A Study to Evaluate the Efficacy and Safety of VX-661 in Combination With Ivacaftor in Subjects Aged 12 Years and Older With Cystic Fibrosis, Heterozygous for the F508del-CFTR Mutation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy and Safety of VX-661 in Combination With Ivacaftor in Subjects Aged 12 Years and Older With Cystic Fibrosis, Heterozygous for the F508del-CFTR Mutation (NCT02516410), a randomized phase 3 study. The primary outcome is Absolute Change From Baseline in Percent Predicted Forced Expiratory Volume in 1 Second (FEV1) Through Week 12.

2. Clinical Question

3. Trial Design

This was a Phase 3 randomized, triple-masked, parallel-group, placebo-controlled trial sponsored by Vertex Pharmaceuticals Incorporated. The registry record describes 168 enrolled participants with cystic fibrosis who were heterozygous for the F508del-CFTR mutation and had a second mutation not likely to respond to VX-661 and/or ivacaftor therapy. Participants were aged 12 years and older. The study was completed, with primary completion on 2016-06-07.

The active group received VX-661 with ivacaftor, while the comparator group received matching placebo for both components. Treatment was scheduled through Week 12. The primary outcome was measured from baseline through Week 12. The record lists 85 participants analyzed in the placebo group and 82 in the active group for this endpoint. The primary outcome description defines the Full Analysis Set as randomized participants who received at least one dose of study drug; it further specifies that the analyzed count represents participants evaluable for that outcome.

Randomization and masking are relevant because they can reduce systematic differences between groups and limit the influence of expectations on conduct or assessment. The registry record identifies the design features but does not report the randomization method, allocation concealment details, or the exact masking roles. It also does not report the original sample-size justification, planned statistical analysis document, or any interim analysis plan. Those details therefore cannot be used to assess whether the conduct followed a more detailed protocol.

The record lists 12 outcome measures, including the primary endpoint and secondary measures relating to respiratory symptoms, pulmonary exacerbations, body mass index, percent predicted FEV1, and sweat chloride. The enrollment figure describes the trial record; it is not interchangeable with the number analyzed for a particular outcome. Outcome-specific denominators can differ, and the reasons for those differences 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: A total of 168 participants were randomized and treated in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) included all randomized participants who received at least 1 dose of study drug. Here 'Number of participants analysed' signifies those participants who were evaluable for this outcome measure.

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.

6. Primary Endpoint

The registry lists the primary outcome as Absolute Change From Baseline in Percent Predicted Forced Expiratory Volume in 1 Second (FEV1) Through Week 12, measured over Baseline, Through Week 12.

The primary endpoint was absolute change from baseline in percent predicted forced expiratory volume in one second (FEV1) through Week 12. FEV1 measures the volume of air a person can forcibly exhale in one second after a full inspiration. Expressing the result as percent predicted compares the measured value with a reference expectation based on age, gender, and height. The registry record says Hankinson and Wang standards were used, with the applicable standard depending on participant age and gender.

Change from baseline focuses on how the measure shifted during follow-up, rather than only comparing the groups’ final measurements. The endpoint is continuous: each participant contributes a measured value, and a group mean change can describe the average shift. Comparing group mean changes is a way to estimate the average difference associated with assignment to the active regimen rather than placebo in this trial.

FEV1 is used as a measure of lung function, but a group average does not describe every participant’s experience. It also does not, by itself, establish whether an observed difference is clinically important. The registry record does not report a threshold for clinical importance or a minimum meaningful difference. Interpretation therefore rests on the estimated group contrast, its uncertainty, the endpoint’s measurement context, and the trial’s design.

7. Results Posted in the Registry

• VX-661/IVA: mean 1.00 versus -0.10 on control; difference 1.10 (95% CI -0.56 to 2.76), standardized effect d = 0.20; z-test p = 0.195.

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.

