PRELUDE:Study to Investigate the Prevention of Relapse in Lymphoma Using Daily Enzastaurin: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for PRELUDE:Study to Investigate the Prevention of Relapse in Lymphoma Using Daily Enzastaurin (NCT00332202), a randomized phase 3 study. The primary outcome is Overall Disease-Free Survival.

2. Clinical Question

The clinical question is about the time until the first of two events: disease recurrence, defined using the study’s progressive-disease criteria, or death from any cause. It is not a question about tumor response alone, because death is also included in the endpoint. The registry record describes recurrence assessment as following International Working Group recommendations and defines progressive disease using changes in the sum of the product of diameters of identified abnormal nodes or the appearance of a new lesion.

The principal comparison is between the assigned groups, rather than a comparison based on treatment actually received. The record identifies the study as randomized and reports the primary analysis population as all randomized participants. The main statistical result is a hazard ratio from a log-rank analysis, alongside median disease-free survival in each group. These statistics address different aspects of the time-to-event data: the medians describe when the estimated survival curves reach their midpoint, while the hazard ratio summarizes the relative event rate over follow-up under the model and analysis used.

3. Trial Design

PRELUDE was a phase 3, randomized, quadruple-masked, parallel-group study sponsored by Eli Lilly and Company. The registry record reports enrollment of 758 participants. The study compared daily enzastaurin with placebo, with the summary describing a 2 to 1 chance of assignment to enzastaurin. The trial status is completed. Its recorded start was 2006-06, and its primary completion was 2013-04.

A parallel-group design assigns participants to one study group and follows them over time. Randomization is intended, in general, to make the groups comparable at the time of assignment with respect to both measured and unmeasured characteristics. Masking is intended, in general, to reduce the influence of knowledge about assigned treatment on participant experience, care, assessment, or analysis. The registry record identifies quadruple masking but does not specify in the record excerpt which roles were masked.

The primary endpoint was overall disease-free survival, measured from study enrollment to objectively determined recurrence or death from any cause. The primary analysis population was all randomized participants. Participants who were alive and had not progressed were censored at their last assessable disease-free assessment. The record reports that censored participant data numbered 369 (73.2%) in the enzastaurin group and 180 (70.9%) in the placebo group.

The record lists secondary outcomes covering disease-free and event-free survival, overall survival, treatment-emergent adverse events, quality-of-life scores, and translational research comparing DLBCL cell subgroups. Detailed results are not reported in the registry record for every listed outcome. The original design assumptions, including the trial’s own sample-size justification, are not reported in the registry record. Neither are details of any interim analyses or the full statistical analysis plan.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants. DFS is censored at the last assessable disease free assessment for participants who are alive or have not progressed. The number of censored participant data for enzastaurin and placebo is 369 (73.2%) and 180 (70.9%), respectively.

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 (ITT): All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Overall Disease-Free Survival, measured over Baseline to Measured Progressive Disease or Death from Any Cause (up to 80.30 months).

Overall disease-free survival (DFS) is a time-to-event endpoint. For each participant, the time begins at study enrollment and ends at the first objectively determined disease recurrence or death from any cause. The registry record says that DFS was assessed according to International Working Group recommendations. It defines progressive disease as a specified increase from the lowest point in the sum of the product of diameters of previously identified abnormal nodes for partial or nonresponders, or the appearance of any new lesion during or at the end of therapy.

DFS is used because it captures whether participants remain alive without documented progression, and it incorporates both recurrence and death into one outcome. In general, a time-to-event measure retains information about when an event occurs, rather than reducing follow-up to only whether an event happened by a particular cut-off. That can be useful when participants have different lengths of observation or when some have not experienced an event by the time follow-up ends.

Participants who remained alive and had not progressed were censored at their last assessable disease-free assessment. Censoring means that the endpoint event was not observed by that point; it does not establish what happened after the last assessment. The interpretation of a time-to-event analysis depends in part on how follow-up and censoring are handled. The registry record gives the censoring counts and proportions for the two groups, but further details about missing assessments or the handling of other forms of missing data are not reported in the registry record.

