Less Infections for the Diabetic Foot: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Less Infections for the Diabetic Foot (NCT03615807), a randomized na study. The primary outcome is Number of Participants Experiencing Clinical Failure.

2. Clinical Question

3. Trial Design

The registry describes a randomized, unblinded, single-centre, parallel-group study comparing different durations of targeted antibiotic treatment for diabetic foot infections. Enrollment is listed as 182, and the study status is completed. The start date is 2017-02-16 and primary completion is listed as 2020-02-29. The registry identifies University Hospital, Geneva as the sponsor. No phase is applicable in the record.

Randomization was described as 1:1 between the two duration strategies. The planned course depended on infection type: soft tissue infections were assigned to 10 days or 20 days, while osteomyelitis was assigned to 3 weeks or 6 weeks. The posted primary-outcome results list 79 participants in the short antibiotic arm and 80 in the long antibiotic arm. The registry does not explain how those outcome denominators relate to the enrollment figure, so the difference should not be attributed to a particular cause.

The brief summary places randomization after any needed surgical debridement and says that amputation was not the debridement procedure under consideration. The registry also lists microbiological sampling, off-loading, wound debridement, patient education and instructions, and revascularisation if needed. It does not report how often these additional measures were used or whether their use differed between arms.

Masking is recorded as none. The registry record does not report a detailed allocation-concealment method, protocol deviations, or a statistical analysis plan. It describes primary efficacy assessment at test of cure approximately 60 days after treatment stopped, while the primary-outcome timeframe field gives 30-60 days. These descriptions indicate the intended follow-up period but do not establish the exact assessment date for each participant.

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.

Population: Diabetic foot infections requiring tretement

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Experiencing Clinical Failure, measured over 30-60 days.

The primary endpoint counts participants experiencing clinical failure. The registry describes the assessment as a visual and dichotomous evaluation of clinical recurrence or failure, with results expressed as numbers of participants. A dichotomous endpoint classifies each assessed participant into an outcome category, rather than measuring the severity of symptoms on a continuous scale. In this trial, the posted event counts are the participants recorded as experiencing clinical failure in each arm.

Clinical recurrence or failure is relevant to a comparison of antibiotic durations because it captures whether the infection was judged to have returned or not to have resolved at follow-up. The endpoint does not, by itself, describe how severe a failure was, why it occurred, or whether it was attributable to antibiotic duration. The registry does not report a more detailed operational definition, adjudication procedure, or criteria for the visual assessment.

The primary-outcome timeframe is listed as 30-60 days. The brief summary describes final primary efficacy assessments at a test-of-cure visit approximately 60 days after treatment was stopped. The record does not explain the relationship between these two timeframe descriptions. The posted counts therefore should be read as the registry’s reported primary-outcome results, without assuming a more precise visit schedule or a particular rule for participants whose assessment timing differed.

Using a participant count makes the arm comparison direct to interpret, but it does not convey how many separate episodes of recurrence occurred or their timing. Those details are not reported in the registry record.

7. Results Posted in the Registry

• Long Antibiotic Arm: 37.5% (30/80) versus 32.9% (26/79) on control; risk difference 4.6 percentage points (95% CI -10.2 to 19.4), risk ratio 1.14 (0.75–1.74); unadjusted two-proportion z-test p = 0.545.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary: each participant is classified as experiencing clinical failure or not experiencing clinical failure for the reported assessment. General statistical explanation: for a binary outcome, an arm’s event count is interpreted together with the number of participants assessed in that arm. Counts without denominators can be misleading when group sizes differ, so the posted comparison uses both the event information and the arm sizes.

What does the risk difference represent?

The risk difference expresses the difference in the proportions with the outcome between two arms. In this registry comparison, the direction is long antibiotic arm relative to short antibiotic arm. A positive estimate therefore points toward a higher observed failure proportion in the long-duration arm, while a negative estimate would point toward a lower observed failure proportion there. This is a descriptive comparison of the posted outcome data; it does not on its own explain why outcomes might differ.

The risk difference is an absolute measure: it describes the separation between the arm-level event proportions on the same scale. Other measures, such as a risk ratio or odds ratio, describe relative contrasts instead. The registry record includes estimates for these relative measures, but interpretation still depends on uncertainty and on how the outcome and analysis population were defined. Different effect measures can convey different aspects of a comparison and should not be treated as interchangeable.

How should the confidence interval be read?

