Phase II Anetumab Ravtansine as 2nd Line Treatment for Malignant Pleural Mesothelioma (MPM): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase II Anetumab Ravtansine as 2nd Line Treatment for Malignant Pleural Mesothelioma (MPM) (NCT02610140), a randomized phase 2 study. The primary outcome is Progression-free Survival (PFS), [95% CI].

2. Clinical Question

The question is a comparative one: whether the time-to-event experience differed between participants assigned to anetumab ravtansine and those assigned to vinorelbine. The registry also lists overall survival, response and disease-control outcomes, response duration, and symptom measures as secondary outcomes. Those outcomes provide related but distinct views of the trial results; they do not replace the prespecified primary endpoint.

The record describes 248 participants enrolled. Its brief study description says 210 eligible patients will be randomized, while the posted PFS groups contain 166 participants for anetumab ravtansine and 82 for vinorelbine. These figures describe different parts of the record and should not be treated as interchangeable without further information about enrollment and eligibility.

3. Trial Design

This was a randomized, parallel-group, open-label phase II study sponsored by Bayer. Participants were assigned to anetumab ravtansine or vinorelbine. The registry lists 248 participants enrolled and describes the population as patients with advanced or metastatic malignant pleural mesothelioma overexpressing mesothelin after progression on first-line platinum/pemetrexed-based chemotherapy. The brief summary refers to stage IV disease.

The posted primary efficacy analysis used the intent-to-treat analysis set. The PFS groups included 166 participants assigned to anetumab ravtansine and 82 assigned to vinorelbine. The registry summary describes anetumab ravtansine given intravenously every three weeks and vinorelbine given intravenously weekly. Treatment was to continue until centrally confirmed disease progression or another withdrawal criterion, followed by a follow-up phase to collect safety and endpoint information.

The primary endpoint was progression-free survival from randomization. The registry describes radiological tumor assessments at defined time points and central blinded radiology review for progression. The primary timeframe was until approximately 117 PFS events were observed, up to approximately 30 months, with a data cut-off of 31-May-2017.

The trial was open label, so masking was not used. The registry record does not report the original sample-size justification, the planned allocation ratio, or further details about the randomization procedure. It also does not report whether interim efficacy analyses were planned. These design details cannot be inferred from the posted group sizes or from the later planning illustrations.

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: Overall, 315 patients were screened; of these, 67 patients were screening failures.

Randomization and Treatment Period

Reasons for not completing this period:

Safety Follow-up

Reasons for not completing this period:

Active Follow-up

Reasons for not completing this period:

Long-term Follow-up

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The primary efficacy analysis (PFS) was performed in the ITT (Intent-to-treat) analysis set.

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: Intent-to-treat set (ITT): all randomized participants

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival (PFS), [95% CI], measured over From randomization till approximately 117 PFS events observed, up to approx. 30 months (data cut-off: 31-May-2017).

Progression-free survival (PFS) measures the time from randomization until disease progression or death. In this study, progression was defined using mRECIST for malignant pleural mesothelioma and assessed by blinded central radiology review. The primary analysis was conducted in the intent-to-treat analysis set, which evaluates participants according to their randomized group.

PFS is a time-to-event endpoint: the analysis uses information about when events occur as well as the fact that some participants may not have had an observed event by the data cut-off. A median PFS is the estimated time by which half of the relevant event-time distribution has occurred. It does not describe the experience of every participant, and it does not by itself show how event timing differs throughout follow-up.

Progression and death are combined in the endpoint, so PFS reflects either type of event rather than progression alone. Central radiology review provides a common assessment process, and the registry identifies that review as blinded. The outcome is useful for comparing the time until disease progression or death between randomized groups, while remaining distinct from overall survival, response rate, and symptom outcomes. The registry record does not report further details of the PFS censoring rules or the handling of missing assessments.

7. Results Posted in the Registry

• Anetumab Ravtansine vs Vinorelbine: hazard ratio 1.22 (95% CI 0.85–1,738), reported p = 0.859 (as reported in the registry).

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.

Overall Survival (OS), [95% CI]

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Anetumab Ravtansine vs Vinorelbine: hazard ratio 1.07 (95% CI 0.76–1.51), reported p = 0.656 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Anetumab Ravtansine vs Vinorelbine and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate (ORR)

• 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:
  • Vinorelbine: 6.1% (5/82) versus 8.4% (14/166) on control; risk difference -2.3 percentage points (95% CI -9.0 to 4.3), risk ratio 0.72 (0.27–1.94); unadjusted two-proportion z-test p = 0.515.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vinorelbine and the control. The interval gives the range of effects that remain compatible with the data.

