Bioimpedance as a Diagnostic Tool for Assessing the Need for Socket Modification in Transtibial Amputees: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bioimpedance as a Diagnostic Tool for Assessing the Need for Socket Modification in Transtibial Amputees (NCT03164356), a randomized na study. The primary outcome is Number of Participants With Significant Increases in Socket Comfort Score (SCS).

2. Clinical Question

3. Trial Design

The registry identifies this as a randomized, single-masked study with a sequential model. It describes an initial observational cohort component followed by a blinded randomized control trial. The record does not specify who was masked, so the masking label cannot establish whether participants, prosthetists, outcome assessors, or another group were unaware of allocation.

The study’s overall purpose was to evaluate whether residual-limb fluid-volume information collected by a non-invasive bioimpedance device could contribute to prosthetic prescription, fit, or comfort, as assessed by amputees and prosthetists. In the first arm, research staff obtained bioimpedance measurements, and participants wore an ActiGraph monitor for at least one week before the prosthetist performed socket modifications. In the experimental arm, practitioners received bioimpedance information and conclusions drawn from the first arm to inform their decision. In the control arm, measurements were collected in parallel but withheld from the prosthetist.

The registry lists an enrollment of 68 and a completed status. It records the study start as 2016-11-09 and primary completion as 2020-09-14. These registry-level study details should not be confused with the denominators for the posted primary outcome: the primary outcome reports arm-specific participant counts, and those counts are the relevant denominators for interpreting that result. The record does not explain the relationship between the overall enrollment figure and the outcome-specific denominators.

The trial’s original sample-size assumptions, allocation ratio, detailed masking procedures, eligibility criteria, and full statistical analysis plan are not reported in the registry record. Although the record describes randomization, it does not provide enough information to assess its implementation or the sequence-generation and concealment procedures.

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: Primary outcome measures from each group were collected pre and post modifications to their prosthesis. The experimental arm involved sharing bioimpedance data with the participants' prosthetist.

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 Significant Increases in Socket Comfort Score (SCS), measured over Baseline taken pre-modification, with a final score taken post-modification. The minimum time between scores was 3 weeks..

The primary endpoint is the number of participants with a significant increase in socket comfort score after a prosthesis modification. Participants rated overall prosthesis comfort on a scale from 0 to 10, with 0 representing the least comfortable possible score and 10 the most comfortable possible score. The registry says a baseline score was collected before modification and a final score afterward, with a minimum interval of 3 weeks.

For this endpoint, “significant” is an operational definition based on change in an individual’s score, not a claim that a group comparison passed a statistical significance test. Participants whose score changed by less than 2 points, or whose score decreased, were not counted as having a significant positive change. The outcome therefore reduces a change in a comfort rating to a participant count: it does not report the size of each person’s score change or the average change in comfort.

A participant-count endpoint can be useful when the clinical question concerns how many people cross a defined threshold of improvement. It is also straightforward to compare between groups using event proportions and their difference. However, dichotomizing a score discards information about the magnitude of changes and makes results dependent on the selected threshold. The registry record does not report the rationale for the threshold, nor does it describe how missing pre- or post-modification scores were handled.

7. Results Posted in the Registry

• Arm 1: 35.7% (5/14) versus 36.4% (4/11) on control; risk difference -0.6 percentage points (95% CI -38.6 to 37.3), risk ratio 0.98 (0.34–2.81); unadjusted two-proportion z-test p = 0.973.
• Arm 2 - Treatment: 60.0% (6/10) versus 36.4% (4/11) on control; risk difference 23.6 percentage points (95% CI -18.0 to 65.2), risk ratio 1.65 (0.65–4.19); unadjusted two-proportion z-test p = 0.279.

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 Net-Positive Increase in Prosthesis Satisfaction, Measured by the Patient's Overall Satisfaction With Their Entire Prosthesis

• 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:
  • Arm 2 - Treatment Group, Pre and Post Modification: 60.0% (6/10) versus 57.1% (8/14) on control; risk difference 2.9 percentage points (95% CI -37.1 to 42.8), risk ratio 1.05 (0.53–2.07); unadjusted two-proportion z-test p = 0.889.
  • Arm 2 - Control Group, Pre and Post Modification: 54.5% (6/11) versus 57.1% (8/14) on control; risk difference -2.6 percentage points (95% CI -41.8 to 36.6), risk ratio 0.95 (0.47–1.93); unadjusted two-proportion z-test p = 0.897.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2 - Treatment Group, Pre and Post Modification and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2 - Control Group, Pre and Post Modification and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Net-Positive Change in Ambulation Score

• 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:
  • Arm 2 - Treatment Group, Pre and Post Modification: 80.0% (8/10) versus 78.6% (11/14) on control; risk difference 1.4 percentage points (95% CI -31.4 to 34.2), risk ratio 1.02 (0.67–1.54); unadjusted two-proportion z-test p = 0.932.
  • Arm 2 - Control Group, Pre and Post Modification: 72.7% (8/11) versus 78.6% (11/14) on control; risk difference -5.8 percentage points (95% CI -39.8 to 28.1), risk ratio 0.93 (0.59–1.46); unadjusted two-proportion z-test p = 0.734.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2 - Treatment Group, Pre and Post Modification and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2 - Control Group, Pre and Post Modification and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Net-Positive Change in Residual Limb Health Score

