Safety and Effectiveness of Juvéderm® VOLUMA XC Injectable Gel for Cheek Augmentation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Effectiveness of Juvéderm® VOLUMA XC Injectable Gel for Cheek Augmentation (NCT00978042), a randomized na study. The primary outcome is Responder Rate Based on Improvement in Score on Validated 6-point Mid-Face Volume Deficit Scale (MFVDS).

2. Clinical Question

The MFVDS is a validated 6-point scale for evaluating mid-face volume deficit. Its scores range from 0, none, to 5, severe. For the primary outcome, improvement meant a reduction of at least one grade from the pre-treatment assessment to the 6-month assessment. The score was based on the average of assessments by blinded, independent Evaluating Investigators.

The comparison is a randomized treatment-versus-no-treatment contrast at the six-month assessment. The control arm’s planned transition to treatment after 6 months matters to interpretation: the primary question concerns the period in which that arm had not yet received treatment, not a continuing untreated comparison over the full follow-up.

The registry lists three secondary outcomes: duration of treatment effect, responder rate based on the Global Aesthetic Improvement Scale, and responder rate based on MFVDS by facial region. Numerical results are posted for duration of treatment effect; results for the other two are not reported in the registry record.

3. Trial Design

This was a randomized, single-blind, parallel-group study described as multicenter. The registry lists an enrollment of 345 and a completed status. The study start is recorded as 2009-08 and primary completion as 2012-11. The phase is listed as NA.

Participants were assigned to a VOLUMA® XC treatment arm or a no-treatment control arm. The treatment arm received Juvéderm® VOLUMA® XC Injectable Gel at study start, with the investigator determining the volume up to 12 mLs. The control arm received no treatment for 6 months and then received the gel. Participants in either arm could be eligible for re-treatment if applicable.

The primary outcome was assessed at 6 months, when the randomized contrast was treatment versus no treatment. For that outcome, the registry describes the analysis population as participants randomized to treatment who received treatment and participants randomized to no treatment, with data available for analysis. The posted primary outcome includes 209 participants in the treatment arm and 36 in the control arm. These outcome counts should not be confused with total enrollment; a full account of the difference is not reported in the registry record.

The registry identifies the intervention as a device and names Allergan as sponsor. It does not report the details of the randomization procedure, allocation concealment, who was masked, or the planned statistical methods. The single-blind designation alone does not identify which study roles were masked. Original sample-size assumptions and any prespecified analysis plan 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: Prior to randomization, 16 patients were excluded as screen failures and the first two participants per site (30 total) were treated as run-in participants. Of the 299 randomized participants, 17 were discontinued prior to treatment, leaving a "modified intent-to-treat" population of 282 participants (235 in Treatment Arm and 47 in Control Arm).

Initial Treatment Period

Reasons for not completing this period:

Received Repeat Treatment

Analysis population for the primary outcome, as defined in the registry: Participants from the Modified-intent-to-treat (MITT) population, all participants randomized to treatment who received treatment and all participants randomized to "no treatment" control arm, with data available for analysis.

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 Responder Rate Based on Improvement in Score on Validated 6-point Mid-Face Volume Deficit Scale (MFVDS), measured over 6 months.

The primary endpoint is the responder rate at 6 months, expressed as the percentage of participants meeting a defined improvement criterion on the validated 6-point MFVDS. A participant counted as a responder if the average overall MFVDS score assigned by blinded, independent Evaluating Investigators was at least one grade lower than the average pre-treatment score. Lower scores indicate less volume deficit, with 0 representing none and 5 representing severe.

A responder rate turns a change in a graded clinical assessment into a binary outcome: each participant either meets the stated threshold or does not. That makes the result straightforward to describe as the proportion of participants with a specified degree of improvement. It also means that the endpoint does not show how far beyond the threshold a responder improved, or how much a non-responder’s score changed.

The one-grade threshold gives the outcome a prespecified clinical interpretation within the registry’s definition, rather than treating every score movement as a response. The endpoint is based on averaged evaluator assessments, which is relevant because the measure is a scored assessment rather than a direct physical measurement. The registry does not report how the threshold was selected or whether other thresholds were examined.

7. Results Posted in the Registry

• VOLUMA® XC Treatment Arm: 85.6% (179/209) versus 38.9% (14/36) on control; risk difference 46.8 percentage points (95% CI 30.1 to 63.4), risk ratio 2.20 (1.46–3.33); 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.

