Clinical Efficacy and Human Factors Validation Testing of the Erchonia EVRL for Providing Temporary Relief of Diabetic Peripheral Neuropathy Foot Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Efficacy and Human Factors Validation Testing of the Erchonia EVRL for Providing Temporary Relief of Diabetic Peripheral Neuropathy Foot Pain (NCT05291975), a randomized na study. The primary outcome is Number of Participants With a 30% or Greater Change in Pain Rating on the Visual Analog Scale (VAS).

2. Clinical Question

3. Trial Design

The registry identifies this as a randomized, triple-masked, parallel-group device trial comparing Erchonia EVRL with a placebo laser. The enrollment field is 64. The listed study status is completed, with a start date of 2022-02-17 and a primary completion date of 2024-10-16. Phase is recorded as NA. Erchonia Corporation is the listed sponsor.

The EVRL is described as a portable handheld device with a 635 nanometers red laser diode and a 405 nanometers violet laser diode. The placebo laser has the same appearance but emits no therapeutic light. The stated study purpose concerns prescription home use for temporary relief of diabetic neuropathy foot pain. These device descriptions and the study purpose do not establish how participants used the devices in practice; further procedural details are not reported in the registry record.

Randomized indicates that treatment assignment was allocated by chance, but the method used to generate or conceal the allocation is not reported in the registry record. Triple masking indicates that masking was planned at multiple levels, but the identities of the masked groups of people and the procedures for maintaining masking are not reported in the registry record. The parallel design means the comparison is between groups assigned to different devices; the record does not describe a crossover arrangement.

The primary outcome reports 33 participants in the EVRL group and 31 in the placebo group. Secondary outcome denominators differ by outcome: the satisfaction measure uses those same group denominators, while the later pain-change measure reports 28 and 24 participants. The reasons for the different denominators, the analysis population definitions, and the handling of missing observations are not reported in the registry record. No sponsor-reported analyses are listed.

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 Number of Participants With a 30% or Greater Change in Pain Rating on the Visual Analog Scale (VAS), measured over Baseline and 3 weeks.

The primary endpoint counts participants whose Visual Analog Scale pain rating changed by 30% or greater across the evaluation period. The record describes a decrease in pain level as positive for individual success and says a lower score at study endpoint represents a better outcome than baseline. Thus the endpoint turns each participant’s change in a continuous pain rating into a binary success or non-success outcome.

A threshold-based endpoint can make the group comparison easier to interpret as the proportion of participants meeting a stated response criterion. It also discards information about the size of each participant’s change: a participant just meeting the threshold and a participant with a much larger decrease both count as successes. Those who do not meet the threshold are grouped together, even if their changes differ. This is a general feature of dichotomizing continuous outcomes, not a separate result from this trial.

The registry lists the primary timeframe as Baseline and 3 weeks, while its outcome description refers to change through endpoint at 6 weeks. The timing is therefore not fully consistent in the record. The record defines overall study success as a 35% or greater difference between the proportions of individual successes in the groups. The posted primary comparison is expressed as a risk difference, which measures that between-group difference in proportions.

7. Results Posted in the Registry

• Erchonia® EVRL™: 72.7% (24/33) versus 29.0% (9/31) on control; risk difference 43.7 percentage points (95% CI 21.6 to 65.7), risk ratio 2.51 (1.39–4.51); unadjusted two-proportion 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.

Satisfaction With Study Outcome

• 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:
  • Erchonia® EVRL™: 60.6% (20/33) versus 25.8% (8/31) on control; risk difference 34.8 percentage points (95% CI 12.1 to 57.5), risk ratio 2.35 (1.22–4.53); unadjusted two-proportion z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Erchonia® EVRL™ than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Four Weeks Post Procedure Change in Foot Pain Visual Analog Scale (VAS) Score

• 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:
  • Erchonia® EVRL™: mean -34.32 versus -13.41 on control; difference -20.91 (95% CI -37.68 to -4.14), standardized effect d = -0.67; z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Erchonia® EVRL™ than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes point in the same broad direction as the primary comparison: the posted estimates favor the EVRL group for satisfaction and for change in foot-pain rating. That directional consistency can be considered alongside the primary finding, but the secondary outcomes measure different aspects of the experience and are not interchangeable replications of the primary endpoint.