• 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:
  • Arm 2 - Treatment Group, Pre and Post Modification: 30.0% (3/10) versus 71.4% (10/14) on control; risk difference -41.4 percentage points (95% CI -78.4 to -4.5), risk ratio 0.42 (0.15–1.15); unadjusted two-proportion z-test p = 0.045.
  • Arm 2 - Control Group, Pre and Post Modification: 54.5% (6/11) versus 71.4% (10/14) on control; risk difference -16.9 percentage points (95% CI -54.6 to 20.9), risk ratio 0.76 (0.41–1.44); unadjusted two-proportion z-test p = 0.383.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Arm 2 - Treatment Group, Pre and Post Modification than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2 - Control Group, Pre and Post Modification and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the assessment beyond socket comfort, covering overall prosthesis satisfaction, ambulation, residual-limb health, prosthesis utility and well-being, communication between prosthetist and patient, socket-modification types, and the effect of modification on socket fit. The registry lists 20 posted secondary outcomes, although the detailed arm counts and comparisons in the record cover only some of these domains. That distinction matters: the number of outcomes listed should not be mistaken for a complete set of numerical results in the registry entry.

Across the detailed secondary results, there is no single consistent pattern that can be treated as a clear, confirmatory signal across all measures. The outcomes address different experiences and are not interchangeable. Their relationship to the primary comfort result is contextual: improvement in satisfaction, mobility, or limb health could complement comfort information, but one outcome cannot establish a change in another. Nor do secondary measures override the primary result when the trial’s main question concerns the comfort endpoint.

One unadjusted comparison for residual-limb health has a p-value of 0.045, while the other detailed secondary comparisons do not have similarly small unadjusted p-values. Because multiple secondary outcomes and comparisons are considered, a nominal result can arise even when there is no robust underlying difference. The registry record does not report a family-wise error procedure, false-discovery approach, or a hierarchy for confirmatory versus exploratory outcomes. The finding should therefore be treated as exploratory rather than as independent confirmation of a treatment effect.

Secondary measures can be informative for generating hypotheses and understanding the range of outcomes considered, but confidence in them depends on prespecification, complete reporting, appropriate multiplicity handling, and adequate precision. Those details are not reported in the registry record. The secondary results are best read alongside the primary estimate and its uncertainty, not as a collection of separate tests from which to select the most favorable result.

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

• Number of Participants With Net-Positive Increase in Prosthesis Satisfaction, Measured by the Patient's Overall Satisfaction With Their Entire Prosthesis
• Number of Participants With Net-Positive Change in Ambulation Score
• Number of Participants With Net-Positive Change in Residual Limb Health Score
• Number of Participants With Net-Positive Change in Prosthesis Utility Score
• Number of Participants With Net-Positive Change in Prosthesis Well Being Score
• Prosthetist Communication Assessment Score, Measured by the Communication Efficacy Between the Prosthetist and Their Patient
• Types of Socket Modifications Implemented Per Group
• Effect of Socket Modification, Measured by the Impact of the Physical Modification Made to the Prosthesis to Socket Fit

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each person is counted as having or not having the defined positive change in socket comfort. For a binary endpoint, a natural descriptive summary is the number meeting the criterion and the number assessed in each arm. A comparison can then express the difference between the two groups’ event proportions. A risk difference is measured on the proportion scale; zero corresponds to equal event proportions, while a positive or negative value indicates which group has the higher observed proportion, according to the comparison’s stated order.

A confidence interval around a risk difference represents a range of values compatible with the observed data under the method used to construct it. A wide interval indicates that the estimate is not precise. If the interval crosses zero, values consistent with either direction of difference remain plausible. This does not prove there is no effect; it indicates that the data do not narrowly determine the direction or size of the contrast.

The registry also reports risk ratios and odds ratios. A risk ratio compares the event proportions between groups as a ratio, while an odds ratio compares the odds of the event. These are different measures and can have different numerical values; they should not be treated as interchangeable. For rare or common outcomes, the relationship between odds and risk can be especially important to interpretation. The registry’s posted comparisons are expressed as risk differences, and the explanations keep the primary interpretation focused on that scale.

The listed p-values are unadjusted. A p-value summarizes how unusual data at least as discrepant as the observed data would be under a specified null model; it is not the probability that the null hypothesis is true, the probability that chance alone caused the result, or a measure of clinical importance. A small p-value does not convey precision by itself, and a large one does not establish equivalence. Interpretation should consider the estimate, interval, endpoint definition, and analysis context together.

The primary endpoint’s use of a threshold turns a numerical score change into an event count. This can make a result easier to communicate as the number of participants meeting a criterion, but it discards detail. Two participants with different-sized improvements can both count as events, while a change just below the threshold is treated differently from a change that reaches it. The registry’s definition excludes decreases and changes of less than 2 points from the positive-event count. The word “significant” in the endpoint label refers to that rule, not to the p-value for a between-arm comparison.

