Evaluation of Clinical Outcomes After the Use of SYSTANE® HYDRATION: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of Clinical Outcomes After the Use of SYSTANE® HYDRATION (NCT02470429), a randomized na study. The primary outcome is Change From Baseline in Total Ocular Surface Staining (TOSS) Score at Day 42.

2. Clinical Question

3. Trial Design

The registry record describes a randomized, double-masked, parallel-group study. Its title is Evaluation of Clinical Outcomes After the Use of SYSTANE® HYDRATION, and the official title specifies subjects with dry eye. The study is marked completed; its phase is listed as NA. The sponsor is Alcon Research.

Enrollment was 114. The primary endpoint timeframe was baseline, identified as Day 0, through Day 42. The two reported primary-outcome arms were SYSTANE HYDRATION and Hyabak 0.15%. Each arm description specifies one drop in each eye four times per day for 42 days. Although 0.9% saline eye drops appear in the intervention list, the primary outcome results presented in the registry record are for the two named eye-drop arms.

Allocation is recorded as randomized, masking as double, and the model as parallel. The record does not specify who was masked or provide further details about the randomization procedure, allocation concealment, or conduct of masking. Those design details are not reported in the registry record.

The primary analysis population is identified as the ITT Analysis Set, and the outcome description says the number analyzed is the number of subjects with a non-missing response. The posted primary outcome has 48 analyzed participants in the SYSTANE HYDRATION arm and 49 in the Hyabak 0.15% arm. The registry record does not give a participant-flow account explaining the difference between overall enrollment and these outcome-specific analyzed counts.

Three secondary outcomes are also listed: change in IDEEL Treatment Effectiveness Score, change in IDEEL Treatment Inconvenience Score, and change in Tear Film Break-up Time. All are assessed at Day 42. The registry record does not report the original sample-size justification or the trial's own statistical analysis plan.

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 114 enrolled, 15 subjects were exited as screen failures prior to randomization. This reporting group includes all randomized subjects (99).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT 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 subjects who were exposed to study drug (including the run-in therapy) (Safety Analysis Set).

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Total Ocular Surface Staining (TOSS) Score at Day 42, measured over Baseline (Day 0), Day 42.

The primary endpoint is change from baseline in Total Ocular Surface Staining (TOSS) score at Day 42. The score is described as a cumulative cornea and conjunctival staining measure. After ophthalmic dye is instilled, an investigator grades three ocular-surface areas for dryness, with each area scored from 0, meaning absent, to 5, meaning severe. The three grades are summed to form an overall score on a 0–15 scale. One eye, designated the study eye, contributed to the analysis.

The endpoint captures staining observed on the ocular surface rather than relying only on a participant's description of symptoms. Change from baseline expresses how the score at follow-up differs from the baseline measurement. The registry description states that a more negative change indicates greater efficacy, so the direction of change matters when reading the arm means. It does not, by itself, determine whether a difference between arms is precise or whether an observed difference is attributable to treatment.

The posted arm estimates are least-squares means, with standard errors as the measure of dispersion. The registry record identifies the analysis population as the ITT Analysis Set and says participants without a non-missing response are not counted in the number analyzed. Details of how the least-squares means were modeled are not reported in the registry record.

7. Results Posted in the Registry

• Hyabak 0.15%: mean -0.92 versus -1.16 on control; difference 0.24 (95% CI -0.41 to 0.89), standardized effect d = 0.15; z-test p = 0.470.

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 IDEEL Treatment Effectiveness Score at Day 42

• 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:
  • Hyabak 0.15%: mean 12.80 versus 9.62 on control; difference 3.18 (95% CI -5.63 to 11.99), standardized effect d = 0.15; z-test p = 0.480.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hyabak 0.15% and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in IDEEL Treatment Inconvenience Score at Day 42

• 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:
  • Hyabak 0.15%: mean 2.24 versus -10.32 on control; difference 12.56 (95% CI 6.41 to 18.71), standardized effect d = 0.83; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Hyabak 0.15% than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Tear Film Break-up Time (TFBUT) at Day 42

• 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:
  • Hyabak 0.15%: mean 0.68 versus 0.39 on control; difference 0.29 (95% CI -0.75 to 1.33), standardized effect d = 0.11; z-test p = 0.585.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hyabak 0.15% and the control. The interval gives the range of effects that remain compatible with the data.

