A Study to Evaluate the Effect of Long-term Treatment With BELVIQ (Lorcaserin HCl) on the Incidence of Major Adverse Cardiovascular Events and Conversion to Type 2 Diabetes Mellitus in Obese and Overweight Subjects With Cardiovascular Disease or Multiple Cardiovascular Risk Factors: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Effect of Long-term Treatment With BELVIQ (Lorcaserin HCl) on the Incidence of Major Adverse Cardiovascular Events and Conversion to Type 2 Diabetes Mellitus in Obese and Overweight Subjects With Cardiovascular Disease or Multiple Cardiovascular Risk Factors (NCT02019264), a randomized phase 4 study. The primary outcome is Time From Randomization to First Occurrence of Major Adverse Cardiovascular Events (MACE) at Interim Analysis.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, placebo-controlled, parallel-group phase 4 study sponsored by Eisai Inc. It enrolled 14673 participants and is listed as completed. The registry gives a start date of 2014-01-24 and a primary completion date of 2018-05-14. The brief description identifies the setting as multicenter and the population as overweight and obese subjects with cardiovascular disease and/or multiple cardiovascular risk factors.

Participants were assigned to lorcaserin hydrochloride 10 mg twice daily or placebo twice daily. The primary outcome assessed time from randomization to the first occurrence of MACE through Month 42, using the intent-to-treat set. The outcome description specifies that events counted whether they occurred on or off treatment. Those without an event were censored at their last study contact or at the visit following sponsor notification of study completion, whichever occurred first.

The registry lists 6000 participants per arm for the primary outcome. It also reports an interim analysis, but further information about the interim-analysis plan, including its timing, decision rules, or any adjustment to the statistical testing, is not reported in the registry record. The original sample-size justification, planned event target, and study-specific assumptions used to design the trial are also not reported in the registry record. The planning illustrations associated with the posted comparison are not the original design calculation.

The study included secondary outcomes on diabetes conversion, glucose homeostasis, mortality, renal impairment, MACE components, and HbA1c. The record lists 15 outcome measures and 20 analyses overall. The registry does not give complete details about the analysis population and missing-data handling for every secondary outcome. Consequently, the primary design and analysis description is more complete than the information available for interpreting the full set of outcomes.

4. Participant Flow and Accounting

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

Before assignment: A total of 14,673 participants were screened and enrolled, of which 2673 participants were screen failures and 12,000 were randomized to receive lorcaserin hydrochloride (HCl) or placebo.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The total time analysis set using the intent-to-treat (ITT) set, events were counted that occurred while participants were on and off treatment. Participants with no events were censored at their last study contact or at the visit following sponsor notification of study completion, whichever occurred first.

5. Baseline Characteristics

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

Population: The full analysis (FA) set included all randomized participants regardless of whether they took study drug or not.

6. Primary Endpoint

The registry lists the primary outcome as Time From Randomization to First Occurrence of Major Adverse Cardiovascular Events (MACE) at Interim Analysis, measured over Baseline up to Month 42.

The primary endpoint measures the time from randomization until a participant first experiences myocardial infarction, stroke, or cardiovascular death. It is a time-to-event outcome: both whether an event occurred and how long participants were followed without an event contribute to the analysis. Participants who had no recorded event were censored according to the follow-up rule described in the registry.

A time-to-first-event endpoint is useful when the research question concerns how quickly participants experience a clinically important event, rather than only the proportion with an event at a single fixed visit. It can incorporate information from participants with different follow-up durations, provided that the analysis and censoring assumptions are appropriate. The registry says that the outcome was assessed using the Kaplan-Meier estimate and Greenwood formula. In general, Kaplan-Meier methods estimate event-free experience over time while accounting for censoring; Greenwood’s formula is used to estimate uncertainty in that estimate.

The posted primary results are expressed as a hazard ratio rather than as a median time or an absolute event risk. The registry does not report arm-specific median times for this endpoint. A hazard ratio summarizes the relative event rate over follow-up under the model used, and should not be read as a difference in median survival time or as an absolute difference in the probability of an event. The registry labels the analysis non-inferiority, but does not report the margin needed to evaluate that framework fully.