Number of Pulmonary Exacerbation Events Per Year

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • VX-661/IVA: 0.97 versus 0.98 (Pulmonary exacerbation events per year) on control; rate ratio 0.99 (95% CI 0.52–1.87, approximate, Poisson model); p ≈ 0.975.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between VX-661/IVA and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With at Least One Pulmonary Exacerbation Through Week 12

• 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:
  • VX-661/IVA: 22.9% (19/83) versus 24.7% (21/85) on control; risk difference -1.8 percentage points (95% CI -14.7 to 11.1), risk ratio 0.93 (0.54–1.59); unadjusted two-proportion z-test p = 0.783.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between VX-661/IVA and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists a broad set of secondary outcomes, including respiratory symptoms, pulmonary exacerbations, body mass index, lung-function change, and sweat chloride. The posted numeric secondary comparisons described for exacerbations use different estimands: an annualized event rate and the proportion of participants with at least one event. Neither comparison shows a clear statistical separation between groups; both unadjusted p-values are large, and their intervals include the respective no-difference value.

Those secondary results are consistent with an overall picture in which the posted data do not establish a clear contrast on the primary endpoint or on these exacerbation summaries. They do not provide a direct confirmation of the primary endpoint, because they measure different outcomes. They should not be combined into a single conclusion about all outcomes, and the registry record does not provide a common summary measure across them.

Secondary results generally carry less weight than the prespecified primary question when many endpoints are examined. Each additional comparison creates another opportunity for an apparently unusual result to arise by chance. The record lists 12 outcome measures, but does not report whether a multiplicity procedure was planned or used. Since the presented secondary p-values are unadjusted, they should be treated as exploratory evidence rather than as independent confirmatory tests. The record does not report enough detail to determine how the investigators prioritized or jointly interpreted the secondary outcomes.

Some secondary outcomes are listed in the record without numeric results in the available outcome summaries. Their results cannot be inferred from the two exacerbation comparisons or from the primary outcome. The overall pattern should therefore be described narrowly: the primary sponsor estimate is uncertain, and the posted exacerbation comparisons are also inconclusive. Missing secondary results do not establish either favorable or unfavorable findings.

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

• Absolute Change From Baseline in Cystic Fibrosis Questionnaire-Revised (CFQ-R) Respiratory Domain Score Through Week 12
• Number of Pulmonary Exacerbation Events
• Number of Pulmonary Exacerbation Events Per Year
• Absolute Change From Baseline in Body Mass Index (BMI) at Week 12
• Relative Change From Baseline in Percent Predicted FEV1 Through Week 12
• Absolute Change From Baseline in Sweat Chloride Through Week 12
• Number of Participants With at Least One Pulmonary Exacerbation Through Week 12
• Absolute Change From Baseline in BMI Z-score at Week 12 (in Participants Less Than [<] 20 Years Old at the Time of Screening)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary estimate represent?

The primary outcome is a continuous measure: change in percent predicted FEV1. A group mean summarizes the average change among the analyzed participants, while a difference between group means contrasts the two randomized groups. The sponsor reported a least-squares mean difference of 1.2. A least-squares mean is a model-based group estimate; it need not equal a simple subtraction of the raw group averages when the analysis uses repeated observations or other model terms. The registry record does not list the model’s covariates or other adjustment details.

Why use a repeated-measures model?

The sponsor’s listed method is mixed-effect repeated measure (MMRM). In general, a repeated-measures model can use measurements made at multiple follow-up times and account for the fact that measurements from the same participant are related. A mixed-effects approach represents that correlation and estimates a group contrast over the stated follow-up. This can use the pattern of observed measurements rather than reducing each participant’s follow-up to a single value. The registry record does not report the precise covariance structure, the time terms, or how the model handled incomplete measurement histories, so those parts of the analysis cannot be reconstructed from the posted description.

The primary endpoint is described as change through Week 12, and its timeframe is baseline through Week 12. The record does not give the individual visit schedule or the specific repeated observations included in the model. It is therefore appropriate to describe the method at the level reported, without assuming a particular visit-by-treatment structure or a particular missing-data procedure.

What do the standard errors and confidence interval add?

