RHA® 4 NLF Cannula: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for RHA® 4 NLF Cannula (NCT04754646), a randomized na study. The primary outcome is Change in NLF-WSRS Score Between Baseline and Week 12 After Last Treatment as Assessed by the BLE.

2. Clinical Question

This is a within-person comparison: each participant received both injection approaches, one on each side of the face. That design makes the contrast between sides the central question rather than a comparison of separate groups of participants. The principal measure is the change in NLF-WSRS score from baseline to the stated follow-up. The scale runs from 1, “Absent,” to 5, “Extreme,” so a decrease represents a lower severity rating.

The study also listed outcomes involving investigator ratings, responder status, global aesthetic improvement, participant satisfaction, and FACE-Q assessment. These provide additional perspectives on severity and perceived outcomes, but they do not replace the prespecified primary comparison. The registry record does not report the non-inferiority margin or the sponsor’s analysis details; without those, a statistical conclusion about the trial’s non-inferiority objective cannot be reconstructed from the posted summary statistics.

3. Trial Design

The registry describes a randomized, controlled, single-blinded, prospective, multicenter study with a within-subject split-face design. Each participant received RHA®4 in both nasolabial folds: one side was treated with a cannula and the other with a sharp needle. The sequence of injections and the side assigned to the cannula were randomized. The treating investigator administered the devices and was unblinded to treatment allocation; effectiveness assessments were conducted by a blinded live evaluator.

The registry lists the study as completed and reports an enrollment of 50. The primary endpoint concerns the per-protocol population. The record states that 4 participants had at least one major protocol deviation that led to exclusion from that population. The primary outcome summaries list 46 observations for each injection approach. Because treatment was split across each participant’s face, those arm-level entries should not be read as separate independent groups of participants.

Initial treatment occurred at Week 0. A touch-up could be given at Week 4 if necessary, using the same approach assigned initially. Participants who received a touch-up had an additional visit 4 weeks later; participants who did not receive one did not attend that visit. The primary assessment was at Week 12 after the last treatment. The record notes that this could be up to 16 weeks after baseline.

The trial’s own sample-size justification, original design assumptions, interim analyses, and detailed statistical analysis plan are not reported in the registry record. The study’s stated objective was non-inferiority, but its non-inferiority margin is also not reported. Those omissions limit what can be concluded about how the design was intended to establish that objective.

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: Per Protocol population (Of the 50 subjects randomized, 4 subjects experienced at least one major protocol deviation that resulted in their exclusion from the PP population)

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 Change in NLF-WSRS Score Between Baseline and Week 12 After Last Treatment as Assessed by the BLE, measured over Week 12 after last treatment.

The primary endpoint is the change from baseline in NLF-WSRS score at Week 12 after the last treatment, as assessed by the blinded live evaluator. NLF-WSRS is a validated five-grade scale for nasolabial-fold severity, with 1 meaning “Absent” and 5 meaning “Extreme.” A lower score therefore indicates a less severe rating; a negative change indicates a reduction in the score from baseline.

Change from baseline is used to describe how the rating shifted over the treatment period, rather than relying only on a follow-up score. The evaluator’s blinding is intended to reduce the chance that knowledge of which injection approach was used affects the rating. Since both approaches were used on each participant, the main scientific contrast is the difference in change between the cannula-treated side and the needle-treated side.

The protocol description states that an NLF-WSRS change of >1 grade would be considered clinically significant. That statement is about the scale change; it is not the non-inferiority margin. The margin required for interpreting a non-inferiority test is not reported in the registry record. Thus, the posted average changes can describe the observed score pattern, but do not by themselves establish whether the study met its stated non-inferiority criterion.

7. Results Posted in the Registry

• RHA®4 - Needle: mean -1.65 versus -1.61 on control; difference -0.04 (95% CI -0.13 to 0.05), standardized effect d = -0.19; z-test p = 0.361.

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 Responders (Change of ≥1-grade From Baseline in the Naso-labial Folds Severity) as Assessed by the Blinded Live Evaluator (BLE) at Week 12 After Last Treatment Using the NLF-WSRS.