7. Results Posted in the Registry

• Placebo vs Lorcaserin 10 mg: hazard ratio 1.00 (95% CI 0.84–1.20), reported p < 0.001 (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.

Time From Randomization to Conversion to Type 2 Diabetes Mellitus (T2DM) for Participants With Prediabetes at Baseline

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Primary Analytic Method); it was not recalculated.
• Result:
  • Placebo vs Lorcaserin 10 mg: hazard ratio 0.81 (95% CI 0.66–0.99), reported p = 0.038 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Placebo vs Lorcaserin 10 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time From Randomization to Event of All-cause Mortality

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Primary Analytic Method); it was not recalculated.
• Result:
  • Placebo vs Lorcaserin 10 mg: hazard ratio 1.08 (95% CI 0.89–1.31), reported p = 0.421 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo vs Lorcaserin 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

Time From Randomization to Conversion to Normal Glucose Homeostasis in Participants With Prediabetes at Baseline

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Primary Analytic Method); it was not recalculated.
• Result:
  • Placebo vs Lorcaserin 10 mg: hazard ratio 1.12 (95% CI 0.95–1.33), reported p = 0.181 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo vs Lorcaserin 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several domains, including conversion to type 2 diabetes among participants with prediabetes, all-cause mortality, conversion to normal glucose homeostasis, MACE components, renal outcomes, and HbA1c. The registry lists 15 outcome measures and 20 analyses overall, while the posted secondary comparisons include different analysis populations and follow-up periods. This breadth means the secondary results address related but distinct questions rather than serving as repeated measurements of the primary MACE endpoint.

Across the three secondary comparisons with reported hazard ratios, the diabetes-conversion result among participants with prediabetes has a confidence interval that excludes 1, whereas the intervals for all-cause mortality and conversion to normal glucose homeostasis include 1. This pattern does not alter the primary estimate or resolve its non-inferiority interpretation. Different endpoints, populations, and event processes can yield different results, and the registry does not report enough detail to treat one as a direct confirmation or refutation of another.

Unadjusted secondary results generally carry less confirmatory weight when many outcomes are examined, because the chance of at least one apparently unusual result can rise with repeated testing. In general, multiplicity procedures can control that risk, but adjustment for multiple comparisons is not reported in the registry record. The status of each secondary outcome in any prespecified testing hierarchy is also not reported. The results are therefore useful as secondary evidence and as questions for further study, but should not be interpreted as if each were an independently confirmed primary finding.

The posted values should be read with attention to the stated population and timeframe for each outcome. The diabetes analysis is restricted to participants with prediabetes at baseline, unlike the broader primary outcome analysis. The registry does not report all details needed to assess missing observations, subgroup rules, or the full analysis plan across the secondary measures.

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

• Time From Randomization to Conversion to Type 2 Diabetes Mellitus (T2DM) for Participants With Prediabetes at Baseline
• Time From Randomization to First Occurrence of the Individual Components of MACE+
• Time From Randomization to Event of All-cause Mortality
• Time From Randomization to Conversion to Normal Glucose Homeostasis in Participants With Prediabetes at Baseline
• Time From Randomization to Conversion to T2DM for Participants Without Any Type of Diabetes at Baseline
• Change From Baseline in HbA1c at Month 6 in Participants With T2DM at Baseline
• Time From Randomization to Event of New Onset Renal Impairment or Worsening Existing Renal Impairment in All Participants
• Time From Randomization to Event of New Onset Renal Impairment or Worsening Existing Renal Impairment in Participants With Prediabetes at Baseline

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time from randomization to first MACE, a time-to-event measure. Each participant contributes follow-up until an event or censoring. The registry states that the analysis used the intent-to-treat set, counted events occurring on and off treatment, and censored participants with no event at their last study contact or at the visit following sponsor notification of study completion, whichever occurred first. How censoring was handled in other circumstances is not reported in the registry record.

