A Study of the Safety and Efficacy of CMX001 for the Prevention of CMV Infection in CMV-seropositive HCT Recipients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of the Safety and Efficacy of CMX001 for the Prevention of CMV Infection in CMV-seropositive HCT Recipients (NCT01769170), a randomized phase 3 study. The primary outcome is Number of Participants With Clinically Significant CMV Infection Through Week 24 Post-Transplant.

2. Clinical Question

3. Trial Design

This was a randomized, phase 3, parallel-group study of oral brincidofovir and matching placebo for prevention of CMV infection in CMV-seropositive hematopoietic stem cell transplant recipients. The registry describes the trial as double-blind and placebo-controlled, and lists quadruple masking. It also describes the study as multicenter. The details of the randomization procedure, allocation concealment, and the roles covered by quadruple masking are not reported in the registry record.

The registry reports 452 participants enrolled. The primary outcome results use an Intent-to-Treat Analysis Set described as including all subjects who received at least one dose of study drug. The posted arm counts are 303 for brincidofovir and 149 for placebo. The registry does not give a separate account of participants randomized but not treated, withdrawals, losses to follow-up, or the number with outcome data available at each assessment.

The primary endpoint was the number of participants with clinically significant CMV infection through week 24 post-transplant. A secondary endpoint assessed the same general clinical outcome through week 14. The registry lists the trial as completed, with a start date of 2013-08 and primary completion in 2015-12. Those dates describe the registry record; they do not provide the timing of individual participant follow-up or the publication history.

Brincidofovir was administered orally at 100 mg twice weekly, while placebo was administered orally twice weekly. Treatment duration, dose interruptions, adherence, concomitant preventive measures, and details of care after the outcome window are not reported in the registry record. The registry names Jazz Pharmaceuticals as sponsor. The original statistical analysis plan, sample-size justification, and trial-specific design assumptions 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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat Analysis Set, which included all subjects who received at least 1 dose of study drug.

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 Analysis Set, which included all randomized subjects who received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Clinically Significant CMV Infection Through Week 24 Post-Transplant, measured over 24 weeks.

The primary endpoint counted participants with clinically significant CMV infection through week 24 post-transplant. A participant met the endpoint if CMV end-organ disease developed or if CMV-specific preemptive therapy was initiated based on documented CMV viremia and the participant’s clinical condition. Viremia was measured as CMV DNA in plasma by the designated central virology laboratory, using quantitative polymerase chain reaction testing at scheduled visits.

This composite endpoint combines a clinical disease outcome with a treatment-initiation outcome. In general, a composite can capture more than one clinically relevant way that a condition becomes important during follow-up. Here, the two components represent different kinds of events: end-organ disease is a clinical manifestation, while starting preemptive therapy depends on the laboratory finding together with clinical judgment. The registry definition makes clear that a positive laboratory measurement alone was not the stated basis for the therapy component; the participant’s clinical condition was also considered.

The endpoint is expressed as a count of participants with an event, rather than as the number of events or the time until an event. This allows a comparison of the proportion experiencing the defined outcome during the stated window, but does not by itself describe when events occurred or distinguish the contribution of each component. Separate component results are not reported in the registry record. The endpoint definition and follow-up window therefore matter when interpreting the group comparison: the result pertains to this specific composite through week 24, not to every CMV outcome or a longer period.

7. Results Posted in the Registry

• Brincidofovir: 51.2% (155/303) versus 52.3% (78/149) on control; risk difference -1.2 percentage points (95% CI -11.0 to 8.6), risk ratio 0.98 (0.81–1.18); unadjusted two-proportion z-test p = 0.811.

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.

Incidence of Clinically Significant CMV Infection Through Week 14

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Brincidofovir: 24.4% (74/303) versus 38.3% (57/149) on control; risk difference -13.8 percentage points (95% CI -23.0 to -4.7), risk ratio 0.64 (0.48–0.85); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Brincidofovir than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary endpoint: clinically significant CMV infection through week 14. Its recalculated unadjusted comparison is in the direction of fewer events in the brincidofovir group, while the primary outcome through week 24 has a point estimate close to zero. This creates a difference in the apparent pattern across the two follow-up windows, rather than a single uniform result across all listed outcomes.