Satisfaction is a participant count, while the later pain-rating outcome retains a continuous score change. The latter is recorded at Baseline and 7 Weeks, whereas the primary record contains a timeframe inconsistency between its listed Baseline and 3 weeks timeframe and description of an endpoint at 6 weeks. The continuous secondary measure also has fewer participants represented than the primary outcome. Differences in measurement, timing, and denominators make direct numerical comparison across endpoints inappropriate.

The registry lists an unadjusted p-value for each secondary comparison, but no sponsor-reported analyses are listed. The secondary results therefore carry less weight than the primary endpoint for confirmatory interpretation, especially because the registry record does not report a multiplicity plan. When several outcomes are examined, the chance of obtaining at least one apparently strong result by chance can increase. Adjustment procedures or a prespecified hierarchy can address this concern, but neither is described in the record.

The direction of the secondary estimates may provide supporting context, but it cannot resolve uncertainties about missing observations, analysis populations, or endpoint timing. Nor should the secondary p-values be treated as independent confirmation: outcomes measured in the same trial may be correlated, and their dependence is not reported. The overall pattern is compatible with the primary direction, while the evidential weight remains constrained by the unadjusted nature of the comparisons and the missing analysis details.

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

• Satisfaction With Study Outcome
• Four Weeks Post Procedure Change in Foot Pain Visual Analog Scale (VAS) Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either meets the stated success threshold or does not. For this kind of outcome, the arm-level result is a count of participants meeting the criterion alongside the number represented in that group. The comparison uses the difference between the two observed proportions, reported as a risk difference. A positive risk difference in the stated direction means a larger observed proportion of successes in the EVRL group than in the placebo group.

What does a risk difference express?

A risk difference is an absolute contrast between proportions. It is not a relative increase and should not be read as a ratio. For the primary endpoint, the posted risk difference is 0.437. The corresponding interval, 0.216 to 0.657, describes uncertainty around the estimated contrast. Intervals are useful because a point estimate alone can imply more certainty than the data support. Their width reflects both the observed contrast and the amount of information available, including the group sizes and the variability inherent in the outcome.

The posted relative measures include a risk ratio of 2.505 with an interval from 1.39 to 4.513, and an odds ratio of 6.519 with an interval from 2.191 to 19.39. These express the group contrast on different scales. A risk ratio compares proportions as a ratio, whereas an odds ratio compares odds. Odds and probabilities are not interchangeable, so the odds ratio should not be interpreted as though it were a risk ratio. For a common outcome, an odds ratio can appear more extreme than a risk ratio. The absolute risk difference is often more directly connected to the observed difference in proportions.

What does the p-value describe?

The primary unadjusted p-value is <0.001. In general, a p-value is calculated under a statistical model that assumes no group difference and describes how compatible the observed data are with that model. A small p-value is evidence against that model under the test assumptions; it is not the probability that there is no effect, nor does it quantify the size of the effect. The record does not report the sponsor’s statistical analysis plan or a sponsor-reported analysis, so the posted unadjusted result should be understood as a summary-data comparison rather than a confirmed account of the prespecified trial analysis.

The other outcomes use different statistical forms. Satisfaction is also a binary count outcome. The later pain-rating outcome is reported as a mean change with a standard deviation in each group, and its comparison is a mean difference. For continuous outcomes, the mean summarizes the average change, while the standard deviation describes variation among participant-level values. The mean difference compares group averages; it does not describe every participant’s change or the spread of individual responses.

Why can different outcome forms tell different things?

The primary success measure converts each participant’s rating change into a threshold classification. The continuous secondary measure retains the magnitude of change in the score. The binary endpoint emphasizes the proportion reaching a chosen response definition; the continuous endpoint uses information about the full measured change. Neither summary replaces the other. Their results also arise from different reported denominators and timeframes, so they should be interpreted as separate outcomes rather than as interchangeable estimates.

