Platelet -Rich Plasma (PRP) Injection for the Treatment of Severe Dry Eye: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Platelet -Rich Plasma (PRP) Injection for the Treatment of Severe Dry Eye (NCT02257957), a randomized phase 3 study. The primary outcome is Change From Baseline in Ocular Surface Staining.

2. Clinical Question

The clinical question is about a measured eye-surface outcome in a small randomized comparison, not a broad assessment of every aspect of dry eye. Ocular surface staining grades damage to the exposed eye using the Oxford scale, where the registry describes scores from 0 to 5: 0 indicates absent surface damage and 5 indicates severe surface damage. The trial also posts change in the Ocular Surface Disease Index (OSDI) as a secondary outcome.

The registry describes 30 participants, with 15 assigned to each arm. It does not report enough detail to establish how participants were recruited, whether the sample represents any particular subgroup, or how diagnoses and severity were operationalized. The record lists Sjogren Syndrome as a condition, but does not give the number of participants with that diagnosis. Therefore, the results should be understood as applying to the trial population recorded in the registry, rather than to a more specifically characterized group.

The comparison can describe the measured differences between the randomized groups in this trial. It cannot, on the posted information alone, establish how those differences translate into symptoms, daily functioning, or longer-term outcomes. The registry’s summary states that the study aimed to evaluate lacrimal production and safety, while the posted primary endpoint is ocular surface staining. Those are related aspects of the study’s stated context, but they are not interchangeable measures.

3. Trial Design

The registry classifies the study as a Phase 3, randomized, parallel-group trial with no masking. The record lists an enrollment of 30. The arm descriptions specify 15 participants receiving PRP and 15 receiving standard care. The study is marked completed. Its recorded start date is 2014-11-30, and its primary completion date is 2015-09-30.

The PRP arm description schedules injections at day 0, 30, 60, and 90. The standard-care arm is described as receiving standard-of-care treatment, with review at the same scheduled points; the intervention list names hyaluronic acid eye drops as standard care. These descriptions establish the recorded treatment and visit schedules, but do not provide further detail about how PRP was prepared or administered, the dose of eye drops, treatment adherence, or co-interventions.

Random allocation can help make treatment groups comparable at the outset, on average, but the registry does not report the sequence-generation method, allocation concealment, or any stratification factors. With a small enrollment, chance differences in participant characteristics may remain important even in a randomized study. Baseline characteristics and baseline outcome values are not reported in the registry record, so the extent of any such imbalance cannot be assessed from the posted results.

No masking is recorded. This matters especially for outcomes that can be influenced by assessment or participant expectations. The registry does not describe whether staining assessments were performed by masked assessors, whether the outcome assessor was separate from the treatment team, or how scoring consistency was maintained. These details are not reported in the registry record.

The design is parallel: participants were assigned to one of the two arms rather than described as crossing between treatments. The record does not report the trial’s original sample-size assumptions, its planned analysis population, its missing-data approach, or whether interim analyses were planned. The fact that the study is labeled Phase 3 does not itself resolve those omissions or establish the strength of the evidence from the posted results.

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

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 From Baseline in Ocular Surface Staining, measured over 90 days.

The primary endpoint is change from baseline in ocular surface staining at 90 days. Staining is used to assess surface damage to the exposed eye: the registry says the Oxford grade panel was used, with scores ranging from 0 to 5. A score of 0 indicates absent surface damage, while 5 indicates severe surface damage. This makes the endpoint a graded measure of an observable feature of the eye surface, rather than a direct measure of symptoms or overall functioning.

Change from baseline is intended to describe how a measurement differs from its starting value over the follow-up period. Comparing changes between randomized groups can help distinguish the groups’ recorded trajectories from their starting measurements. However, the registry does not report the baseline means or explain the sign convention used for the change scores. It therefore does not establish whether a positive change means an increase or a decrease in staining. The posted means and contrast can be described numerically, but the clinical direction of the change should not be inferred from the sign alone.

Staining is relevant to the study’s stated focus on severe dry eye because it grades surface damage. It is not, by itself, a complete measure of the condition. The registry also posts OSDI as a secondary outcome, which is a separate measure. The endpoint description does not state a threshold for an important change, and no such threshold is reported in the registry record. Statistical differences and clinical importance are therefore separate questions.

7. Results Posted in the Registry

• Platelet -Rich Plasma (PRP): mean 1.20 versus 2.40 on control; difference -1.20 (95% CI -1.33 to -1.07), standardized effect d = -6.67; z-test p = <0.001.

