Lowering Events in Non-proliferative Retinopathy in Scotland: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Lowering Events in Non-proliferative Retinopathy in Scotland (NCT03439345), a randomized phase 4 study. The primary outcome is Number of Participants With Progression to Referable Diabetic Retinopathy or Maculopathy, or Treatment.

2. Clinical Question

This is a question about a composite clinical endpoint and the timing of its first occurrence. The composite combined a grading-defined change in retinopathy or maculopathy with treatment events, including retinal laser therapy, vitrectomy, or intravitreal injection of medication. It therefore captures more than a single type of eye disease progression. The registry specifies an intention-to-treat comparison of allocation groups, so the primary contrast concerns assignment to fenofibrate versus assignment to placebo, rather than only participants who adhered to treatment.

The posted primary analysis reports a hazard ratio of 0.73, with a 95% confidence interval from 0.58 to 0.91 and p = 0.006. These statistics describe the relative timing of the first composite event under the analysis reported in the registry; they do not by themselves establish how any individual participant would fare, or how much of the result was associated with each component. The components and the time-to-first framework are important for interpreting the primary finding.

3. Trial Design

LENS was a phase 4, randomized, quadruple-masked, parallel-group trial sponsored by the University of Oxford. The registry reports enrollment of 1151 participants and completed status. The recorded start date is 2018-07-23, and the primary completion date is 2023-11-17. The brief description characterizes the study as a streamlined, multicentre, randomized, placebo-controlled investigation of fenofibrate for progression of diabetic retinopathy or maculopathy.

Participants were assigned to fenofibrate 145 mg or a placebo oral tablet. Both were described as tablets taken daily with normal renal function and every second day with chronic kidney disease. The placebo dosage is not applicable. The registry identifies the design as parallel-group, meaning the treatment allocation groups were followed as separate groups rather than participants crossing between treatments. The stated masking level is quadruple; the registry record does not identify the specific roles covered by that masking label.

The primary endpoint was assessed over a median-like follow-up description of 4.0 years, with an interquartile range of 3.6 to 4.3 years. The registry describes the main comparison as intention-to-treat and focused on time to first occurrence during the scheduled treatment period. There were 576 participants in the fenofibrate group and 575 in the placebo group in the posted primary outcome counts. These are the group denominators used for the event counts, not a separate claim about how many participants contributed complete follow-up at every point.

The registry lists diabetic retinopathy as the condition, and identifies additional outcomes relating to retinopathy grading, maculopathy, visual acuity, visual function, and quality of life. Detailed eligibility criteria, the original sample-size justification, allocation-concealment procedures, the precise masking arrangements, and other protocol details are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention-to-treat comparisons among all randomised participants of the effects of allocation to fenofibrate versus placebo during the scheduled treatment period on time to the first occurrence.

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 Number of Participants With Progression to Referable Diabetic Retinopathy or Maculopathy, or Treatment, measured over 4.0 years (interquartile range, 3.6 to 4.3) years.

The primary endpoint counted participants with progression to referable diabetic retinopathy or maculopathy, or with treatment for diabetic retinopathy or maculopathy. The registry defines referable disease using NHS Scotland grading criteria. The listed criteria include R3 referable background diabetic retinopathy, R4 proliferative diabetic retinopathy, and M2 referable maculopathy. Examples in the definition include specified hemorrhages, venous beading, intraretinal microvascular abnormalities, active new vessels, vitreous hemorrhage, and blot hemorrhages or hard exudates within a radius of ≤1 optic disc diameter of the centre of the fovea.

Treatment also counted as an event. The record names retinal laser therapy, vitrectomy, and intravitreal injection of medication. Adverse event reports of eye procedures, vitreous hemorrhages, and macular oedema were adjudicated by experienced doctors at the Central Co-ordinating Office, masked to treatment allocation.