7. Results Posted in the Registry

• Enzastaurin: Arm A - Experimental vs Placebo: Arm B - Control: hazard ratio 0.92 (95% CI 0.69–1.22), reported p = 0.541 (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.

Disease Free Survival at 2 Years

• 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:
  • Enzastaurin: Arm A - Experimental: 0.8% (4/504) versus 0.8% (2/254) on control; risk difference 0.0 percentage points (95% CI -1.3 to 1.3), risk ratio 1.01 (0.19–5.47); unadjusted two-proportion z-test p = 0.993.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enzastaurin: Arm A - Experimental and the control. The interval gives the range of effects that remain compatible with the data.

Event-Free Survival at 2 Years

• 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:
  • Enzastaurin: Arm A - Experimental: 0.8% (4/504) versus 0.8% (2/254) on control; risk difference 0.0 percentage points (95% CI -1.3 to 1.3), risk ratio 1.01 (0.19–5.47); unadjusted two-proportion z-test p = 0.993.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enzastaurin: Arm A - Experimental and the control. The interval gives the range of effects that remain compatible with the data.

Translational Research: DFS Participants With Diffuse Large B-cell Lymphoma (DLBCL) Germinal-center B-cells (GCB) Versus Non-germinal-center B-cells

• 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:
  • Enzastaurin: Arm A - Experimental With Germinal-center B-cells: 75.9% (60/79) versus 66.7% (20/30) on control; risk difference 9.3 percentage points (95% CI -10.0 to 28.6), risk ratio 1.14 (0.86–1.51); unadjusted two-proportion z-test p = 0.327.
  • Enzastaurin: Arm A - Experimental Non-germinal-center B-cells: 76.2% (48/63) versus 66.7% (20/30) on control; risk difference 9.5 percentage points (95% CI -10.4 to 29.4), risk ratio 1.14 (0.86–1.52); unadjusted two-proportion z-test p = 0.333.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enzastaurin: Arm A - Experimental With Germinal-center B-cells and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enzastaurin: Arm A - Experimental Non-germinal-center B-cells and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning disease-free and event-free survival, overall survival, adverse events, quality of life, and translational comparisons by DLBCL cell subgroup. The available secondary results extend the picture beyond the primary endpoint, but the registry record does not report detailed results for every listed outcome. The posted secondary evidence is therefore incomplete as a full account of all prespecified secondary questions.

Overall, the secondary information does not supply a basis for overturning the primary interpretation. The two-year survival summaries and the translational subgroup findings are compatible with uncertainty, and the reported subgroup confidence intervals are broad. The registry’s reported Cox comparisons for the cell subgroups do not show a statistically clear difference under their reported tests. These analyses concern narrower questions and smaller groups than the full randomized comparison, so they should be regarded as supporting context rather than as decisive evidence about the primary endpoint.

In general, secondary outcomes can help assess whether the primary result is accompanied by a consistent pattern across related measures or whether different aspects of outcome suggest a different interpretation. However, examining many endpoints and subgroups increases the opportunity for chance findings. Unadjusted p-values do not account for that wider set of comparisons. The multiplicity adjustment strategy is not reported in the registry record, so isolated secondary p-values deserve less weight than the primary result and should not be treated as confirmatory evidence on their own.

Quality-of-life measures, overall survival, and treatment-emergent adverse events are listed among the secondary outcomes, but their complete results are not reported in the registry record information available for this analysis. Absence of detailed results in the record should not be mistaken for a finding of no difference. It means those outcomes cannot be fully evaluated from the posted results.

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

• Disease Free Survival at 2 Years
• Event-Free Survival
• Event-Free Survival at 2 Years
• Overall Survival
• Number of Participants With Treatment-Emergent Adverse Events
• Quality of Life: Change From Baseline in Functional Assessment of Cancer Therapy - Lymphoma (FACT-Lym) Score
• Change From Baseline in EuroQol-5D (EQ-5D) Score
• Translational Research: DFS Participants With Diffuse Large B-cell Lymphoma (DLBCL) Germinal-center B-cells (GCB) Versus Non-germinal-center B-cells

9. Statistical Interpretation

10. Statistical Methods Explained

Overall DFS is analyzed as a time-to-event outcome because the endpoint records both whether an event occurred and the time until it occurred. The primary endpoint combines objectively determined recurrence and death from any cause. The registry record reports median DFS for each treatment group and a hazard ratio from a log-rank analysis. Those summaries are complementary: the medians describe the midpoint of each estimated event-free survival distribution, while the hazard ratio compares event rates over follow-up in the form used by the analysis.

