Letermovir (MK-8228) Versus Placebo in the Prevention of Clinically-Significant Cytomegalovirus (CMV) Infection in Adult, CMV-Seropositive Allogeneic Hematopoietic Stem Cell Transplant Recipients (MK-8228-001): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Letermovir (MK-8228) Versus Placebo in the Prevention of Clinically-Significant Cytomegalovirus (CMV) Infection in Adult, CMV-Seropositive Allogeneic Hematopoietic Stem Cell Transplant Recipients (MK-8228-001) (NCT02137772), a randomized phase 3 study. The primary outcome is Percentage of Participants With Clinically-significant CMV Infection up to Week 24 Post-transplant.

2. Clinical Question

The clinical question concerns prevention over a defined period after transplant, rather than CMV infection at any time or in any population. The trial record describes a hypothesis that letermovir would be superior to placebo for preventing clinically-significant CMV infection through Week 24. The endpoint combines a disease outcome with a treatment decision made in response to documented viremia and clinical condition. Consequently, an event could be counted because of end-organ disease or because pre-emptive therapy was initiated.

The comparison is between randomized groups, with placebo serving as the control. Random assignment supports a comparative interpretation of the groups, while the prespecified population definition and endpoint definition establish which participants and events contribute to the primary result. This question does not directly address people outside the stated adult, CMV-seropositive transplant population, or outcomes beyond the recorded follow-up window.

3. Trial Design

This was a Phase III, randomized, double-masked, parallel-group, placebo-controlled clinical trial sponsored by Merck Sharp & Dohme LLC. It evaluated letermovir for prevention of clinically-significant CMV infection in adult, CMV-seropositive recipients of an allogeneic hematopoietic stem cell transplant. The registry record lists enrollment of 570 and trial status as completed. The recorded start date was 2014-06-06, and the primary completion date was 2016-08-08.

Participants were assigned to letermovir or placebo. Letermovir was administered orally or intravenously once daily for up to 14 weeks, starting up to Day 28 post-transplant. The dose depended on concomitant cyclosporin A use: 240 mg once daily for participants receiving it and 480 mg once daily for those not receiving it. Placebo was administered in a formulation intended to mimic the number of letermovir tablets according to cyclosporin A status. The registry record does not report further usable detail about the administration description beyond that account.

The primary analysis population was the Full Analysis Set: randomized participants who received at least one dose of study drug and had no detectable CMV DNA on Day 1, the randomization day. The primary outcome denominators were 325 for letermovir and 170 for placebo. These denominators are distinct from the stated enrollment, and the registry record does not report a complete accounting of the difference.

For the primary outcome, participants who prematurely discontinued or had a missing outcome through the 24-week visit window were considered treatment failures. Other details of the trial’s original design assumptions, such as its sample-size justification and planned interim analyses, are not reported in the registry record.

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: Screening could occur up to 15 days before Hematopoietic Stem Cell Transplant (HSCT) and no more than Day 28 post-transplant. From the time of screening to randomization, participants were tested weekly for Cytomegalovirus (CMV) viremia; a positive test resulted in exclusion from the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) was all randomized participants who received ≥1 dose of study drug and had no detectable CMV DNA on Day 1 (randomization). Participants who prematurely discontinued or had a missing outcome through the 24-week visit window were considered treatment failure (i.e. Non-completers equal failure \[NC=F\] approach was used).

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: Randomized participants

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Clinically-significant CMV Infection up to Week 24 Post-transplant, measured over Up to Week 24 post-transplant.

The primary endpoint was the percentage of participants with clinically-significant CMV infection up to Week 24 post-transplant. The registry definition counted either onset of CMV end-organ disease or initiation of anti-CMV pre-emptive therapy. The latter had to be based on documented CMV viremia and the participant’s clinical condition. Thus, the endpoint combines a clinical disease event and a response to evidence of viremia.