Duration of Treatment Effect

• 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:
  • VOLUMA® XC Treatment Arm: 44.7% (105/235) versus 45.7% (16/35) on control; risk difference -1.0 percentage points (95% CI -18.7 to 16.7), risk ratio 0.98 (0.66–1.44); unadjusted two-proportion z-test p = 0.909.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between VOLUMA® XC Treatment Arm and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists three secondary outcomes: duration of treatment effect, responder rate based on improvement in GAIS, and responder rate based on improvement in MFVDS by facial region. Numerical results are posted for duration of treatment effect at 24 Months. Numerical results for the GAIS responder rate and the facial-region MFVDS responder rate are not reported in the registry record.

The overall pattern is that the primary six-month comparison shows a clear separation in responder rates, while the posted later duration comparison does not show a similarly clear difference. These outcomes address distinct questions: the primary endpoint is whether participants reached the overall MFVDS responder threshold at 6 months, whereas duration concerns persistence of treatment effect at a later assessment. The secondary outcome therefore does not simply replicate the primary endpoint at another time.

Secondary outcomes can add context, but their inferential weight depends on how they were specified and analyzed. The registry does not report a multiplicity adjustment plan or a complete set of numerical findings for the listed secondary endpoints. When several outcomes are assessed, the chance of observing apparently notable results across the set can increase if each is interpreted independently. Without a prespecified testing hierarchy or adjustment details, unadjusted secondary comparisons are more appropriately treated as supportive or descriptive than as confirmatory evidence.

The absence of posted numerical results for two listed secondary outcomes is also relevant. It prevents a reader from assessing whether their findings align with the primary outcome, how precise they are, or whether they raise any conflicting pattern. The record does not say why those results are absent. They should therefore be described as not reported in the registry record, rather than interpreted as showing no effect.

Secondary outcomes may differ in scale, definition, timing, and analysis population. General statistical explanation: agreement across independently meaningful outcomes can strengthen a coherent interpretation, but outcomes are not interchangeable, and apparent agreement may be less informative if analyses are correlated or selected after data review. The registry does not provide enough analysis detail to assess those possibilities for the secondary measures.

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

• Duration of Treatment Effect
• Responder Rate Based on Improvement in Score on Global Aesthetic Improvement Scale (GAIS)
• Responder Rate Based on Improvement in Score on MFVDS by Facial Region

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is classified as a responder or not a responder using the MFVDS improvement rule. A responder rate is the share of analyzed participants who meet the rule. The treatment and control rates describe each arm separately, while the risk difference compares those two proportions on an additive scale. A positive reported difference means that the observed responder proportion was higher in the treatment arm than in the control arm.

What does the confidence interval add?

General statistical explanation: a confidence interval represents uncertainty around an estimated effect under the procedure used to construct it. It is not a range containing a fixed percentage of individual participant outcomes, and it does not mean that every effect within the interval is equally plausible. The primary risk-difference interval extends from 0.301 to 0.634. Because the interval is entirely above zero, the reported estimate is compatible with a positive difference across the interval’s values. Its width also shows that the exact magnitude is less precisely determined than the direction of the contrast.

What does the p-value mean?

General statistical explanation: a p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be if that null hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, and it does not quantify the size or importance of an effect. The registry reports an unadjusted p-value of <0.001 for the primary comparison. The specific test and its assumptions are not reported in the registry record, so the p-value should be read as posted rather than as evidence about a particular unreported test procedure.

Why distinguish the risk difference from relative measures?

The risk difference expresses the contrast between proportions as an additive quantity. Relative measures such as a risk ratio or odds ratio express the relationship on a different scale and answer a different descriptive question. The registry comparison also reports relative measures, but they should not be treated as interchangeable with the risk difference. In particular, an odds ratio is not itself a difference in responder percentages. The appropriate scale depends on the scientific question; the primary result is framed as responder rates and a risk difference.

How does randomization support interpretation?

General statistical explanation: random allocation is intended to make treatment groups comparable, on average, with respect to both measured and unmeasured baseline characteristics. That supports interpreting an observed between-arm contrast as a treatment-assignment comparison, provided the trial conduct and analysis preserve that comparison. The registry identifies the study as randomized, but the randomization method, allocation concealment, and details of analysis by assigned group are not reported. The primary population description includes treatment-arm participants who received treatment and control-arm participants with data available for analysis, so the registry does not describe a complete all-randomized analysis for both arms.

What does the responder definition leave out?

A binary endpoint can be easy to communicate, but dichotomizing a scale loses information. It does not distinguish a participant just meeting the threshold from one with a larger score reduction. Nor does it describe the distribution of score changes among those who did not meet the threshold. The registry posts the responder outcome and its analysis population, but does not report the underlying score-change distribution or the number of participants at each MFVDS score. Interpretation should therefore stay focused on the defined responder event.