• 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:
  • RHA®4 - Needle: 94.0% (47/50) versus 94.0% (47/50) on control; risk difference 0.0 percentage points (95% CI -9.3 to 9.3), risk ratio 1.00 (0.91–1.10); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RHA®4 - Needle and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning evaluator-rated severity, responder status, global aesthetic improvement, participant satisfaction, and FACE-Q assessment. These outcomes extend the primary severity-score comparison by considering categorical improvement, overall impressions, satisfaction, and participant-reported experience. They can offer complementary descriptions, but they do not change what the primary endpoint measured or supply the missing non-inferiority margin.

The detailed secondary responder comparison in the posted results has the same responder count for the two approaches. That pattern is directionally consistent with the close primary mean changes, but the outcomes use different definitions and should not be treated as interchangeable evidence. A count crossing a response threshold describes how many observations meet that definition; a mean change describes the average score shift. Agreement in broad pattern does not substitute for an analysis of the primary objective.

The registry identifies 16 secondary outcomes as posted, but detailed reported analyses are not available for most of the secondary outcome categories in the record. The listed outcomes include several time points and ratings by different assessors, as well as participant-reported measures. Without complete estimates and methods for these outcomes, an overall pattern across all secondary results cannot be evaluated reliably.

Secondary comparisons generally carry less weight than a prespecified primary analysis, especially when many outcomes, time points, or assessors are considered. Each additional test creates more opportunity for a seemingly notable result to arise by chance. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. The posted secondary results should therefore be viewed as supportive or exploratory rather than as a substitute for the primary comparison.

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

• Change in Score From Baseline in the Nasolabial Folds Severity Rated by the Treating Investigator (TI) at Weeks 4, 8 and 12 After Last Treatment Using the NLF-WSRS.
• Number of Responders (Change of ≥1-grade From Baseline in the Naso-labial Folds Severity) as Assessed by the Blinded Live Evaluator (BLE) at Week 12 After Last Treatment Using the NLF-WSRS.
• Number of Responders (Change of ≥1-grade From Baseline in the Naso-labial Folds Severity) as Assessed by the Treating Investigator (TI) at Weeks 4, 8 and 12 After Last Treatment Using the NLF-WSRS.
• Number of Subjects Scored Either "Much Improved" or "Improved" on Global Aesthetic Improvement (GAI) Scale by the Blinded Live Evaluator (BLE) at 12 Weeks Following Last Treatment.
• Number of Subjects Scored Either "Much Improved" or "Improved" on Global Aesthetic Improvement (GAI) Scale by the Treating Investigator (TI) at 4, 8 and 12 Weeks Following Last Treatment.
• Number of Subjects Who Scored Themselves Either "Much Improved" or "Improved" on Global Aesthetic Improvement (GAI) Scale at 4, 8 and 12 Weeks Following Last Treatment.
• Number of Subjects "Satisfied" or "Very Satisfied" With Study Treatment Using the Subject Satisfaction Scale at 4, 8 and 12 Weeks Following Last Treatment.
• Subject's Perception of Treatment Effectiveness as Per the FACE-Q | Aesthetics© (Nasolabial Folds Domain) Questionnaire. The FACE-Q Measures the Experience and Outcomes of Aesthetic Facial Procedures From the Patient's Perspective.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary measure is continuous: it is a score on a five-grade scale, and the registry reports the mean change and standard deviation for each injection approach. A mean summarizes the average change across observations. A standard deviation describes the spread of individual changes around that average; it is not the uncertainty in the mean itself. A small standard deviation means the observed changes are more clustered around the average, while a larger one means they are more dispersed.

What does the mean difference represent?

The recalculated mean difference compares the posted average changes. The arm means are -1.61 for cannula and -1.65 for needle, and the recalculated difference is -0.04, expressed as needle relative to cannula. A difference near zero indicates that the two posted averages are close. The sign identifies the direction of the subtraction, but the clinical interpretation still depends on the scale and the study’s objective. Because lower scores correspond to lower severity, the negative mean changes indicate reductions in the rating from baseline.

This difference is a simple unadjusted recalculation from the posted summary statistics. It does not represent a reported sponsor analysis: the registry record lists no reported analyses for the primary outcome. The recalculation also does not incorporate individual-level paired differences. In a split-face design, the two sides belong to the same participant, so observations within a participant are related rather than independent. A paired analysis can use that relationship, but the within-participant correlation and the sponsor’s analysis method are not reported in the registry record.