The three secondary outcomes cover participant-reported IDEEL treatment effectiveness, participant-reported IDEEL treatment inconvenience, and tear film break-up time. Together, they broaden the set of outcomes beyond ocular-surface staining: the IDEEL measures address treatment experience, while TFBUT is an additional tear-film measure. Their overall pattern is not uniform. The recalculated contrasts differ in direction and precision, and only the inconvenience-score comparison has an unadjusted interval that excludes zero and an unadjusted p-value below 0.001.

That pattern does not overturn or settle the primary result. The primary endpoint is the stated main comparison, and its unadjusted interval spans zero. Secondary endpoints can provide additional context, but they do not substitute for a clear and well-specified primary analysis. The different measures also capture different aspects of the study, so a result on one should not automatically be interpreted as confirmation of a result on another.

The registry record does not report named statistical analyses for the secondary outcomes. The posted comparisons are simple unadjusted recalculations from summary statistics, and the record does not state whether the original protocol specified a testing hierarchy or multiplicity control. When several outcomes are examined, the chance of finding at least one apparently unusual result can increase if each is tested independently without adjustment. In general, multiplicity procedures can limit that risk, but no such procedure is reported in the registry record.

For that reason, the secondary results carry less inferential weight than a prespecified, multiplicity-controlled analysis would. Their unadjusted p-values should be viewed as descriptive signals rather than definitive evidence. The registry record does not report whether these measures were designated as confirmatory or exploratory, so their intended role cannot be established. A reader should consider the coherence of the outcomes and the uncertainty around each comparison, while avoiding a single-result focus.

The registry record lists three secondary endpoints and reports values for each, but does not provide a multiplicity plan, analysis population details beyond the outcome-level analyzed counts, or a detailed model specification. These gaps make it difficult to determine how the secondary findings relate to any original inferential strategy. They are useful as supplementary descriptions of the posted results, but not as a replacement for the primary endpoint's uncertain comparison.

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

• Change From Baseline in IDEEL Treatment Effectiveness Score at Day 42
• Change From Baseline in IDEEL Treatment Inconvenience Score at Day 42
• Change From Baseline in Tear Film Break-up Time (TFBUT) at Day 42

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numeric change score rather than a count or a time until an event. The registry record reports a least-squares mean for each arm and a standard error. A least-squares mean is generally a model-based estimate of an arm average; the exact model, covariates, and assumptions used for these estimates are not reported in the registry record. The reported standard error describes uncertainty in an estimated mean, not the spread of individual participants' scores.

What does the arm comparison represent?

The comparison is expressed as the mean for Hyabak 0.15% minus the mean for SYSTANE HYDRATION. The posted estimate is 0.24. A positive value under this ordering means the Hyabak estimate is numerically higher, while the primary endpoint description says that more negative change indicates greater efficacy. The subtraction order is important: reversing the arm order would reverse the sign without changing the underlying contrast.

The comparison and confidence interval are simple unadjusted recalculations from the posted summary statistics. They do not incorporate an adjustment for additional variables, and the registry record does not describe the model used for the posted least-squares means. The discrepancy indicator is false, so the recalculated contrast does not conflict with a sponsor analysis recorded in the registry record for this trial. The registry record nevertheless lists zero reported analyses, so it does not identify a sponsor-run inferential analysis to use as the primary account.

What do the standard errors and interval convey?

In general, a standard error quantifies the sampling uncertainty of an estimated mean. It is not the same as a standard deviation, which describes variation among individual observations. The arm standard errors for the primary outcome are 0.24 and 0.23. In general, a confidence interval gives a range of values compatible with the data and the method's assumptions; it is not a guarantee that the true value lies in that range. The interval for the arm contrast extends on both sides of zero, so the posted summary does not sharply locate the contrast in one direction.

The recalculated pooled standard deviation is approximate. The posted outcome estimates are least-squares means and their dispersion is reported as standard error, rather than as standard deviation. A standard deviation used for standardized-effect and planning calculations was therefore approximated from these summaries. Any standardized-effect value or planning illustration based on that approximation should be interpreted as an aid to understanding, not as a directly reported trial estimate.

Why can over-dispersion matter?