The posted primary comparison has no discrepancy flag. The displayed calculations are unadjusted re-calculations from the arm-level summary statistics, and the record lists zero sponsor-reported analyses. When a registry’s own analysis conflicts with a summary-statistic re-calculation, the sponsor’s analysis takes precedence; that circumstance is not indicated for this record. Still, an unadjusted calculation cannot account for any covariates, stratification, or analysis procedures that may have been specified elsewhere. Such details are not reported in the registry record.

Over-dispersion is a general concern for count outcomes when variation exceeds what a simple probability model expects. It can make standard errors too small if the model assumes less variation than the data contain. The primary endpoint is reported as participant success counts, but no model specification or over-dispersion assessment is reported in the registry record. Therefore, no claim can be made about whether an over-dispersion adjustment was used. For the continuous secondary result, the standard deviations show observed spread, but the record does not report a full model specification or whether any adjustment was used.

Statistical significance does not by itself establish that the endpoint is clinically meaningful, that the outcome assessment was unbiased, or that the result generalizes to all people with diabetic peripheral neuropathy. Interpretation depends on the outcome definition, follow-up timing, missingness, analysis choices, and precision, as well as the observed effect estimate. The posted values permit a descriptive comparison, while the unreported methodological details leave important uncertainties.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.437, with a reported interval from 0.216 to 0.657. The interval lies above zero, consistent with the unadjusted p-value of <0.001 for a no-difference comparison. Its range nevertheless indicates that the data are compatible with a range of possible group differences, rather than identifying the true contrast exactly. A point estimate should therefore not be read as a perfectly precise value.

The record does not identify the confidence level or interval-construction method for the reported interval, so those details are not reported in the registry record. The interval should not be interpreted as a guarantee that the true effect lies within its bounds. In general, a confidence interval reflects the sampling uncertainty under its specified method; it does not account automatically for biases due to missing observations, outcome measurement, allocation procedures, or selective reporting.

The relative measures also have intervals: the risk ratio is 2.505, with an interval from 1.39 to 4.513, and the odds ratio is 6.519, with an interval from 2.191 to 19.39. The different scales yield different numerical magnitudes and should not be compared as if they were the same quantity. The risk difference describes an absolute contrast in proportions; the relative measures express contrasts as ratios.

For the secondary continuous outcome, the mean difference is -20.91, with an interval from -37.68 to -4.144. This interval describes uncertainty in the difference between group means on that outcome’s scale. It is not a range containing most individual participant changes. The reported standard deviations also indicate substantial observed variation in individual changes relative to the group means.

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 are per arm, not totals or total events. They use the observed effect as a reference and show planning scenarios for 100%, 75%, and 50% of that effect. The stated 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 the stated fraction of the observed effect. For the outcomes in this trial, the figures are participants per arm.

The 80% power column gives the planned number of participants per arm for a hypothetical study with an 80% chance of detecting the stated effect under the listed assumptions, if that effect and those assumptions were correct. The 90% column uses the same planning idea but targets a greater chance of detection, and therefore generally calls for more participants. These are design illustrations, not observed power.

For the primary outcome, planning for 100% of the observed effect lists 20 participants per arm for 80% power and 26 for 90% power. Planning for 75% lists 36 and 47 participants per arm, while planning for 50% lists 78 and 104. The smaller-effect scenarios require more participants because weaker contrasts are harder to distinguish from random variation. This relationship is a general feature of power planning, not a prediction of what a future trial will observe.

The planning calculations are based on the observed effect, which is uncertain and may be larger or smaller than the effect in a future study. They are not the trial’s original sample-size justification. The trial’s own original design assumptions and sample-size justification are not reported in the registry record. The illustrations should therefore be read as conditional planning aids rather than evidence that the completed trial had a particular design target.