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 Ocular Surface Disease Index (OSDI)

• 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:
  • Platelet -Rich Plasma (PRP): mean 34.00 versus 55.00 on control; difference -21.00 (95% CI -23.39 to -18.61), standardized effect d = -6.30; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Platelet -Rich Plasma (PRP) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary outcome: change from baseline in OSDI at 90 days. Its mean contrast is numerically negative, as is the posted primary contrast for ocular surface staining. This is a limited pattern of numerical alignment, not proof that the measures represent the same construct or have the same clinical direction. The outcomes are on different scales, and the registry does not state the sign convention for either change score.

The OSDI result can add context because it addresses a measure distinct from ocular surface staining. However, it should not be treated as a replication of the primary endpoint: it is a separate outcome, and only one secondary endpoint is posted in the record. The registry’s outcome count is three, while one secondary endpoint is listed in the posted results; the other outcome details are not reported in the registry record.

Secondary results generally carry less weight when the analysis plan and multiplicity strategy are unavailable. If researchers examine several outcomes, the chance of obtaining a statistically striking result can increase unless the analysis accounts for multiple comparisons or distinguishes confirmatory from exploratory outcomes. The registry does not report a multiplicity adjustment, a hierarchy for outcome testing, or a prespecified secondary-outcome analysis plan. The posted secondary finding therefore contributes descriptive evidence, but its inferential status is uncertain.

The secondary result should be interpreted alongside, not substituted for, the primary result. It does not resolve the primary endpoint’s missing change-score direction convention, and it does not establish whether the measured differences are clinically important. Nor can a single secondary measure establish the broader effects or safety profile of the intervention. The main value of the secondary result is that it shows what the record reports for another outcome at the stated follow-up; its limitations should remain visible in any overall interpretation.

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

• Change From Baseline in Ocular Surface Disease Index (OSDI)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is a continuous measure summarized as a mean and standard deviation. A mean gives the average score or average change among the participants included in the calculation. A standard deviation describes the spread of participant values around that average. It is not the same as a confidence interval: the standard deviation describes variability among observations, while a confidence interval describes uncertainty in an estimated quantity such as a group mean or mean difference.

The registry reports means and standard deviations for both arms, then gives a mean difference for PRP relative to standard care. The primary mean difference is -1.2. The negative sign reflects the order of subtraction used in the posted contrast: the PRP mean is compared with the standard-care mean. The sign itself does not indicate whether the result is clinically favorable, since the direction convention for the change-from-baseline measure is not stated.

A difference in means is an absolute contrast on the outcome’s scale. It is distinct from a standardized effect size, which expresses a contrast relative to variability. Standardized effects can help describe the size of a contrast in relation to the observed spread, but they do not convey the outcome’s clinical importance by themselves. The registry reports a standardized effect for the primary comparison, but a large standardized contrast in a small dataset can be sensitive to the observed means and standard deviations. It should not be treated as a guarantee that a similar contrast would recur.

The registry also posts a confidence interval around the primary mean difference. In general, a confidence interval describes values compatible with the observed data under the analysis assumptions and method. A narrower interval indicates greater statistical precision for the estimated contrast, while a wider one indicates more uncertainty. The interval does not capture all possible biases, such as measurement differences or missing outcomes, and it does not say that a fixed proportion of individual participants experienced results inside the interval.

The registry posts p < 0.001 for the primary and secondary comparisons. In general, a p-value is calculated under a null hypothesis, often that there is no group difference, and measures how compatible the data are with that hypothesis under a specified statistical model. It is not the probability that the observed result arose “by chance,” nor a measure of effect size. The statistical test and exact model used for these p-values are not reported in the registry record. The p-value therefore cannot identify the analysis choices or assumptions behind the calculation.

Why does the mean difference need context?

The outcome scale supplies the context for interpreting an absolute difference. For ocular surface staining, lower scale values correspond to less surface damage as described by the registry, but the endpoint is a change from baseline and the sign convention for that change is absent. The group means can be compared as posted, yet the clinical meaning of their signs remains unclear. The registry also does not state what magnitude of change would be important to patients or clinicians. Statistical evidence for a difference and evidence that a difference matters clinically are not the same.

For OSDI, the registry posts a different scale and a different mean difference. The record does not give the scale range or explain the direction of its change score in the results description. It is therefore safest to keep its estimate separate from the staining measure rather than compare their numerical sizes directly. Scales with different units and ranges cannot be interpreted as though a one-unit change had the same meaning across outcomes.