A standard error describes the estimated sampling uncertainty of an estimate. The arm summaries list standard errors of 0.6 for both groups. A confidence interval gives a range of values compatible with the estimate under the analysis and its assumptions. The sponsor’s 95% interval for the difference extends from -0.3 to 2.6. Because zero lies within that interval, the data do not isolate a nonzero difference at that confidence level. An interval is not a range containing a fixed proportion of individual participant outcomes, and it does not show the spread of responses between participants.

The sponsor’s p-value, 0.118, summarizes how unusual an estimate 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, nor is it a measure of clinical importance. The registry record labels the comparison as a superiority analysis, but does not report a multiplicity adjustment or a broader analysis plan for interpreting multiple endpoints.

How does the recalculation differ?

The unadjusted recalculation uses posted group summaries to form a simple contrast. It estimates a mean difference of 1.1 and gives an unadjusted p-value of 0.195. The pooled standard deviation used in that calculation is approximate because the arm summaries provide standard errors rather than participant-level variability; it is derived from the posted standard errors and sample sizes. Such a calculation does not retain the repeated observations or model structure used in the sponsor’s MMRM. It is useful as a transparent summary-statistics check, but it is not a replication of the sponsor analysis.

The sponsor’s estimate and the recalculated estimate are close in direction and scale, and the registry record does not flag a discrepancy. The sponsor’s model-based result remains the reported trial analysis. The recalculation should be understood as an unadjusted analysis of posted summaries rather than an alternative primary conclusion.

How should event outcomes be analyzed?

The secondary outcome for pulmonary exacerbation events per year is a rate, not a continuous lung-function measure or a count of participants with at least one event. The posted rate comparison uses a rate ratio. In general, a rate ratio compares event rates between groups; a value at the no-difference point represents equal rates. The registered summaries list rates of 0.98 and 0.97 events per year and an unadjusted p-value of 0.975. The interval is broad and includes the no-difference value, so it does not precisely distinguish between lower and higher rates.

The outcome counting participants with at least one pulmonary exacerbation is binary at the participant level: each participant either did or did not have at least one event during the stated period. The reported comparison is a risk difference. The unadjusted risk difference is -0.018, with an interval from -0.147 to 0.111 and a p-value of 0.783. The interval crosses zero, representing uncertainty about the direction as well as the size of the group contrast. These event outcomes are not interchangeable: one counts events over time, while the other indicates whether a participant experienced at least one event.

For both secondary comparisons, the posted p-values are unadjusted. General statistical guidance is that multiple comparisons increase the chance that at least one result appears noteworthy by chance. Interpreting these results therefore requires caution, especially because the registry record lists multiple outcomes and does not report a multiplicity-control strategy. No causal or clinical conclusion should be based on an isolated secondary comparison without the broader analysis plan and context.

11. Confidence Intervals and Precision

Precision concerns how tightly the data estimate a group contrast. The primary sponsor analysis reports a 95% confidence interval from -0.3 to 2.6 around the least-squares mean difference of 1.2. The interval includes zero and covers values on both sides of it. This means the data do not sharply determine whether the average contrast is positive, negative, or close to no difference under the model. The interval also allows a range of magnitudes, rather than identifying a single effect as exact.

The arm-level standard errors for the primary outcome are 0.6 in each group. A standard error reflects uncertainty in an estimated mean, not the range of individual participant measurements. Variation among participants can be much larger or smaller than the standard error, and the registry record does not report the primary endpoint’s standard deviation directly. The recalculated pooled standard deviation is approximate, based on the posted standard errors and group sizes, and should not be confused with a sponsor-reported measure of participant variability.

The two posted exacerbation comparisons are also uncertain. The event-rate interval includes the rate-ratio no-difference value, while the interval for the risk difference includes zero. Their respective unadjusted p-values, 0.975 and 0.783, do not provide evidence of a clear group separation. The intervals are more informative than a yes-or-no reading of a p-value because they communicate the range of contrasts compatible with the data and method.

