RHA® Redensity Eye Versus No-treatment for the Infra-Orbital Hollows: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for RHA® Redensity Eye Versus No-treatment for the Infra-Orbital Hollows (NCT04577898), a randomized na study. The primary outcome is Change of 1 Point From Baseline in Infra-Orbital Hollows Severity Rated by the Blinded Live Evaluator (BLE) at Week 12 After Last Treatment, Using the TIOHS - Phase 1a.

2. Clinical Question

3. Trial Design

This was a multicenter, prospective, randomized, parallel-group clinical study with a no-treatment control. The registry identifies the study as single-masked and specifies that the blinded live evaluator (BLE) was blinded to whether a participant was assigned to RHA® Redensity Eye or no treatment. The treating investigator and BLE assessed infra-orbital hollows independently at screening. For eligible participants, the BLE’s assessment was used as the baseline for the primary endpoint.

The registry planned random assignment in a 3:1 ratio to RHA® Redensity Eye or no treatment. The posted Phase 1a primary endpoint includes 183 participants in the RHA® Redensity Eye group and 65 in the no-treatment control group. Total enrollment was 248. The treatment group could receive injections using a needle or cannula; the administration method was to be set for each site, with the aim of an approximately even distribution between those methods. The registry record does not report the number of participants who received each administration method.

The primary endpoint was assessed at Week 12 after the last treatment in Phase 1a. For the no-treatment control group, the registry describes Week 12 assessments before participants proceeded to treatment. The study status is completed. The recorded start date is 2020-12-02, and the primary completion date is 2023-05-16. The registry lists the phase as not applicable. The original sample-size rationale and the trial’s planned statistical analysis methods 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.

Period 1: Phase 1a

Period 2: Phase 1b

Period 3: Phase 2

Analysis population for the primary outcome, as defined in the registry: Period 1: Phase 1a - Primary endpoint on the ITT 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 of 1 Point From Baseline in Infra-Orbital Hollows Severity Rated by the Blinded Live Evaluator (BLE) at Week 12 After Last Treatment, Using the TIOHS - Phase 1a, measured over Period 1 - Phase 1a: Week 12 after last treatment.

The primary endpoint is the percentage of participants who had a one-point change from baseline in infra-orbital hollow severity at Week 12 after the last treatment in Phase 1a. Severity was rated by a blinded live evaluator using the Teoxane Infraorbital Hollows Scale. The registry describes the TIOHS as a validated five-point scale, ranging from 0, absent, to 4, very severe. It identifies a one-grade change as clinically significant.

This endpoint converts an evaluator’s scale assessment into a binary outcome: a participant either meets the specified change criterion or does not. The resulting percentage summarizes how common that criterion was in each group. The registry record describes the endpoint as a one-point change but does not specify in the endpoint description whether the response rule requires a reduction, an increase, or either direction. That detail matters when interpreting what counts as a response, so the result should be read according to the registry’s stated criterion rather than assuming a direction that is not described.

Using the BLE’s assessment supports a consistent evaluator-based comparison, while blinding the evaluator to assignment is intended to reduce the possibility that knowledge of treatment influences the rating. The primary endpoint population is identified as the intention-to-treat population for Phase 1a. Further details about how that population was defined or handled are not reported in the registry record.

7. Results Posted in the Registry

• RHA Redensity Eye Group: 79.2% (145/183) versus 9.2% (6/65) on control; risk difference 70.0 percentage points (95% CI 60.8 to 79.2), risk ratio 8.58 (3.99–18.46); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary because each participant is classified as meeting or not meeting the one-point TIOHS change criterion. A binary outcome can be summarized by the number of responders and the total number assessed, and by the corresponding response percentage. The posted group results are 145 of 183 participants in the RHA® Redensity Eye group and 6 of 65 in the no-treatment control group, with reported percentages of 79.0 and 9.0. The percentages describe the observed proportions in these study groups; they are not guarantees of the response rate in a different population.

What the risk difference describes

The risk difference compares the response probability in one group with the response probability in the other group by subtraction. It is an absolute measure: unlike a ratio, it stays on the probability scale and describes the size and direction of the group contrast. The recalculated risk difference reported for this comparison is 0.7. Its confidence interval gives a range of values compatible with the data and the interval method, under the method’s assumptions. Because the interval’s bounds are above zero, the estimated contrast is positive throughout that reported interval. The registry record does not state which confidence-interval procedure was used.

