Clinical Evaluation Following Use of SYSTANE® ULTRA in the Management of Dry Eye: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Evaluation Following Use of SYSTANE® ULTRA in the Management of Dry Eye (NCT02446015), a randomized na study. The primary outcome is Change From Baseline in Total Ocular Surface Staining (TOSS) Score at Day 28.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-masked, parallel-group study of SYSTANE® ULTRA Lubricant Eye Drops in people with dry eye syndrome. It lists the study as completed and records enrollment of 159. The study began on 2015-06-19, and primary completion was recorded as 2016-06-21. The registry lists the phase as NA.

The two regimens differed in frequency of use. The Systane Ultra QID group used 1 drop in each eye 4 times per day, while the Systane Ultra PRN group used 1 drop in each eye as needed. Both regimens lasted 28 days. Because both groups received the same eye drops, the principal contrast concerns scheduled versus as-needed use.

For the primary outcome, the posted analysis lists 33 analyzed subjects in the QID group and 62 in the PRN group. These are outcome-specific analyzed numbers, not the enrollment figure. The registry explains that the number analyzed is the number of subjects with a non-missing response. The reason the analyzed numbers differ from enrollment, and the details of participant flow between enrollment and analysis, are not reported in the registry record.

The registry does not report the masking details, such as who was masked, or the method used to generate or conceal random allocation. It also does not report the original sample-size assumptions or a detailed statistical analysis plan. Those omissions prevent a fuller assessment of how allocation, masking, and analysis decisions were implemented. The posted comparison remains informative as a description of the outcome results, but it cannot by itself establish how all design safeguards operated.

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: Of the 159 enrolled, 58 subjects were exited as screen failures prior to randomization. An additional 4 subjects were randomized in error and did not receive investigational product (IP). This reporting group includes all treated subjects (97).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat Analysis Set. Number Analyzed is the number of subjects with non-missing response.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: This analysis population includes all randomized subjects who received at least 1 dose of the randomized investigational product (Intent-to-Treat Analysis Set).

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Total Ocular Surface Staining (TOSS) Score at Day 28, measured over Baseline (Day 0), Day 28.

The primary endpoint was change from baseline in total ocular surface staining score at Day 28. The registry describes the score as a cumulative measure of corneal and conjunctival staining. After an ophthalmic dye was instilled, an investigator graded three areas of the ocular surface for dryness on a scale from 0, meaning Absent, to 5, meaning Severe. The area scores were summed to produce an overall score on a 0–15 scale.

Change was defined as the Day 28 score minus the baseline score. A negative change therefore indicates a lower score at Day 28 than at baseline; the registry specifically states that a more negative change indicates greater efficacy. The endpoint is used to quantify change in an observed ocular-surface sign over the treatment period. It is distinct from a report of symptoms or treatment satisfaction.

Only one eye from each subject was selected as the study eye, and only that eye was used for eye-level efficacy analyses. This approach defines which eye contributed to the endpoint and avoids treating two eyes from one person as if they were separate participants. The registry does not report the rule used to select the study eye.

The reported arm values are least-squares means, with standard errors as the measure of dispersion. The primary outcome timeframe is baseline (Day 0) to Day 28. No longer-term primary outcome is listed in the registry record.

7. Results Posted in the Registry

• Systane Ultra PRN: mean -0.94 versus -1.19 on control; difference 0.25 (95% CI -0.44 to 0.94), standardized effect d = 0.14; z-test p = 0.480.

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.

Change From Baseline in Impact of Dry Eye on Everyday Life Symptom-Bother (IDEEL SB) Score at Day 28

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Systane Ultra PRN: mean -2.94 versus -7.00 on control; difference 4.06 (95% CI -1.29 to 9.41), standardized effect d = 0.30; z-test p = 0.137.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Systane Ultra PRN and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcome pattern is limited in what it can add to the primary result. The registry names two secondary outcome areas: change in IDEEL symptom-bother and change in IDEEL treatment satisfaction, including treatment effectiveness and treatment-related inconvenience. Quantitative posted results are available for the symptom-bother comparison; treatment-satisfaction results are not reported in the registry record.