Confidence intervals rely on assumptions of the analysis used to calculate them. The registry record identifies MMRM for the sponsor’s primary analysis but does not report enough detail to evaluate all model assumptions or missing-data handling. The recalculated intervals use simpler, unadjusted summaries and are not the sponsor’s model-based intervals. Precision should therefore be read alongside the analysis method, the endpoint-specific sample size, and the limitations of the posted record.

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.

Sample-size figures are planning illustrations based on the observed effect, not the original trial’s design justification. The registry record’s illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers detecting the full observed effect and smaller fractions: 100%, 75%, and 50% of that effect. The trial’s own original design assumptions are not reported in the registry record.

For these outcomes, the figures are participants per arm. The registry’s general convention says time-to-event tables would instead give total events, but the outcomes are not presented as time-to-event calculations. A per-arm figure is the planned number in each group, not the combined total across groups.

The 80% power column describes the planned group size for a hypothetical study to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and assumptions are correct. The 90% power column describes the corresponding planning target for a 90% chance. Greater target power generally requires more participants for the same effect. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants when the effect used for planning is reduced from the full observed effect to a smaller fraction.

These are planning calculations, not observed power. They do not tell whether the completed trial was adequately designed for its original question, because the original design assumptions are not reported. Nor do they estimate the probability that the observed result is true. The calculations depend on the observed effect, which is itself uncertain, and use simplified assumptions that may not match the sponsor’s analysis.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 1.100; pooled standard deviation σ = 5.484.
2. n = 2 × (1.96 + 0.842)² × 5.484² / 1.100² = 390.1, rounded up to 391 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
delta <- 1.1                      # observed difference in means
sigma <- 5.48359536999387                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2516410)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 391 (80% power), 523 (90% power)
 75% of observed effect: n per arm = 694 (80% power), 929 (90% power)
 50% of observed effect: n per arm = 1,561 (80% power), 2,089 (90% power)
power.t.test: 391.1 
Simulated power at n = 391 per arm: 0.799 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 sponsor’s reported primary analysis used a mixed-effect repeated-measures model and estimated a least-squares mean difference of 1.2, with a 95% confidence interval from -0.3 to 2.6 and a reported p-value of 0.118. That is the trial’s model-based result for the primary endpoint.

The unadjusted recalculation from the posted group summaries estimates a mean difference of 1.1, with an unadjusted p-value of 0.195. It is a simple contrast based on summary statistics, not a reconstruction of the repeated-measures model. Its assumptions and information differ from those of the sponsor analysis, including the use of an approximate pooled standard deviation for the planning calculations.

The two estimates point in the same direction and are similar in scale, and the registry record does not identify a discrepancy between them. That agreement is reassuring as a basic consistency check, but the recalculation does not supersede the sponsor’s analysis. It cannot reproduce the model’s use of repeated observations or any model adjustments. The sponsor result should therefore anchor interpretation of the primary endpoint, while the recalculation remains a supplementary, unadjusted check. Neither analysis makes the estimate exact; the sponsor’s confidence interval includes zero, indicating substantial uncertainty about the group contrast.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 12 outcome measures, including the primary endpoint and secondary outcomes. When multiple outcomes or repeated comparisons are assessed, the chance of at least one apparently unusual result can increase. Statistical methods can address this issue by defining a hierarchy, adjusting significance thresholds, or controlling a family-wise error rate or false discovery rate. The registry record does not report whether any such multiplicity strategy was planned or applied. The secondary p-values available for the exacerbation outcomes are explicitly unadjusted, so they should not be treated as confirmatory evidence in isolation.

The record does not report a complete statistical analysis plan, the original sample-size justification, or whether interim analyses were planned or conducted. These details should be regarded as not reported in the registry record, rather than assumed absent. Without the plan, it is not possible to assess whether the outcome hierarchy, analysis population, model, or handling of multiple testing matched the design decisions made before the results were known.