The endpoints are related because they use the same general composite definition and differ in the length of the stated observation window. They are not independent questions: events occurring by an earlier assessment can also contribute to a later cumulative outcome. The registry does not provide participant-level event timing, separate results for end-organ disease and preemptive treatment, or information that would explain how the secondary and primary patterns relate. It is therefore not possible to identify from these summaries when or why the observed contrast changed across windows.

The secondary result is an unadjusted recalculation, and the registry does not list a sponsor analysis for it. The record also does not report a multiplicity strategy, such as a hierarchy of outcomes or an adjustment to account for examining multiple endpoints. In general, when more than one outcome or analysis is considered, the chance of at least one apparently notable result can increase unless the analysis plan addresses that issue. This does not mean the secondary finding is false; it means it carries less inferential weight without a reported plan and a sponsor-reported analysis.

The primary endpoint remains the main outcome designated in the registry record. The secondary finding can add context about the earlier follow-up period, but it should not be treated as confirmation of a primary result or as a replacement for it. Its interpretation depends on the stated time window, the composite endpoint definition, the unadjusted nature of the calculation, and the missing information about multiplicity and analysis procedures.

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

• Incidence of Clinically Significant CMV Infection Through Week 14

9. Statistical Interpretation

10. Statistical Methods Explained

What is being compared?

The primary result is a binary outcome: each participant either met the definition of clinically significant CMV infection during the stated window or did not. For binary outcomes, a risk is the proportion of participants in a group with the event. The registry posts a risk of 0.512 for brincidofovir and 0.523 for placebo. The risk difference subtracts the comparator-group risk from the intervention-group risk. Its posted estimate is -0.012, so the point estimate is in the direction of a lower event proportion with brincidofovir. The estimate alone is not a complete account of uncertainty; it must be considered with its confidence interval.

The risk ratio and odds ratio are alternative ways to express a binary comparison. The registry lists a risk ratio of 0.977 with interval limits of 0.809 and 1.18, and an odds ratio of 0.953 with interval limits of 0.644 and 1.412. These measures answer related but not identical questions, and their numerical scales differ. The risk difference is often easier to interpret as an absolute contrast in proportions. None of these summary measures explains the timing of events or which part of the composite endpoint occurred.

What does a confidence interval express?

In general, a confidence interval gives a range of values compatible with the observed data under the statistical procedure used. It is not a guarantee that the true effect lies within that particular interval, nor is it a range containing a specified proportion of individual participant outcomes. When an interval for a risk difference includes zero, the data do not rule out no difference at the confidence level associated with the interval. The primary interval runs from -0.110 to 0.086, so it includes zero and values on either side. Its width indicates that the point estimate is not highly precise.

What does the p-value add?

A p-value measures how unusual the observed data, or data more extreme, would be under a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The primary comparison has a recalculated unadjusted p-value of 0.811. The secondary comparison has a recalculated unadjusted p-value of 0.002. These are unadjusted calculations from posted summary statistics. The statistical analysis used by the sponsor is not reported in the registry record, and no sponsor analysis is listed among the posted analyses.

Why distinguish unadjusted and adjusted results?

An unadjusted comparison uses the posted group counts without accounting for additional variables or design features through a model. This gives a transparent summary of the observed arm-level event proportions, but it may not match a prespecified analysis that uses stratification, covariate adjustment, or other methods. The registry does not report such an analysis for these outcomes. Because the discrepancy flag is false, no conflict between the posted counts and the registry’s reported result is identified; still, the recalculated values should be understood as simple unadjusted comparisons rather than a substitute for a complete trial analysis.

Why can over-dispersion matter in other analyses?

General statistical context: over-dispersion arises when observed variation is greater than a model assumes. It can make model-based uncertainty too small if the extra variation is ignored. This concern is especially relevant to some count-data and clustered-data models. The posted primary and secondary outcomes are participant counts for binary events, and the record does not report an over-dispersion model or a model-based analysis. There is no basis in the registry record to claim that over-dispersion was assessed or affected these results.

What analysis population is described?

