TearCare System to Treat Dry Eye Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for TearCare System to Treat Dry Eye Disease (NCT03857919), a randomized na study. The primary outcome is Change in Tear Break-Up Time (TBUT) From Baseline.

2. Clinical Question

The registry describes a randomized, controlled comparison intended to evaluate safety and effectiveness in relieving signs and symptoms of dry eye disease. The statistical question addressed by the posted primary outcome is narrower: whether the groups’ mean changes in TBUT differed at the stated assessment time. The posted summaries give the change in each group and an unadjusted contrast, with uncertainty represented by a confidence interval.

This comparison is not a test of every symptom or sign associated with dry eye disease. The registry lists additional measures, including OSDI, staining scores, SANDE, eye dryness, and meibomian gland measures. Those outcomes address different aspects of the condition and should not be treated as interchangeable with TBUT. Nor does a difference in a measure, by itself, establish that a particular intervention is clinically preferable. The record’s stated endpoint and the quality and completeness of its reported analysis determine what can be concluded from these results.

3. Trial Design

The registry describes NCT03857919 as a randomized, controlled, parallel-group trial comparing the TearCare System with the LipiFlow Thermal Pulsation System. The listed allocation is randomized, and the masking is single. Which participants or study personnel were masked is not reported in the registry record. The record lists the study as completed and gives an enrollment of 235.

The two arms used different device procedures. TearCare was described as eyelid heating followed by manual expression of the meibomian glands; LipiFlow was described as eyelid heat and pressure. These intervention descriptions identify what was compared, but do not establish how consistently procedures were delivered or whether participants received additional care. Those details are not reported in the registry record.

The primary endpoint was mean change in Tear Break-Up Time from baseline, measured in seconds, at 1 month. The primary analysis population is named, and the arm-level outcome summaries list 67 participants for TearCare and 68 for LipiFlow. Those endpoint counts should be read as the numbers associated with the posted outcome summaries, not as a complete account of enrollment, follow-up, or missing observations. The record does not explain the relationship between the enrollment figure and the outcome-specific counts.

The registry lists Dry Eye and Meibomian Gland Dysfunction as conditions. It also lists seven secondary outcome measures addressing symptoms, ocular surface staining, and meibomian gland output. The detailed numerical secondary summaries cover OSDI and corneal and conjunctival staining. Further information about the protocol, the original design assumptions, masking procedures, and the statistical analysis plan is 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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Primary Analysis Population

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change in Tear Break-Up Time (TBUT) From Baseline, measured over 1 month.

Tear Break-Up Time (TBUT) is defined in the registry record as the time measured until the first observation of a break in the tear film. The primary outcome is the mean change in TBUT from baseline, in seconds, assessed at 1 month. A change score expresses how the measurement at follow-up differs from the baseline measurement; it is not the follow-up value itself.

TBUT is used as an objective sign related to the tear film. In general, a measurement of time to an observed tear-film break can help characterize tear-film stability. That makes it a relevant sign to examine in a study of dry eye disease, while leaving symptoms and other ocular signs to be assessed by separate measures. The endpoint does not capture every aspect of the condition, and its meaning depends on the measurement procedure and the population analyzed.

The reported group means are changes, and the comparison is a difference between those mean changes. A positive or negative difference describes the numerical direction of the contrast under the stated group ordering; it does not, on its own, determine clinical importance. The registry record does not report a threshold for a clinically meaningful TBUT change, nor does it give a protocol-defined interpretation threshold. The statistical result should therefore be read as an estimate on the seconds scale, together with its uncertainty, rather than as a stand-alone judgment about patient benefit.

7. Results Posted in the Registry

• LipiFlow: mean 2.58 versus 3.02 on control; difference -0.44 (95% CI -1.75 to 0.87), standardized effect d = -0.11; z-test p = 0.511.

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.

Mean Change in Ocular Surface Disease Index (OSDI) Score From Baseline

• 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 deviations.
• Result:
  • LipiFlow: mean -23.40 versus -27.88 on control; difference 4.48 (95% CI -1.98 to 10.94), standardized effect d = 0.23; z-test p = 0.174.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LipiFlow and the control. The interval gives the range of effects that remain compatible with the data.