A risk difference is often useful for communicating a group comparison because it relates directly to the difference in response probability. It does not identify the mechanism behind the difference, and it does not separate the influence of treatment from all other possible sources of variation. Random assignment supports a comparative interpretation, while the observed response rates remain estimates based on the participants included in the analysis.

What the p-value does and does not say

The unadjusted p-value is reported as p < 0.001. In general, a p-value measures how unusual data at least as extreme as the observed data would be if the null hypothesis and the test’s assumptions held. It is not the probability that a treatment effect is absent, and it does not measure the probability that the result will replicate. It also does not quantify the size of the group difference; the risk difference and its interval are more informative for that purpose.

The p-value is labeled unadjusted. No multiplicity adjustment is described in the registry record. The record identifies multiple secondary outcomes, but it does not report a complete testing hierarchy or explain how any repeated tests were handled. The p-value should therefore be read as the posted unadjusted comparison, not as evidence that the result has been adjusted for multiple endpoints or analyses.

Why evaluator blinding is relevant

The primary outcome is based on an evaluator’s rating rather than a purely mechanical measurement. The study describes the BLE as blinded to group assignment and says the treating investigator and BLE assessed participants independently at screening. In general, blinding can reduce the risk that an evaluator’s knowledge of assignment affects a subjective assessment. It cannot eliminate all measurement error, and the registry record does not report assessments of evaluator agreement or other validation checks within this trial.

The TIOHS has five ordered severity scores from 0, absent, to 4, very severe. Treating a one-point change as a binary response simplifies the result for group comparison, but it also discards information about the size of changes beyond the threshold. A participant meeting the criterion and one with a larger change are both counted as responders under a binary summary. The endpoint description does not specify the direction of change required, so the meaning of “responder” depends on the exact operational rule used in the analysis.

Unadjusted estimates and the reported population

The comparison is recalculated from the posted summary statistics and is unadjusted. That means it is a direct group contrast rather than an estimate adjusted for participant or site characteristics. General statistical practice may use adjustment to improve precision or account for prespecified factors, but whether that was planned or performed for this trial is not reported in the registry record. No claim about an adjusted treatment effect can be made from the posted comparison.

The primary endpoint is stated to use the intention-to-treat population. In general, intention-to-treat analysis aims to retain participants in their randomized groups, regardless of treatment received, to preserve the comparison created by randomization. The registry record does not give a detailed population definition, describe exclusions, or explain how missing endpoint values were handled. The posted denominators indicate the group sizes used for the presented results, but do not disclose whether any missing observations or other analysis rules affected those counts.

Over-dispersion and model choice

Over-dispersion is a general issue in count or proportion models when variability exceeds what a chosen model assumes. It can make standard errors too small if the model does not account for extra variability. The primary outcome is binary, and the posted comparison is a simple unadjusted risk difference rather than a reported model-based estimate. The registry record does not identify a model, an over-dispersion assessment, or a method for adjusting uncertainty for clustering by site. Those details should not be inferred from the study’s multicenter description.

The analysis record does not report the sponsor’s full statistical plan, interim analyses, missing-data procedures, or detailed confidence-interval method. Consequently, the posted statistics can be explained as a group-level binary comparison, but the underlying implementation cannot be reconstructed beyond the available summary results. The reported p-value and interval should be interpreted as the results of the methods used to generate those posted summaries, with the unreported methods remaining uncertain.

10. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate. A confidence interval expresses a range of values compatible with the observed data under a particular statistical method and its assumptions. For the primary risk difference, the posted interval has both bounds above zero. This indicates that the reported interval does not include no difference, while its width shows that the effect is not known with perfect precision. The exact interval bounds and the method used to calculate them are recorded with the posted comparison.

The group response percentages are based on different numbers of participants: 183 in the RHA® Redensity Eye group and 65 in the no-treatment control group. In general, estimates based on fewer observations tend to be less precise, all else equal. The control estimate therefore comes from the smaller of the two groups, and its uncertainty contributes to uncertainty in the group contrast. The confidence interval is more informative about that uncertainty than the p-value alone.

Precision is not the same as validity or clinical importance. A narrow interval can still be affected by measurement limitations, missing data, or analysis choices, while a statistically distinguishable difference does not by itself establish that the observed change is important to participants. The registry record identifies a one-grade change as clinically significant, but does not report the endpoint’s exact directional response rule or a separate interpretation of the size of the group difference.

The interval is a property of the estimate under the method used; it does not mean that there is a specified probability that the true effect lies inside the realized interval. The confidence level and calculation procedure are not reported in the registry record, so precision should be read from the posted interval without assuming an unreported method.