A composite endpoint can capture several clinically relevant routes to an event, which may make it more informative than a single narrow outcome. Its interpretation depends on the definitions and frequency of its components: the same composite result can reflect different patterns among its component events. The registry also reports the analysis as time to the first event, so later events after a participant’s initial qualifying event do not add further time-to-first events. Component counts are posted separately, but the registry record does not report a detailed breakdown of time-to-first events by component in the primary analysis.

7. Results Posted in the Registry

• Fenofibrate 145 mg: 22.7% (131/576) versus 29.2% (168/575) on control; risk difference -6.5 percentage points (95% CI -11.5 to -1.4), risk ratio 0.78 (0.64–0.95); unadjusted two-proportion z-test p = 0.012.

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.

Number of Participants With the Individual Component of the Composite Primary Outcome: Development of Referable Diabetic Retinopathy or Maculopathy

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fenofibrate 145 mg: 22.6% (130/576) versus 29.2% (168/575) on control; risk difference -6.6 percentage points (95% CI -11.7 to -1.6), risk ratio 0.77 (0.63–0.94); unadjusted two-proportion z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Fenofibrate 145 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With the Individual Component of Composite Primary Outcome: Treatment for Diabetic Retinopathy or Maculopathy

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fenofibrate 145 mg: 3.0% (17/576) versus 4.9% (28/575) on control; risk difference -1.9 percentage points (95% CI -4.2 to 0.3), risk ratio 0.61 (0.34–1.09); unadjusted two-proportion z-test p = 0.093.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fenofibrate 145 mg and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Any Progression of Diabetic Retinopathy or Maculopathy Across the NHS Scotland Retinopathy Grading Scale

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fenofibrate 145 mg: 32.1% (185/576) versus 40.2% (231/575) on control; risk difference -8.1 percentage points (95% CI -13.6 to -2.5), risk ratio 0.80 (0.68–0.93); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Fenofibrate 145 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes provide additional perspectives on retinopathy and maculopathy progression, the individual elements of the primary composite, and broader visual or quality-of-life measures. Among the posted event-based comparisons, the direction of the estimates generally aligns with the primary composite for progression outcomes. The results are not uniform in precision: outcomes with fewer events have wider uncertainty, and the treatment component is less clearly estimated than the composite progression result.

Secondary endpoints help show whether the primary finding is accompanied by a coherent pattern across related measures, but they do not replace the primary analysis. They differ in definition, event frequency, and statistical precision. Some measure a component already included in the composite; others measure progression across a grading scale or distinct aspects of visual function and quality of life. Similar directions across related endpoints can be informative, but overlap between outcomes means they are not independent replications.

The registry lists 24 secondary results as posted, while its record lists 28 outcome measures and 28 analyses. Not every secondary outcome necessarily has the same type of estimate or the same amount of information. The record identifies several secondary outcomes, including visual acuity, visual function based on the National Eye Institute Visual Functioning Questionnaire 25, and quality of life based on the EQ-5D Index Score, but detailed result values for those outcomes are not included in the registry record used for this analysis.

Unadjusted secondary results carry less weight because multiple outcomes create multiple opportunities for chance findings. The registry does not report a multiplicity adjustment, a formal testing hierarchy, or a distinction between confirmatory and exploratory secondary analyses. Secondary p-values should therefore be treated as descriptive evidence and interpreted with their estimates and intervals, rather than as a series of independent definitive conclusions. The broad pattern can complement the primary finding, but it does not establish that every secondary domain changed or changed to a similar extent.

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

• Number of Participants With the Individual Component of the Composite Primary Outcome: Development of Referable Diabetic Retinopathy or Maculopathy
• Number of Participants With the Individual Component of Composite Primary Outcome: Treatment for Diabetic Retinopathy or Maculopathy
• Number of Participants With Any Progression of Diabetic Retinopathy or Maculopathy Across the NHS Scotland Retinopathy Grading Scale
• Number of Participants With Referable Maculopathy (Exudates or Blot Haemorrhages Within One Disc Diameter of the Fovea)
• Number of Participants With The Development of Macular Oedema
• Visual Acuity
• Visual Function, Based on the National Eye Institute Visual Functioning Questionnaire 25 (VFQ-25).
• Quality of Life, Based on the EQ-5D Index Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint has two statistical features: it is binary at the participant level, because each participant either experiences a qualifying event or does not within the specified follow-up, and it is analyzed as a time-to-event outcome in the reported Cox model. The posted counts provide a simple event-proportion comparison. The Cox analysis incorporates the timing of the first event and the time participants remain under observation, subject to the model and censoring assumptions. These approaches use the same clinical endpoint but summarize it differently.