Why do analysis details matter?

General statistical explanation: inference depends on how observations are selected, how missing measurements are handled, and how the comparison is calculated. The registry specifies that primary participants needed data available for analysis, but it does not report a missing-data procedure, sensitivity analyses, or a detailed analysis plan. It also does not report whether the primary analysis adjusted for baseline values or other characteristics. These omissions prevent a reader from determining whether the posted estimates came from an adjusted or unadjusted model, or how the result might change under alternative assumptions about unavailable observations.

The primary comparison is listed with a risk difference and a confidence interval, alongside relative measures and an unadjusted p-value. These summaries are complementary, but none supplies information that is absent from the analysis description. The registry lists 4 outcome measures and 0 analyses in its analysis listing; the posted outcome statistics are still available, but a full record of prespecified analysis methods is not. That distinction limits the ability to verify which analyses were planned before results were examined.

General statistical explanation: confidence intervals are most informative when read with the estimand, population, and analysis method in view. In this study, the estimand is naturally read as a six-month difference in the proportion meeting the MFVDS responder definition between the randomized treatment and no-treatment groups represented in the posted primary analysis. Any broader interpretation requires caution because the registry does not give complete details of participant disposition, missing observations, or the analysis plan.

11. Confidence Intervals and Precision

For the primary comparison, the reported risk difference is 0.468, with a 95% confidence interval from 0.301 to 0.634. The interval is wholly above zero, supporting the interpretation that the observed responder proportion was higher in the treatment arm in this analysis. The interval also indicates uncertainty about the size of the difference: the data are compatible with multiple positive values, not a single exact effect.

A confidence interval describes the precision of an estimated contrast under the method used to calculate it. General statistical explanation: a narrower interval indicates greater precision than a wider interval when the same quantity and method are being compared. Precision is not the same as validity; a narrow interval cannot correct for bias, incomplete outcome data, or an inappropriate analysis. The registry does not report the confidence-interval method, so the interval can be interpreted as posted but not independently assessed against a specified procedure.

The treatment and control outcome counts are 209 and 36, respectively. The smaller control group contributes less information to its proportion than an equally sized group would, all else being equal. The registry does not provide a participant-flow account explaining why the primary outcome counts are smaller than the enrollment of 345, nor does it report the number of missing primary outcomes by arm. Those gaps make it difficult to assess whether the analyzed participants represent all randomized participants.

The duration-of-treatment-effect comparison has a confidence interval for the risk difference that includes zero, unlike the primary contrast. Its arm-specific intervals are also wider for the control group, consistent with the smaller posted control count for that outcome. These intervals describe uncertainty at a different assessment and for a different endpoint; they should not be used to alter the meaning of the six-month primary estimate.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are expressed as participants per arm for 80% power and participants per arm for 90% power. This outcome is binary, not time-to-event, so the figures refer to participants per arm rather than a total number of events. The calculations use a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. They use the observed effect or a stated fraction of it as the effect to detect. The trial’s original design assumptions are not reported in the registry record.

For the primary comparison, the planning illustration using 100% of the observed effect gives 16 participants per arm for 80% power and 21 participants per arm for 90% power. Planning for 75% of the observed effect gives 31 participants per arm for 80% power and 40 participants per arm for 90% power. Planning for 50% of the observed effect gives 71 participants per arm for 80% power and 95 participants per arm for 90% power.

In plain language, the 80% column describes the planned number per arm for a design with an 80% chance of detecting the chosen effect under the stated assumptions; the 90% column describes the corresponding number for a 90% chance. Smaller effects need more participants to detect, which is why the illustrations increase as the assumed fraction of the observed effect decreases. These are planning illustrations based on the observed effect, not the original trial’s design calculation. They are not observed power.

For the secondary duration outcome, the same planning assumptions produce much larger participant requirements because the observed comparison is close to zero. The figures for that outcome are also per arm. Such illustrations are sensitive to the effect chosen and should not be treated as proof that a study of a particular size would reproduce the observed result.