The posted symptom-bother comparison has an unadjusted recalculated p-value of 0.137, and its interval spans zero. This result does not provide a clear, precise distinction between the two use schedules. It is a different kind of measure from ocular surface staining: symptom-bother reflects reported impact in everyday life, while TOSS is an investigator-graded ocular-surface measure. The outcomes may offer complementary perspectives, but agreement between them cannot be assumed.

Secondary outcomes generally carry less confirmatory weight when the analysis plan, hierarchy, and multiplicity handling are not reported. Testing several outcomes can increase the chance that at least one result appears notable by chance. No adjustment for multiple testing or prespecified ordering of outcomes is reported in the registry record. The secondary result should therefore be viewed as supportive descriptive evidence, not as a separate proof of a treatment-schedule effect.

The absence of posted quantitative treatment-satisfaction results also limits assessment of the full secondary outcome pattern. It is not appropriate to infer those results from the symptom-bother outcome or from the primary endpoint. Taken together, the secondary record does not materially resolve the uncertainty in the primary comparison. It indicates that a symptom-bother outcome was assessed and has an imprecise posted comparison, while the other named secondary outcome lacks reported numerical results.

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

• Change From Baseline in Impact of Dry Eye on Everyday Life Symptom-Bother (IDEEL SB) Score at Day 28
• Change From Baseline in IDEEL Treatment Satisfaction Scores (Treatment Effectiveness and Treatment-related Inconvenience) at Day 28

9. Statistical Interpretation

10. Statistical Methods Explained

For a continuous outcome, a group mean describes the average measured value or change among the analyzed participants. Here, the primary outcome is a change score, and the registry reports least-squares means for each regimen. A least-squares mean is an adjusted mean from a statistical model in the usual sense; however, the model details and covariates used for the posted primary estimates are not reported in the registry record. The label alone does not establish which adjustments were made.

The registry reports standard errors alongside the arm estimates. In general, a standard error describes the precision of an estimated mean: smaller standard errors indicate less sampling uncertainty in that estimate, all else being equal. A standard error is not the same as the standard deviation of individual outcomes. The posted standard errors for the primary estimates are 0.26 for QID and 0.24 for PRN. Without individual-level data, these values do not describe the spread of subject-level TOSS changes.

The mean difference compares the group estimates. The posted direction is PRN minus QID, producing an estimate of 0.25. The sign depends on that ordering: a positive value means the PRN estimate is numerically higher than the QID estimate. Because lower, more negative change is described as greater efficacy, the positive contrast places the QID estimate farther in the negative direction. The estimated difference should not be interpreted independently of its uncertainty.

In general, an interval around a mean difference expresses a range of values compatible with the data under the interval’s statistical assumptions. It is not a range containing a fixed proportion of individual outcomes. The posted primary interval extends from -0.444 to 0.944. Since it includes zero, the data do not exclude no difference under the interval calculation. The confidence level and the method used to form this interval are not reported in the registry record, so those details should not be inferred.

The posted p-value for the primary comparison is an unadjusted recalculation from summary statistics. In general, a p-value measures how incompatible the observed result is with a specified null model, assuming that model and the analysis assumptions apply. It is not the probability that the null hypothesis is true, and it does not quantify the clinical importance of an effect. The value 0.48 does not establish equivalence or prove that a difference is absent. No sponsor-reported primary inferential analysis is included in the registry record.

The recalculation uses posted summary statistics and is not a substitute for an analysis of individual participant data. The pooled standard deviation is marked as approximate because it was derived from the reported standard errors. Any recalculated comparison can be affected by rounding, assumptions used to recover variability, and differences between a simple unadjusted calculation and the sponsor’s intended model. The registry does not report enough detail to verify the original model specification or reproduce a sponsor analysis.

Randomization is intended, in general, to make treatment groups comparable in expectation with respect to measured and unmeasured characteristics. It does not ensure that groups will be identical in a particular study, especially when analyzed numbers are limited or outcome data are missing. The registry identifies the allocation as randomized but does not report the sequence-generation or concealment procedures. Single masking is reported, but who was masked is not specified. These gaps limit evaluation of possible selection or measurement influences.