The primary population is called the Intent-to-Treat Analysis Set, but its registry definition includes all subjects who received at least one dose of study drug. That definition is important: it describes a treated population and does not establish how randomized participants who received no dose were handled. The record does not give enough detail to assess exclusions, missing outcomes, or analysis-population deviations. The posted denominators are 303 and 149, and the associated event counts are 155 and 78.

What should be treated as a recalculation?

The posted risk differences, confidence intervals, risk ratios, odds ratios, and p-values are presented as unadjusted recalculations from arm-level summary statistics. They permit readers to understand the arithmetic comparison of the recorded counts, but do not reveal the original protocol assumptions, data-cleaning decisions, or any prespecified inferential procedure. Those details, along with the full statistical analysis plan, are not reported in the registry record. General statistical interpretation should therefore be kept distinct from claims about what the trial team planned or performed.

11. Confidence Intervals and Precision

The primary risk difference is -0.012, with a 95% confidence interval from -0.110 to 0.086. The interval includes zero, so the posted data are compatible with no difference as well as with effects in either direction. It is also wide relative to the point estimate, leaving considerable uncertainty about the size of any group contrast. The point estimate should not be read as an exact measure of the underlying effect.

In general, a confidence interval describes the uncertainty around an estimate under the method used to calculate it. It does not show the range of outcomes for individual participants, and a 95% interval does not mean there is a 95% probability that the true value is in this specific interval. The confidence level refers to the long-run behavior of the procedure under its assumptions. The registry does not report the full statistical method or assumptions underlying the trial’s own analysis.

The alternative primary measures also have intervals that include their null values: the risk ratio is 0.977 with limits 0.809 and 1.18, and the odds ratio is 0.953 with limits 0.644 and 1.412. These estimates describe relative rather than absolute contrasts, and neither removes the uncertainty evident in the risk-difference interval. The risk difference is useful for expressing the absolute contrast in the proportions observed in these groups; the relative measures provide complementary scales.

Precision is not the same as whether a result crosses a significance threshold. A narrow interval can still include a clinically important range, and a p-value alone cannot indicate how large an effect might be. The primary interval leaves uncertainty about both direction and magnitude. For the secondary endpoint, the posted risk-difference interval is -0.230 to -0.046, which does not include zero, but that result is unadjusted and concerns a different follow-up window. It should not be used to erase the uncertainty in the primary endpoint or to imply that both outcomes answer the same question.

The record does not report interval estimates for separate composite components or for important subgroups. As a result, precision cannot be assessed for those questions from the registry results.

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 translate an observed effect into hypothetical sample-size requirements under stated assumptions. Because these outcomes are binary, the figures are participants per arm, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one and the assumptions held. The 90% power column applies the higher target chance of detection under the same general framework. These are planning quantities, not descriptions of the chance that the completed trial found an effect. This is not observed power.

The illustrations include planning for 100% of the observed effect, planning for 75% of the observed effect, and planning for 50% of the observed effect. The smaller the effect chosen for planning, the more participants the calculation requires, because a smaller separation between groups is harder to distinguish from random variation. The figures should be read as conditional illustrations based on the observed estimate, not as a recommendation or as evidence that the trial was designed around these values.

The calculation assumes equal allocation even though the posted arm sizes are unequal. It also uses a normal approximation and does not account for design details that are not represented in the listed assumptions. The registry record does not report whether the original design used different assumptions, allowed for attrition, incorporated interim analyses, or based its target on another expected effect. These planning values therefore help explain the relationship between effect size and sample size, but they cannot establish whether the completed trial met its original design targets.

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 = 0.523; treatment proportion p₁ = 0.512; average p̄ = 0.518.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7067 = 1.3851.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7066 = 0.5947.
4. n = (1.3851 + 0.5947)² / (-0.0119)² = 27,498.3, rounded up to 27,499 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 <- 0.523489932885906                          # control proportion
p1 <- 0.511551155115512                          # 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(1769170)
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 = 27,499 (80% power), 36,812 (90% power)
 75% of observed effect: n per arm = 48,877 (80% power), 65,431 (90% power)
 50% of observed effect: n per arm = 109,947 (80% power), 147,187 (90% power)
power.prop.test: 27498.3 
Simulated power at n = 27,499 per arm: 0.800 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary and one secondary outcome measure. It does not report a multiplicity plan describing how the trial handled inference across endpoints, time windows, or other analyses. It also does not report whether a hierarchy was prespecified, whether any adjustment was made, or whether the secondary outcome was intended to be confirmatory. The secondary p-value is therefore best treated as an unadjusted result, not as evidence that a family-wise error rate or another multiplicity criterion was controlled.