What does a median time-to-event estimate mean?

In general, the median is the time at which the estimated proportion remaining free of the endpoint event reaches one half. It is not the arithmetic average of individual event times. In this trial, the registry reports median DFS of 42.8 months for enzastaurin and 43.1 months for placebo. Each median has a 95% confidence interval, which expresses uncertainty in the estimate under the statistical procedure used. The intervals are wide, so the median estimates themselves should not be treated as exact event times for all participants.

What does the hazard ratio describe?

In general, a hazard is the rate at which events occur among participants who have not yet experienced the event, at a particular point in follow-up. A hazard ratio compares those rates between groups. A value of 1 corresponds to equal hazards under this measure; values on either side indicate different relative rates. The sponsor-reported hazard ratio was 0.92, with a 95% confidence interval of 0.689 to 1.216. Because the interval includes 1, the data are compatible with equal hazards as well as with effects in either direction within the interval.

A hazard ratio is not a difference in median survival time, and it is not a direct estimate of the probability that an individual participant will have an event. Its interpretation depends on the event definition, follow-up, censoring, and analysis assumptions. The registry record reports the hazard ratio and identifies the method as log rank. Further details about the fitted model, including any covariate adjustment, are not reported in the registry record.

How does the log-rank test fit into the comparison?

In general, the log-rank test compares the event experience of groups across follow-up while accounting for the ordering of event times and censoring. It is commonly used for time-to-event outcomes. The registry reports a log-rank method and a p-value of 0.541 for the primary comparison. A p-value is calculated under a null hypothesis and the test’s assumptions; it is not a measure of effect size or a probability that the observed result occurred by chance. The hazard ratio and confidence interval communicate the estimated direction and precision, while the p-value addresses compatibility with the null comparison under the test.

What does censoring mean in this analysis?

Censoring occurs when a participant’s event time is not observed during the available follow-up. For the primary endpoint, the record says DFS was censored at the last assessable disease-free assessment for participants who were alive or had not progressed. The number of censored participant data was 369 (73.2%) for enzastaurin and 180 (70.9%) for placebo. In general, a censored participant contributes information up to the last known event-free assessment, but the analysis does not treat that participant as having remained event-free indefinitely. Time-to-event methods rely on assumptions about the relation between censoring and future event risk; details of how those assumptions were assessed are not reported in the registry record.

Why are confidence intervals important?

In general, a confidence interval gives a range of values compatible with the observed data and the method’s assumptions. It helps distinguish a point estimate from its precision. A narrow interval indicates greater precision than a wide one, though precision does not by itself establish that an estimate is unbiased or clinically important. For the primary hazard ratio, the interval extends from 0.689 to 1.216 and crosses 1. This conveys uncertainty on both sides of the equal-hazard value. The reported p-value of 0.541 is consistent with the absence of a statistically clear difference under the reported test, but neither the interval nor the p-value demonstrates equivalence.

The registry record also lists secondary time-to-event and binary outcomes. Methods for interpreting them depend on their endpoint definitions and analysis populations. The record does not report detailed sponsor analyses for every listed outcome. Where there are multiple outcomes or subgroup comparisons, general statistical practice treats unadjusted findings cautiously because the chance of at least one apparently unusual result can rise as more comparisons are examined. The registry record does not report whether or how multiplicity was addressed.

11. Confidence Intervals and Precision

Precision is reflected in the width of an estimate’s confidence interval. The primary hazard ratio was 0.92, with a 95% confidence interval from 0.689 to 1.216. This interval includes 1, so it is compatible with no relative difference in hazards as well as with values indicating different hazards in either direction. It is therefore more informative to read the estimate together with its interval than to focus on the point estimate alone.