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 = 0.290; treatment proportion p₁ = 0.727; average p̄ = 0.509.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7070 = 1.3857.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6359 = 0.5352.
4. n = (1.3857 + 0.5352)² / (0.4370)² = 19.3, rounded up to 20 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 <- 0.290322580645161                          # control proportion
p1 <- 0.727272727272727                          # 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(5291975)
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 = 20 (80% power), 26 (90% power)
 75% of observed effect: n per arm = 36 (80% power), 47 (90% power)
 50% of observed effect: n per arm = 78 (80% power), 104 (90% power)
power.prop.test: 19.3 
Simulated power at n = 20 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The record lists one primary endpoint and two secondary outcomes. It does not report a multiplicity adjustment, a hierarchy among the outcomes, or other procedures for controlling the chance of false-positive findings across multiple comparisons. The primary result is therefore the central outcome for interpretation; unadjusted secondary p-values are exploratory in the absence of a reported multiplicity strategy. This does not mean the secondary findings are invalid, but their nominal p-values do not account for the number of outcomes examined.

The registry does not report whether there were interim analyses, stopping rules, or changes to the outcome definitions after the study began. These details are not reported in the registry record. There is also no sponsor-reported analysis listed, and no statistical analysis plan is included in the information recorded for the posted outcomes. As a result, it is not possible to assess whether the displayed comparisons were prespecified, whether any additional analyses were conducted, or how the final analysis choices were made.

The primary outcome reports denominators of 33 for EVRL and 31 for placebo. The satisfaction outcome uses the same denominators, while the continuous secondary outcome reports 28 and 24 participants. The record does not explain the difference in denominators, report missing-data counts, or describe imputation or other missing-data handling. It also does not state whether each outcome used an intention-to-treat, per-protocol, or other analysis population. Those omissions limit assessment of possible bias if outcome availability or trial adherence differed by group.

The record does not report participant flow, exclusions from analysis, protocol deviations, or reasons for missing measurements. The primary timeframe is also described inconsistently: the listed timeframe says Baseline and 3 weeks, while the outcome description says measurement through endpoint at 6 weeks. Clarification of the timing and analysis population would help readers judge whether the comparison follows the intended trial design. In the absence of those details, the posted summaries support a descriptive group comparison but not a complete audit of the analysis process.

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.

The posted adverse-event figures show zero serious adverse events attributed to the study device in the EVRL group, with 33 at risk, and zero in the placebo group, with 31 at risk. The non-serious adverse-event figures are also zero in each group, using the same respective numbers at risk. The record reports zero deaths in both groups.

These entries describe what the registry record reports; they do not establish that no adverse events of any kind occurred. The record does not provide event narratives, the method for attributing events, the duration or completeness of safety follow-up, or details about how events were collected. It also does not report participant-level exposure or whether all participants were included in safety monitoring. Zero recorded events should be read as zero reported in these fields, not as proof that risk is absent or that rare events could be ruled out.

The group sizes are limited, and no interval estimates for adverse events are reported. Therefore, the safety figures offer a record of the events posted but do not precisely quantify the possibility of uncommon harms. They should be interpreted alongside the limitations in reporting rather than as a comprehensive safety assessment.

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

The posted data show a higher observed proportion meeting the primary pain-rating success threshold in the EVRL group than in the placebo group. The risk-difference estimate is 0.437, with a reported interval from 0.216 to 0.657 and an unadjusted p-value of <0.001. These statistics describe the trial’s reported comparison; they do not by themselves establish what an individual will experience or settle the treatment’s effects in other settings.

The primary endpoint is based on a thresholded change in a subjective pain rating. Its interpretation depends on the threshold definition, the timing of the assessment, the completeness of follow-up, and the method used to collect the rating. The registry’s timeframe wording is inconsistent, and missing-data handling and analysis populations are not reported. Those uncertainties limit how fully the result can be evaluated.

The result should not be confused with the continuous secondary pain-change outcome. The secondary measure describes mean score change at a later timeframe and includes fewer participants. Its direction is consistent with the primary comparison, but it answers a related, not identical, question. Satisfaction is another distinct outcome and does not substitute for pain measurement.

The trial record states that the placebo device looked the same as the EVRL but did not emit therapeutic light. It does not report masking checks, so the success of masking cannot be assessed. Allocation methods and the identities of those masked are also not reported. These features matter because beliefs and expectations can influence subjective pain ratings, even in a randomized design.