The primary endpoint population is described as the Full Analysis Set, defined as randomized participants who received at least one dose. The endpoint description also says that the number analyzed refers to participants evaluable for that outcome. Those statements do not explain why a randomized participant might not be included in an endpoint analysis, or how any unavailable measurements were treated. The registry record does not report a detailed missing-data method, reasons for missing observations, or sensitivity analyses assessing the effect of missingness.

MMRM is identified as the sponsor’s primary method, but its use alone does not reveal the assumptions made about incomplete follow-up. General statistical interpretation of repeated-measures analyses depends in part on how missing observations relate to observed and unobserved outcomes. Since the record does not report that information, robustness to missing data cannot be judged from the posted results.

Denominators also vary by outcome: the primary endpoint lists 85 placebo participants and 82 active participants, while the exacerbation outcomes list 85 and 83. The record does not explain the differences. These are outcome-specific analyzed counts, not evidence by themselves of a particular exclusion or missing-data mechanism.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: infective pulmonary exacerbation of cystic fibrosis (14.1%), distal intestinal obstruction syndrome (3.6%), haemoptysis (2.4%), adenocarcinoma of colon (1.2%), lower respiratory tract infection bacterial (1.2%).

The registry record lists serious adverse events for 14 of 85 participants at risk in the placebo group and 11 of 83 at risk in the VX-661/IVA group. It reports zero deaths in each group. These counts describe the recorded serious adverse events during the trial; they do not, by themselves, establish that the groups had the same or different safety experience. The record also lists infective pulmonary exacerbation of cystic fibrosis at 14.1% among the serious adverse event terms, with other listed terms including distal intestinal obstruction syndrome, haemoptysis, adenocarcinoma of colon, lower respiratory tract infection bacterial, and pulmonary function test decreased.

Serious adverse event counts are not the same as counts of all adverse events, and a participant can potentially experience more than one event. The registry record gives the number at risk and number affected for serious events, but the summary alone does not describe event timing, duration, recurrence, relatedness assessment, or clinical course. It also does not provide a complete account of all harms in the excerpted results. The group counts should therefore be read descriptively and in the context of the trial’s follow-up through Week 12, not as a stand-alone assessment of comparative safety.

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

The primary result is an estimate of the average difference in change in percent predicted FEV1 between randomized groups through Week 12. The sponsor’s estimate is 1.2, and its 95% confidence interval ranges from -0.3 to 2.6. Because the interval includes zero, the result does not rule out no average difference under the analysis. It also permits values on either side of zero, so the estimate is not precise enough to establish the direction and size of the underlying group contrast with confidence.

This does not mean that the groups are known to be identical. Failure to establish a clear difference is not proof of equivalence. An equivalence conclusion would require an appropriate design and a prespecified margin, neither of which is reported in the registry record. Similarly, a non-significant result does not establish that the active regimen has no effect. It indicates that the posted data and analysis do not provide sufficiently clear evidence to distinguish the estimated contrast from no difference at the stated confidence level.

The result also does not establish clinical importance. The registry record does not provide a threshold for a clinically meaningful change in percent predicted FEV1. A statistical estimate and its uncertainty need clinical context to assess importance, and the average contrast does not convey the full range of individual responses. No individual-level response distribution is described in the posted summary.

General interpretation is bounded by the trial’s population, regimen, and follow-up. The record concerns participants aged 12 years and older with cystic fibrosis, an F508del mutation, and a second mutation described as not likely to respond to VX-661 and/or ivacaftor therapy. Treatment was assessed through Week 12. The result alone does not answer questions about different populations, regimens, outcomes, or longer follow-up.

Secondary outcomes and serious adverse event counts provide additional descriptions, but do not remove the uncertainty in the primary estimate. The exacerbation comparisons are also inconclusive, and secondary testing is unadjusted in the posted comparisons. The safest statistical summary is therefore limited: the registry reports a positive primary point estimate with an interval that includes no difference, alongside secondary event comparisons that do not clearly separate the groups.

18. Why This Trial Matters Statistically

This trial illustrates why an estimated effect, its uncertainty, and the analysis method need to be read together. The primary point estimate alone is positive, but its confidence interval crosses zero and extends in both directions. A reader who focuses only on the point estimate could overstate what the data establish; a reader who focuses only on a p-value could miss the range of effects compatible with the analysis.