In general, over-dispersion means that variability in the observed data is greater than a model assumes. When a model understates variability, it can make standard errors too small and intervals too narrow, giving an overly precise impression. When variability is modeled appropriately, uncertainty estimates better reflect the scatter in the data. The registry record does not report a dispersion check or an over-dispersion adjustment for this continuous endpoint, so no claim can be made about whether such a check was performed. This general issue is relevant whenever a statistical model's assumptions determine the reported uncertainty.

What does the p-value add?

The unadjusted p-value for the primary comparison is 0.47. In general, a p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the test assumptions held. It does not measure the probability that the null hypothesis is true, the probability that the result occurred by chance, or the clinical importance of an estimate. The registry record does not report the test procedure or a multiplicity adjustment for this comparison. The p-value should therefore be read with the estimate and its interval, not as a standalone verdict.

The comparison is unadjusted, meaning no reported adjustment is reflected in the recalculated contrast. The registry record does not state whether a different adjustment was prespecified in the trial plan. It also does not give the original sample-size assumptions. The trial's own design assumptions are not reported in the registry record; the planning illustrations use a separate set of stated assumptions and must not be attributed to the original protocol.

How should the analysis population be understood?

The primary outcome identifies the ITT Analysis Set and defines the number analyzed as participants with a non-missing response. The analyzed counts are 48 for SYSTANE HYDRATION and 49 for Hyabak 0.15%. In general, an intention-to-treat approach aims to retain participants in their assigned groups, but the label alone does not establish how missing values were treated or whether every randomized participant contributed to the endpoint analysis. The missing-data method, handling of protocol deviations, and details of the analysis population are not reported in the registry record.

The record describes one study eye contributing to the TOSS analysis, which avoids treating two eyes from one person as if they were independent observations for this endpoint. The precise rule for selecting that eye and any other analysis details are not reported in the registry record. These omissions limit how fully an independent reader can reproduce or audit the analysis from the registry outcome summary alone.

11. Confidence Intervals and Precision

The primary arm means are -1.16 for SYSTANE HYDRATION and -0.92 for Hyabak 0.15%. The recalculated mean difference is 0.24, with a confidence interval that runs from a negative value to a positive value. Because zero lies within that interval, the range of values supported by the posted summary includes no between-arm difference as well as differences in either direction. The unadjusted p-value is 0.47.

In general, a confidence interval communicates both the direction and the precision of an estimate. A narrow interval concentrates support around a smaller range of values; a wider interval leaves more possible values compatible with the data and method. Here, the interval does not narrow the contrast to a single direction. The point estimate alone is therefore a limited description of the comparison, and its direction should not be confused with certainty about the underlying difference.

The reported arm standard errors are 0.24 and 0.23. These describe uncertainty around the least-squares means, while the interval for the comparison concerns the difference between those means. The registry record does not report the full model or adjustment procedure behind the least-squares means, and the recalculated interval is unadjusted. Precision should be understood in that context.

The comparison does not establish that the treatments are equivalent. Equivalence requires a prespecified range of differences considered acceptably small and an analysis designed to assess that range; neither is reported in the registry record. Nor does the interval alone identify which differences would matter clinically, because a clinically important TOSS threshold is not reported. The available precision supports a cautious description of the observed contrast, not a definitive claim of sameness or separation.

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 figures are planning illustrations based on the observed effect, not the trial's own original design assumptions. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The listed effect to detect is a stated fraction of the observed effect: 100%, 75%, or 50%. The figures are participants per arm for the continuous outcomes, not total event counts.

The 80% power column indicates the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the calculation assumptions hold. The 90% power column gives the corresponding planning number for a 90% chance. These percentages describe the design calculation, not the probability that a result in this trial is true or that a treatment has a particular effect.

Across the listed rows, planning for a smaller fraction of the observed effect requires more participants per arm. This is expected in general: smaller differences are harder to distinguish from random variation when measurement variability and other assumptions remain fixed. The figures depend on the observed effect used as their starting point, so they are sensitive to how precisely that effect was estimated in this trial.

The sample-size assumptions for the original trial are not reported in the registry record. These calculations are not observed power; they are hypothetical planning illustrations based on the observed contrast and the stated assumptions. They should not be read as evidence that the original design used these targets, nor as a retrospective judgment about whether the trial was adequately designed.

The plotted curve represents the same planning relationship across effect assumptions. It should be read as an illustration of how the required per-arm sample size changes with the effect being targeted, not as a new analysis of participant outcomes. No additional exact values need to be inferred from the curve beyond the listed planning figures.