Missing outcome data and participant disposition are also incompletely described. The record gives the primary analysis population definition and arm denominators, but does not state how many randomized participants received no dose, withdrew, were lost to follow-up, or lacked outcome ascertainment. It does not describe imputation, censoring, sensitivity analyses, or assumptions about missing outcomes. These details matter because the interpretation of an event proportion depends on who is included in the denominator and how unavailable outcomes are handled.

The population is labeled Intent-to-Treat Analysis Set, yet its definition is all subjects who received at least one dose of study drug. That wording does not establish whether the analysis included every randomized participant. The registry does not explain how this set relates to the randomized population or whether additional analysis populations were used. The posted results should be understood using the population definition actually stated, without assuming that it matches a different conventional definition of intention-to-treat.

The registry record does not report the original statistical analysis plan, the planned sample-size justification, interim analyses, subgroup-analysis plans, or detailed methods for handling deviations from treatment. It also does not list sponsor-reported outcome analyses. As a result, the available unadjusted comparisons provide a useful description of the posted counts but cannot answer whether every analysis followed a prespecified plan. These gaps limit assessment of selective reporting and of the robustness of the findings under alternative missing-data or multiplicity assumptions.

15. 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: acute graft versus host disease (32.3%), diarrhoea (6.9%), pyrexia (5.4%), clostridium difficile colitis (3.0%), acute kidney injury (3.0%).

The registry lists serious adverse events affecting 173 of 303 participants in the brincidofovir group and 56 of 149 participants in the placebo group. It also lists other adverse events affecting 302 of 303 and 146 of 149 participants, respectively. These are group-level counts in the adverse-event record; they do not by themselves establish that an event was caused by study treatment.

The registry’s listed serious adverse-event terms include acute graft versus host disease (32.3%), diarrhoea (6.9%), pyrexia (5.4%), Clostridium difficile colitis (3.0%), acute kidney injury (3.0%), and pneumonia (2.7%). The record does not specify in this listing whether each percentage is presented by treatment arm or give the accompanying term-specific counts. These figures should therefore be read as registry-listed serious-event terms, not as a direct comparative estimate between groups.

The adverse-event summary does not report deaths in the posted group fields. It also does not provide event onset, duration, severity grading beyond the serious classification, exposure-adjusted rates, or a causal assessment for each event. Without those details, the counts and terms describe what is recorded but do not support a complete comparative safety analysis.

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

The primary result describes the proportion of participants who met the registry’s composite definition of clinically significant CMV infection through week 24 post-transplant. The observed arm proportions are close, and the unadjusted risk-difference interval includes zero while extending in both directions. The posted data therefore leave uncertainty about whether the underlying group difference was positive or negative and about its magnitude.

This finding does not establish that the treatments are equivalent. Equivalence or non-inferiority requires a prespecified margin and an analysis designed to assess that question; such a margin and analysis are not reported in the registry record. Likewise, a non-significant p-value does not prove no effect. It indicates that the observed data do not provide strong evidence against the no-difference model under the unadjusted calculation used.

The earlier secondary outcome has a different pattern, but it concerns a shorter follow-up window and is an unadjusted result. The registry does not report a multiplicity plan, component-specific event counts, or event timing that would reconcile the two windows. It is not appropriate to treat the secondary result as a substitute for the primary endpoint or to infer a sustained effect from it.

The results apply to the trial population and outcome definition recorded: CMV-seropositive transplant recipients who were negative for viremia before treatment, with the primary analysis set described as participants who received at least one dose. The registry does not provide enough detail to determine how the findings generalize to other populations, treatment regimens, or follow-up periods. The results also do not identify the separate contributions of end-organ disease and preemptive therapy to the composite.