Change in Corneal Staining Score From Baseline

• 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 deviations.
• Result:
  • LipiFlow: mean -0.57 versus -0.25 on control; difference -0.32 (95% CI -0.99 to 0.35), standardized effect d = -0.16; z-test p = 0.351.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LipiFlow and the control. The interval gives the range of effects that remain compatible with the data.

Change in Conjunctival Staining Score From Baseline

• 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 deviations.
• Result:
  • LipiFlow: mean -0.78 versus -0.66 on control; difference -0.12 (95% CI -1.05 to 0.81), standardized effect d = -0.04; z-test p = 0.800.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LipiFlow and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists seven secondary outcome measures spanning symptoms, ocular surface staining, and meibomian gland output. Detailed numerical summaries are posted for OSDI and corneal and conjunctival staining. Numerical results for the other listed secondary measures are not reported in the registry record. The available results therefore give only a partial view of the secondary outcomes named in the record.

Across the posted summaries for OSDI and the two staining scores, the group mean changes are negative in both arms. The estimated between-group contrasts vary in direction and magnitude, and their confidence intervals include zero. This broad pattern does not identify a clear, precise separation between the groups across these additional measures. The outcomes have different scales and assess different features, so their values should not be combined into a single overall effect or interpreted as if they measured the same construct.

These secondary findings provide context for the primary TBUT comparison but do not override it. Nor do they independently confirm a primary result: secondary measures may differ in reliability, relevance, and analysis choices. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary outcomes. When multiple outcomes are examined, the chance of finding apparently notable results by chance can increase unless the analysis plan accounts for the number and structure of tests. For that reason, unadjusted secondary results generally carry less evidential weight than a prespecified primary result, especially when the full analysis strategy is not documented.

The secondary outcomes also include symptom scores and gland-output measures, which could add distinct information if complete results and analysis details were available. Since those numerical summaries are not reported in the registry record, they cannot be used to strengthen or qualify the interpretation of the posted primary estimate. The available secondary results should be viewed as complementary but limited evidence, not as a substitute for a complete outcome report.

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

• Mean Change in Ocular Surface Disease Index (OSDI) Score From Baseline
• Change in Corneal Staining Score From Baseline
• Change in Conjunctival Staining Score From Baseline
• Change in Symptom Assessment in Dry Eye (SANDE) Scores From Baseline
• Change in Eye Dryness Score (EDS) From Baseline
• Change in Total Number of Meibomian Glands Yielding Clear Liquid From Baseline
• Change in Total Number of Meibomian Glands Yielding Any Liquid From Baseline

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary result can be understood by separating the group summaries, the between-group estimate, and the uncertainty around that estimate. This distinction matters because a group mean is not itself a comparison, and a comparison estimate without an uncertainty measure can be misleadingly definitive.

What does the mean change represent?

For each arm, the reported outcome is the mean change from baseline in TBUT at 1 month. The TearCare mean change is 3.02 seconds, and the LipiFlow mean change is 2.58 seconds. The accompanying standard deviations are 4.41 and 3.28 seconds, respectively. A mean describes the average change in the analyzed group. A standard deviation describes how dispersed individual changes are around that group mean; it is not the uncertainty of the mean itself and is not a range containing every participant’s value.

The primary outcome summary gives 67 participants for TearCare and 68 for LipiFlow. The registry labels the analysis population as the Primary Analysis Population, but does not give more detail about how that population was defined. The arm counts therefore identify the outcome summaries’ analysis sizes, not necessarily all randomized participants or all participants with any follow-up.

How should the contrast be read?

The estimated mean difference is -0.44 seconds for LipiFlow relative to TearCare. This ordering is important: the contrast is calculated as the LipiFlow mean change compared with the TearCare mean change. A negative estimate indicates a lower mean change for LipiFlow in the posted summaries. It does not imply that one treatment is better, because the clinical interpretation depends on the endpoint’s direction, meaningful-change criteria, and study context. The registry does not report a threshold for interpreting the size of a TBUT difference.

The recalculated comparison uses the posted summary statistics and is unadjusted. An unadjusted comparison does not account for covariates or other modeling choices. The registry record does not report a sponsor analysis for the primary outcome or explain whether another analysis was used for the trial’s conclusions. The posted recalculation is therefore useful for understanding the summaries, but should not be mistaken for a fully documented analysis plan.

What does a confidence interval add?