A binary percentage is useful for communicating how many participants in each group experienced at least one qualifying event during a specified period. It also makes a direct group comparison possible using a risk difference: the difference between the event probabilities in the two groups. The reported primary analysis uses a risk difference, while the posted group percentages describe the event frequency in each arm.

For this endpoint, an event did not require end-organ disease: pre-emptive therapy could also qualify. That feature is important when interpreting the result, because the endpoint reflects both CMV-related disease and the clinical decision to initiate therapy under the recorded definition. The endpoint does not measure every aspect of CMV infection, and it does not by itself describe safety, survival, or outcomes beyond Week 24.

The registry record specifies that participants who discontinued early or had a missing outcome through the 24-week visit window were considered treatment failures. This rule affects how missing primary outcomes are represented in the analysis and should be kept in mind when reading the reported percentages.

7. Results Posted in the Registry

• Letermovir: 37.5% (122/325) versus 60.6% (103/170) on control; risk difference -23.0 percentage points (95% CI -32.1 to -14.0), risk ratio 0.62 (0.51–0.75); unadjusted two-proportion z-test p = <0.001.

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 to Onset of Clinically-significant CMV Infection (Kaplan-Meier Estimate of Percentage of Participants With a Qualifying Event at Week 24 Post-transplant)

• 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:
  • Letermovir: 18.8% (61/325) versus 44.1% (75/170) on control; risk difference -25.3 percentage points (95% CI -33.9 to -16.8), risk ratio 0.43 (0.32–0.56); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Letermovir than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Clinically-significant CMV Infection up to Week 14 Post-transplant

• 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:
  • Letermovir: 19.1% (62/325) versus 50.0% (85/170) on control; risk difference -30.9 percentage points (95% CI -39.6 to -22.3), risk ratio 0.38 (0.29–0.50); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Letermovir than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With CMV End-organ Disease up to Week 24 Post-transplant

• 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:
  • Letermovir: 2.0% (5/254) versus 2.4% (3/123) on control; risk difference -0.5 percentage points (95% CI -3.7 to 2.7), risk ratio 0.81 (0.20–3.32); unadjusted two-proportion z-test p = 0.766.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Letermovir and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question in several directions: earlier assessment through Week 14, time to a qualifying event, end-organ disease, and pre-emptive therapy for viremia. The record also identifies outcomes concerning CMV end-organ disease and pre-emptive therapy at different time points, as well as time to initiation of pre-emptive therapy. These outcomes are related to the primary endpoint but are not interchangeable with it.

Among secondary outcomes with numerical results, the Week 14 clinically-significant CMV infection outcome is reported as 19.1% for letermovir and 50.0% for placebo, with the sponsor’s Mantel Haenszel risk difference of -31.3, a 95% confidence interval from -39.9 to -22.6, and p < 0.001. The Kaplan-Meier estimate for clinically-significant CMV infection at Week 24 is 18.9% and 44.3%, with a Log Rank p-value < 0.001. The Week 24 end-organ disease outcome is uncommon in both groups; its recalculated interval includes zero, while the sponsor’s reported p-value is 0.406. These are separate outcome definitions, and their estimates should not be collapsed into a single summary.

The broad pattern in the reported secondary results for clinically-significant infection is directionally consistent with the primary result. The end-organ disease outcome is distinct from the composite and has fewer observed events, so its estimate is less precise. Numerical results for the other listed secondary outcomes are not reported in the registry record.

In general, multiple secondary comparisons create a multiplicity concern: the more outcomes and time points examined, the greater the chance of at least one apparently unusual result even when no underlying effect exists. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Therefore, unadjusted secondary p-values carry less confirmatory weight than the designated primary analysis and are best treated as supporting or exploratory evidence.