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 = 0.240; pooled standard deviation σ = 1.636.
2. n = 2 × (1.96 + 0.842)² × 1.636² / 0.240² = 729.7, rounded up to 730 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 <- 0.24                      # observed difference in means
sigma <- 1.6363193614425                     # 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(2470429)
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 = 730 (80% power), 977 (90% power)
 75% of observed effect: n per arm = 1,298 (80% power), 1,737 (90% power)
 50% of observed effect: n per arm = 2,919 (80% power), 3,908 (90% power)
power.t.test: 730.7 
Simulated power at n = 730 per arm: 0.803 (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 record does not report a statistical analysis plan describing how the primary and secondary endpoints were to be tested. It lists three secondary outcomes, but does not specify a testing hierarchy, a family of hypotheses, or an adjustment for multiple comparisons. The posted secondary p-values are unadjusted recalculations. In general, examining multiple outcomes without controlling multiplicity can raise the chance that at least one result appears statistically unusual even when the underlying effects are absent or small. The record does not say whether the original trial used a multiplicity procedure.

The primary endpoint is identified as an ITT Analysis Set outcome, with the number analyzed defined as participants with a non-missing response. The primary outcome counts are 48 and 49. However, the registry record does not report a participant-flow description that accounts for all enrolled participants, nor does it describe whether missing outcomes were imputed, excluded under any additional rule, or addressed through sensitivity analyses. The definition of the analyzed count clarifies who contributes a response, but not the method for handling absent responses.

The record also does not provide details on protocol deviations, treatment adherence, or how the analysis population was maintained after randomization. Those details are not reported in the registry record. The ITT label should not be treated as proof that all enrolled or randomized participants contributed data to the endpoint estimate, since the record explicitly defines the analyzed count by response availability.

The registry record lists zero reported analyses. This means it does not present a named analysis procedure for the endpoints; it does not establish that no analysis was conducted during the trial. The original sample-size justification, interim-analysis plan, and rules for stopping or modifying analyses are not reported in the registry record. No assumptions about those procedures can be inferred from the posted outcome summaries.

These omissions matter because the interpretation of an estimate depends not only on its numerical value but also on how outcomes, missing data, and multiple testing were handled. The published registry summaries permit a descriptive comparison and simple unadjusted recalculations, but they do not support a full audit of the original analysis strategy.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: intervertebral disc operation (2.0%), cholelithiasis (2.0%).

The registry record reports serious adverse events by group. In the pretreatment group, 114 participants were at risk and 0 were reported with a serious adverse event. In the SYSTANE HYDRATION group, 50 were at risk and 1 was reported with a serious adverse event. In the Hyabak 0.15% group, 49 were at risk and 1 was reported with a serious adverse event. The record reports 0 deaths in each of these groups.

The serious-event figures are counts within the groups, not comparisons adjusted for differences in exposure or other factors. The pretreatment group is a distinct record category and should not be interpreted as a concurrent treatment arm. The registry also lists Intervertebral disc operation and Cholelithiasis among top serious-event terms, each at 2.0%; it does not provide enough context in these summaries to assign those terms to a particular treatment group.

These numbers describe what was recorded in this trial and do not, by themselves, establish that an event was caused by a treatment or that the groups have different safety profiles. The registry record does not provide further detail about event timing, duration, relatedness assessments, or exposure-adjusted comparisons.

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

The posted primary results describe a change in TOSS over the study period for the two reported arms. The SYSTANE HYDRATION mean change is more negative than the Hyabak 0.15% mean change, and the endpoint description says that a more negative value indicates greater efficacy. The recalculated between-arm difference is 0.24 when expressed as Hyabak minus SYSTANE HYDRATION. Its unadjusted confidence interval spans zero, and the unadjusted p-value is 0.47. These statistics describe an uncertain comparison rather than a precise separation of the arm results.

The result does not show that the arms are equivalent, because the registry record does not report an equivalence margin or a design intended to demonstrate equivalence. It also does not establish that either arm is superior. The interval includes values in both directions, and the record does not report a clinically important difference threshold that would help determine the practical importance of the estimated contrast.

The result applies to the posted outcome analysis in this study: a Day 42 change in a staining score, based on one study eye and analyzed among participants with non-missing responses. It should not be generalized automatically to other populations, timeframes, outcomes, or interventions. In particular, although saline appears in the intervention list, no saline primary outcome estimate is included in the posted results described in the registry record.