For planning, the registry’s illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects equal to stated fractions of the observed effect. These are planning assumptions for the illustration, not documented assumptions for the original trial. The original trial’s sample-size justification, intended power, and any interim analyses are not reported in the registry record. The planning figures are prospective illustrations, not observed power.

Multiplicity is a general concern when several outcomes or comparisons are examined: the chance of at least one apparently notable result can increase when many tests are considered. The registry lists two secondary outcomes in addition to the primary outcome. The posted secondary results include a comparison for IDEEL symptom-bother, while the treatment-satisfaction outcomes do not have quantitative results reported in the registry record. No multiplicity adjustment or testing hierarchy is reported. The secondary comparison should consequently be treated as exploratory rather than as an independently confirmatory finding.

Missing data affect interpretation because an analysis restricted to participants with observed responses may differ from the result that would have been obtained had all enrolled participants provided outcomes. General methods can address missingness under stated assumptions, but the registry does not report the amount, reasons, or handling of missing primary outcome data beyond defining analyzed numbers as subjects with non-missing responses. It is therefore not possible to assess whether the missingness assumptions were plausible or whether sensitivity analyses were conducted.

11. Confidence Intervals and Precision

The primary comparison is estimated as a mean difference of 0.25 units on a scale, with a posted interval from -0.444 to 0.944. The interval is broad enough to cover zero and values favoring either numerical direction. This means the result is not precise enough to establish the direction of the between-schedule difference from the interval alone.

Precision concerns how narrowly the data locate an estimate, not whether the estimate is important. The point estimate sits at one location, while the interval represents uncertainty around it. Since the interval reaches across zero, the observed contrast is compatible with no difference as well as with nonzero differences. The posted interval does not establish that all values within it are equally likely, nor that values beyond it are impossible.

The arm-level standard errors are 0.26 for QID and 0.24 for PRN. These describe uncertainty in the estimated group means, not the distribution of individual changes. The primary result has analyzed counts of 33 for QID and 62 for PRN, and the registry defines analyzed counts by availability of a non-missing response. The reasons for the difference between enrollment and the analyzed outcome population are not reported in the registry record.

The registry does not state the confidence level or construction method for the posted interval. The comparison and interval are recalculated from summary statistics, rather than reported as a sponsor analysis. In general, interval interpretation depends on the statistical model and assumptions used to calculate it. The estimate should therefore be read with the posted uncertainty in mind, without treating its endpoints as exact boundaries for the true effect or as a test of clinical relevance.

No clinically important difference threshold for TOSS is reported. Without such a threshold, the interval cannot be classified as excluding or including a clinically meaningful difference. The registry also does not report an equivalence or noninferiority margin. Thus, the interval’s inclusion of zero should not be recast as proof that the two schedules perform identically.

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 figures are participants per arm, not total event counts. The registry describes the calculation as an illustration based on the observed effect, with two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. It shows planning for 100%, 75%, and 50% of the observed effect. The assumptions used for the trial’s original design are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm under the stated assumptions for a design intended to have an 80% chance of detecting the specified effect, if that effect and the assumptions hold. The 90% power column represents a higher detection probability under those same planning assumptions. These are design calculations, not probabilities that the observed trial result is correct and not measures of how likely the observed finding is to replicate.

The figures increase as the effect being planned for becomes smaller. A smaller difference is harder to distinguish from random variation, so more participants are generally needed to achieve the same target power under otherwise unchanged assumptions. The illustration is anchored to the observed effect, which may itself be uncertain and may not match an effect chosen for a future study. The registry does not report the original sample-size justification, so these planning numbers should not be attributed to the completed trial’s design. This is not observed power.

The figures are conditional on the stated calculation assumptions. They do not account for details that are not included in the illustration, such as the trial’s actual allocation, missing outcome data, or an adjustment for multiple outcomes. A planning calculation can help show how precision requirements change with the effect size being targeted, but it does not determine whether a particular study was adequately designed for its original objectives.