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 = 0.389; treatment proportion p₁ = 0.856; average p̄ = 0.623.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6855 = 1.3435.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6005 = 0.5054.
4. n = (1.3435 + 0.5054)² / (0.4676)² = 15.6, rounded up to 16 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 <- 0.388888888888889                          # control proportion
p1 <- 0.856459330143541                          # 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(978042)
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 = 16 (80% power), 21 (90% power)
 75% of observed effect: n per arm = 31 (80% power), 40 (90% power)
 50% of observed effect: n per arm = 71 (80% power), 95 (90% power)
power.prop.test: 15.6 
Simulated power at n = 16 per arm: 0.829 (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 lists one primary outcome and three secondary outcomes, but does not report a multiplicity strategy. It is not reported in the registry record whether the primary outcome was the sole confirmatory test, whether secondary outcomes were arranged in a testing hierarchy, or whether any adjustment was planned for making multiple comparisons. The primary p-value is explicitly unadjusted. Without a stated plan, readers cannot determine whether the nominal interpretation of individual p-values accounts for the number of outcomes or analyses considered.

Multiplicity matters because each additional statistical test creates another opportunity to observe a result that appears unusual under a null hypothesis. General statistical explanation: adjustment methods or prespecified testing sequences can control how evidence is judged across multiple tests, but they may change the threshold or interpretation for each test. No such method should be inferred from the registry’s list of outcomes. In addition, numerical results for two listed secondary outcomes are not reported in the registry record, so the full pattern across planned outcomes cannot be reviewed.

The primary population is described as Modified-intent-to-treat: all participants randomized to treatment who received treatment and all participants randomized to the no-treatment control arm, with data available for analysis. This definition uses treatment receipt for the active arm and available data for both groups. The registry does not report a participant flow by arm, the number excluded from the primary analysis, reasons for unavailable data, or a comparison of included and excluded participants.

Missing-data handling is not reported in the registry record. It is also not reported whether missing primary outcomes were imputed, whether incomplete observations were treated as non-responders, or whether sensitivity analyses assessed alternative assumptions. Those choices can affect a binary responder rate, especially if the likelihood of missing data differs between arms or is related to outcome status. No such difference should be presumed, but it cannot be assessed from the posted description.

The record lists 0 analyses in its analysis listing, while providing outcome estimates and a primary comparison. A detailed statistical analysis plan, model specification, test procedure, baseline adjustment, and analysis-population sensitivity checks are not reported in the registry record. The available results support description of the posted comparison, but do not supply the information needed to establish how closely the analyses followed prespecified methods.

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: basal cell carcinoma (0.7%), cerebrovascular accident (0.6%), hip fracture (0.6%), inflammation (0.4%), injection site mass (0.4%).

For adverse events after initial treatment, the registry reports serious adverse events in 11 of 270 participants at risk, and other adverse events in 98 of 270 participants at risk. After repeat treatment, serious adverse events are reported in 2 of 167 participants at risk, and other adverse events in 15 of 167 participants at risk. These are separate reporting periods; the figures should not be added or treated as a single participant-level total.

The listed serious adverse event terms and percentages include basal cell carcinoma, 0.7%; cerebrovascular accident, 0.6%; hip fracture, 0.6%; inflammation, 0.4%; injection site mass, 0.4%; and carcinoid tumour pulmonary, 0.4%. The registry does not report deaths in these adverse-event entries. A relationship between these events and treatment is not established by the figures alone, and details of event timing, severity beyond the serious classification, and comparative attribution are not reported in the registry record.

These counts describe reported events in the listed groups; they do not by themselves establish whether the treatment caused an event or permit a complete comparison of safety between randomized groups. Interpretation is limited by the absence of detailed event definitions, exposure time, and a full account of how adverse events were collected and assessed.

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

The primary result describes the proportion of analyzed participants who met a specific improvement threshold on the overall MFVDS at 6 months. The treatment arm had a higher posted responder rate than the no-treatment control arm, and the reported confidence interval for the risk difference lies above zero. This is evidence about the study’s defined endpoint and comparison, not a complete account of all changes in facial volume deficit or all dimensions of participant experience.

The endpoint is threshold-based. It distinguishes participants who improved by at least one grade from those who did not meet that criterion, but it does not show the amount of improvement for each participant. A non-responder could have had some score improvement without reaching the threshold; the registry does not report those score distributions. The outcome also relies on averaged Evaluating Investigator assessments, and the record does not describe inter-rater agreement or the procedures used to resolve differing assessments.

The randomized comparison is limited to the six-month period before the no-treatment control group began treatment. It does not provide a continuing untreated control comparison at later times. The duration outcome has a different time frame and does not answer exactly the same question as the primary endpoint. The registry’s secondary outcomes should not be treated as interchangeable evidence, and two of the listed secondary outcomes have no numerical results reported in the registry record.