How should the confidence interval be read?

A confidence interval gives a range of values compatible with the data under the method used to calculate it. The recalculated interval for the mean difference runs from -0.126 to 0.046. It includes zero, which is the value representing no average difference under this contrast. The interval is not a range that guarantees the true value lies within it, and it does not indicate the probability that one approach is better. It describes uncertainty in the estimate under the calculation’s assumptions.

For a non-inferiority question, the important comparison is not only whether the interval includes zero. The interval must be interpreted relative to a prespecified non-inferiority margin. If the estimated difference and its uncertainty satisfy that margin in the direction required by the trial, non-inferiority may be supported. The margin is not reported in the registry record, so that determination cannot be made from the posted summaries.

What does the p-value add?

The unadjusted p-value of 0.361 is part of the recalculated comparison. In general, a p-value measures how unusual the observed data, or data more extreme, would be under a specified null hypothesis and model. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. A p-value that does not indicate a conventional difference cannot prove equivalence or non-inferiority. Those are different claims and require their own specified hypotheses and decision criteria.

The p-value is unadjusted, and the registry record does not describe a sponsor analysis or a multiplicity procedure for the primary and secondary outcomes. It should therefore be read as a descriptive inferential calculation, not as a definitive trial-level conclusion. In addition, an analysis that treats the two sides as independent would not reflect the paired design; the posted summary statistics do not supply the paired information needed to reproduce a paired test.

Why does over-dispersion matter?

For a continuous outcome, the standard deviation describes variability around the mean. In general, over-dispersion is most often discussed with count or binary data: it means outcomes vary more than a model assumes. If a model understates variability, its standard errors can be too small and its confidence intervals too narrow. The primary outcome is continuous, and the registry reports standard deviations rather than a count model. No over-dispersion assessment is reported in the registry record, so it should not be assumed to have been tested or corrected.

For secondary responder outcomes, a general binomial model would assume a specified relationship between the response probability and its variability. The split-face pairing also matters for those outcomes because both sides are measured in the same participant. Without individual-level data and the analysis plan, neither the dependence structure nor any adjustment for extra variability can be assessed.

What does the split-face design change?

In general, pairing can improve precision when each participant’s two measurements are strongly related, because each participant serves as their own comparison. The analysis then focuses on the within-participant contrast. The benefit depends on the degree of correlation between the two sides and on whether the paired differences are analyzed appropriately. The registry record does not report the correlation, paired differences, or detailed analysis method.

The recalculated comparison uses the posted arm means, standard deviations, and sample sizes and is therefore a simple unadjusted summary-based calculation. It cannot reconstruct the participant-level paired analysis. The trial’s stated design and outcome summaries should be considered together: the means describe the two treatment-side averages, while the available recalculation cannot fully use the within-person structure. The sponsor’s analysis is not reported, so the recalculation should not be mistaken for it.

11. Confidence Intervals and Precision

The recalculated primary mean difference is -0.04, with a 95% confidence interval from -0.126 to 0.046. The interval is the key description of precision: it shows that the posted summaries are compatible with a range of average differences on either side of zero under the unadjusted calculation. Its inclusion of zero means the summaries do not establish a clear average difference by this comparison. It does not demonstrate that the approaches are equivalent.

Precision describes how tightly an estimate is determined, not whether the estimate is clinically important or whether a study objective has been met. The endpoints of this interval are close to the point estimate, but assessing whether that range is acceptably small requires a clinical or statistical threshold. The trial’s non-inferiority margin is not reported in the registry record. The protocol’s statement that a change greater than 1 grade is clinically significant concerns score change and does not supply that margin.

The interval is recalculated from posted summary statistics and does not use the within-participant pairing information that would be needed for a paired analysis. Since the study assigns both approaches to each participant, the actual uncertainty under an analysis that accounts for pairing could differ. The registry record does not report the paired correlation, the sponsor’s analysis, or a sponsor confidence interval.

The group means and standard deviations provide useful descriptive context, but they do not show the distribution of participant-level changes or the number of participants with particular changes. The interval should therefore be read as precision for the recalculated average contrast, not as a statement about the likely response of an individual participant or the proportion meeting a threshold.

