fraction of the observed effect. The sample-size figures for this binary outcome are participants per arm, not total events.

The rows describe planning for 100%, 75%, and 50% of the observed effect. For each assumed effect, the 80% power column gives the participants per arm in a hypothetical study that would have an 80% chance of detecting that specified effect under the listed assumptions. The 90% power column gives the corresponding number for a 90% chance. These are design calculations, not results observed in this trial. This is not observed power.

Under the full observed-effect scenario, the illustration gives 591 participants per arm for 80% power and 790 for 90% power. For planning at 75% of the observed effect, it gives 1,088 and 1,456 participants per arm. For planning at 50% of the observed effect, it gives 2,531 and 3,388 participants per arm. These figures show the relationship between the assumed effect size and the planned group size: smaller effects need more participants to detect under otherwise unchanged assumptions.

The calculation uses the observed effect as a starting point. Observed effects from relatively small groups can be uncertain, and using them for planning does not ensure that a future study will have the same effect. The figures should not be interpreted as a recommendation or as evidence that the original trial was intended to enroll those numbers. The original study’s sample-size justification and design assumptions are not reported in the registry record. The planning figures are best understood as hypothetical illustrations of how sample size changes when the target effect or desired power changes.

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 = 0.200; treatment proportion p₁ = 0.139; average p̄ = 0.169.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5305 = 1.0398.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5288 = 0.4450.
4. n = (1.0398 + 0.4450)² / (-0.0611)² = 590.4, rounded up to 591 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 <- 0.2                          # control proportion
p1 <- 0.138888888888889                          # 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(5613088)
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 = 591 (80% power), 790 (90% power)
 75% of observed effect: n per arm = 1,088 (80% power), 1,456 (90% power)
 50% of observed effect: n per arm = 2,531 (80% power), 3,388 (90% power)
power.prop.test: 590.4 
Simulated power at n = 591 per arm: 0.800 (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

Multiplicity concerns arise when a study evaluates many outcomes or performs several comparisons. The registry lists 14 outcome measures and identifies one analysis. It also lists multiple secondary safety outcomes, including adverse events, serious adverse events, treatment-related outcomes, discontinuations, deaths, and laboratory abnormalities. The record does not report a testing hierarchy, a family-wise error strategy, or another multiplicity adjustment. Consequently, the secondary comparisons should be interpreted cautiously, particularly if individual p-values are considered in isolation.

The registry identifies the primary population as all randomized participants. That statement clarifies the intended population for the ORR endpoint, but it does not fully describe how the analysis was implemented. Missing response assessments, participants who did not receive treatment, and any exclusions or imputation procedures are not described in the registry record. The record also does not provide sensitivity analyses showing how alternative assumptions about missing outcomes might affect the result.

The registry’s safety results use denominators that differ between endpoints and groups. For example, the serious adverse event counts are given for 70 participants in the MORAb-202 group and 34 in the chemotherapy group. The reason the chemotherapy safety denominator differs from its primary endpoint group size is not reported in the registry record. No assumptions about the reason or its effect should be made without a participant disposition account.

The primary endpoint is based on investigator assessment in an open-label study. The record does not report whether responses were independently reviewed, whether assessment timing was uniform, or how subsequent therapy affected endpoint classification beyond the stated timeframe. These are relevant details for understanding potential assessment and missing-data issues, but their absence does not establish that a particular bias occurred.

The original statistical analysis plan, interim analyses, sample-size justification, and missing-data methods are not reported in the registry record. The sample-size illustrations are not a substitute for those original design details. With this information unavailable, it is not possible to verify whether the posted analyses follow the complete planned approach. The available results should therefore be treated as the registry’s reported endpoint summaries and unadjusted comparisons, with their stated uncertainty and limitations.

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: intestinal obstruction (8.8%), intestinal pseudo-obstruction (5.9%), pyrexia (5.9%), abdominal pain (4.3%), small intestinal obstruction (4.3%).

The serious adverse event counts are 22 among 70 participants in the MORAb-202 group and 11 among 34 participants in the investigator’s choice chemotherapy group. These are counts of participants with serious adverse events, not counts of every individual serious event. The denominators are the safety populations listed for this outcome. The registry record does not explain the difference between the chemotherapy safety denominator and the 36 participants in its primary endpoint group.

The registry lists intestinal obstruction at 8.8%, intestinal pseudo-obstruction at 5.9%, pyrexia at 5.9%, abdominal pain at 4.3%, small intestinal obstruction at 4.3%, and ascites at 2.9% among the top serious-event terms. The record does not establish in this listing that those terms are exclusive categories, nor does it provide a basis to assign them to one treatment group. They should be read as listed serious-event terms, not as comparative rates.

General statistical explanation: event counts depend on how many participants are observed and for how long. A simple count comparison does not account for differences in exposure duration or follow-up. The registry does not provide exposure-adjusted serious-event rates. The figures describe the posted safety results, but by themselves they do not establish which treatment has a more favorable safety profile.

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

The registry result answers a focused question: what proportion of randomized participants had a confirmed complete or partial response under the investigator’s RECIST v1.1 assessment? The posted rates are 20.0% for MORAb-202 and 13.9% for investigator’s choice chemotherapy. The confidence intervals are broad, and the unadjusted comparison has a p-value of 0.437. The evidence does not establish a clear difference in ORR between the groups.