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

• Time to Onset of Clinically-significant CMV Infection (Kaplan-Meier Estimate of Percentage of Participants With a Qualifying Event at Week 24 Post-transplant)
• Percentage of Participants With Clinically-significant CMV Infection up to Week 14 Post-transplant
• Percentage of Participants With CMV End-organ Disease up to Week 24 Post-transplant
• Percentage of Participants With CMV End-organ Disease up to Week 14 Post-transplant
• Percentage of Participants With Pre-emptive Therapy for CMV Viremia up to Week 14 Post-transplant
• Percentage of Participants With Pre-emptive Therapy for CMV Viremia up to Week 24 Post-transplant
• Time to Initiation of Pre-emptive Therapy for CMV Viremia (Kaplan-Meier Estimate of Percentage of Participants With a Qualifying Event at Week 24 Post-transplant)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the clinically-significant CMV infection definition during the specified period or did not. The registry reports percentages by group and a risk difference for the comparison. A risk difference expresses the contrast as one group’s event probability minus the other group’s event probability, using the stated group order. A negative estimate indicates a lower observed event probability in the letermovir group under that ordering.

What does a confidence interval describe?

In general, a confidence interval is a range produced by a statistical procedure to show the uncertainty around an estimate. Its width reflects how precisely the data estimate the quantity under that procedure. An interval that excludes zero for a risk difference is evidence against an exact zero difference at the corresponding confidence level, under the model and analysis used. It does not show that every value inside the interval is equally plausible, nor does it quantify clinical importance.

The recalculated primary comparison is an unadjusted calculation from the posted group summaries. It gives a risk difference of -0.231, a 95% confidence interval from -0.321 to -0.140, and p < 0.001. This calculation is not the same as the sponsor’s reported analysis, which used the Mantel Haenszel method and reported a risk difference of -23.5, a 95% confidence interval from -32.5 to -14.6, and p < 0.001. The different scales should be kept distinct rather than treated as mismatched units of a single display.

What does the reported method contribute?

The Mantel Haenszel method is the method named for the registry’s primary analysis. In general, this method can combine comparisons across strata, but the registry record does not report the specific stratification details or enough information to reconstruct the analysis. The registry’s reported estimate and test should therefore be read as the sponsor’s trial analysis, not as a result fully reproducible from the summary figures alone.

The p-value summarizes how unusual data at least as incompatible with the no-difference hypothesis would be under that hypothesis and the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of the effect. The primary p-value is reported as p < 0.001 for the Mantel Haenszel analysis and p < 0.001 for the unadjusted recalculation. These values use different analyses and should not be presented as if they were identical tests.

How do time-to-event outcomes differ?

Some secondary outcomes are framed as time to a qualifying event and reported using Kaplan-Meier estimates. In general, Kaplan-Meier methods estimate the event experience over time while accounting for participants whose event time is not observed through the full follow-up, under assumptions about censoring. The registry reports a Kaplan-Meier estimate for time to onset of clinically-significant CMV infection at Week 24, with group estimates of 18.9% and 44.3% and confidence intervals of 14.4% to 23.5% and 36.4% to 52.1%, respectively. A Log Rank test is the method named for that comparison, with p < 0.001. Further details of censoring rules and model assumptions are not reported in the registry record.

Another general statistical issue is over-dispersion. It arises when observed variation is greater than a model assumes, which can make standard errors too small and intervals too narrow if not addressed. The primary outcome is a binary participant-level event, and the registry does not report an over-dispersion adjustment for it. There is no basis in the registry record to claim that over-dispersion was present or that a particular correction was used.

The trial’s analysis population and missing-outcome rule also form part of the method. The Full Analysis Set required randomization, at least one dose, and no detectable CMV DNA on Day 1. Participants who discontinued prematurely or had a missing outcome through the primary visit window were considered treatment failures. Other details of the statistical analysis plan, including any planned interim analyses, are not reported in the registry record.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.231, with a 95% confidence interval from -0.321 to -0.140. The interval lies entirely below zero. This conveys greater precision about the direction of the difference than an interval that spans zero, while still leaving a range of possible effect sizes under the recalculation’s assumptions. The estimate itself should not be treated as exact: its interval is part of the result.