What does Kaplan-Meier estimation do?

In general, the Kaplan-Meier method estimates the probability of remaining free of the event over time while accounting for participants whose follow-up ends before an event is observed. A censored participant contributes information up to the point of censoring but is not treated as having experienced the event. This approach relies on assumptions about censoring; in general, the estimate can be biased if censoring is related to future event risk in a way the analysis does not account for. The registry names Kaplan-Meier estimation but does not report diagnostic checks or sensitivity analyses for those assumptions.

What does Greenwood’s formula contribute?

In general, Greenwood’s formula estimates the sampling variance of the Kaplan-Meier estimate. That variance is used to express uncertainty, commonly through a confidence interval. It does not remove uncertainty or correct bias from an inappropriate censoring process. The registry says Greenwood’s formula was used for the primary outcome, but does not report further computational details.

How should the hazard ratio be read?

The posted comparison reports a hazard ratio for placebo versus lorcaserin 10 mg. In general, a hazard ratio compares the instantaneous event rates between groups among participants who have not yet experienced the event, under the model and assumptions used. A value of 1 represents equal hazards in the comparison’s orientation. A value on one side of 1 indicates a higher relative hazard for the group in the numerator of the reported comparison, and a value on the other side indicates a lower relative hazard. It is not an absolute risk difference, a ratio of cumulative event probabilities, or a ratio of median times.

The registry labels the primary analysis as non-inferiority. In general, a non-inferiority analysis evaluates whether a confidence bound excludes a prespecified degree of disadvantage, defined by a margin. The margin and other detailed testing rules are not reported in the registry record. The reported p-value alone cannot substitute for those details, and the direction and interpretation of a non-inferiority test depend on how the comparison and margin are specified.

What does the confidence interval show?

In general, a confidence interval gives a range of estimates compatible with the data under the statistical method used. Its width reflects precision, while its position reflects the estimate. The primary reported interval is a 97.5% confidence interval from 0.842 to 1.198 around a hazard ratio of 1.005. The interval includes 1, but the non-inferiority question requires comparison with the margin, which is not reported. The secondary analyses use reported 95% confidence intervals. Confidence levels and analysis goals should be kept distinct when reading estimates from different outcomes.

What can the reported p-values establish?

A p-value measures how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions were correct. It is not the probability that the null hypothesis is true, nor does it measure clinical importance. The primary p-value is reported as < 0.001 within an analysis classified as non-inferiority. Because the margin and full testing details are absent from the registry record, the p-value cannot independently establish the non-inferiority conclusion for a reader. Secondary p-values also need to be considered alongside their confidence intervals, analysis populations, and the number of outcomes assessed.

Why can time-to-event methods be useful?

In general, time-to-event methods make use of event timing and can accommodate different follow-up durations through censoring. They are useful when not every participant has an observed event by the end of follow-up. Their interpretation depends on follow-up quality, the censoring process, and the model used to compare groups. The registry provides the outcome method and censoring description for the primary analysis, but does not report detailed model diagnostics, proportional-hazards checks, or sensitivity analyses. Those omissions limit independent assessment of the assumptions behind the reported hazard ratio.

The outcome record gives median as the parameter type, but arm-specific median values and confidence limits are null. The posted comparison therefore supports interpretation of the reported hazard ratio and interval, not a comparison of median event times. No unreported median should be inferred from the hazard ratio or from the stated follow-up period.

11. Confidence Intervals and Precision

The primary hazard ratio is 1.005, with a 97.5% confidence interval from 0.842 to 1.198. The estimate lies close to 1, while the interval spans values on either side of 1. In general, a confidence interval describes the uncertainty around an estimate under the method used; it does not guarantee that the true effect lies within that particular interval or account for bias from design or analysis limitations. The reported interval is not narrow enough to identify a single precise relative effect.

The interval includes 1, which is the no-relative-hazard-difference value for a hazard ratio. That observation is relevant to a conventional superiority interpretation, but the registry identifies the primary analysis as non-inferiority. Evaluating non-inferiority requires the margin and the appropriate confidence-bound rule. The margin is not reported in the registry record, so the interval alone cannot determine whether the study met its non-inferiority objective.