What does the risk difference describe?

The risk difference is the observed event proportion in the fenofibrate group minus the observed event proportion in the placebo group. In the recalculated primary comparison, the estimate is -0.065. A negative value means the observed proportion was lower in the fenofibrate allocation group in this unadjusted calculation. The confidence interval from -0.115 to -0.014 describes the uncertainty around that difference under the calculation used. It is an absolute contrast on the risk scale, not a relative measure and not an adjusted estimate.

The unadjusted p-value of 0.012 addresses how compatible the observed group difference is with a null comparison under the assumptions of the test. A p-value is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The p-value is also not a substitute for considering the confidence interval and endpoint definition.

What does the hazard ratio describe?

The registry reports a Cox regression analysis with a hazard ratio of 0.73 and a 95% confidence interval from 0.58 to 0.91. A hazard ratio compares the instantaneous event rates between groups among participants who have not yet experienced the event and remain under observation. It uses event timing, unlike a simple comparison of the final counts. A hazard ratio is not an absolute risk difference and should not be translated directly into a difference in the proportion of participants with an event.

Cox regression generally relies on assumptions about how the relative hazard behaves over follow-up and how censoring relates to event risk. The registry record does not report diagnostic checks for those assumptions, details of censoring, or any covariate adjustment in the reported analysis. The analysis method is described as regression and Cox, but more detailed modeling specifications are not reported in the registry record.

Why are the recalculated and reported results distinct?

The recalculated risk difference uses only the posted counts and denominators, making it a simple, unadjusted comparison. The registry’s reported Cox model is the trial analysis and incorporates time-to-event information. The two estimates can differ because they use different information and statistical scales. The discrepancy flag is false, so the stated summaries do not indicate a conflict requiring the recalculation to override the trial’s own reported analysis. For interpretation of the trial’s primary analysis, the registry’s Cox result takes precedence; the unadjusted calculation is a supplementary way to understand the posted counts.

Why does over-dispersion matter in general?

Over-dispersion is a general concern when observed variability exceeds what a statistical model assumes. It can make standard errors too small and intervals too narrow if the model does not account for the extra variability. The primary outcome is a participant-level event and the reported primary analysis is a Cox model; the registry does not report an over-dispersion assessment. This general concept should not be taken as evidence that over-dispersion occurred in this trial.

How should secondary p-values be read?

The registry reports separate analyses for outcomes such as the individual components and any progression across the grading scale. Each comparison is an additional statistical question. When many outcomes are examined, some apparently notable results can arise by chance even if no underlying difference exists for those outcomes. A multiplicity adjustment or a hierarchy controlling how results are tested is not reported in the registry record. Therefore, unadjusted secondary p-values should be interpreted cautiously and alongside effect estimates, confidence intervals, endpoint definitions, and the primary analysis.

The primary comparison is described as intention-to-treat, which means participants are analyzed according to their randomized allocation for the stated comparison. This preserves the randomized groups as the basis for estimating the effect of assignment. The registry record does not report detailed analysis populations for every secondary outcome, nor does it describe how missing outcome data were handled. Such details matter because exclusions or missingness can alter the composition of the analyzed groups and the precision of the estimates.

11. Confidence Intervals and Precision

The reported primary hazard ratio is 0.73, with a 95% confidence interval from 0.58 to 0.91. The interval expresses the precision of the estimated relative event rate under the reported Cox analysis and its assumptions. It does not mean that there is a 95% probability that the true value lies within this particular interval. Rather, a confidence interval procedure is designed so that, under repeated use of the same method and assumptions, intervals constructed in this way cover the fixed underlying parameter at the stated frequency.