Statistical evidence is not the same as a statement about clinical importance. The registry’s responder definition supplies a threshold, but it does not report how that threshold relates to participants’ judgments of meaningful benefit. The result also does not establish how well the findings generalize beyond the enrolled study population, because detailed eligibility criteria and participant characteristics are not reported in the registry record.

The safety counts are descriptive and do not establish causation. The registry does not give sufficient detail to determine from these figures alone whether any particular event was related to treatment, nor do the counts replace a full evaluation of benefits and risks. The results should be read as posted outcome and adverse-event summaries, with their population, timing, and reporting limitations in view.

17. Why This Trial Matters Statistically

This study illustrates how a responder endpoint translates a clinical rating scale into a binary outcome. That makes the primary result accessible as a proportion meeting a defined threshold, while also discarding information about the amount and distribution of score changes. Statistical interpretation therefore depends on understanding the responder definition, not only reading the treatment and control rates.

It also illustrates why timing and comparator matter. The six-month comparison is between treatment and no treatment, but the control group then received the intervention. A later outcome cannot automatically be interpreted as another randomized treatment-versus-untreated contrast. Distinguishing the original comparison from later follow-up prevents the primary finding from being extended beyond the period and question it addresses.

The reported confidence interval is essential alongside the point estimate and p-value. It communicates a range of effect magnitudes compatible with the data under the interval method, while the p-value addresses evidence against a null comparison under the test assumptions. Neither statistic replaces the need to assess the analysis population, completeness of outcomes, and prespecified methods. In this record, several of those details are not reported.

The study also highlights the importance of separating observed results from planning calculations. The sample-size illustrations use the observed effect as a planning reference, while the original design assumptions are not reported. The illustrations can show how required enrollment changes with the effect to detect, but they cannot establish what assumptions guided the trial or how much power the completed trial had.

Finally, multiplicity and incomplete secondary reporting affect the overall evidence picture. A strong-looking primary comparison does not resolve the missing analysis details, and the absence of numerical results for listed secondary outcomes should not be mistaken for null findings. Clear statistical reporting needs to show how outcomes, populations, missing data, and multiple tests were handled.

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

The primary outcome counts are 209 in the treatment arm and 36 in the control arm, compared with total enrollment of 345. The registry does not report participant flow or explain the differences between total enrollment and the outcome analysis counts. It also does not provide the number or reasons for missing outcome measurements by arm, limiting assessment of potential selection or missing-data effects.

The registry describes the primary analysis population as participants randomized to treatment who received treatment and no-treatment participants with data available. This is not described as a complete all-randomized analysis in both arms. The record does not report sensitivity analyses using alternative populations or assumptions about missing observations, so robustness to those choices cannot be assessed.

Details of the randomization procedure and concealment are not reported, and the single-blind designation does not specify which parties were masked. The registry does not report the statistical test, model, confidence-interval method, baseline adjustment, or a prespecified statistical analysis plan. It also does not report the original sample-size justification or any interim-analysis plan.

Two listed secondary outcomes have no numerical results reported in the registry record, and no multiplicity plan is reported. This limits assessment of the full pattern across outcomes and the inferential status of secondary findings. The study’s no-treatment control changed to treatment after 6 months, restricting the untreated randomized comparison to the primary assessment period.

Participant characteristics and detailed eligibility criteria are not reported in the registry record for this record, limiting assessment of generalizability. Safety summaries do not include detailed attribution, event timing, or exposure information, and deaths are not reported in the adverse-event entries. These limitations do not negate the posted primary comparison, but they constrain how precisely its methods, robustness, safety context, and broader applicability can be evaluated.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Effectiveness of Juvéderm® VOLUMA XC Injectable Gel for Cheek Augmentation — NCT00978042.
• Registry record last updated 2015-11-03; status last verified 2015-09.
• Results first posted 2014-02-13.
• 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

NCT00978042 is a completed, randomized, single-blind, parallel-group, multicenter study sponsored by Allergan. The registry lists enrollment of 345, a study start of 2009-08, and primary completion of 2012-11. The intervention was Juvéderm® VOLUMA XC for cheek augmentation; the comparator received no treatment for 6 months and then received VOLUMA® XC.

The primary outcome was the six-month responder rate on the validated 6-point MFVDS, requiring an improvement of at least one grade. The posted analysis reports higher responder proportions in the treatment arm than in the no-treatment arm, with a positive risk-difference interval and an unadjusted p-value of <0.001. The primary analysis population is described as Modified-intent-to-treat participants with data available for analysis.

The registry lists three secondary outcomes, with numerical results reported for duration of treatment effect. Original design assumptions, detailed statistical methods, missing-data procedures, and multiplicity handling are not reported in the registry record.