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

The figures are participants per arm, not total events. The 80% power column describes the planned number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the illustration’s assumptions, if that effect were the true one and the model assumptions held. The 90% power column makes the same kind of planning calculation with a higher target chance of detecting that effect. These are design concepts, not guarantees about what a future study would observe.

The rows show planning for 100%, 75%, and 50% of the observed effect. As the effect to detect becomes smaller, more participants are needed to distinguish it from random variation under the same assumptions. The displayed counts are therefore sensitive to the observed effect used as a starting point. In this study, the primary design is split-face, while the planning assumptions specify equal allocation between two arms; these illustrations should not be treated as a reconstruction of the trial’s actual paired design plan.

This is not observed power. It is a planning exercise based on the observed effect and stated assumptions, not a measure of the probability that the completed study found a true effect.

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 = -0.040; pooled standard deviation σ = 0.210.
2. n = 2 × (1.96 + 0.842)² × 0.210² / -0.040² = 432.7, rounded up to 433 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 <- -0.0399999999999998                      # observed difference in means
sigma <- 0.21                     # 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(4754646)
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 = 433 (80% power), 580 (90% power)
 75% of observed effect: n per arm = 770 (80% power), 1,030 (90% power)
 50% of observed effect: n per arm = 1,731 (80% power), 2,317 (90% power)
power.t.test: 433.6 
Simulated power at n = 433 per arm: 0.794 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and a broad set of secondary outcomes covering severity ratings, response thresholds, global aesthetic improvement, satisfaction, and FACE-Q. Several outcomes are assessed at multiple follow-up times or by different evaluators. When many outcomes and time points are tested, the chance of at least one apparently notable result can increase. Statistical methods can address that issue through prespecified testing hierarchies or multiplicity adjustments, but those plans are not reported in the registry record.

The registry record lists no reported analyses for the primary endpoint and no reported analyses for the secondary outcomes in the analysis field. The recalculated comparisons are unadjusted calculations from posted summary statistics, not documented sponsor analyses. No multiplicity strategy, missing-data method, or sensitivity analysis is reported. The original statistical analysis plan is not reported in the registry record.

The primary endpoint uses the per-protocol population. The record states that 4 participants with at least one major protocol deviation were excluded from that population. Arm summaries list 46 observations for each treatment approach. Because the design is split-face, these entries reflect treatment sides within participants, not separate randomized participant groups. The registry does not report details about missing primary outcome values, reasons for missingness, imputation, or how participants with incomplete paired measurements were handled.

Per-protocol analysis can be relevant to a non-inferiority objective, but it can also be affected by exclusions and protocol deviations. In general, examining both per-protocol and intention-to-treat analyses can help assess robustness in a non-inferiority trial. The registry record does not report an intention-to-treat analysis or enough detail to evaluate how the exclusions affected the result. The non-inferiority margin and the sponsor’s primary analysis method are also not reported, preventing a full appraisal of the intended decision process.

15. 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 non-serious adverse event terms

The registry lists zero serious adverse events for the cannula approach among 50 at risk and zero for the needle approach among 50 at risk. It also lists zero deaths. These counts describe the safety entries in the registry record; they do not establish that no events of any kind occurred, and they do not quantify the chance of a rare event.

The record separately lists other adverse events affecting 23 participants in the cannula group and 29 in the needle group, each with 50 at risk. These are counts, not a comparison adjusted for the split-face design or an account of event severity. The registry record does not provide further detail on event types, timing, or the statistical method used to compare safety outcomes. Differences in counts should therefore be read descriptively rather than as evidence of a causal safety difference.

Safety observations come from the study’s recorded follow-up and population. They do not by themselves establish safety beyond the study setting or duration. The primary endpoint was an effectiveness measure, so the serious-event counts are a separate part of the trial record.

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

The posted results describe a randomized split-face comparison of two ways to inject the same filler. The primary summaries show mean NLF-WSRS changes of -1.61 with cannula injection and -1.65 with needle injection. The recalculated unadjusted difference is -0.04, and its 95% confidence interval spans -0.126 to 0.046. These results indicate that the posted average changes are close under the summary-based comparison.

That observation is not the same as proving that the approaches are equal, interchangeable, or non-inferior. Non-inferiority requires a margin chosen in advance and an analysis showing that the relevant uncertainty falls within that margin. The margin is not reported in the registry record. The sponsor’s primary analysis is also not reported, and the summary-based recalculation does not account for the within-participant pairing.