General statistical explanation: a confidence interval describes the range of effect estimates reasonably compatible with the observed data under the method’s assumptions. It is not a guarantee that the true effect lies within the particular interval, and its width reflects the precision of the estimate. Here, the reported interval for the risk difference spans both negative and positive values. That means the posted data are compatible with effects in either direction, not only with the point estimate.

A confidence interval crossing the no-difference value is consistent with the reported unadjusted p-value of 0.545. Neither the interval nor the p-value demonstrates that the arms are equivalent. An equivalence or non-inferiority conclusion would require a suitable prespecified framework and margin; such a framework is not reported in the registry record.

What does the p-value add?

General statistical explanation: a p-value measures the compatibility of the observed data with a null model, assuming that model and the testing procedure are appropriate. It is not an effect size and does not indicate whether a difference would be clinically important. A comparatively large p-value can occur when the true difference is small, when data are noisy, or when the estimate is imprecise. In this trial, the confidence interval’s span is especially important for understanding the uncertainty.

The registry labels the comparison p-value as unadjusted. The record does not report a more detailed testing plan, adjustment for covariates, or a multiplicity procedure. The comparison should therefore be described as posted rather than assumed to reflect an unreported analysis strategy.

Why do event counts and denominators matter?

The short arm reports 26 clinical failures among 79 participants, and the long arm reports 30 among 80. The registry reports the arm sizes for this outcome, but does not describe the analysis population in more detail or explain whether all randomized participants had outcome assessments. In general, differences between randomized, treated, and analyzed populations can affect interpretation. Without further information, the reported denominators should be used as posted and not treated as proof of a particular missing-data or intention-to-treat approach.

General statistical explanation: binary outcomes do not describe event timing. A time-to-event analysis would use when an event occurred and how long participants were observed, with methods that account for differing follow-up. The registry’s primary outcome is reported as participant counts, and no time-to-event analysis is posted. The stated assessment period does not turn the endpoint into a time-to-event outcome.

The study compared duration strategies within a randomized design, which supports a direct comparison between assigned arms when the analysis and follow-up are appropriately conducted. However, randomization alone does not provide details about concealment, adherence, crossover, missing observations, or analysis populations. Those details are not reported in the registry record, so they cannot be assumed when interpreting the posted estimates.

10. Confidence Intervals and Precision

The risk-difference estimate is accompanied by a confidence interval that includes values on both sides of no difference. Its lower endpoint is negative and its upper endpoint is positive. This direction-spanning interval is a central feature of the result: the data do not pin down whether the long-duration strategy had a lower or higher failure proportion than the short-duration strategy.

General statistical explanation: precision refers to how narrowly an estimate is determined by the data and the statistical method. A wider interval leaves more possible effect sizes compatible with the observed results. It does not mean the estimate is invalid; it means the data do not identify the contrast closely. The p-value of 0.545 should be read alongside this uncertainty rather than as a stand-alone verdict.

The arm counts are 79 and 80, and clinical failure was reported for 26 and 30 participants, respectively. Those counts convey the observed event experience but do not make the interval narrow by themselves. Precision depends on the amount of information in the data and the variability of the outcome, as well as the analysis method. The registry record does not report a confidence-interval method or an adjusted analysis that would permit a more detailed assessment of those assumptions.

The posted relative-effect estimates also have uncertainty intervals, but a relative measure does not remove the uncertainty evident in the risk-difference comparison. The registry record does not report a prespecified clinical margin against which the interval could be judged. Consequently, the interval should not be interpreted as establishing equivalence or excluding potentially important differences.

11. 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. This is a binary participant-outcome comparison, rather than a time-to-event calculation in which the planning quantity would be the total number of events. The planning assumptions listed are a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect.

For planning at 100% of the observed effect, the figures are 1,700 participants per arm for 80% power and 2,275 participants per arm for 90% power. At 75% of the observed effect, they are 3,000 per arm for 80% power and 4,015 per arm for 90% power. At 50% of the observed effect, they are 6,697 per arm for 80% power and 8,965 per arm for 90% power.

The 80% power column gives the per-arm sample size estimated to provide an 80% chance of detecting the specified effect under the listed assumptions, if that effect were the true one and the planning model applied. The 90% column describes the corresponding planning target for a 90% chance. Higher power requires more participants for a given effect size, and smaller effects need more participants because they are harder to distinguish from random variation.