The unadjusted risk-difference estimate is -0.065, with a 95% confidence interval from -0.115 to -0.014. Because the interval is expressed on the absolute-risk scale, it gives a different view from the hazard ratio. Its endpoints indicate a range of values compatible with the posted counts and calculation, subject to sampling uncertainty and the method used. The two intervals should not be compared as if they shared a scale.

For the separate treatment component, the recalculated risk difference is -0.019, with a 95% confidence interval from -0.042 to 0.003. The interval includes zero, indicating that the posted data do not pin down the direction of the absolute difference for that component with the same precision as the primary composite. This is consistent with the smaller number of treatment events, but the registry does not report a formal comparison of precision between components.

Confidence intervals do not capture every source of uncertainty. They do not account automatically for uncertainty about endpoint selection, missing data, model fit, or multiplicity. They also do not establish whether an estimated difference is important in practice. The registry record does not report a minimally important difference against which to judge the estimates. Precision is therefore best understood together with the study design, endpoint definition, reported model, and limitations of the record.

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 illustrations translate an observed effect into hypothetical sample-size requirements under stated statistical assumptions. For the binary outcomes in this analysis, the figures are participants per arm, not total events. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column gives the corresponding number for a higher chance of detection. These are planning targets rather than guarantees; actual results also depend on the event pattern, follow-up, and assumptions used in the calculation.

The rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect illustrate how the target effect size changes the required sample. Smaller effects need more participants to distinguish them from random variation at the same significance level and power target. The calculations use the observed effect as a reference point, which is not necessarily the effect that would be expected in a future study. In general, estimates from completed trials have sampling uncertainty, so planning around an observed effect should be treated cautiously.

For time-to-event planning calculations, the stated method uses the total number of events, whereas the other planning figures give participants per arm. The primary outcome figures discussed for this trial are participant counts per arm. This is not observed power: observed power is not a useful substitute for reading the estimated effect and its confidence interval. These illustrations describe hypothetical design requirements under stated assumptions, not the power achieved by the completed trial.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.292; treatment proportion p₁ = 0.227; average p̄ = 0.260.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6202 = 1.2155.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6185 = 0.5205.
4. n = (1.2155 + 0.5205)² / (-0.0647)² = 719.0, rounded up to 719 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.292173913043478                          # control proportion
p1 <- 0.227430555555556                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3439345)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 719 (80% power), 963 (90% power)
 75% of observed effect: n per arm = 1,305 (80% power), 1,746 (90% power)
 50% of observed effect: n per arm = 2,993 (80% power), 4,006 (90% power)
power.prop.test: 719 
Simulated power at n = 719 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s own primary analysis is a Cox regression result: hazard ratio 0.73, 95% confidence interval from 0.58 to 0.91, and p = 0.006. It uses time-to-first-event information and is the trial’s reported analysis for the primary endpoint. The simple recalculation from the posted counts gives a risk difference of -0.065, with a 95% confidence interval from -0.115 to -0.014 and an unadjusted p-value of 0.012.

These estimates are not competing versions of the same statistic. The recalculation is an unadjusted comparison of event proportions; the reported Cox model compares event rates over time. Their different scales and use of information mean that exact numerical agreement is not expected. Both point in the same direction in the primary comparison, but the reported Cox analysis is the appropriate result to cite as the trial’s own analysis.

The registry marks no discrepancy between the recalculated and reported results. The recalculation is therefore best read as a transparent check based on the available counts, not as a replacement for the trial analysis. The record does not report enough model detail to reconstruct the Cox analysis independently or assess all its assumptions. The sponsor’s own analysis takes precedence when describing the trial’s primary result.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the trial adjusted for multiple comparisons, used a prespecified hierarchy for testing outcomes, or classified particular secondary analyses as confirmatory or exploratory. This matters because the record includes numerous outcome measures and analyses. When many hypotheses are tested, the chance of obtaining one or more small p-values by chance can increase. Without a reported multiplicity strategy, secondary p-values should not be interpreted as if each were the sole primary test.