The secondary endpoints add information about treatment experience and tear-film break-up time, but their unadjusted results do not repair the primary comparison's uncertainty. The registry record does not report a multiplicity strategy or identify the confirmatory status of those outcomes. Similarly, the adverse-event counts provide a descriptive account of serious events recorded in the groups; they do not prove causality or establish comparative safety.

The registry record also lacks details needed to reconstruct the original statistical analysis fully, including the model specification, missing-data handling, and original sample-size justification. A responsible interpretation stays close to the posted estimates, uncertainty, and design information, while treating unreported procedures as unknown rather than assuming how they were handled.

17. Why This Trial Matters Statistically

This trial illustrates why a directionally different point estimate is not the same as a precise treatment contrast. The primary outcome means are not identical, and the endpoint's scoring direction gives a clear way to describe which arm's estimate is more negative. But the confidence interval spans values on both sides of zero. Reading the estimate together with its uncertainty prevents the direction alone from carrying more weight than the data support.

It also shows the value of distinguishing model-based arm summaries from direct measures of participant-level variability. The registry reports least-squares means and standard errors, not standard deviations. The standardized-effect and planning illustrations therefore depend on an approximate pooled standard deviation derived from those summaries. This is a practical reminder that downstream calculations can involve additional assumptions when the original report does not provide every statistic needed directly.

Several outcomes are posted, yet the registry record does not describe a multiplicity plan or identify which secondary analyses were confirmatory. When many outcomes are considered, isolated unadjusted findings require restraint. The secondary endpoints may provide useful context, but they should not be treated as independent confirmation without a prespecified analysis framework.

Finally, the registry record contains meaningful gaps for statistical interpretation: no named analyses, no original sample-size justification, no detailed missing-data method, and no full model specification. Those omissions do not erase the value of the posted results, but they set a boundary on what can be independently checked. A careful reader can describe the estimates and their precision while keeping conclusions proportionate to the available record.

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 describe the randomization sequence, allocation concealment, or who was masked, despite listing the study as randomized and double-masked. The exact procedures supporting those design labels are not reported in the registry record. The intervention list includes 0.9% saline eye drops, but the posted primary outcome arms contain only SYSTANE HYDRATION and Hyabak 0.15%; the role of saline in the reported primary comparison is therefore not clear from the outcome results.

The primary endpoint analysis includes 48 and 49 participants, while overall enrollment is 114. The record defines analyzed participants as those with non-missing responses but does not supply a full participant-flow account or explain missing outcomes. It also does not describe the model behind the least-squares means, the method for missing data, or sensitivity analyses. These details limit reproducibility and assessment of how robust the estimates are to analysis choices.

The registry record does not report the original sample-size rationale, a prespecified clinically important TOSS difference, or whether the study was designed to test superiority, non-inferiority, or equivalence. The planning illustrations are based on the observed effect under separate assumptions, not the original trial design. Consequently, they cannot answer whether the original design had a particular target or whether its assumptions were met.

There are three secondary outcomes, but no reported multiplicity strategy or named secondary analyses. The unadjusted results should therefore be interpreted cautiously. Safety summaries are limited to group counts and listed terms; further information on timing, relatedness, and exposure is not reported in the registry record. Together, these limitations constrain causal, clinical, and confirmatory interpretations beyond the descriptive statistical results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluation of Clinical Outcomes After the Use of SYSTANE® HYDRATION — NCT02470429.
• Registry record last updated 2018-07-02; status last verified 2017-06.
• 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 record describes a completed, randomized, double-masked, parallel-group study of SYSTANE HYDRATION and Hyabak 0.15% in subjects with dry eye. Enrollment was 114. The primary outcome was change from baseline in TOSS at Day 42, with one study eye contributing to the analysis. The posted arm means were -1.16 and -0.92, respectively, and the unadjusted recalculated mean difference was 0.24 with an interval spanning zero and an unadjusted p-value of 0.47.

Three secondary outcomes are listed: IDEEL Treatment Effectiveness, IDEEL Treatment Inconvenience, and TFBUT. The record also posts serious adverse-event counts and reports 0 deaths in each listed group. It does not report named statistical analyses, the original sample-size justification, a multiplicity plan, detailed missing-data methods, or the model specification behind the least-squares means. The secondary comparisons and planning illustrations should be read with those limits in mind.