These are planning illustrations based on the observed effect, not the trial’s original design calculation. The original design assumptions are not reported in the registry record. This is not observed power. The figures are conditional planning estimates; they do not alter the uncertainty in the completed trial’s posted comparison.

12. 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 = 0.329; treatment proportion p₁ = 0.375; average p̄ = 0.352.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6754 = 1.3238.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6747 = 0.5678.
4. n = (1.3238 + 0.5678)² / (0.0459)² = 1,699.5, rounded up to 1,700 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 <- 0.329113924050633                          # control proportion
p1 <- 0.375                          # 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(3615807)
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 = 1,700 (80% power), 2,275 (90% power)
 75% of observed effect: n per arm = 3,000 (80% power), 4,015 (90% power)
 50% of observed effect: n per arm = 6,697 (80% power), 8,965 (90% power)
power.prop.test: 1699.5 
Simulated power at n = 1,700 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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists two outcome measures and one posted secondary outcome, concerning participants experiencing adverse events related to antibiotic therapy. It reports no registered analyses in the analysis listing. The record does not report a multiplicity strategy describing whether or how statistical testing across outcomes or analyses was controlled. Without such a strategy, the primary comparison should be read as the posted comparison, not as a fully documented family of confirmatory tests.

The record does not report how missing primary-outcome assessments were handled, how many participants lacked an assessment, or whether any imputation or sensitivity analyses were performed. The primary-outcome population field is blank. It also does not report whether the analysis followed intention-to-treat, per-protocol, or another population definition. These details matter because excluding participants or handling unavailable outcomes differently can affect a binary outcome comparison.

The registry record does not report an interim-analysis plan, stopping rule, or detailed statistical analysis plan. It therefore is not possible to establish from the record whether the posted analysis followed a prespecified plan or whether any outcome or analysis choices were made after data review. The absence of these details is not evidence that a particular method was or was not used; it means the information is not reported in the registry record.

The study was unblinded according to the registry. The record does not describe blinded outcome adjudication or the procedures used to reduce assessment bias. Because clinical failure was described as a visual and dichotomous evaluation, information about assessment criteria and adjudication would help readers understand how consistently the outcome was classified. Those details are not reported in the registry record.

These reporting gaps limit evaluation of robustness and multiplicity, but they do not change the posted counts or comparison estimate. Interpretation should remain anchored to the information that is recorded, without assigning an unreported analysis population or missing-data method.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: progressive ischemia leading to necrosis and amputation (7.5%).

The registry reports serious adverse events related to antibiotic therapy for 5 participants in the short antibiotic arm, among 79 at risk, and 6 participants in the long antibiotic arm, among 80 at risk. Deaths are recorded as 0 in each arm. These are descriptive safety counts; the registry record does not provide a comparative estimate or confidence interval for them.

The record also lists 5 other adverse events in the short arm and 6 in the long arm. The registry’s serious-event terms include progressive ischemia leading to necrosis and amputation, listed at 7.5%. The record does not specify the arm distribution for that term in the information, so it should not be assigned to either arm or treated as an arm-specific rate.

Counts of participants with events do not by themselves describe event severity beyond the serious-event classification, timing, duration, or clinical course. The registry record does not report detailed definitions, exposure-adjusted rates, or a method for assessing causal relationship beyond the outcome’s description as related to antibiotic therapy. These numbers therefore describe the posted safety reporting and should not be taken as a complete account of all possible harms.

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

The posted results document clinical failures in both randomized arms: 26 participants in the short antibiotic arm and 30 in the long antibiotic arm. The comparison estimate is expressed as long duration relative to short duration. Its confidence interval extends across no difference, and the unadjusted p-value is 0.545. Taken together, these results leave substantial uncertainty about the direction and size of the difference in this study.

The data do not show that the strategies have identical outcomes. A finding of no statistically persuasive difference is not the same as evidence of equivalence, and the registry record does not report an equivalence or non-inferiority margin. Nor do the results establish that one duration strategy produces fewer failures. The interval allows for both lower and higher failure proportions in the long-duration arm.

The trial addressed distinct duration pairs for soft tissue infection and osteomyelitis, but the posted primary comparison does not give separate outcome estimates for those infection types. It therefore cannot show whether the observed arm-level pattern was similar across both groups. The record also does not identify a specific antibiotic drug in the arm descriptions, so the results should not be generalized to a particular agent or regimen beyond the duration strategies described.