Disease Control Rate (DCR)

• 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:
  • Vinorelbine: 68.3% (56/82) versus 73.5% (122/166) on control; risk difference -5.2 percentage points (95% CI -17.3 to 6.9), risk ratio 0.93 (0.78–1.11); unadjusted two-proportion z-test p = 0.392.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vinorelbine and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide additional views of survival, tumor response, disease control, and symptoms. The posted numerical results include overall survival, objective response rate, and disease control rate. The registry also lists duration of response, durable response, symptom improvement, worsening of mesothelioma symptoms, and time to worsening of pain; detailed numerical results for those listed measures are not reported in the registry record.

Overall survival is another time-to-event outcome, but it concerns death from any cause rather than the earlier composite of progression or death. The posted median estimates and reported hazard-ratio analysis do not establish a distinct conclusion from the primary endpoint. The response and disease-control measures describe proportions rather than event timing. They are therefore related evidence, but they measure different aspects of outcome and cannot be treated as alternate measures of PFS.

The registry reports sponsor analyses for the time-to-event outcomes, while the ORR and DCR comparisons are unadjusted recalculations and have no reported sponsor comparative analyses. The unadjusted ORR p-value is 0.515 and the unadjusted DCR p-value is 0.392. These values should not be used as if they were multiplicity-adjusted confirmatory tests.

In general, testing several outcomes creates more opportunities for chance findings. When no adjustment strategy is reported, isolated secondary p-values carry less weight than the primary analysis, especially when the outcomes are numerous and clinically distinct. The registry record does not report a multiplicity procedure or a hierarchy for secondary hypotheses. The secondary results are best read as supportive descriptions, considered alongside the primary PFS result and its uncertainty rather than as a collection of independent definitive tests.

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

• Overall Survival (OS), [95% CI]
• Objective Response Rate (ORR)
• Disease Control Rate (DCR)
• Duration of Response (DOR)
• Durable Response Rate (DRR)
• Percentage of Participants With Confirmed Improvement of Symptoms Characteristic of Mesothelioma
• Time to Worsening of Symptoms Characteristic of Mesothelioma
• Time to Worsening of Pain

9. Statistical Interpretation

10. Statistical Methods Explained

What does a time-to-event analysis use?

In general, a time-to-event analysis considers both the length of follow-up and whether an event was observed. Participants who have not had an event by the analysis cut-off can still contribute information up to the time they were last known to be followed. This is different from treating every participant as if follow-up ended at the same time. The registry defines PFS as time from randomization until progression under mRECIST by blinded central radiology review, or death.

The registry reports median PFS for each group and a hazard ratio from a log-rank analysis. A median provides a single point on the estimated event-time distribution. A hazard ratio, by contrast, summarizes a relative event hazard across follow-up under the analysis framework. These are different summaries and need not tell the same story in every dataset. Neither one gives a complete account of the shape of the event-time distributions.

What does the hazard ratio mean?

In general, a hazard ratio compares the instantaneous event rates between groups among participants who have not yet had an event. It is not a direct comparison of the number of participants who experienced an event, nor is it a ratio of medians. The reported comparison is named as anetumab ravtansine versus vinorelbine, with a hazard ratio of 1.215. Interpretation of its direction assumes the conventional coding of the named groups, and interpretation of its size must account for the uncertainty interval.

The registry reports a log-rank method for the primary comparison. In general, the log-rank test compares event-time patterns between groups while accounting for censoring. It tests a null hypothesis of no difference in the event-time distributions under its assumptions. A p-value describes how compatible the observed test statistic is with that null model; it is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect.

Why is the confidence interval important?

In general, a confidence interval shows the range of effect estimates compatible with the data and the statistical procedure at the stated confidence level. A wide interval signals low precision: the data do not pin down the effect narrowly. For the primary hazard ratio, the reported 95% interval extends from 0.850 to 1,738. It includes 1 and spans a very broad range. That uncertainty matters more than treating the point estimate as an exact description of the underlying effect.

The confidence intervals around the group medians are also useful for conveying uncertainty in each estimate. They are not, by themselves, a confidence interval for the difference between medians. A direct comparison should rely on the reported comparative analysis rather than visually comparing separate intervals.

What role does the analysis population play?

The primary PFS analysis was performed in the intent-to-treat set. In general, an intent-to-treat analysis retains participants in their randomized groups, which preserves the comparison created by random assignment. The record does not report details of the analysis populations used for all secondary outcomes, or how missing assessments and censoring were handled. Those omissions limit a full assessment of the analysis implementation.