The median DFS estimates were 42.8 months for enzastaurin and 43.1 months for placebo. Their respective 95% confidence intervals were 0.03 to 76.81 months and 0.03 to 80.3 months. These ranges are broad, indicating substantial uncertainty around the medians. The interval endpoints should not be interpreted as predictions for individual participants or as a range containing a fixed proportion of individual survival times.

In general, confidence intervals quantify statistical uncertainty under the analysis method and its assumptions; they do not account for every potential source of bias, such as problems in outcome measurement or incomplete follow-up. The record reports censoring of 369 (73.2%) enzastaurin participants and 180 (70.9%) placebo participants at their last assessable disease-free assessment. Those counts help describe the observed data, but do not by themselves establish whether censoring was informative.

The reported p-value of 0.541 is not a precision measure. It does not tell readers how large or small the true effect must be, nor establish equivalence. The confidence interval is the more direct guide to the range of hazard ratios compatible with the primary estimate under the reported analysis.

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 illustration for the primary time-to-event comparison is expressed as the total number of events required, not participants per arm. It uses the observed hazard-ratio effect as a reference and also considers planning for 75% and 50% of that observed effect. The event totals are planning quantities; they are not the numbers of participants enrolled in this trial and should not be confused with its observed event count.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect defined as the stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record. These planning figures are an illustration based on the observed effect, not a reconstruction of the original protocol.

The 80% power column gives the calculated total event count for a design intended to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect is real. The 90% power column gives the corresponding event count for a design intended to have a 90% chance. These are design targets, not guarantees that a study will detect an effect. In general, a smaller effect is harder to distinguish from random variation and requires more information. Accordingly, planning for a smaller fraction of the observed effect requires more events.

This is not observed power. It is a planning illustration, and its estimates depend on the assumptions used. The outcome is time to event, so the relevant quantity in these calculations is events, rather than a fixed number of participants per arm. Actual enrollment and the number and timing of events are distinct from the planning totals.

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 = 0.920, so ln(HR) = -0.0834.
2. d = 4 × (1.96 + 0.842)² / [ln(0.920)]² = 4,515.7, rounded up to 4,516 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 <- 0.92                              # 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(332202)
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 = 4,516 (80% power), 6,046 (90% power)
 75% of observed effect: events = 8,028 (80% power), 10,748 (90% power)
 50% of observed effect: events = 18,063 (80% power), 24,182 (90% power)
Simulated power with 4,516 events: 0.801 (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. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 14,325 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 758 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 42.8          # control-arm median, months (converted from the posted unit)
hr          <- 0.92          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
     Analysis               Value Efficacy
    IA 1: 33%                   Z   3.7103
     N: 13738         p (1-sided)   0.0001
 Events: 2040        ~HR at bound   0.8485
    Month: 23    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.92   0.0338
    IA 2: 67%                   Z   2.5114
     N: 14326         p (1-sided)   0.0060
 Events: 4079        ~HR at bound   0.9244
    Month: 37    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.92   0.5603
        Final                   Z   1.9930
     N: 14326         p (1-sided)   0.0231
 Events: 6118        ~HR at bound   0.9503
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.92   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The primary comparison is the sponsor-reported analysis: a log-rank hazard ratio of 0.92, with a 95% confidence interval of 0.689 to 1.216 and p = 0.541. That analysis is the appropriate primary result to emphasize. The registry record does not report a discrepancy between the sponsor’s analysis and a separate recalculation, and the time-to-event interpretation uses the sponsor-reported hazard ratio.

A hazard ratio analysis uses event-time information and censoring, whereas a simple recalculation from summary counts would not reproduce the same analysis. The record’s primary result therefore should not be replaced by a calculation that ignores the timing of recurrence or death. The reported log-rank comparison and its confidence interval provide the trial’s stated inferential result.

The point estimate is close to 1, and the confidence interval crosses 1. The p-value is 0.541. Together, these indicate that the reported analysis did not establish a statistically clear difference in overall DFS. They do not prove that the groups are equivalent, and they do not establish the probability that either treatment is beneficial. The estimates should be interpreted in conjunction with the endpoint definition and the reported censoring of participants at their last assessable disease-free assessment.