What does randomization contribute?

Randomization is intended to reduce systematic differences between groups at assignment. It supports a causal comparison when allocation is implemented as intended and follow-up and analysis preserve that comparison. The registry labels the study randomized, but does not report the sequence-generation or concealment methods. It also does not post baseline characteristics. The label alone cannot show whether the groups were balanced on factors that might affect the outcomes.

No masking is recorded. Masking can reduce the influence of expectations on treatment delivery, participant reporting, and assessment. Its relevance depends on the outcome and study procedures. The registry does not state whether outcome assessors were masked, so the degree to which assessment could have been influenced cannot be determined. This is particularly relevant for an outcome involving grading against charts, where assessor procedures matter.

The posted summaries do not describe participant-level distributions, baseline adjustment, or covariate adjustment. The registry does not report whether an intention-to-treat analysis or another analysis population was used. These omissions limit assessment of how the analysis handled randomization and follow-up. They also prevent reconstructing the exact model from the summary statistics alone.

How should variability be read?

Standard deviations summarize observed variation, but their interpretation depends on the scale and the sample. They do not show whether all participants had similar changes, whether a few observations were extreme, or whether the distribution was skewed. Participant-level data or a fuller distribution would be needed to assess those features. A mean can be sensitive to unusually high or low observations, and the small arm sizes make the individual observations consequential.

Over-dispersion is a general concern when the observed variability is greater than a model assumes. In count outcomes, for example, such a mismatch can make standard errors too small and intervals too narrow if not addressed. The posted primary and secondary outcomes are continuous measures, and the registry does not describe a model that would allow assessment of this issue. The general lesson is that uncertainty estimates depend on whether the analysis assumptions fit the data; the record does not provide enough methodological detail to evaluate all such assumptions.

What is not established by the record?

The original statistical analysis plan, test choice, missing-data method, analysis population, and multiplicity strategy are not reported in the registry record. The trial’s own sample-size justification is also not reported. The separate planning illustration is based on the observed effects and should not be mistaken for the rationale used to enroll participants. These gaps do not erase the posted numerical results, but they constrain how fully those results can be audited or interpreted.

General statistical principles help explain what the estimates mean, but they cannot fill in unreported design decisions. In particular, one cannot infer from a p-value which test was used, from a completed-study status that all enrolled participants were analyzed, or from a narrow confidence interval that all relevant sources of uncertainty have been addressed. Interpretation should stay close to the registered outcomes, posted summaries, and the limitations of the record.

11. Confidence Intervals and Precision

The primary mean difference is -1.2, with a 95% confidence interval from -1.329 to -1.071. This interval is centered around the posted estimate and is relatively narrow on the reported scale. Under the method and assumptions used for the calculation, it describes a range of plausible values for the group mean contrast. The interval does not show the range of changes among individual participants, and it does not account for unreported sources of uncertainty such as outcome-assessment procedures or missing data.

The interval does not include zero, and the posted p-value is p < 0.001. These are related summaries of evidence against a no-difference hypothesis under the underlying analysis, though the precise test is not reported in the registry record. Neither statistic establishes the clinical importance of the contrast. The missing sign convention for change from baseline also limits interpretation of which direction the numerical difference represents in clinical terms.

Precision is not the same as reliability. A confidence interval can be narrow because the observed standard deviations are small relative to the contrast, while other features of the study still create uncertainty. The enrollment is 30, and the registry does not report the participant-level data, baseline values, missing-data approach, or analysis population. Those omissions make it harder to assess how robust the interval is to analytic choices or departures from assumptions.

The interval pertains to the mean difference in the enrolled trial population as analyzed, not to every person with severe dry eye or to a future treatment setting. Generalizability depends on participant characteristics, eligibility, and implementation details that are not fully reported. Thus, the interval gives a precise statistical summary of the posted contrast, while leaving important questions about clinical meaning and transportability unresolved.

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 events. They are illustrative calculations based on the observed effect, not the trial’s original design justification. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. The trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column indicates the number of participants per arm estimated to give an 80% chance of detecting the assumed effect under those planning assumptions, if that effect and the model assumptions held. The 90% power column uses a higher target probability of detection, also under the stated assumptions. These are planning illustrations, not a guarantee of what a future study will achieve. This is not observed power.

The rows consider planning for the full observed effect and for smaller fractions of that effect. The smaller the effect that a study is intended to detect, the more participants are generally needed, because a smaller group contrast is harder to distinguish from sampling variability. In these calculations, the displayed participant counts are unusually small, reflecting the very large observed contrast relative to the reported variability. Such estimates can be unstable when they are derived from a small trial, and should not be treated as a reliable recommendation for a new study without independent design assumptions and clinical justification.