The study was open label, but the registry specifies blinded central radiology review for the PFS progression determination. That central review is relevant because progression assessment involves radiological evaluation. The record does not report additional safeguards or operational details for that review, so they should not be assumed.

What is the status of recalculated comparisons?

The posted primary time-to-event comparison is the sponsor's reported analysis, not an independent recalculation from group-level summary statistics. A hazard ratio and its uncertainty cannot be reconstructed reliably from medians alone. For that reason, the reported log-rank hazard ratio is the appropriate inferential result to discuss. The registry record does not identify a discrepancy between the sponsor's result and a recalculated primary analysis.

For binary outcomes, simple unadjusted recalculations can be made from posted event counts and group sizes. Such calculations do not necessarily reproduce a sponsor's analysis plan, adjustment methods, or endpoint definitions. The ORR and DCR comparisons have unadjusted p-values in the posted recalculations, but the registry does not post corresponding sponsor-reported analyses for those endpoints. These unadjusted calculations should therefore be treated as descriptive supporting analyses rather than as substitutes for a reported confirmatory analysis.

In general, statistical significance is not a binary verdict on the truth of a treatment effect. It depends on the observed data, the analysis method, and the threshold chosen for a test. Effect estimates and confidence intervals are needed to understand both direction and precision. Here, the primary result combines a hazard-ratio estimate with a broad interval and a log-rank p-value greater than 0.05; each element informs interpretation, and none alone establishes equivalence.

11. Confidence Intervals and Precision

The PFS median estimates were 4.3 months for anetumab ravtansine and 4.5 months for vinorelbine. Their respective 95% confidence intervals were 4.1 to 5.5 and 4.1 to 5.8 months. These intervals describe uncertainty around each group’s median estimate, not a direct interval for the difference between medians.

The comparative hazard-ratio estimate was 1.215, with a sponsor-reported 95% confidence interval of 0.850 to 1,738. The interval includes 1, the value corresponding to equal hazards under the conventional interpretation, and is very wide. This means the posted estimate is imprecise: it is compatible with substantially different relative hazard values. The registry record does not explain the especially large upper limit, so no cause should be inferred from the number alone.

In general, a 95% confidence interval is a measure of statistical uncertainty produced by a method; it is not a guarantee that the true value lies within the particular interval. A narrow interval would indicate greater precision, while a broad interval leaves more uncertainty about the magnitude and direction of an effect. The p-value greater than 0.05 does not remove that uncertainty or prove that the treatments have the same effect.

The group sizes in the PFS analysis were 166 and 82, and the primary timeframe referred to approximately 117 PFS events. The record does not provide the exact number of events in the analysis, the censoring distribution, or further details needed to independently evaluate precision. The posted confidence interval is therefore central to understanding how little the point estimate alone can establish.

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 figures are illustrations based on observed effects, not the trial’s original sample-size design. The original design assumptions, including the rationale for the planned sample size, are not reported in the registry record. The illustrations assume a two-sided significance level of 0.05, equal allocation between two groups, and a normal approximation. They consider effects set at 100%, 75%, and 50% of the observed effect.

For the time-to-event outcomes, the figures refer to the total number of events needed, not participants per arm. For the binary outcomes, they refer to participants per arm. The 80% power column means the illustrated sample size or event count that would give an 80% chance of detecting the stated effect under those assumptions, if that effect and the other assumptions were true. The 90% power column gives the corresponding planning target for a 90% chance. These are design calculations, not guarantees about what a future study would find.

Across the displayed scenarios, planning around a smaller fraction of the observed effect requires more participants or events than planning around the full observed effect. This is a general consequence of trying to distinguish a smaller signal from random variation. The estimates are particularly sensitive to the observed effect used as the starting point, so they should not be read as a recommended design for a new trial.

These figures are not observed power. Observed power is not a useful way to reinterpret the completed trial’s result; the observed estimates and their confidence intervals convey the data and uncertainty more directly. The planning calculations do not show that the trial was adequately or inadequately powered, because the original design assumptions are not reported in the registry record.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 1.215, so ln(HR) = 0.1947.
2. d = 4 × (1.96 + 0.842)² / [ln(1.215)]² = 827.8, rounded up to 828 events in total 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
hr <- 1.215                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(2610140)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 828 (80% power), 1,109 (90% power)
 75% of observed effect: events = 1,472 (80% power), 1,971 (90% power)
 50% of observed effect: events = 3,312 (80% power), 4,433 (90% power)
Simulated power with 828 events: 0.792 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Analyses Reported by the Sponsor

The registry reports the sponsor's primary PFS analysis as a log-rank hazard ratio of 1.215, with a 95% confidence interval of 0.850 to 1,738 and a p-value greater than 0.05. That is the reported inferential analysis for the primary endpoint. The time-to-event result is not recalculated from the group medians because medians alone do not contain enough information to reconstruct a log-rank hazard ratio or its confidence interval.