For translational subgroup comparisons, the registry also reports Cox regression hazard ratios, confidence intervals, and p-values. Those are separate secondary analyses and should not be substituted for the primary overall comparison. The registry record does not report enough detail to characterize all model specifications or to determine whether the subgroup results were adjusted for multiple comparisons.

16. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is identified as all randomized participants. For DFS, participants who were alive or had not progressed were censored at their last assessable disease-free assessment. The registry reports 369 censored participants (73.2%) in the enzastaurin group and 180 (70.9%) in the placebo group. This indicates that many participants did not have an observed endpoint event before their last assessable disease-free assessment. Censoring is part of time-to-event analysis, but its interpretation depends on follow-up and assumptions about why observation ends.

The registry record does not report the full approach to missing data, including details about missing assessments, reasons for loss of observation, or sensitivity analyses for alternative assumptions. It also does not report how missing data were handled for the secondary outcomes. The censoring rule for the primary endpoint is described, but that is not a complete account of all missing-data procedures.

Multiplicity is relevant because the record lists multiple secondary outcomes and includes subgroup comparisons. In general, testing many outcomes can increase the chance of observing at least one apparently notable result by chance. Adjustment procedures can address this issue, but may also change how evidence is interpreted. The registry record does not report a multiplicity adjustment plan, a hierarchy of hypotheses, or whether secondary analyses were intended to be confirmatory or exploratory. The secondary p-values should consequently be read with caution, particularly when considered separately from the primary result.

The original sample-size justification, details of interim analyses, and the complete statistical analysis plan are not reported in the registry record. The reported analysis identifies the primary endpoint, population, censoring rule, log-rank method, hazard ratio, confidence interval, and p-value, but does not provide every detail needed to reconstruct the full analysis. The record also does not report which roles were masked under the stated quadruple masking.

17. Safety Results

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

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: pneumonia (2.8%), pulmonary embolism (1.6%), febrile neutropenia (1.2%), syncope (1.2%), hepatitis b (1.2%).

The registry reports serious adverse event terms and overall adverse-event counts for participants at risk. For serious adverse events, pneumonia is listed at 2.8%, pulmonary embolism at 1.6%, and febrile neutropenia, syncope, and hepatitis b at 1.2% each; anaemia is listed at 1.0%. These are the leading serious terms recorded in the available information, not a complete description of every event or its clinical course.

For the enzastaurin group, the record lists 493 participants at risk for serious events and 135 with an event; for placebo, it lists 249 at risk and 72 with an event. The corresponding all-event counts are 406 of 493 and 185 of 249. These figures describe participant counts, not event rates over a specified person-time, and should be interpreted using the registry’s reporting definitions. The record does not report deaths in these safety data.

Adverse-event comparisons can be affected by observation time, event definitions, and whether participants experienced more than one event. The registry record does not provide enough detail to evaluate those factors or to establish a causal interpretation of individual event terms. The numbers describe reported safety events; they do not by themselves establish a treatment benefit or risk balance.

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

The primary result estimates overall DFS in the randomized groups and reports no statistically clear difference under the sponsor’s log-rank analysis. The hazard ratio was 0.92, its 95% confidence interval was 0.689 to 1.216, and the reported p-value was 0.541. The median DFS estimates were 42.8 months for enzastaurin and 43.1 months for placebo. Taken together, these results indicate that the posted analysis did not provide strong statistical evidence of a difference in the primary endpoint.

That conclusion is not the same as demonstrating that the treatments have identical effects. The confidence interval includes the equal-hazard value and also allows estimates on either side. A non-significant p-value cannot establish equivalence or rule out effects that the study may not have estimated precisely. The registry record does not report an equivalence or noninferiority framework for the primary question.

The endpoint combines recurrence and death, so the result concerns time to either of those events as defined in the protocol record. It does not separately establish effects on recurrence alone, overall survival alone, quality of life, or every safety outcome. Those questions require their own results and analyses. Some secondary outcomes are listed, but full results are not reported in the registry record.