A confidence interval expresses uncertainty around an estimated difference using a range of values compatible with the data and the calculation method. The primary interval runs from -1.753 to 0.873 seconds. Because this interval crosses zero, it includes the possibility of no between-group difference, along with possible differences in either direction. Its breadth also shows that the estimate is not highly precise. A confidence interval is not a guarantee that the true effect lies within its endpoints, and it is not a probability statement about the effect after observing the data.

The p-value of 0.511 is an unadjusted test result associated with the recalculated contrast. In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under the assumptions of the test. It is not an effect-size measure and does not establish equivalence. Interpretation should give priority to the estimate and its interval, while recognizing that the statistical method and assumptions are not fully documented in the registry record.

Why distinguish observed results from planning illustrations?

The registry’s planning illustrations use an observed effect as their starting point and consider alternative fractions of that effect. They are not the trial’s original design justification. The record states a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation for the planning calculations. The illustrations give participants per arm for this continuous outcome. The original trial’s sample-size assumptions and justification are not reported in the registry record.

These planning figures describe hypothetical future study sizes under stated assumptions. They are not a retrospective measure of how likely the completed trial was to detect an effect, and they do not change the observed estimate or its uncertainty. In particular, they should not be described as observed power. The calculations are sensitive to the effect size chosen: planning for a smaller fraction of the observed effect requires more participants under the stated method.

What is not documented?

The registry record does not report the sponsor’s detailed statistical analysis plan, the approach to missing data, whether there were interim analyses, or how multiplicity across outcomes was addressed. It also does not report whether the primary comparison was adjusted for baseline values or other covariates. These omissions limit the ability to assess whether the posted summaries represent the prespecified primary analysis, how departures from the protocol were handled, or how uncertainty from multiple testing should be interpreted.

In general, statistical conclusions depend not only on the reported means and standard deviations but also on analysis-population definitions, missing-data assumptions, model specifications, and outcome selection. Those are not reasons to assume the analysis was flawed; they are reasons to keep conclusions proportionate to what the registry record documents. The posted summaries support a cautious description of the one-month group contrast, while leaving important analytic details unreported.

11. Confidence Intervals and Precision

The primary estimate is a difference of -0.44 seconds, with a confidence interval from -1.753 to 0.873 seconds. The interval includes zero and extends in both directions from the estimated contrast. Thus, the results do not identify a single precise between-group difference. The data are compatible with a negative contrast, little or no difference, and a positive contrast within the stated interval.

Confidence intervals are useful because they show the scale of uncertainty around an estimate, rather than reducing the result to a yes-or-no decision based on a p-value. Here, the interval is broad relative to the point estimate. That means the estimate alone should not be treated as a precise measure of the difference that would necessarily be seen in another study. The interval also does not say that every value inside it is equally likely, nor does it assign a probability to the true effect.

The group standard deviations, 4.41 seconds for TearCare and 3.28 seconds for LipiFlow, describe variation in participant-level changes. The confidence interval reflects uncertainty in the between-group estimate, which is related to the amount of variation and the outcome-specific group sizes. These are distinct quantities: dispersion among individual changes is not the same as uncertainty around a group difference.

The p-value of 0.511 is consistent with substantial uncertainty about whether the observed contrast differs from zero under the unadjusted calculation. It should not be read as evidence that the groups are equivalent. The registry record does not provide an equivalence margin or a clinically meaningful threshold for TBUT. Consequently, neither the confidence interval nor the p-value establishes clinical equivalence or a clinically important difference.

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 for this continuous outcome are participants per arm, not total events. They are illustrations computed from the observed effect under the stated assumptions: a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers planning for a stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the hypothetical number of participants per arm associated with an 80% chance of detecting the effect used for that planning row, under the calculation assumptions. The 90% power column describes the corresponding hypothetical number per arm for a 90% chance. These are planning targets, not guarantees about a future study; actual results depend on the true effect, variability, adherence to the assumptions, and analysis choices.

For planning at 100% of the observed effect, the illustrations give 1,222 participants per arm for 80% power and 1,636 participants per arm for 90% power. Planning for 75% of the observed effect gives 2,173 participants per arm for 80% power and 2,909 participants per arm for 90% power. Planning for 50% of the observed effect gives 4,888 participants per arm for 80% power and 6,544 participants per arm for 90% power. The pattern reflects a general statistical principle: smaller effects are harder to distinguish from random variation, so detecting them requires more participants under otherwise similar assumptions.