The primary confidence level is 97.5%, while the secondary comparisons are reported with 95% confidence intervals. These are not interchangeable summaries: the confidence level reflects the interval procedure and should be read alongside the analysis objective. The primary p-value is reported as < 0.001, but the registry does not give the margin or full testing specifications necessary to reconcile that value with a non-inferiority decision.

For the secondary outcomes, one reported interval does not include 1 and two include 1. Their precision and interpretation differ by endpoint, and the record does not provide absolute risks for these comparisons. A confidence interval around a hazard ratio also does not quantify the range of absolute event rates. The posted intervals should thus be treated as estimates of relative effects with uncertainty, not as direct measures of participant-level prognosis.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are based on the observed effect and are not the trial’s original design calculation. For the time-to-event comparisons, the figures are total events, not participants per arm. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect targeted is the stated fraction of the observed effect, and the event calculations use the Schoenfeld method.

The 80% power column represents the planned event total under the stated assumptions that would give an 80% chance of detecting the specified effect if that effect and the planning model were correct. The 90% column describes the corresponding event total for a 90% chance. These are planning concepts, not guarantees about what a future study will find. A smaller effect is harder to distinguish from chance variation, so the planning illustration requires more events when the target effect is smaller.

The illustration is not observed power. It does not report the probability that the completed study detected its true effect, and it should not be used as a substitute for the estimated hazard ratio and its confidence interval. The registry does not report the original sample-size justification, its target event count, or the assumptions used when the trial was designed. The planning figures are therefore best read as hypothetical illustrations under their stated assumptions, separate from the observed enrollment and results.

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 = 1.005, so ln(HR) = 0.0050.
2. d = 4 × (1.96 + 0.842)² / [ln(1.005)]² = 1,262,102.5, rounded up to 1,262,103 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 <- 1.005                              # 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(2019264)
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 = 1,262,103 (80% power), 1,689,598 (90% power)
 75% of observed effect: events = 2,243,738 (80% power), 3,003,729 (90% power)
 50% of observed effect: events = 5,048,410 (80% power), 6,758,389 (90% power)
Simulated power with 1,262,103 events: 0.800 (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 primary analysis as a hazard ratio of 1.005, with a 97.5% confidence interval from 0.842 to 1.198 and p < 0.001. It identifies the method as the Primary Analytic Method and classifies the analysis as non-inferiority. These are the sponsor’s reported results. The record does not state the non-inferiority margin or provide the complete decision rule.

The recalculation associated with this analysis is a simple unadjusted calculation from posted summary statistics; it is not a replacement for the sponsor’s analysis. In this case, the discrepancy indicator is false, so no disagreement between the posted sponsor result and the recalculation is flagged. The sponsor’s own analysis takes precedence as the trial’s reported inferential result.

Agreement between a recalculation and the reported estimate does not supply missing protocol details. In particular, it cannot establish the non-inferiority margin, the analysis plan, or how interim monitoring was handled. The reported p-value should remain connected to the stated non-inferiority method rather than being recast as a conventional test of difference. Interpretation of the sponsor’s conclusion requires the margin and testing details, which are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports multiple endpoints and analyses, including a primary MACE outcome and secondary outcomes spanning diabetes, mortality, renal impairment, glucose homeostasis, MACE components, and HbA1c. It identifies the primary analysis as non-inferiority and reports an interim analysis. However, the interim-analysis plan, including its timing, any monitoring boundaries, and any adjustment to the significance level, is not reported in the registry record. The primary non-inferiority margin is also not reported.

Multiplicity concerns arise when statistical tests are conducted across several outcomes or analyses. In general, the more tests that are considered, the greater the chance of an apparently notable result arising by chance if no effect exists. A prespecified hierarchy or adjustment can address this issue, but the registry record does not report whether such a procedure was used for the secondary outcomes. The relative confirmatory status of the secondary analyses is not reported either. Their p-values should therefore be interpreted cautiously and in the context of the broader set of analyses.