The sponsor’s reported Mantel Haenszel analysis gives a risk difference of -23.5 and a 95% confidence interval from -32.5 to -14.6. This interval also excludes zero. It is the trial’s reported analysis, whereas the other interval comes from an unadjusted recalculation of posted group summaries. Their scales and analysis methods differ, so they should be read as separate estimates rather than combined.

For the secondary Kaplan-Meier estimate of clinically-significant CMV infection at Week 24, the reported intervals are 14.4% to 23.5% for letermovir and 36.4% to 52.1% for placebo. For CMV end-organ disease through Week 24, the recalculated risk difference is -0.005, with a 95% confidence interval from -0.037 to 0.028. That interval includes zero and extends in both directions, reflecting considerable uncertainty for this less frequent outcome.

In general, confidence intervals describe statistical precision, not all sources of uncertainty. They do not account automatically for bias, missing information, endpoint choices, or limits on generalizability. The registry record does not provide all analysis details needed to assess those sources fully.

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 the observed effect, not the trial’s original design calculation. The registry record does not report the trial’s own sample-size justification or original design assumptions. For ordinary binary outcomes, the figures are participants per arm; for time-to-event outcomes, the figures are total events. This distinction matters because an event count is not the same quantity as the number of participants enrolled.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The columns for 80% and 90% power describe the planned chance of detecting an effect of that chosen size under those assumptions, if the assumed effect and statistical model are appropriate. They do not describe what happened in the completed trial.

Each row considers a different planning effect: 100%, 75%, or 50% of the observed effect. A smaller assumed effect requires more participants or, for a time-to-event calculation, more total events to attain the same target power. For example, the primary comparison’s planning illustration lists 73 participants per arm for 80% power and 97 participants per arm for 90% power when using 100% of the observed effect; using 50% of the observed effect gives 292 and 390 participants per arm, respectively.

These calculations are not observed power. They are conditional planning illustrations, and they should not be used to infer the probability that the trial’s finding is correct. 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

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.606; treatment proportion p₁ = 0.375; average p̄ = 0.491.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7070 = 1.3857.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6879 = 0.5790.
4. n = (1.3857 + 0.5790)² / (-0.2305)² = 72.6, rounded up to 73 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.605882352941176                          # control proportion
p1 <- 0.375384615384615                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2137772)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 73 (80% power), 97 (90% power)
 75% of observed effect: n per arm = 130 (80% power), 174 (90% power)
 50% of observed effect: n per arm = 292 (80% power), 390 (90% power)
power.prop.test: 72.6 
Simulated power at n = 73 per arm: 0.822 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry’s own primary analysis is a Mantel Haenszel comparison. It reports a risk difference of -23.5, a 95% confidence interval from -32.5 to -14.6, and p < 0.001. The unadjusted recalculation from posted summary statistics reports -0.231, a 95% confidence interval from -0.321 to -0.140, and p < 0.001. The reported estimates use different numeric scales and different analysis methods. Both point in the same direction, and both confidence intervals exclude zero.

The recalculation is useful as a transparent, simple comparison of the posted group summaries. It is not a substitute for the sponsor’s analysis, which is the analysis recorded for the trial. The registry marks no discrepancy between the reported and recalculated primary results. Even so, the recalculation does not reproduce any features of the Mantel Haenszel analysis that are not specified in the record.

When describing the primary result, the sponsor’s reported analysis should be identified as such, and the unadjusted calculation should be labeled separately. Neither the p-value nor the numerical estimate alone conveys all relevant context: the endpoint is a composite, the analysis population is defined, and the registry’s missing-outcome rule counts certain missing or prematurely discontinued outcomes as failures.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies one primary outcome and multiple secondary outcomes, including related outcomes assessed at different time points. It reports numerical findings for the primary outcome and several secondary outcomes, but it does not report a multiplicity adjustment, a prespecified hierarchy among secondary endpoints, or a family-wise error strategy. Without those details, secondary p-values should not be interpreted as if each were an isolated confirmatory test. In general, testing many outcomes increases the chance of a nominally small p-value arising by chance.