The figures are not evidence that the completed trial was adequately powered according to its original plan. Nor do they show the probability that the reported finding is true. They describe a hypothetical design calculation under the stated assumptions and observed effect fractions. The original enrollment rationale, target effect, and planned power are not reported in the registry record.

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 = -1.200; pooled standard deviation σ = 0.180.
2. n = 2 × (1.96 + 0.842)² × 0.180² / -1.200² = 0.4, rounded up to 1 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 <- -1.2                      # observed difference in means
sigma <- 0.18                     # 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(2257957)
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 (80% power), 1 (90% power)
 75% of observed effect: n per arm = 1 (80% power), 1 (90% power)
 50% of observed effect: n per arm = 2 (80% power), 2 (90% power)
power.t.test: 1.9 
Simulated power at n = 1 per arm: NA (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 multiplicity strategy. It does not state whether the primary outcome was the only confirmatory test, whether secondary outcomes were exploratory, whether a testing hierarchy was planned, or whether any adjustment was made for multiple comparisons. Without that information, the posted p-values should not be interpreted as though the full family of outcome tests and decision rules were known.

Multiplicity is a general concern when several hypotheses are evaluated. If each is tested separately, the chance of at least one apparently notable result can increase. Adjustments or prespecified testing plans can address this issue, but their use and details are not reported in the registry record. There is one secondary endpoint listed in the posted results; the record also gives an overall outcome-measure count of three, and the remaining outcome details are not reported in the registry record.

Missing-data methods are also not reported. The registry does not state whether all randomized participants contributed to each endpoint, how incomplete follow-up was handled, or whether any values were imputed. The arm summaries list 15 participants per group, but those counts alone do not establish that every enrolled participant had an outcome measurement or was included in the analysis. Participant flow and reasons for missing measurements are not reported in the registry record.

The analysis population is not reported. It is therefore unclear whether results were analyzed according to original assignment, among participants who completed treatment, or using another population. The registry also does not describe baseline adjustment or other covariate handling. Those choices can affect the estimate and its uncertainty, especially in a small randomized study.

Interim analyses and stopping rules are not reported in the registry record. The original statistical analysis plan, including planned outcome definitions and analysis methods, is also not reported. These omissions do not demonstrate that the procedures were inadequate; they mean that readers cannot evaluate them from the record. In combination, the missing details limit assessment of selective outcome reporting, analysis flexibility, and the robustness of the posted inference.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry lists 15 participants at risk in each arm. It records zero serious adverse events in the PRP arm and zero in the standard-care arm. It also records zero other adverse events in each arm. These are event counts as entered in the registry record, not proof that no event could occur or that every possible event was captured.

The record does not list any serious adverse-event terms. Death counts are not reported in the registry record. The safety entries should therefore be read narrowly: the posted record contains no reported serious or other adverse events for the participants at risk in either arm, while the death information is unavailable.

Safety interpretation depends on how events were defined, actively collected, checked, and followed over time. The registry does not report those procedures or give further detail about the duration of safety follow-up beyond the study’s overall schedule. With 15 participants at risk per arm, the record also offers limited information about uncommon events. The absence of posted events is a description of this trial’s record, not a general estimate of risk.

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

The primary results describe a difference between the two randomized groups in their recorded mean change in ocular surface staining at 90 days. The posted contrast is -1.2, with a confidence interval that excludes zero. The registry also reports a numerical difference for the secondary OSDI outcome. These findings show that the posted group summaries differ, but the numerical sign of a change score does not by itself convey whether the score moved in a clinically favorable direction.

The trial does not establish from the registry record how large a change would be meaningful to participants, or how the measured differences relate to daily symptoms or function. The staining scale grades surface damage, while OSDI is a distinct outcome. Their estimates should not be combined or treated as interchangeable. The record’s brief summary refers to lacrimal production and safety, but the listed primary outcome is staining and the posted secondary outcome is OSDI; these results do not answer every aspect of the study’s stated purpose.

The randomized design is useful for comparing the assigned groups, but interpretation remains constrained by the small enrollment and missing methodological details. The registry does not report baseline values, participant flow, the analysis population, missing-data handling, or assessor masking procedures. It also does not explain the statistical test or the original sample-size justification. These gaps make it difficult to determine how sensitive the estimates are to study conduct or analytic choices.