The findings should also be understood in the context of censoring: 369 (73.2%) participants in the enzastaurin group and 180 (70.9%) in the placebo group were censored at their last assessable disease-free assessment. Censoring is expected in time-to-event studies, but the record does not provide full detail on follow-up completeness or sensitivity analyses. The reported statistics therefore describe the available analysis under its stated endpoint and censoring approach; they do not settle every question about the comparison.

These statistical results are not medical advice and do not determine what any individual should receive. They describe what the registry’s posted trial analysis estimates, with the uncertainty reflected in the confidence interval and the limitations of the reported information.

19. Why This Trial Matters Statistically

This trial illustrates why a time-to-event endpoint should be read through more than one statistic. The median DFS values describe the midpoint of the estimated event-time distributions, while the hazard ratio summarizes the relative event rate across follow-up. The log-rank p-value addresses evidence against a null comparison under its test assumptions. None of these alone provides a complete account of the effect or its precision.

It also demonstrates the distinction between absence of clear statistical evidence and evidence of no effect. The primary hazard-ratio interval crosses 1, and the reported p-value is 0.541, but the interval remains broad. A careful interpretation therefore acknowledges both the lack of a statistically clear difference and the uncertainty around the estimate, rather than converting a non-significant result into a claim of equivalence.

The censoring figures matter for interpretation because time-to-event methods use the period during which participants are known to remain event-free. The record states that censored participants were followed through their last assessable disease-free assessment. Understanding the endpoint definition and censoring rule is essential to reading the hazard ratio and median estimates correctly.

Finally, the registry lists multiple secondary outcomes and subgroup questions, while the multiplicity plan and complete results for all outcomes are not reported. This is a useful reminder that a primary result should remain the anchor for interpretation, while secondary findings require attention to precision, analysis plans, and the number of comparisons. The planning event counts are illustrations based on the observed effect, not evidence about the trial’s original design or its achieved power.

20. Limitations

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

The registry record does not report the original sample-size justification, the trial’s own design assumptions, interim analyses, or the complete statistical analysis plan. It identifies the primary endpoint and reports the sponsor’s log-rank hazard ratio, but does not provide enough detail to reconstruct every analysis decision. Details about allocation concealment and which roles were masked are also not reported in the registry record.

For the primary endpoint, the record gives the censoring rule and group-specific censored counts, but does not describe all reasons for censoring, the completeness of follow-up, or sensitivity analyses. The confidence intervals around the primary hazard ratio and median estimates are broad. Thus, the posted result is uncertain and should not be interpreted as proof of equivalence.

The secondary-outcome record is incomplete: several outcomes are listed, but detailed results are not reported in the registry record for all of them. The multiplicity strategy is also not reported. The translational subgroup comparisons have limited group sizes and broad intervals, so they cannot be treated as precise estimates of subgroup effects. The record does not establish whether these analyses were prespecified or confirmatory.

The safety information lists leading serious adverse-event terms and counts, but does not provide full event-level context, person-time, or death counts in the reported safety data. These constraints limit comparisons based solely on the listed counts. More generally, registry summaries are not a substitute for a complete account of trial conduct, data quality, and analysis decisions.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: PRELUDE:Study to Investigate the Prevention of Relapse in Lymphoma Using Daily Enzastaurin — NCT00332202.
• Registry record last updated 2018-09-10; status last verified 2018-09.
• Results first posted 2018-09-10.
• 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.

24. Record Summary

PRELUDE was a completed, randomized, quadruple-masked, parallel-group phase 3 study of daily enzastaurin versus placebo in lymphoma, with the study summary identifying DLBCL as the target population. The registry reports enrollment of 758 participants and a 2 to 1 chance of assignment to enzastaurin.

The primary endpoint was overall DFS, defined as time from enrollment to objectively determined recurrence or death from any cause. The sponsor-reported log-rank hazard ratio was 0.92 (95% confidence interval 0.689 to 1.216; p = 0.541). Median DFS was 42.8 months with enzastaurin and 43.1 months with placebo.

The primary result does not show a statistically clear difference, while the confidence interval leaves uncertainty about the relative effect. The record reports censoring at the last assessable disease-free assessment and provides selected secondary and safety results. The full statistical plan, multiplicity approach, and detailed results for all listed secondary outcomes are not reported in the registry record.