Finally, these efficacy summaries do not establish individual benefit or harm, and the adverse-event counts are not a complete causal comparison. They are group-level registry results with limited information about missing data, treatment exposure, analysis methods, and event timing. Any interpretation should stay within those limits and should not be treated as medical advice.

17. Why This Trial Matters Statistically

This trial illustrates why an endpoint definition is central to statistical interpretation. The primary outcome combines CMV end-organ disease with initiation of preemptive therapy based on laboratory evidence and clinical condition. A single count of participants with the composite cannot reveal whether the observed events were mainly disease, treatment initiation, or a mixture. Component-specific results would help distinguish those possibilities, but they are not reported in the registry record.

It also shows why a point estimate and a p-value are not enough. The primary risk difference is close to zero, but its confidence interval spans values in both directions. The interval communicates uncertainty more directly than a binary label of statistically significant or not significant. The secondary endpoint gives a different impression over a shorter window, making it especially important to distinguish outcome timing, multiplicity, and the status of each analysis.

The trial record also demonstrates the value of transparent analysis documentation. The registry identifies the primary population and provides event counts, but does not report the original statistical analysis plan, sample-size justification, multiplicity procedure, interim analyses, or detailed missing-data methods. Without these, readers can describe the posted summaries and their uncertainty but cannot fully assess whether the reported analyses match the intended design.

Finally, the planning illustrations show the general relationship between effect size and required sample size under explicit assumptions. They are not a substitute for the trial’s own design rationale. Keeping those illustrations separate from the observed results helps avoid treating a post hoc planning calculation as evidence about the trial’s original power or design intentions.

18. Limitations

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

Several trial-specific limitations of interpretation follow from the registry information. The primary outcome is a composite, but the record does not give separate counts for CMV end-organ disease and initiation of preemptive therapy. Those components may differ in clinical meaning and ascertainment, so the combined count cannot show which component drove the group-level result.

The primary and secondary endpoints use different follow-up windows. The registry does not give event timing, the number of participants assessed at each visit, or the pattern of events between the two time points. This limits interpretation of why the shorter-window comparison differs from the primary comparison. The record also does not provide subgroup results, baseline characteristics, or detailed transplant characteristics that would support assessment of variation across participant groups.

The analysis population is described as participants who received at least one dose, but the record does not explain how this set relates to all randomized participants. Participant flow, treatment discontinuation, adherence, exposure duration, and missing outcome data are not described in enough detail to evaluate their potential effect on the posted proportions. No sensitivity analyses are reported.

The registry does not report the original statistical analysis plan, the trial’s sample-size assumptions, multiplicity control, interim analyses, or an adjusted sponsor analysis. The available estimates are unadjusted recalculations from posted summary counts. The safety summary likewise lacks term-specific comparative counts, event timing, exposure-adjusted rates, and detailed causal assessments. These limitations constrain how far the efficacy and safety summaries can be interpreted beyond the recorded group-level outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of the Safety and Efficacy of CMX001 for the Prevention of CMV Infection in CMV-seropositive HCT Recipients — NCT01769170.
• Registry record last updated 2021-07-21; status last verified 2021-07.
• Results first posted 2021-01-05.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01769170 is a completed randomized phase 3, double-blind, placebo-controlled, parallel-group, multicenter study sponsored by Jazz Pharmaceuticals. It compared oral brincidofovir, 100 mg twice weekly, with matching placebo in CMV-seropositive hematopoietic stem cell transplant recipients who were CMV-viremia negative before treatment. The registry reports 452 participants enrolled.

The primary outcome was clinically significant CMV infection through week 24 post-transplant, defined as CMV end-organ disease or initiation of CMV-specific preemptive therapy based on documented viremia and clinical condition. The posted primary counts were 155 of 303 with brincidofovir and 78 of 149 with placebo. The recalculated unadjusted risk difference was -0.012, with a 95% confidence interval from -0.110 to 0.086 and p = 0.811.

One secondary outcome assessed the same general endpoint through week 14. The registry does not report sponsor analyses, the original statistical analysis plan, the sample-size justification, or detailed missing-data and multiplicity methods.