The posted results should not be read as a guarantee that the same estimates would occur in a larger or different population. Participant characteristics beyond the diagnosis of severe dry eye are not reported in the registry record, and the number with Sjogren Syndrome is not stated. Follow-up beyond the scheduled 90-day endpoint is not described in the outcomes posted here, so longer-term results cannot be inferred.

Likewise, the adverse-event entries do not establish that treatment is free of risk. They report no serious or other adverse events in either group, while deaths are not reported in the registry record. The available safety information is limited to those entries and the recorded participants at risk. Overall, the data support a precise description of the posted numerical contrasts, while leaving clinical direction, importance, broader applicability, and completeness of safety reporting uncertain.

17. Why This Trial Matters Statistically

This trial illustrates why a small study can produce a statistically precise-looking contrast without resolving every question relevant to interpretation. The primary confidence interval is narrow and the posted p-value is small, but those summaries answer a limited statistical question about the group mean difference under the calculation’s assumptions. They do not address whether the direction of change is favorable, whether the magnitude matters clinically, or whether bias and missing information altered the estimate.

It also shows the value of separating outcome measurement from outcome meaning. Ocular surface staining grades visible surface damage, while OSDI is a different measure. A mean difference on one scale cannot be translated directly into a difference on another scale. When a registry reports change from baseline without a stated sign convention, even the direction of movement can be ambiguous. Clear outcome definitions and change-score conventions are essential for readers to interpret results correctly.

Randomization is an important design feature, but transparency about implementation and analysis remains necessary. The record identifies the trial as randomized and unmasked, yet does not report the allocation method, baseline characteristics, analysis population, missing-data strategy, or statistical test. These details help determine what the estimate represents and how much confidence to place in its interpretation.

Finally, the planning illustration emphasizes a common statistical caution: calculations based on an observed effect can suggest very small future sample sizes when the observed contrast is large relative to variability. Such illustrations are not a substitute for a prospective design rationale. The registry’s original sample-size justification is not reported. The distinction between planning calculations and the completed trial’s actual design is central to responsible interpretation.

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 small enrollment is an important limitation for assessing the stability and generalizability of the results. With 15 participants in each arm, individual observations can have substantial influence on group summaries. The registry does not provide participant-level distributions, so readers cannot assess whether the means represent broadly similar responses or are strongly affected by a few values.

The population is described as people with severe dry eye, and the registry lists Sjogren Syndrome as a condition, but eligibility criteria, demographic characteristics, disease duration, and the number of participants with Sjogren Syndrome are not reported. This limits assessment of how representative the enrolled group may be and which subgroups the findings might describe.

The primary endpoint is a change-from-baseline measure, but baseline values and the sign convention for change are not reported. The scale description explains that lower staining grades correspond to less surface damage, yet does not resolve the direction of the posted change scores. The registry also does not report a threshold for clinical importance. These gaps prevent a complete clinical interpretation of the estimate.

The study is listed as having no masking. The record does not say whether assessors were masked, how staining was scored, or what steps were taken to ensure consistent assessment. It also does not describe PRP preparation, dose, adherence, or other co-interventions. These procedural details could matter when judging reproducibility and the possibility of measurement or implementation differences.

Finally, participant flow, missing-data handling, analysis populations, the original statistical plan, multiplicity handling, and the trial’s sample-size justification are not reported in the registry record. The safety record lists no events but provides limited information about collection procedures and follow-up. These are limitations of what can be evaluated from the registry record, rather than evidence that a particular procedure was or was not performed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Platelet -Rich Plasma (PRP) Injection for the Treatment of Severe Dry Eye — NCT02257957.
• Registry record last updated 2021-08-24; status last verified 2021-07.
• Results first posted 2021-08-24.
• 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, parallel-group Phase 3 trial with no masking and an enrollment of 30. It compares PRP injection with standard care described as hyaluronic acid eye drops. The arm descriptions schedule PRP injections and standard-care reviews at day 0, 30, 60, and 90.

The primary outcome is change from baseline in ocular surface staining at 90 days. The record posts a mean difference of -1.2, with a 95% confidence interval from -1.329 to -1.071 and p < 0.001. One secondary outcome, change from baseline in OSDI, is posted. The registry also records zero serious and zero other adverse events in each arm among 15 participants at risk per arm; deaths are not reported in the registry record.

The record does not report the sign convention for change scores, baseline results, analysis population, missing-data method, multiplicity plan, or original sample-size justification. Those omissions limit interpretation of clinical direction, importance, and analytic robustness.