These figures are not observed power for the completed trial. They are prospective planning illustrations based on the observed effect, not evidence that the trial was designed around these assumptions or that the effect is reliable as a planning target. Because the observed estimate is uncertain, treating it as a fixed value for future planning may be misleading; the alternative fractions help show how required sample sizes change when the target effect is smaller.

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 = -0.440; pooled standard deviation σ = 3.882.
2. n = 2 × (1.96 + 0.842)² × 3.882² / -0.440² = 1,222.0, rounded up to 1,222 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 <- -0.44                      # observed difference in means
sigma <- 3.88208474339332                     # 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(3857919)
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 = 1,222 (80% power), 1,636 (90% power)
 75% of observed effect: n per arm = 2,173 (80% power), 2,909 (90% power)
 50% of observed effect: n per arm = 4,888 (80% power), 6,544 (90% power)
power.t.test: 1222.9 
Simulated power at n = 1,222 per arm: 0.797 (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 outcome and several secondary measures, but does not report how the trial handled multiplicity. Multiplicity arises when multiple outcomes, time points, or statistical comparisons are examined. In general, testing many hypotheses without an adjustment or a prespecified hierarchy can increase the chance of at least one apparently significant finding occurring by chance. The record does not say whether an adjustment was used, whether secondary outcomes were treated as exploratory, or how conclusions were to be prioritized.

There are seven listed secondary outcome measures, while detailed secondary numerical summaries are posted for OSDI and corneal and conjunctival staining. The registry does not report numerical results for the other listed secondary measures. Without a complete outcome set and a stated multiplicity strategy, it is difficult to assess the overall pattern of testing or the evidential weight of any individual secondary finding. This limitation is separate from the size and uncertainty of the primary estimate.

Missing-data methods are also not reported in the registry record. The outcome-specific summaries list 67 participants for TearCare and 68 for LipiFlow, while the record gives an overall enrollment of 235. The record does not explain how these numbers relate to the randomized population, whether outcome measurements were unavailable for some participants, or how missing observations were handled. It would be inappropriate to infer that all missing observations were excluded, imputed, or treated in any particular way.

The primary outcome names a Primary Analysis Population, but its membership and definition are not described in the posted information. The record does not specify whether the primary analysis followed an intention-to-treat approach, a per-protocol approach, or another population rule. It also does not report whether baseline adjustment, subgroup analyses, or interim analyses were conducted. These gaps prevent a full appraisal of the analysis population and the prespecified statistical plan. They do not establish that a particular method was or was not used; they mean that the method is not reported in the registry record.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The safety record lists serious adverse events affecting 0 of 115 participants at risk in the TearCare group and 0 of 120 at risk in the LipiFlow group. It lists other adverse events affecting 7 of 115 at risk for TearCare and 8 of 120 at risk for LipiFlow. Deaths are recorded separately as 7 for TearCare and 8 for LipiFlow. These are descriptive counts from the registry record.

The serious-event counts do not establish that no serious events occurred outside the reported accounting or that the interventions have identical safety profiles. The registry record lists no serious adverse-event terms. It does not report the causes of the recorded deaths, their timing, or whether they were considered related to either device or to the trial. The counts should therefore not be interpreted as evidence of causation or as a direct comparison of treatment-related risk.

Counts alone also do not provide the clinical details, severity, duration, or resolution of other adverse events. The registry’s safety information supports a limited description of recorded events and affected participants, but not a comprehensive safety assessment.

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

The posted primary result describes the mean change in TBUT at 1 month for the analyzed groups and the estimated difference between them. The point estimate is -0.44 seconds for LipiFlow relative to TearCare. Its confidence interval includes zero and is broad, so the comparison does not establish a precise difference between the groups. The unadjusted p-value of 0.511 likewise should not be treated as proof that the interventions are equivalent or that any difference is absent.

These findings do not by themselves determine whether either device is effective, ineffective, or clinically preferable. The registry describes the study objective as evaluating safety and effectiveness, but the posted primary result addresses one measure at one assessment time. A conclusion about clinical benefit would require context such as a clinically meaningful threshold, complete outcome reporting, and a clear understanding of the analysis population and methods. Those details are not reported in the registry record.