The primary analysis population is described as the Full Analysis Set. It includes randomized participants who received at least one dose of study drug and had no detectable CMV DNA on Day 1. The registry’s definition is narrower than enrollment alone. It does not report a full participant-flow explanation for the difference between enrollment and the primary outcome denominators, so the reasons should not be inferred.

For the primary endpoint, participants who prematurely discontinued or had a missing outcome through the 24-week visit window were considered treatment failures. This is a specific missing-data rule, not evidence that missing outcomes were observed events in the ordinary clinical sense. The registry record does not provide the number of participants classified this way, a sensitivity analysis under alternative missing-data assumptions, or detailed reasons for missing outcomes. Those absences limit assessment of how robust the primary estimate is to missing-data handling.

The registry record also does not report the complete statistical analysis plan, the trial’s original sample-size justification, or whether interim analyses were planned or conducted. Their absence does not establish that such procedures were or were not used; those details are not reported in the registry record. Interpretation should therefore distinguish the methods that are explicitly recorded from those that remain unspecified.

16. 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: graft versus host disease (15.1%), acute myeloid leukaemia recurrent (8.9%), cytomegalovirus infection (7.8%), acute kidney injury (4.7%), pneumonia (4.0%).

The serious adverse event summary lists 202 affected participants among 373 at risk in the letermovir group and 115 among 192 at risk in the placebo group. These are counts and denominators as reported in the registry record; they are not the primary efficacy endpoint. The record also lists other adverse events affecting 360 of 373 participants in the letermovir group and 186 of 192 in the placebo group.

Listed serious adverse event terms include graft versus host disease at 15.1%, acute myeloid leukaemia recurrent at 8.9%, cytomegalovirus infection at 7.8%, acute kidney injury at 4.7%, pneumonia at 4.0%, and septic shock at 3.6%. The record does not specify in the listed summary how those term percentages are apportioned between arms, so they should not be assigned to a particular group.

These summaries do not by themselves establish whether an event was caused by study treatment or permit a complete benefit-risk comparison. Death counts are not reported in the registry record. The available figures should be read as descriptive safety reporting, alongside the trial’s eligibility, follow-up, and outcome definitions.

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

The primary result describes a lower observed percentage of participants meeting the clinically-significant CMV infection definition in the letermovir group than in the placebo group through Week 24 post-transplant. The reported Mantel Haenszel risk difference is -23.5, with a 95% confidence interval from -32.5 to -14.6 and p < 0.001. The unadjusted recalculation also places the estimated difference below zero. These findings describe the trial comparison; they do not, by themselves, resolve every question about clinical importance or applicability.

The event definition combines CMV end-organ disease with initiation of pre-emptive therapy for documented viremia based on clinical condition. The primary result therefore should not be interpreted as an estimate of end-organ disease alone. It also does not describe all CMV outcomes, every potential safety outcome, or outcomes outside the recorded follow-up period.

The trial involved adult, CMV-seropositive recipients of allogeneic hematopoietic stem cell transplant, and the primary analysis population required no detectable CMV DNA on Day 1 and at least one dose of study drug. The result does not automatically extend to people who differ from that population. The registry record does not report detailed demographic or clinical subgroup results in the registry record for this analysis.

A statistically significant result is not the same as proof that an effect is important to every patient or setting. A p-value does not give the probability that the treatment effect is true, while a confidence interval expresses statistical uncertainty under a specified analysis rather than all uncertainty. Missing outcomes, endpoint construction, and differences between trial participants and other populations remain relevant to interpretation.