11. 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 values are planning illustrations based on the observed effect, not the trial’s original design calculations. For this binary outcome, the figures refer to participants per arm, not total events. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

Each power column describes a planning target. The 80% power column gives the estimated number of participants per arm for a design with an 80% chance of detecting the specified effect under the listed assumptions, if that effect is the true effect and the statistical model is appropriate. The 90% power column gives the corresponding planning estimate for a 90% chance. These are prospective design calculations, not a measure of the probability that the observed result is correct.

The rows consider planning for 100%, 75%, and 50% of the observed effect. The smaller the effect a study is designed to detect, the more participants are generally needed to distinguish it from random variation under otherwise similar assumptions. Thus, the reduced-effect scenarios require larger per-arm planning figures than the full observed-effect scenario. The figures are illustrations tied to assumptions, not recommendations or guarantees about what a future study would achieve. This is not observed power.

12. 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 = 0.092; treatment proportion p₁ = 0.792; average p̄ = 0.442.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7024 = 1.3767.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4983 = 0.4194.
4. n = (1.3767 + 0.4194)² / (0.7000)² = 6.6, rounded up to 7 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 <- 0.0923076923076923                          # control proportion
p1 <- 0.792349726775956                          # 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(4577898)
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 = 7 (80% power), 9 (90% power)
 75% of observed effect: n per arm = 12 (80% power), 16 (90% power)
 50% of observed effect: n per arm = 24 (80% power), 32 (90% power)
power.prop.test: 6.6 
Simulated power at n = 7 per arm: 0.854 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and five secondary outcomes. The secondary outcomes cover subject-rated and evaluator-rated global aesthetic improvement, satisfaction, later TIOHS assessments, and a FACE-Q questionnaire. Results for those secondary outcomes are not reported in the registry record. No complete analysis plan, prespecified testing hierarchy, or multiplicity procedure is reported.

Multiplicity arises when multiple outcomes, time points, or comparisons are tested. In general, conducting more tests can increase the chance of at least one apparently strong result arising by chance. Methods such as adjusting significance thresholds or specifying a hierarchy can address that issue, but there is no basis in the registry record to say that any such method was used. The posted primary comparison is explicitly unadjusted, so it should not be described as multiplicity-adjusted.

The primary endpoint population is identified as the intention-to-treat population for Phase 1a. The record does not describe how that population was operationalized, whether all randomized participants contributed endpoint data, or how exclusions were handled. The displayed group counts are 183 and 65, but the record does not explain whether those counts represent all randomized participants or the participants with evaluable endpoint results.

Missing-data handling is not reported in the registry record. It is therefore not possible to tell whether missing Week 12 ratings occurred, how any missing observations were treated, or whether sensitivity analyses were conducted. The record also does not report interim analyses, stopping rules, or a detailed statistical analysis plan. These omissions limit assessment of whether the analysis fully followed a prespecified approach and how robust the primary comparison is to alternative missing-data assumptions.

14. 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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cholecystitis acute (0.4%), cellulitis (0.4%).

The safety summaries use separate populations. The RHA® Redensity Eye group lists 183 participants at risk for serious adverse events, with 0 affected, and 183 at risk for other adverse events, with 28 affected. The no-treatment control group lists 65 at risk for serious adverse events, with 0 affected, and 65 at risk for other adverse events, with 0 affected. These figures describe the safety groups as posted; they should not be treated as a comparison of identical exposure periods.

A pooled safety assessment lists 233 participants at risk, with 2 affected by serious adverse events and 30 affected by other adverse events. The registry lists acute cholecystitis and cellulitis as serious adverse event terms, each at 0.4%. Deaths are listed as 0 in each of the three safety summaries. The pooled group is reported separately, so its counts should not be added to the individual groups. The record does not explain the composition of the pooled population or provide event timing, exposure-adjusted rates, or detailed causal assessments.

These summaries count participants affected, not necessarily every event occurrence. They describe recorded safety outcomes and do not establish that an event was caused by or unrelated to the study treatment.

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

The posted primary comparison describes a higher observed percentage meeting the one-point TIOHS change criterion in the RHA® Redensity Eye group than in the no-treatment control group: 79.0 compared with 9.0. The recalculated risk difference is 0.7, and its reported confidence interval excludes zero. The unadjusted p-value is p < 0.001. Together, these results describe a statistically distinguishable difference in this Phase 1a endpoint under the calculation represented by the posted comparison.