The primary outcome and its intention-to-treat population are described. The record states that all randomized participants were compared according to allocation for the effect of assignment during the scheduled treatment period. This is useful information about the main analysis population. However, detailed analysis-population definitions for every outcome are not reported in the registry record. The number of participants with posted primary outcome counts is given by group, but the record does not provide a complete participant-flow account.

Missing-data methods are not reported in the registry record. It does not specify how missing endpoint assessments were handled, whether any imputation was used, or how incomplete follow-up affected the analyses. The record also does not report detailed censoring rules for the time-to-event analysis. These omissions limit assessment of whether the analyzed observations represent the randomized groups throughout follow-up and whether loss to follow-up could have affected the estimates.

Other statistical details are also not reported in the registry record, including the original sample-size justification, interim analyses, the full statistical analysis plan, model diagnostics, and the handling of deviations from assigned treatment. Their absence from the registry information does not establish that these procedures were absent from the trial; it means their use cannot be assessed from this record. Readers should distinguish what is explicitly described—the randomized design, the stated primary intention-to-treat comparison, and the posted analyses—from methodological details that remain undocumented in the registry record.

16. 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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: surgical and medical procedures (9.0%), infections and infestations (8.7%), cardiac disorders (6.4%), nervous system disorders (5.7%), neoplasms benign, malignant and unspecified (incl cysts and polyps) (5.0%).

The registry lists 208 participants affected by serious adverse events among 576 at risk in the fenofibrate group, and 204 among 575 at risk in the placebo group. It lists 17 participants affected by other adverse events among 576 at risk in the fenofibrate group and 21 among 575 at risk in the placebo group. Deaths are listed as 35 and 38, respectively. These are the posted counts; they should not be converted into comparative conclusions without considering event definitions, follow-up, and the trial’s safety analysis.

The record also lists serious adverse-event categories with percentages, including surgical and medical procedures, infections and infestations, cardiac disorders, nervous system disorders, neoplasms, and injury, poisoning and procedural complications. The denominator and detailed method for those category percentages are not reported in the registry record. Categories may describe types of reported events and should not be read as a complete account of all clinical circumstances.

Counts of affected participants are not sufficient to establish whether groups differ in safety. The registry information does not provide a detailed adjudication framework for all adverse events, exposure-adjusted comparisons, or a statistical analysis of the safety outcomes. The figures describe what was posted, not a clinical recommendation or a complete benefit-risk assessment.

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

The primary result describes a randomized comparison of allocation to fenofibrate versus placebo for time until the first qualifying retinopathy or maculopathy progression event, or treatment for those conditions. The reported Cox estimate and the unadjusted comparison of the posted counts both favor a lower event occurrence in the fenofibrate allocation group in this trial. The reported result is specific to the composite endpoint, the trial population, the follow-up period, and the analyses recorded.

It does not mean that every participant allocated to fenofibrate avoided progression, nor that every component of the composite had the same pattern. It does not provide an individual prediction. A group-level hazard ratio does not directly tell an individual’s absolute chance of an event, and the primary composite combines grading-defined disease changes with treatment events. The separate component results show why the composite should not be interpreted as a single uniform clinical event.

The confidence intervals describe statistical uncertainty under the relevant methods, but they do not resolve uncertainties about missing data, model assumptions, multiplicity, or the practical importance of the estimated effects. The registry record does not report the original sample-size justification, missing-data handling, full statistical plan, or several other details needed for a complete methodological appraisal.

The finding should not be generalized automatically to people who differ from the trial participants or to settings not described in the record. Detailed eligibility and demographic information are not reported in the registry information. Nor do the statistics alone provide a basis for treatment decisions. Such decisions require clinical context and a complete assessment of evidence, which is beyond what the posted registry results establish.