The record indicates no discrepancy between the sponsor's result and a recalculated primary analysis. In any event, a sponsor-reported analysis takes precedence when it differs from a simple unadjusted recalculation, because the sponsor's analysis may reflect the trial's chosen method and data handling. No independent recalculation is offered for the primary time-to-event comparison.

For ORR and DCR, the registry has no sponsor-reported comparative analyses. The posted unadjusted calculations are therefore separate descriptive checks based on the available group counts, not a replacement for an analysis specified by the sponsor. They should be interpreted cautiously and should not be presented as the sponsor's conclusion. The registry record does not report further details about the sponsor's analysis plan for these secondary outcomes.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint, PFS, and multiple secondary outcomes, including overall survival, objective response, disease control, response duration, durable response, and symptom measures. It also indicates 13 outcome measures and 8 analyses in the posted record. The registry record does not report a multiplicity adjustment, a testing hierarchy for secondary outcomes, or a rule specifying which secondary hypotheses were intended to be confirmatory.

In general, when many statistical hypotheses are tested, the chance of at least one apparently notable result can increase. Multiplicity procedures can control that risk, but they may also affect the thresholds or intervals used for interpretation. Without a reported plan, secondary p-values should not be treated as if they had a known family-wise error control. This matters particularly for ORR and DCR because their posted comparisons are unadjusted recalculations rather than sponsor-reported analyses.

The primary PFS analysis population is identified as the intent-to-treat set. That information helps define which participants contributed to the primary efficacy analysis, but it does not answer every question about the analysis. The registry record does not report detailed missing-data procedures, censoring rules, handling of missed radiological assessments, or sensitivity analyses for PFS. It also does not report analysis-population definitions for every secondary endpoint.

The record does not report whether interim efficacy analyses were planned or conducted. It does describe a data cut-off for PFS and a later cut-off for overall survival, but these dates alone do not establish an interim-testing strategy or statistical adjustment. The registry also does not report the original sample-size justification. These omissions limit assessment of the full prespecified analysis plan and how it was implemented.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (6.9%), dyspnoea (4.3%), neutropenia (4.2%), pyrexia (4.2%), abdominal pain (3.1%).

The posted safety figures give the numbers at risk and the numbers affected by serious adverse events and other adverse events for each group. For serious adverse events, the at-risk counts were 163 for anetumab ravtansine and 72 for vinorelbine; the affected counts were 56 and 25, respectively. For other adverse events, the at-risk counts were 163 and 72, with 161 and 68 affected. The registry also reports 126 deaths in the anetumab ravtansine group and 55 in the vinorelbine group.

The listed serious adverse event terms and percentages include pneumonia at 6.9%, dyspnoea at 4.3%, neutropenia at 4.2%, pyrexia at 4.2%, abdominal pain at 3.1%, and respiratory tract infection at 2.8%. These figures describe reported events; the registry record does not establish from these figures alone whether an event was caused by a study drug.

In general, safety counts depend on the number of participants assessed, the definitions used, and the period of observation. The group counts are not directly comparable without considering exposure and follow-up, details not reported in the registry record. The figures should be read as descriptive safety information, not as a complete characterization of comparative risk.

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

The registry reports a randomized comparison of anetumab ravtansine and vinorelbine in patients with advanced or metastatic mesothelin-overexpressing malignant pleural mesothelioma after first-line platinum/pemetrexed-based chemotherapy. For the primary endpoint, the median PFS estimates were 4.3 months and 4.5 months, and the sponsor-reported hazard ratio was 1.215. Its 95% confidence interval, 0.850 to 1,738, is very broad and includes 1; the log-rank p-value was greater than 0.05.

These data do not establish that the groups were equivalent. Failure to obtain a p-value at or below a conventional threshold is not evidence that any difference is absent. The wide interval also means the point estimate should not be treated as precise. At the same time, the posted result does not demonstrate a definitive difference in PFS. The registry record supports a description of the observed estimates and their uncertainty, rather than a conclusive claim about comparative benefit.