The study compares two active device procedures, not a device with no treatment. Consequently, the reported contrast is relative to the other device under the trial’s circumstances; it does not quantify change against no intervention. The posted data also do not establish whether the findings generalize to people or settings beyond those represented by the trial. The record identifies dry eye disease and meibomian gland dysfunction, but gives limited detail about participant characteristics and eligibility in the information summarized.

Secondary outcomes and safety counts add context but have their own limitations. Some secondary numerical summaries are available, while other listed outcomes lack numerical results in the registry record. The multiplicity and missing-data approaches are not reported, and safety counts do not provide causes or treatment relationships. A careful reading is therefore descriptive: the registry reports group changes and event counts, with substantial uncertainty around the primary contrast and important analytic and reporting details left unspecified.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between an estimated effect and the certainty attached to it. The primary comparison has a numerical direction and a confidence interval, but the interval includes zero and spans a range that leaves the true between-group difference uncertain. A reader who focuses only on the point estimate or only on the p-value would miss that uncertainty.

The study also highlights the importance of distinguishing outcome-level counts from overall enrollment. The primary summaries have their own analysis counts, and the registry names an analysis population without fully defining it. Clear reporting of who contributed data, how missing observations were handled, and whether analyses followed a prespecified plan is essential for interpreting randomized comparisons.

Another statistical lesson concerns the role of secondary outcomes. Measures of symptoms, staining, and gland output can add useful perspectives, but multiple outcomes require a transparent approach to interpretation. Without a reported multiplicity strategy and complete numerical results, secondary findings are best treated as supportive context rather than as a set of independent confirmations.

Finally, the planning illustrations show why sample-size calculations should be tied to explicit assumptions and a defensible target effect. Their figures are not the original trial design rationale and are not observed power. Their value is in showing how planned sample size changes when the target effect is reduced, while emphasizing that the observed estimate itself is uncertain. Together, these issues make the registry a useful example of why effect estimates, precision, analysis transparency, and design assumptions should be read as connected but distinct parts of 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.

Several trial-specific limitations follow from what is and is not reported. The primary result is available as group means, standard deviations, and an unadjusted recalculated contrast, but a separate sponsor analysis is not listed. The registry record does not describe the primary analysis method in sufficient detail to establish whether the recalculation matches the trial’s prespecified analysis. The record’s discrepancy flag is false, but that does not supply the missing statistical plan or additional analysis details.

The primary outcome is measured at 1 month. The reported result therefore concerns that assessment time and does not describe longer-term outcomes. The registry record does not provide a clinically meaningful threshold for TBUT, making it difficult to judge the practical importance of the estimated difference even apart from its statistical uncertainty.

The posted outcome counts are smaller than the enrollment figure, but the registry does not explain the relationship between them. Analysis-population membership, participant flow, reasons for missing outcome data, and missing-data methods are not reported. These omissions limit assessment of how representative the analyzed data are of the randomized groups.

Masking is described as single, without specifying who was masked. The available intervention descriptions do not report implementation fidelity or other care received. The registry also does not report multiplicity handling, interim analyses, or the original sample-size justification. For safety, event terms and the causes or treatment relationships of deaths are not described. These reporting gaps limit interpretation; they do not, by themselves, show that a bias or safety problem occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: TearCare System to Treat Dry Eye Disease — NCT03857919.
• Registry record last updated 2025-10-01; status last verified 2025-08.
• Results first posted 2025-10-01.
• 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

NCT03857919 is a completed randomized, controlled, parallel-group comparison of TearCare and LipiFlow for dry eye disease. The registry lists an enrollment of 235 and single masking, without specifying who was masked. The primary outcome is mean change in TBUT from baseline at 1 month, measured in seconds.

The posted mean changes are 3.02 seconds for TearCare and 2.58 seconds for LipiFlow. The unadjusted recalculated contrast for LipiFlow relative to TearCare is -0.44 seconds, with a confidence interval that includes zero and an unadjusted p-value of 0.511. The result is therefore uncertain and does not establish equivalence or clinical importance.

Secondary summaries and adverse-event counts provide limited additional context. The registry record does not report important details about analysis methods, missing data, multiplicity, or the original design assumptions. The planning illustrations are hypothetical participants-per-arm calculations, not observed power.