This does not mean the groups have been shown to be equivalent. A result that does not provide strong evidence of a difference is not the same as evidence that any difference is small enough to be clinically unimportant. The registry record does not report an equivalence margin or a non-inferiority framework. The confidence intervals also permit a range of possible rates and differences, so the point estimates should not be mistaken for precise underlying values.

The result also does not answer whether one group had longer-lasting responses, delayed progression, or longer survival. ORR records whether response criteria were met; it is not a measure of response duration. Although the registry lists deaths as a secondary outcome, the posted death counts do not constitute a time-to-event survival analysis. The record does not provide an analysis of progression-free survival, overall survival, symptoms, or quality of life in the information summarized by these results.

Likewise, the safety counts should not be collapsed into a single conclusion about overall risk. Event counts and adverse-event categories are descriptive, and the record does not report exposure-adjusted rates or all details needed to assess comparative safety. Open-label investigator assessment is another context for interpreting the primary endpoint. The registry record does not report independent central review.

The study is listed as terminated, but the reason is not reported in the registry record. Termination alone does not show why the study ended or whether it was related to efficacy, safety, recruitment, or another consideration. The findings describe the posted data and their limits; they are not medical advice and do not establish that either treatment should or should not be used.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate, a p-value, and a confidence interval answer different statistical questions. The primary ORR estimates are 20.0% and 13.9%, but the confidence intervals extend from 11.4% to 31.3% and from 4.7% to 29.5%. The p-value of 0.437 does not establish a difference, while the intervals show that considerable uncertainty remains about the rates represented by the point estimates.

The study also highlights the distinction between a randomized comparison and a definitive conclusion. Randomization is an important design feature, but the record’s group sizes are 70 and 36 for the primary endpoint, and the available information does not include all the planned analysis details. An open-label design combined with investigator-assessed response makes assessment procedures relevant to interpretation. The record does not report independent review or the original analysis plan.

Another statistical lesson is that secondary outcomes can broaden the clinical picture without necessarily adding confirmatory evidence. Safety results matter for understanding the study, but multiple secondary outcomes, unadjusted comparisons, and differing denominators make individual results less conclusive. The registry does not report a multiplicity strategy or a complete exposure-adjusted safety analysis.

Finally, the planning illustrations show how demanding a study can become when the target effect is smaller or the desired probability of detection is higher. Those hypothetical figures are not the original trial design and are not observed power. The original sample-size rationale is not reported. Taken together, the registry record demonstrates the value of presenting estimates with uncertainty and of separating the observed results from unreported protocol and analysis details.

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.

Several limitations are specific to the available record. The study is listed as terminated, but the reason for termination is not reported. Without that information, the termination status should be treated as context, not as evidence of a particular efficacy or safety problem. The record gives a primary completion date but does not provide a full explanation of the study’s operational history.

The primary endpoint is investigator-assessed in an open-label study. The criteria are defined using RECIST v1.1, but the registry record does not report independent central review or describe any procedures to reduce assessment bias. The response-rate confidence intervals are broad, and the chemotherapy group has 36 participants in the primary endpoint result. Those features limit the precision of the comparison.

The record does not report why the chemotherapy safety denominator is 34 while the primary endpoint group includes 36 participants. Nor does it give enough participant-flow detail to determine how many participants had missing response assessments, left treatment, or were excluded from particular analyses. The missing-data approach and sensitivity analyses are not reported.

The comparator is investigator’s choice chemotherapy, with paclitaxel, pegylated liposomal doxorubicin, and topotecan listed as interventions. The record does not show how many participants received each option or provide treatment-specific results within that comparator group. A pooled comparator result therefore does not describe the outcomes for each chemotherapy option separately.

Finally, the posted summary does not include detailed treatment schedules, exposure-adjusted safety analyses, response duration, or a complete time-to-event analysis. The sample-size illustrations do not replace the unreported original design assumptions. These gaps constrain interpretation of the results but do not, on their own, indicate the direction or size of any bias.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of MORAb-202 Versus Investigator's Choice Chemotherapy in Female Participants With Platinum-resistant High-grade Serous (HGS) Ovarian, Primary Peritoneal, or Fallopian Tube Cancer — NCT05613088.
• Registry record last updated 2026-10-28; status last verified 2026-10.
• Results first posted 2025-07-03.
• 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

NCT05613088 is a phase 2 randomized, open-label, parallel-group study of MORAb-202 versus investigator’s choice chemotherapy in female participants with platinum-resistant high-grade serous ovarian, primary peritoneal, or fallopian tube cancer. The registry lists 106 enrolled participants and the study status as terminated. The primary endpoint is investigator-assessed ORR under RECIST v1.1.

The posted response rates are 20.0% among 70 participants assigned to MORAb-202 and 13.9% among 36 assigned to investigator’s choice chemotherapy. Their 95% confidence intervals are 11.4% to 31.3% and 4.7% to 29.5%, and the unadjusted comparison p-value is 0.437. The result does not establish a clear between-group difference and remains imprecise. Safety outcomes are also listed, but the registry record does not report the original sample-size rationale, detailed missing-data methods, or reason for termination.