18. Why This Trial Matters Statistically

This trial is statistically informative because it pairs a randomized, masked, placebo-controlled design with a defined time-to-first primary endpoint. Random allocation supports a comparison of groups that is less vulnerable to confounding than an observational comparison, while masking can reduce some forms of measurement and behavior bias. The registry’s intention-to-treat description also clarifies that the primary comparison is based on assignment rather than adherence alone.

The endpoint combines referable retinopathy or maculopathy with treatment events. That construction can capture more than one route to a clinically relevant outcome, but it also makes component interpretation essential. The posted component information illustrates why a composite result should be considered alongside the individual event types and their precision. Statistical significance for a composite does not automatically imply equally clear evidence for every component.

The record also demonstrates the value of distinguishing a time-to-event estimate from a simple event-count comparison. The Cox hazard ratio incorporates timing, while the recalculated risk difference gives an absolute-scale summary based on the posted counts. Reading both can help clarify the statistical question each estimate answers, without treating one as a replacement for the other.

Finally, the registry record shows why completeness of statistical reporting matters. The trial’s primary analysis and major design features are stated, but details about multiplicity, missing data, model assumptions, and the original sample-size justification are not reported. Those gaps do not invalidate the posted results, but they constrain how fully readers can assess robustness and generalizability. The distinction between reported evidence and unreported methods is central to careful clinical-trial interpretation.

19. 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 provides a concise account rather than the full protocol and statistical analysis plan. Detailed eligibility criteria, participant characteristics, the original sample-size justification, interim analyses, and the full set of modeling specifications are not reported in the registry record. As a result, it is not possible from these registry entries alone to evaluate the representativeness of the enrolled population, the rationale for the target sample, or every prespecified analysis decision.

The main result is a composite endpoint. Although the registry defines its components and posts several component outcomes, a composite can conceal differences in frequency, importance, or pattern among its elements. The primary analysis is time to the first event, so it does not summarize recurrent events after the first qualifying event. Further detail about the distribution and timing of each component is not reported in the registry record.

Information on missing data, loss to follow-up, censoring, adherence, treatment discontinuation, and crossovers is not reported in the registry record. These details could affect interpretation of a time-to-event comparison and the meaning of an intention-to-treat estimate. The record also does not report model diagnostics or proportional-hazards checks for the Cox analysis.

Multiple outcomes were assessed, but the registry does not report multiplicity control or a formal hierarchy for secondary tests. Several posted secondary comparisons are therefore less secure as confirmatory evidence than the primary analysis. The planning illustrations are based on observed effects and stated generic assumptions, not the original trial design justification. Finally, the adverse-event figures lack some context needed for comparative safety assessment, including detailed definitions and analysis methods. These limitations define what can be concluded from the registry record, rather than establishing that the unreported procedures were not performed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Lowering Events in Non-proliferative Retinopathy in Scotland — NCT03439345.
• Registry record last updated 2025-05-14; status last verified 2025-01.
• Results first posted 2025-05-14.
• 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.

23. Record Summary

The record describes LENS, a completed phase 4 randomized, quadruple-masked, parallel-group, placebo-controlled trial sponsored by the University of Oxford. Enrollment was 1151 participants. The intervention was fenofibrate 145 mg, compared with a placebo oral tablet, for participants with diabetic retinopathy.

The primary endpoint was time to first referable diabetic retinopathy or maculopathy, or treatment for either condition. The reported Cox analysis gave a hazard ratio of 0.73, a 95% confidence interval from 0.58 to 0.91, and p = 0.006. The posted event counts were 131 of 576 in the fenofibrate group and 168 of 575 in the placebo group.

The record describes an intention-to-treat primary comparison and posts secondary outcomes and adverse-event counts. Details about multiplicity, missing-data handling, the original sample-size justification, and several analysis assumptions are not reported in the registry record. The results should be interpreted as endpoint- and analysis-specific evidence, with secondary findings and safety counts considered in that context.