The primary analysis population is described as the intent-to-treat set. Events were counted on and off treatment, and participants without events were censored at their last study contact or at the visit following sponsor notification of study completion, whichever occurred first. The record does not report detailed information about missing covariate data, loss to follow-up, reasons for censoring, or sensitivity analyses addressing missing outcomes. It also does not give complete analysis-population definitions for every secondary outcome.

These gaps do not show that the analyses were inappropriate; they limit what can be independently assessed from the registry record. In general, interpretation depends on whether the analysis plan was prespecified, how interim testing was controlled, and whether missingness and censoring could be related to outcome risk. Those details are not reported in the registry record, so the posted estimates should be considered with that uncertainty in mind.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: angina pectoris (2.4%), non-cardiac chest pain (2.2%), acute myocardial infarction (2.0%), angina unstable (1.9%), osteoarthritis (1.8%).

The registry lists serious adverse-event figures for both arms, along with the number at risk for those summaries. For placebo, 2021 serious adverse events are recorded among 5992 at risk; for lorcaserin 10 mg, 1974 are recorded among 5995 at risk. The record also lists 202 deaths for placebo and 219 for lorcaserin 10 mg. These are descriptive counts, not estimates of a treatment effect, and the registry excerpt does not provide a formal comparative safety analysis for these figures.

The most frequently listed serious adverse-event terms include angina pectoris at 2.4%, non-cardiac chest pain at 2.2%, acute myocardial infarction at 2.0%, angina unstable at 1.9%, osteoarthritis at 1.8%, and cardiac failure congestive at 1.8%. The record separately reports other adverse events, with 4788 among 5992 at risk for placebo and 4946 among 5995 at risk for lorcaserin 10 mg. The relationship between event counts and the number of participants affected is not further detailed in the available description.

Counts and listed percentages should be read as registry safety summaries, not as proof that an event was caused by treatment. Differences in follow-up, event definitions, and repeated events can affect comparisons. Details of adjudication, exposure-adjusted rates, and statistical testing for safety are not reported in the registry record.

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

The posted primary result describes the relative hazard of first MACE in the randomized comparison. The estimate is 1.005 and the 97.5% confidence interval ranges from 0.842 to 1.198. The interval includes 1 and allows for a range of relative effects. It does not demonstrate that the arms are exactly equivalent, nor does it establish a clinically meaningful benefit or harm on its own.

The registry labels the primary analysis non-inferiority and reports p < 0.001, but does not report the non-inferiority margin. Because the margin defines what degree of possible disadvantage would be considered acceptable, the reported result cannot be independently checked against that criterion from the registry record alone. The p-value should not be interpreted as proof of superiority or as a probability that the null hypothesis is true.

The hazard ratio is a relative time-to-event measure. It does not state how many participants experienced MACE, how large any absolute risk difference was, or how an individual participant would fare. The registry describes a follow-up endpoint through Month 42 and a censoring rule, but does not report the arm-specific median event times or primary event counts in the posted outcome summary. Those quantities cannot be inferred from the hazard ratio.

The secondary findings concern different outcomes and, in some cases, a subgroup defined by prediabetes at baseline. They should not be treated as interchangeable with the primary MACE result. Because a multiplicity adjustment is not reported, a secondary association—particularly one among numerous analyses—has less confirmatory weight. Safety counts likewise provide descriptive context, not a causal comparison by themselves.

Overall, the registry supports a careful account of the reported estimates and their uncertainty, but not a broad conclusion that lorcaserin is effective, ineffective, safe, or unsafe. Such claims would require the complete analysis plan, non-inferiority margin, event and absolute-risk data, and fuller safety and missing-data information, much of which is not reported in the registry record.

18. Why This Trial Matters Statistically

This trial raises several important statistical issues in a setting where both event timing and long-term follow-up matter. The primary outcome combines myocardial infarction, stroke, and cardiovascular death, and is analyzed as time to first event. That structure requires attention to censoring and to the assumptions behind time-to-event comparisons. The registry reports a Kaplan-Meier approach and Greenwood formula, but the detail available for evaluating assumptions and sensitivity analyses is limited.