The randomized design provides a basis for comparing assigned strategies, but important analysis details are not reported, including missing-data handling and the primary analysis population. The single-centre, unblinded design also defines the setting and conduct described by the registry. These features should be considered alongside the confidence interval and the limits of the registry reporting.

The safety counts add descriptive context, with serious adverse events recorded in both arms and no deaths recorded in either. They do not settle the primary efficacy question or establish a complete safety comparison. Overall, the registry results characterize observed outcomes in this trial; they do not by themselves determine treatment choices or settle what would occur in other populations or settings.

16. Why This Trial Matters Statistically

This trial is statistically informative because it places a randomized comparison around a practical question: whether shorter antibiotic courses have different observed clinical-failure counts from longer courses in diabetic foot infections. The two arms used different duration pairs according to infection type, so the design reflects more than a single uniform treatment duration. The outcome is reported in a form that is easy to understand as participant counts.

The central statistical lesson is the distinction between the observed point estimate and its uncertainty. The reported risk-difference interval crosses no difference, and the unadjusted p-value is 0.545. Those details do not prove that the arms are the same. They show that the posted estimate does not determine the direction of the contrast with precision. A meaningful reading therefore considers both the event counts and the uncertainty interval, rather than relying on a significance label alone.

The record also illustrates why planned sample size and observed evidence are different questions. The sample-size figures are planning illustrations based on fractions of the observed effect, not a report of the original design calculation. Smaller target effects require larger per-arm samples under the stated planning assumptions. Those calculations cannot retrospectively make the completed trial more or less conclusive.

Finally, transparent interpretation depends on analysis details as well as outcome numbers. The registry does not report the primary analysis population, missing-data methods, or a multiplicity plan. These omissions matter when assessing how robust an estimate may be, while not changing the reported counts themselves. The combination of randomized allocation, a clinically interpretable binary endpoint, a wide direction-spanning interval, and incomplete analysis reporting makes careful distinction between observation and inference especially important.

17. 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 study is described as unblinded and single-centre. These features define the trial setting and may limit how directly its findings apply to other settings. The registry does not report whether outcome assessors were independently blinded or whether clinical failure was adjudicated using standardized criteria. Because the endpoint includes a visual assessment, those details would help readers assess consistency of outcome classification.

The registry gives enrollment as 182, while the primary outcome summaries list 79 participants in the short arm and 80 in the long arm. It does not explain the relationship between these figures or report the number and reasons for any participants without primary-outcome data. No assumptions should be made about why the denominators differ from enrollment.

The record does not report the primary analysis population, missing-data approach, adherence to assigned treatment, crossover, or protocol deviations. It also does not provide a detailed statistical analysis plan, multiplicity approach, or interim-analysis information. These omissions limit assessment of the analysis process and of how sensitive the posted comparison might be to alternative choices.

The primary endpoint is reported for the arms as a whole, without separate posted estimates for soft tissue infections and osteomyelitis. The registry describes different duration pairs for these conditions, so the combined arm-level result cannot establish whether effects varied by infection type. The antibiotic agents and further regimen details are not identified in the arm descriptions.

The timeframe is expressed in two ways: 30-60 days in the primary-outcome field and approximately 60 days after treatment stopped in the brief summary. The registry does not explain how these descriptions correspond for individual assessments. These limitations qualify interpretation of the posted comparison without changing the outcome counts recorded for each arm.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Less Infections for the Diabetic Foot — NCT03615807.
• Registry record last updated 2020-06-09; status last verified 2020-06.
• Results first posted 2020-06-01.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT03615807 is a completed, randomized, unblinded, parallel-group, single-centre study titled Less Infections for the Diabetic Foot. It compared shorter and longer targeted antibiotic durations for diabetic foot infections, with different durations specified for soft tissue infections and osteomyelitis. Enrollment is listed as 182.

The primary outcome was the number of participants experiencing clinical failure, described as visual and dichotomous evaluation of clinical recurrence or failure. The posted results report 26 failures among 79 participants in the short antibiotic arm and 30 among 80 in the long antibiotic arm. The reported risk-difference interval spans both directions of effect, and the unadjusted p-value is 0.545.

The registry lists serious adverse events related to antibiotic therapy for 5 participants in the short arm and 6 in the long arm, with 0 deaths in each. It does not report a detailed primary analysis population, missing-data approach, or multiplicity strategy. The posted results are descriptive of this trial and retain substantial uncertainty around the comparative outcome.