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 = 0.250; pooled standard deviation σ = 1.764.
2. n = 2 × (1.96 + 0.842)² × 1.764² / 0.250² = 781.1, rounded up to 782 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 <- 0.25                      # observed difference in means
sigma <- 1.763515550477                     # 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(2446015)
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 = 782 (80% power), 1,046 (90% power)
 75% of observed effect: n per arm = 1,389 (80% power), 1,860 (90% power)
 50% of observed effect: n per arm = 3,125 (80% power), 4,183 (90% power)
power.t.test: 782.1 
Simulated power at n = 782 per arm: 0.799 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary TOSS outcome and two secondary outcome areas. When several outcomes are analyzed, multiplicity can matter because repeated testing increases the opportunity for results to appear statistically notable by chance. In general, investigators may address this through a prespecified hierarchy, an adjustment to significance thresholds, or by explicitly treating secondary analyses as exploratory. The registry record does not report a testing hierarchy or a multiplicity adjustment.

The posted p-values for comparisons are unadjusted recalculations from summary statistics. They should not be treated as multiplicity-controlled confirmatory results. The sponsor’s full analysis plan, including any prespecified outcome ordering, is not reported in the registry record. It is also not reported whether interim analyses were planned or conducted.

The primary analysis population is described as the Intent-to-Treat Analysis Set, but the registry further defines the number analyzed as the number of subjects with a non-missing response. These statements do not provide a complete account of the analysis population or missing-data handling. The primary outcome has analyzed counts of 33 for QID and 62 for PRN. The registry does not report the number of missing primary responses by group, reasons for missingness, or whether any imputation or sensitivity analyses were used.

In general, missing outcomes can affect a comparison if the likelihood of having an observed response is related to treatment assignment or to the outcome itself. The direction and size of any effect cannot be determined from the available record. The enrollment figure does not by itself explain how many participants contributed to each endpoint, and no total should be inferred by combining the reported group counts. The registry’s definition of analyzed numbers is the relevant information for interpreting the posted outcome estimates.

The record also does not report a detailed statistical analysis plan, model covariates, or procedures for handling deviations from the assigned regimen. These missing details limit assessment of whether the posted comparisons correspond to a prespecified analysis and how robust the findings are to alternative analysis choices.

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.

The registry reports serious adverse events, other adverse events, and deaths for a pretreatment group and the two regimen groups. In the pretreatment group, 0 serious adverse events and 0 other adverse events were reported among 159 at risk, and deaths were 0. In the QID group, 0 serious adverse events and 0 other adverse events were reported among 34 at risk, and deaths were 0. In the PRN group, 0 serious adverse events and 0 other adverse events were reported among 63 at risk, and deaths were 0.

These figures describe events recorded in the registry for the listed at-risk groups. The safety counts differ from the primary efficacy analyzed counts, so they should not be substituted for the outcome-specific populations. The registry lists no top serious adverse-event terms.

Zero reported events in these groups does not establish that an event is impossible or that the regimens have no safety risks. Event counts are observations over the registry’s reported study period; the record does not provide detailed exposure time, event-collection procedures, or a fuller narrative of safety monitoring. The figures should be read as the reported counts, not as evidence extending beyond the participants and period covered by the study record.

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

The posted primary estimates show negative average changes in TOSS in both analyzed groups by Day 28. The QID estimate is -1.19 and the PRN estimate is -0.94. The comparison is an estimated mean difference of 0.25 for PRN minus QID. The interval for that difference spans zero, and the unadjusted recalculated p-value is 0.48. Together, these results show that the observed group contrast is uncertain and does not sharply separate the two schedules on this endpoint.

This does not mean that the schedules are equivalent. A finding of equivalence requires a defined margin and an analysis designed to evaluate that margin; neither is reported in the registry record. Nor does a result that does not clearly distinguish the groups show that there is no difference. It indicates that the posted estimate and its uncertainty do not establish a clear between-group contrast.

The endpoint is a score of ocular-surface staining, measured in one selected study eye per subject. It is not a direct measure of all aspects of dry eye, and it is distinct from subjective symptom impact and treatment satisfaction. The study’s primary timeframe was baseline to Day 28. The result does not establish what happens beyond that timeframe or answer questions about outcomes not listed in the record.

The secondary record contains a symptom-bother comparison but no reported quantitative results for treatment satisfaction. The secondary evidence therefore does not remove the uncertainty around the primary comparison. The safety record lists zero serious adverse events, other adverse events, and deaths in the reported groups, but those counts do not prove the absence of risk.