It also demonstrates the distinction between a sponsor’s model-based analysis and a simple recalculation from group summaries. The reported MMRM uses repeated measurements, whereas the recalculation uses summary statistics and is unadjusted. Their similar direction offers a basic check, but they answer the question using different information and assumptions. Transparent recalculation can help readers inspect results, but it cannot substitute for participant-level data or reproduce an analysis whose details are not reported.

The registry record also makes endpoint-specific denominators and populations important. The primary and secondary analyses do not all list the same number analyzed. Recognizing those differences avoids treating enrollment as if every participant contributed to every outcome. At the same time, the record does not explain the differences, which limits assessment of missingness and analysis-population choices.

Finally, the trial shows why secondary outcomes and safety counts need context. Different endpoints measure distinct features of health, multiple unadjusted comparisons require caution, and descriptive serious event counts are not a complete comparative safety analysis. Statistical interpretation is strongest when it stays close to the estimand, method, precision, and scope of the posted record.

19. Limitations

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

The primary endpoint’s sponsor analysis is described as MMRM, but the registry record does not report the model’s covariates, covariance structure, visit terms, or missing-data assumptions. That limits independent assessment of the model specification. The record defines the Full Analysis Set and says participants analyzed were evaluable for the outcome, but does not explain exclusions or incomplete follow-up.

The summary-statistics recalculation is unadjusted and uses an approximate pooled standard deviation derived from standard errors and group sizes. It cannot reproduce the repeated-measures analysis and should not be given the same status as the sponsor result. Its confidence interval is also not the sponsor’s model-based interval.

The posted record does not report the original sample-size justification, the complete statistical analysis plan, any interim analysis plan, or a multiplicity strategy. The planning illustrations use the observed effect and simplified assumptions; they cannot establish whether the original design was adequately powered for the planned primary question. Secondary p-values are unadjusted, and the registry lists multiple outcomes, making isolated secondary findings particularly difficult to interpret as confirmatory.

The primary analysis has outcome-specific counts of 85 in the placebo group and 82 in the VX-661/IVA group; the exacerbation outcomes list 85 and 83. The reasons for the denominator differences are not reported. Some secondary outcomes are listed, but numeric results are not included in the available outcome summaries, limiting an assessment of the full secondary-outcome pattern.

Finally, the trial’s primary outcome timeframe ends at Week 12. The posted result does not address longer-term outcomes. Serious adverse event counts are descriptive and do not include enough detail in this summary to assess timing, recurrence, relatedness, or the full range of adverse events. These limitations constrain what can be concluded from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of VX-661 in Combination With Ivacaftor in Subjects Aged 12 Years and Older With Cystic Fibrosis, Heterozygous for the F508del-CFTR Mutation — NCT02516410.
• Registry record last updated 2018-06-12; status last verified 2018-05.
• Results first posted 2018-06-12.
• 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

NCT02516410 was a completed, randomized, triple-masked, parallel-group, placebo-controlled Phase 3 trial of VX-661 plus ivacaftor in participants aged 12 years and older with cystic fibrosis, an F508del mutation, and a second CFTR mutation described as not likely to respond to VX-661 and/or ivacaftor. The listed enrollment was 168, and treatment was assessed through Week 12.

The primary endpoint was absolute change from baseline in percent predicted FEV1. The sponsor’s MMRM analysis reported a least-squares mean difference of 1.2, with a 95% confidence interval from -0.3 to 2.6 and p = 0.118. The interval includes no difference. The unadjusted recalculation gives a similar-direction mean difference of 1.1 and p = 0.195, but does not reproduce the sponsor’s repeated-measures analysis.

Posted exacerbation comparisons also do not clearly distinguish the groups. The registry lists serious adverse events in both groups and zero deaths in each. Details of the original design assumptions, multiplicity strategy, and missing-data handling are not reported in the registry record.