The result does not, on its own, establish the broader importance of the difference for participants. The registry describes a one-grade change as clinically significant, but does not specify in the endpoint description exactly which direction of change qualified as a response. It also does not report the analysis plan, missing-data procedures, or detailed methods used to calculate the uncertainty. Those limits affect how fully the result can be interpreted.

The comparison concerns a particular evaluator-rated measure at Week 12, in the recorded study population and under the no-treatment control design. It does not provide results for all secondary outcomes, later follow-up time points, or the treatment administration subgroups. Those secondary results are not reported in the registry record. The safety summaries are separate from the efficacy endpoint and do not establish causation for adverse events.

Random assignment supports a group comparison, while evaluator blinding is relevant because the primary outcome is an assessment of severity. Still, a result in this trial does not guarantee the same response rates in other populations or settings. Statistical significance is not a substitute for examining the endpoint definition, uncertainty, assessment process, analysis choices, and completeness of reporting. The posted data support describing the observed contrast; they do not answer questions that the registry record does not report.

16. Why This Trial Matters Statistically

This trial illustrates how a clinical study can turn an ordinal severity scale into a binary responder outcome. A five-point assessment is reduced to whether a participant meets a one-point change threshold. That makes the result easy to summarize as a percentage, but the interpretation depends on the exact response rule and its direction. The registry says the threshold is clinically significant, yet the endpoint description does not specify the direction required. That makes clarity of endpoint definitions central to understanding the result.

The study also highlights why masking matters for evaluator-rated outcomes. The BLE was blinded to group assignment, and baseline scoring for the primary endpoint used the BLE’s assessment. Such design features are relevant when an outcome involves judgment rather than a purely objective measurement. The record does not report evaluator agreement or other trial-specific checks on measurement reliability, leaving those aspects uncertain.

The observed group contrast is large on the scale of the posted risk difference and is accompanied by a confidence interval excluding zero. The analysis is nevertheless described as recalculated and unadjusted, while important details about the registry’s own analysis plan, missing data, and multiplicity are not reported. Statistical interpretation therefore involves both reading the numerical contrast and recognizing the limits of what the record explains about how it was obtained.

Finally, the sample-size figures demonstrate the dependence of planning on the effect size one wants to detect. Illustrations based on the observed effect can look very different from planning for smaller effects, and they should not be confused with the actual rationale used to design this completed study. Distinguishing observed results, uncertainty, and prospective planning assumptions is essential for responsible reading of trial statistics.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific details that would sharpen interpretation are not reported in the registry record. Most importantly, the primary endpoint description identifies a one-point change but does not specify whether a decrease, increase, or either direction qualified. This leaves uncertainty about the exact responder definition behind the posted percentages.

The record does not give the original sample-size justification, a detailed statistical analysis plan, the method used for the confidence interval, or the model behind the reported p-value. It also does not report whether results were adjusted for site or other participant characteristics. The recalculated comparison is unadjusted and should not be mistaken for a reported adjusted analysis.

Missing endpoint data and their handling are not described, nor are exclusions from the intention-to-treat population. Although the primary endpoint population is named, its implementation is not fully specified. The registry also identifies secondary outcomes but does not report their results or a plan for controlling multiplicity. This restricts evaluation of the full outcome pattern and the role of multiple testing.

The study is multicenter, but site-level results and any handling of possible variation across sites are not reported. The registry describes two possible administration methods, but does not report their actual distribution or comparative results. The pooled safety population is listed as 233 participants, but its composition is not explained. These reporting gaps do not negate the posted results, but they constrain the conclusions that can be drawn from them.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: RHA® Redensity Eye Versus No-treatment for the Infra-Orbital Hollows — NCT04577898.
• Registry record last updated 2026-01-26; status last verified 2026-01.
• Results first posted 2026-01-26.
• 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.

21. Record Summary

The completed randomized, single-masked, multicenter study compared RHA® Redensity Eye with no treatment for moderate to severe tissue volume deficiencies in the infra-orbital regions. Total enrollment was 248. The primary endpoint assessed the percentage meeting a one-point change criterion on the TIOHS at Week 12 in Phase 1a, using the blinded live evaluator’s rating.

The posted responder percentages were 79.0 for RHA® Redensity Eye and 9.0 for no treatment. The recalculated risk difference was 0.7, with an unadjusted p < 0.001. The registry record does not report the original sample-size justification, detailed analysis plan, missing-data handling, or results for the listed secondary outcomes. Safety summaries report 0 serious events in the treatment and control groups and 2 in the pooled safety assessment.