No medical advice follows from these statistics. The registry findings provide a quantitative description of one randomized trial, not an individualized assessment or a complete account of treatment decisions.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition deserves as much attention as the numerical contrast. Clinically-significant CMV infection was defined through two pathways: CMV end-organ disease or initiation of pre-emptive therapy in response to documented viremia and the participant’s clinical condition. A reader who treats the result as an end-organ disease result would be describing a different outcome from the primary endpoint.

It also demonstrates the value of distinguishing the registry’s reported analysis from a simple recalculation. The sponsor reports a Mantel Haenszel risk difference and a corresponding confidence interval and p-value. The unadjusted recalculation uses the posted summary statistics and gives a separately scaled estimate. Comparing them requires attention to the method and scale, not just the signs or the p-values.

The primary endpoint’s missing-outcome rule is another important statistical feature. Premature discontinuation or a missing outcome through the 24-week window was classified as treatment failure. That rule affects what the analyzed event percentage represents, and the absence of a reported sensitivity analysis leaves uncertainty about how alternative missing-data approaches would affect the estimate.

Finally, the secondary outcomes show why a coherent pattern should not be confused with multiple independent confirmations. Time points and related endpoint definitions can provide context, but multiple unadjusted tests carry less evidential weight. The separate end-organ disease outcome is less precise than the primary composite in the posted results. These distinctions help keep the interpretation tied to what the trial actually measured and reported.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific limitations affect interpretation. The primary endpoint is a composite of CMV end-organ disease and pre-emptive therapy. Because the second component depends on documented viremia and clinical condition, the endpoint is not a direct measure of end-organ disease alone. The registry record does not provide a breakdown of primary events by component, so the relative contribution of each component cannot be assessed from the recorded summary.

The primary analysis population required participants to have no detectable CMV DNA on Day 1 and to have received at least one dose. The posted primary outcome denominators are 325 for letermovir and 170 for placebo, while enrollment is 570. The registry record does not provide a complete participant-flow account to explain the difference. It is therefore not possible to determine from the recorded summary alone how exclusions, withdrawals, or other population definitions contributed.

Early discontinuation and missing primary outcomes through the 24-week window were treated as failures. The registry record does not give counts for these classifications or report sensitivity analyses using alternative assumptions. This limits evaluation of the primary result’s dependence on that missing-outcome rule.

The record does not report the original sample-size justification, planned interim analyses, full statistical analysis plan, or multiplicity strategy. The listed secondary outcomes include multiple related endpoints and time points, but the statistical handling of that multiplicity is not reported. In addition, detailed results for several listed secondary outcomes are not reported in the registry record.

Safety summaries are descriptive, and the listed serious event terms are not apportioned by arm in the available summary. Death counts are not reported in the registry record. These limitations constrain the scope of conclusions that can be drawn from the posted efficacy and safety summaries.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Letermovir (MK-8228) Versus Placebo in the Prevention of Clinically-Significant Cytomegalovirus (CMV) Infection in Adult, CMV-Seropositive Allogeneic Hematopoietic Stem Cell Transplant Recipients (MK-8228-001) — NCT02137772.
• Registry record last updated 2019-09-11; status last verified 2019-08.
• Results first posted 2017-11-17.
• 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

NCT02137772 was a completed Phase III randomized, double-masked, parallel-group, placebo-controlled trial sponsored by Merck Sharp & Dohme LLC. It evaluated letermovir for prevention of clinically-significant CMV infection among adult, CMV-seropositive allogeneic hematopoietic stem cell transplant recipients. Enrollment was 570, with a recorded start date of 2014-06-06 and primary completion date of 2016-08-08.

The primary outcome was clinically-significant CMV infection through Week 24 post-transplant, defined as CMV end-organ disease or initiation of anti-CMV pre-emptive therapy for documented viremia in light of clinical condition. The registry’s Mantel Haenszel analysis reported a risk difference of -23.5, a 95% confidence interval from -32.5 to -14.6, and p < 0.001. The primary analysis population and missing-outcome rule are specified in the registry record, while several design and analysis details are not reported.