The secondary outcomes do not change that interpretation. Overall survival is a different time-to-event endpoint, and response and disease control are different outcome types. The ORR and DCR comparisons are unadjusted recalculations without sponsor-reported comparative analyses. The registry lists further symptom and response outcomes but does not report detailed numerical results for them. Multiplicity procedures are not reported, so secondary findings should be given limited confirmatory weight.

The results apply to the trial population and analysis as described in the registry. They do not establish what would happen in other populations, under other treatment conditions, or with different follow-up. Nor do the posted efficacy figures alone provide a complete assessment of safety. The registry record is a source of clinical-trial results, but important details of the statistical plan, missing-data handling, and sample-size rationale are not reported.

18. Why This Trial Matters Statistically

This study illustrates why a point estimate should not be read in isolation. The PFS medians are close, and the reported hazard ratio is 1.215, but the sponsor's confidence interval extends from 0.850 to 1,738. Its breadth makes precision a central feature of interpretation. The p-value greater than 0.05 does not prove no effect, while the point estimate alone cannot establish an effect.

It also shows the distinction between a trial's reported analysis and a simple recalculation. A time-to-event hazard ratio cannot be reconstructed from medians alone, so the sponsor's log-rank result is the pertinent comparative analysis. For binary endpoints, unadjusted recalculations can describe the posted counts, but they are not equivalent to an analysis plan or a sponsor-reported test. Keeping those categories separate helps prevent descriptive calculations from being mistaken for the trial's inferential conclusions.

The record offers a further lesson about secondary outcomes. Survival, response, disease control, and symptom measures address different questions. When many outcomes are considered and multiplicity handling is not reported, secondary results should not be treated as independent confirmation of the primary finding. The absence of reported analysis details also limits how fully the statistical conduct can be evaluated.

Finally, planning illustrations based on observed effects are not a retrospective measure of power. They depend on assumptions and show how planning targets change for different effect sizes. Since the original sample-size justification is not reported, those illustrations cannot establish what the study was designed to detect. Together, these considerations emphasize estimation, uncertainty, and careful separation of reported trial analyses from exploratory or illustrative calculations.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary hazard-ratio confidence interval is unusually broad, with a reported upper limit of 1,738. The registry record does not explain this width or provide enough information to independently assess the model, event pattern, or calculation. The estimate should therefore be interpreted with particular caution rather than as a precise summary of the comparison.

The record identifies the PFS population as intent to treat and describes blinded central radiology review, but does not report detailed censoring rules, missing-assessment handling, or sensitivity analyses. It also does not report the original sample-size justification, randomization procedure details, interim-analysis plans, or full statistical analysis plan. Without those details, the statistical robustness of the posted findings cannot be comprehensively evaluated.

The study was open label. Blinded central review is specified for radiological PFS assessment, but the registry does not provide further operational information about that process. The available safety summaries are also limited: at-risk and affected counts and selected serious adverse event terms are reported, but the record does not give enough information to account for differences in exposure or follow-up between groups.

Several secondary outcomes are listed without detailed numerical results in the registry record. For ORR and DCR, there are unadjusted recalculations but no sponsor-reported comparative analyses. The record does not report multiplicity control or a testing hierarchy, making secondary inferential claims difficult to calibrate. The discrepancy between the brief description's 210 eligible patients and the overall enrollment of 248 is not explained in the registry record, so their relationship should not be assumed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Phase II Anetumab Ravtansine as 2nd Line Treatment for Malignant Pleural Mesothelioma (MPM) — NCT02610140.
• Registry record last updated 2020-11-04; status last verified 2020-10.
• Results first posted 2020-07-17.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

This completed, randomized, open-label, parallel-group phase II study compared intravenous anetumab ravtansine with intravenous vinorelbine in advanced or metastatic mesothelin-overexpressing malignant pleural mesothelioma after progression on first-line platinum/pemetrexed-based chemotherapy. The record lists 248 participants enrolled.

The primary endpoint was PFS, defined as time from randomization until disease progression under mRECIST by blinded central radiology review or death. In the intent-to-treat analysis, median PFS was 4.3 months with anetumab ravtansine and 4.5 months with vinorelbine. The reported hazard ratio was 1.215, with a 95% confidence interval of 0.850 to 1,738 and a log-rank p-value greater than 0.05.

Overall survival, response, disease control, and safety outcomes are also reported, with additional symptom and response measures listed. The registry record does not report the original sample-size justification, multiplicity approach, interim-analysis plans, or several details of missing-data and endpoint handling.