Overall, the registry supports a cautious description of the measured results in this completed study. It does not, by itself, justify a broad claim about clinical benefit, comparative effectiveness across other settings, or safety beyond the reported observations. The clinical importance of the TOSS difference cannot be judged against a threshold because no clinically important difference is reported.

17. Why This Trial Matters Statistically

This trial illustrates why a difference between group averages should be interpreted together with its uncertainty. The point estimate alone suggests a numerical contrast between scheduled and as-needed use, but the interval spans zero and reaches values on either side. The result is consequently less informative about which schedule has the more favorable average change than the point estimate might appear when read alone.

It also shows the distinction between a within-group change and a between-group comparison. Both groups have negative estimated changes from baseline, but the primary comparative question concerns the difference between those changes. Observing change within each group does not establish that the schedules differ; the randomized comparison is the relevant contrast for that question.

The analysis further highlights how outcome-specific denominators matter. Enrollment is 159, while the primary estimates are based on 33 analyzed subjects in QID and 62 in PRN. The record defines analyzed numbers as subjects with non-missing responses but does not describe missingness in detail. A reader needs to distinguish overall enrollment from the population contributing to a particular result.

Finally, the result demonstrates the limits of a registry record for methodological reconstruction. Randomization, masking, and parallel allocation are identified, but details of sequence generation, masking roles, the original sample-size rationale, analysis plan, and missing-data methods are not reported. These omissions do not change the numerical estimates, but they restrict how confidently the design and analysis can be audited. Clear reporting of estimates, uncertainty, analyzed populations, and analysis decisions is essential for interpreting clinical trial evidence.

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 primary comparison is recalculated from posted summary statistics rather than presented as a sponsor-reported inferential analysis. The record does not provide the underlying participant-level data, full model specification, or the confidence level and construction method for the posted interval. The pooled standard deviation used in recalculation is approximate, derived from the reported standard errors. These features limit independent verification of the contrast.

The analyzed primary counts are 33 for QID and 62 for PRN, while enrollment is 159. The registry defines analyzed counts as subjects with non-missing responses but does not report the missing outcome counts by group, reasons for missingness, or sensitivity analyses. This leaves uncertainty about how missing responses may affect the result.

The registry identifies randomization and single masking but does not describe sequence generation, allocation concealment, or who was masked. It also does not report the original sample-size justification, a detailed statistical plan, interim analyses, or a clinically important threshold for TOSS. The planning illustration should not be treated as the trial’s original design rationale.

The primary endpoint covers change through Day 28 and uses one selected study eye per subject. The method of eye selection is not reported. The result therefore addresses this specific score and timeframe, rather than all manifestations of dry eye or later outcomes. Treatment-satisfaction results are not reported in the registry record, and the available symptom-bother comparison is unadjusted. Multiplicity handling for the primary and secondary outcomes is also not reported.

The safety counts are reported without detailed information about exposure duration, event definitions, or monitoring procedures. Zero recorded events should not be generalized beyond the groups and period represented by the record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Evaluation Following Use of SYSTANE® ULTRA in the Management of Dry Eye — NCT02446015.
• Registry record last updated 2018-07-02; status last verified 2017-04.
• Results first posted 2017-06-16.
• 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

The registry describes a completed, randomized, single-masked, parallel-group study of SYSTANE® ULTRA in dry eye syndrome, with enrollment of 159. It compared scheduled use, 1 drop in each eye 4 times per day, with as-needed use for 28 days.

The primary outcome was change from baseline in total ocular surface staining score at Day 28. The estimated changes were -1.19 for QID and -0.94 for PRN; the PRN-minus-QID mean difference was 0.25. The interval spans zero, and the unadjusted recalculated p-value is 0.48. The estimate is therefore uncertain as a comparison between schedules.

The registry names symptom-bother and treatment-satisfaction secondary outcomes. Quantitative results are posted for symptom-bother, but treatment-satisfaction results are not reported in the registry record. The listed safety groups report zero serious adverse events, other adverse events, and deaths. Several details needed to assess the original analysis plan, missing data, and design implementation are not reported.