These findings should be read as evidence about the outcomes posted for this completed trial, not as medical advice or a definitive conclusion about every person with diabetic peripheral neuropathy. The registry does not report enough detail to assess generalizability, missingness, multiplicity, or the complete prespecified analysis. Statistical evidence and clinical meaning are related but separate questions: the posted comparison estimates a group difference, while the record leaves uncertainty about how that difference should be applied beyond the trial.

17. Why This Trial Matters Statistically

This trial illustrates why a binary response definition needs to be read alongside the underlying measurement. The primary outcome counts participants who cross a threshold on a pain scale, which communicates the share meeting a chosen criterion but compresses the size of each person’s change into a success or non-success category. The continuous secondary measure preserves more information about score changes, but it has a different timeframe and denominator. Together, these endpoints show how measurement choices shape the statistical question.

The reported primary risk difference gives an absolute contrast in observed proportions, while the risk ratio and odds ratio describe relative contrasts. These measures can communicate different aspects of the same comparison, and their numerical values are not interchangeable. Reporting the group counts, comparison estimate, and interval allows readers to distinguish the observed data from the uncertainty around the estimated contrast.

The record also highlights the importance of complete analysis reporting. It is randomized and triple-masked, but the allocation procedure, masking roles, analysis populations, missing-data handling, and multiplicity strategy are not reported. Without these details, readers cannot fully judge the robustness of the analysis or whether the posted summaries match a prespecified plan. The lack of sponsor-reported analyses further limits comparison between the posted summary calculations and a formal trial analysis.

Finally, the sample-size illustrations show how planning depends on the effect a future study aims to detect. Smaller target effects require larger per-arm samples under the stated assumptions. Those calculations are conditional planning aids, not a record of the trial’s original design rationale. Distinguishing planning illustrations from observed trial results is essential to avoid treating a completed study’s effect estimate as a guaranteed future effect.

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 reporting gaps limit interpretation. The primary timeframe is listed as Baseline and 3 weeks, but its description refers to measurement through endpoint at 6 weeks. The registry does not explain that discrepancy. The later pain-change outcome is listed as Baseline and 7 Weeks, so the outcomes do not have matching stated timeframes.

The outcome denominators differ, particularly for the continuous secondary measure, and the reasons are not reported. There is no posted account of participant flow, missing observations, withdrawals, exclusions, protocol deviations, or analysis populations. Without these details, it is difficult to assess whether data availability differed between groups or how incomplete observations may have affected estimates.

Although the design is identified as randomized and triple-masked, the allocation method, concealment procedure, and identities of masked participants or personnel are not reported. Masking checks are not listed. These details are relevant because the primary outcome relies on participant-reported pain ratings and satisfaction.

The record lists no sponsor-reported analyses and does not describe a statistical analysis plan, multiplicity handling, interim analyses, or the original sample-size justification. The posted comparisons are unadjusted. The record also does not report further eligibility criteria, device-use adherence, or the completeness and duration of safety monitoring. These omissions do not negate the posted results, but they constrain assessment of bias, precision, generalizability, and the completeness of outcome reporting.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Efficacy and Human Factors Validation Testing of the Erchonia EVRL for Providing Temporary Relief of Diabetic Peripheral Neuropathy Foot Pain — NCT05291975.
• Registry record last updated 2025-08-13; status last verified 2025-08.
• Results first posted 2025-08-13.
• 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

NCT05291975 is a completed randomized, triple-masked, parallel-group device trial sponsored by Erchonia Corporation. It compared Erchonia EVRL with a placebo laser for temporary relief of diabetic peripheral neuropathy foot pain. Enrollment is recorded as 64, the study start date as 2022-02-17, and primary completion as 2024-10-16. Phase is listed as NA.

The primary endpoint counts participants meeting a 30% or greater change threshold on the Visual Analog Scale. The posted comparison favors the EVRL group on this measure, with a risk-difference estimate of 0.437 and an unadjusted p-value of <0.001. Secondary outcomes concern satisfaction and later change in foot-pain rating. The registry reports zero serious adverse events, zero non-serious adverse events, and zero deaths in each group.

Interpretation is limited by the inconsistent primary timeframe wording and the absence of reported details on missing data, analysis populations, multiplicity, allocation procedures, masking roles, and sponsor analyses.