The average change does not reveal how much participants differed from one another, how many had a particular score change, or whether each participant experienced a similar result. The secondary responder outcome uses a threshold-based definition, while other listed outcomes assess evaluator and participant impressions. These measures answer related but distinct questions, and the registry record does not report complete analyses for all of them.

The trial record lists no serious adverse events in either treatment group and no deaths, alongside other adverse-event counts. Those observations describe the recorded study outcomes and do not establish the absence of all possible harms or address effects outside the trial’s follow-up.

In short, the registry supports a descriptive statement that the reported average severity-score changes were similar in magnitude. It does not provide the information needed to determine whether the prespecified non-inferiority criterion was met. Any stronger conclusion would require the missing margin, the sponsor’s analysis details, and an approach that accounts for the paired design.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its split-face design places the comparison within each participant. That arrangement can control for participant-level characteristics shared by both sides, but it also means that the two treatment observations are correlated. An analysis that ignores pairing may not capture the design’s intended comparison or its precision. The registry’s arm-level summaries do not provide the individual paired differences or correlation needed to assess that issue.

The trial also illustrates why a non-inferiority objective requires more than similar observed means. The posted changes are close, and the recalculated confidence interval includes zero, but a non-inferiority decision depends on a margin and a suitable analysis. The margin and sponsor analysis are not reported in the registry record. Without them, readers can describe the observed pattern but cannot verify the trial’s stated objective from the posted summaries.

The distinction between a mean change and a responder outcome is also important. A mean summarizes the average shift, whereas a responder count applies a threshold to each observation. Those outcomes can complement each other, but neither alone describes the full distribution of individual responses. The trial’s multiple secondary outcome types and assessment times further underline the need for a clear analysis hierarchy and multiplicity plan, which are not reported.

Finally, planning calculations based on an observed effect should not be confused with the original design justification or with power after the study is complete. The registry’s planning illustrations use stated assumptions, while the trial’s own design assumptions are not reported. Keeping those distinctions clear helps prevent descriptive similarity, unadjusted calculations, or planning figures from being overstated.

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.

The registry record does not report the non-inferiority margin, which is essential for judging the stated primary objective. It also lists no reported primary analyses and does not describe the sponsor’s statistical method. The recalculated mean difference and interval are based on posted summary statistics; they are not a substitute for the sponsor’s analysis.

The within-subject split-face design creates paired observations, but the available summaries do not include the participant-level differences or the correlation between sides. The recalculation therefore cannot fully reflect the pairing. The arm-level sample sizes should not be interpreted as separate randomized groups of participants.

The primary endpoint is reported for the per-protocol population, with 4 participants excluded after major protocol deviations. The registry record does not describe missing outcome data, the handling of incomplete pairs, an intention-to-treat analysis, or sensitivity analyses. It also does not report the original sample-size assumptions or a detailed analysis plan.

Many secondary outcomes and assessment times are listed, but detailed analyses are not reported for most of them. No multiplicity procedure is described. This limits interpretation of secondary findings as a coherent set and makes it difficult to distinguish confirmatory from exploratory comparisons. The safety record gives event counts but does not provide further detail on event types, timing, or comparative methods.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: RHA® 4 NLF Cannula — NCT04754646.
• Registry record last updated 2023-03-09; status last verified 2023-03.
• Results first posted 2023-03-09.
• 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

NCT04754646 is a completed randomized, controlled, single-blinded, multicenter study with a split-face comparison of RHA®4 injected using a cannula or a sharp needle. Its primary endpoint was change in NLF-WSRS score at Week 12 after the last treatment, assessed by a blinded live evaluator. The primary summaries show mean changes of -1.61 and -1.65, respectively; the recalculated unadjusted mean difference is -0.04, with a 95% confidence interval from -0.126 to 0.046.

The results describe close average changes but do not establish non-inferiority: the margin and sponsor’s primary analysis are not reported in the registry record, and the available recalculation does not account for the paired design. The registry lists zero serious adverse events and zero deaths for both approaches. Other adverse-event counts are also reported. Secondary outcomes span evaluator and participant assessments, but most detailed analyses are not reported.