The non-inferiority framework is also central to interpretation. A hazard ratio close to 1 can look reassuring at first glance, but a non-inferiority claim depends on a prespecified margin and an appropriate confidence-bound rule. The margin is not reported in the registry record. This illustrates why a point estimate and p-value cannot be interpreted apart from the design and decision criteria that define the trial’s objective.

The study also includes a broad set of secondary outcomes, including cardiometabolic and renal measures. Such outcomes can be informative, but a large collection of tests makes prespecification and multiplicity handling important. The registry’s listing of many analyses, without reporting adjustment details, means secondary results should be treated as supportive or exploratory rather than automatically confirmatory.

Finally, planning illustrations based on observed effects are distinct from the original sample-size justification and from the uncertainty in the observed treatment comparison. Separating a hypothetical planning calculation from observed evidence helps prevent mistaken claims about achieved power. Together, these considerations show why statistical interpretation depends not only on an estimate, but also on the endpoint, analysis plan, assumptions, and completeness of reporting.

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.

Several limitations are specific to the information recorded for this study. The primary analysis is classified as non-inferiority, yet the non-inferiority margin and full decision rule are not reported in the registry record. This prevents an independent reader from checking the central criterion against the reported confidence interval and p-value. The record also mentions an interim analysis without reporting its timing or statistical safeguards.

The primary outcome description gives a censoring rule and identifies the intent-to-treat set, but does not provide detailed information about loss to follow-up, reasons for censoring, or sensitivity analyses. Model diagnostics, including checks relevant to interpretation of the hazard ratio, are not reported. Arm-specific primary event counts, absolute risks, and median times are not available in the posted outcome values, limiting translation of the relative estimate into absolute terms.

Secondary outcomes vary in population and timeframe, and adjustment for multiple comparisons is not reported. Complete analysis-population and missing-data details are not given for all secondary measures. Safety summaries list event counts and selected terms, but detailed comparative analyses, exposure-adjusted rates, and adjudication information are not reported.

The registry lists enrollment of 14673, while 6000 participants are listed in each arm for the primary outcome. The record does not explain the relationship between those figures in the outcome description, so they should not be reconciled by assumption. The original sample-size justification and study-specific design assumptions are also not reported; planning illustrations based on the observed effect do not fill that gap.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Effect of Long-term Treatment With BELVIQ (Lorcaserin HCl) on the Incidence of Major Adverse Cardiovascular Events and Conversion to Type 2 Diabetes Mellitus in Obese and Overweight Subjects With Cardiovascular Disease or Multiple Cardiovascular Risk Factors — NCT02019264.
• Registry record last updated 2019-07-16; status last verified 2017-11.
• Results first posted 2019-07-16.
• 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

NCT02019264 is a completed phase 4 randomized, double-blind, placebo-controlled, parallel-group study sponsored by Eisai Inc. The registry title describes long-term BELVIQ (lorcaserin HCl) treatment and outcomes involving major adverse cardiovascular events and conversion to type 2 diabetes among overweight and obese participants with cardiovascular disease or multiple cardiovascular risk factors. Enrollment is listed as 14673. The study start date is 2014-01-24, and primary completion is listed as 2018-05-14.

The primary outcome was time from randomization to first MACE through Month 42, analyzed using Kaplan-Meier estimation and Greenwood formula. The reported hazard ratio for placebo versus lorcaserin 10 mg is 1.005, with a 97.5% confidence interval from 0.842 to 1.198 and p < 0.001. The analysis is classified as non-inferiority, but the margin is not reported in the registry record.

Secondary outcomes include diabetes, mortality, glucose homeostasis, renal impairment, MACE components, and HbA1c. The record lists 15 outcome measures and 20 analyses. The posted findings require cautious interpretation because key details about multiplicity, interim analysis, and several analysis assumptions are not reported.