For general statistical context, randomization is intended to make treatment groups comparable on average, including with respect to factors that are not measured. It does not guarantee balance in every realized trial, particularly when outcome denominators are limited. Masking can reduce some forms of bias, depending on who is masked and how outcomes are measured. The registry provides the design labels but does not report enough detail to evaluate the implementation of either process.

The posted primary comparisons are Arm 1 versus Arm 3 - Control, and Arm 2 - Treatment versus Arm 3 - Control. The registry also supplies secondary contrasts against Arm 1 for the secondary outcomes. The outcome-specific denominators should be used for each contrast; the overall enrollment figure is not a substitute for them. The record does not report whether all randomized participants were included in an intention-to-treat analysis, whether a per-protocol population was used, or how participants with unavailable outcome data were handled.

No formal analyses are listed in the registry record. The displayed unadjusted comparisons are therefore not accompanied by a reported model specification, covariate adjustment, prespecified hypothesis-testing hierarchy, or details of the statistical test. The registry record does not report whether interim analyses were planned or conducted. Without those details, the results can be interpreted descriptively and through the posted estimates, but the full analytical procedure cannot be reconstructed from the record alone.

For general explanation, a comparison of event proportions assumes that the event classification and the participant group definitions are applied consistently. If outcomes are missing or measurement procedures differ between groups, the observed proportions may not represent the same underlying process. The record gives outcome counts and denominators but does not describe missingness patterns, reasons for non-assessment, or sensitivity analyses. Those omissions matter because the interpretation of a binary count depends both on who is included and on how the event is defined.

11. Confidence Intervals and Precision

Precision concerns how narrowly the observed data identify a plausible range for the group difference. The confidence intervals for the primary risk-difference comparisons are wide and extend across zero. Thus, the record is compatible with a range of possible contrasts in both directions; the point estimates alone should not be read as precise measures of the effect of sharing bioimpedance data.

The limited outcome-specific denominators contribute to uncertainty in binary comparisons. With relatively few observations, the addition or reclassification of a participant can have a noticeable influence on an event proportion. Confidence intervals make that uncertainty visible, whereas a single point estimate does not. The intervals should be considered alongside the actual event counts and the endpoint’s threshold-based definition.

The unadjusted p-values do not remedy imprecision. A p-value and a confidence interval answer related but different questions: the p-value summarizes compatibility with a null model, while the interval communicates a range of effect sizes compatible with the data under its method. A result that does not meet a conventional significance threshold may still be compatible with a potentially meaningful effect; conversely, a result with a small p-value can still be imprecise or vulnerable to multiple testing.

The record does not report adjusted analyses or additional sensitivity analyses that might help assess robustness. Accordingly, precision should be understood as precision of the posted, unadjusted comparisons, not as a guarantee that the estimates capture the effect in other settings or populations.

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 sample-size figures are planning illustrations, not the trial’s original design justification. For these binary outcomes, the reported figures are participants per arm, not a total across arms and not a total number of events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect.

The 80% power column gives the illustrative number of participants per arm associated with an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions were correct. The 90% power column represents a higher target probability of detection and therefore generally calls for more participants. These are design calculations, not outcomes observed in the trial.

Rows that plan for 75% or 50% of the observed effect use smaller effects than the row based on 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so the planning illustrations require more participants per arm. In some comparisons, the observed effect used as the starting point is very small, which can produce very large illustrative sample sizes. Such values are sensitive to the observed estimate and should not be treated as a recommended sample size without a separate design decision and a justified target effect.

The trial’s own original sample-size assumptions and justification are not reported in the registry record. These figures are planning illustrations based on the posted effect estimates; they are not observed power and do not measure the probability that the completed study found a true effect.

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 = 0.364; treatment proportion p₁ = 0.357; average p̄ = 0.360.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6790 = 1.3308.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6790 = 0.5714.
4. n = (1.3308 + 0.5714)² / (-0.0065)² = 85,814.5, rounded up to 85,815 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 <- 0.363636363636364                          # control proportion
p1 <- 0.357142857142857                          # 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(3164356)
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 = 85,815 (80% power), 114,881 (90% power)
 75% of observed effect: n per arm = 152,710 (80% power), 204,435 (90% power)
 50% of observed effect: n per arm = 343,933 (80% power), 460,428 (90% power)
power.prop.test: 85814.5 
Simulated power at n = 85,815 per arm: 0.800 (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 registry identifies a primary outcome and lists 20 posted secondary outcomes. Examining many endpoints and multiple group contrasts creates a multiplicity issue: even when each individual test uses the same nominal threshold, the chance of at least one apparently notable result across a family of tests can increase. This is a general statistical concern, not proof that any particular finding is spurious.

The registry record does not report a multiplicity adjustment, a testing hierarchy, or a distinction between confirmatory and exploratory secondary analyses. It also does not report a detailed statistical analysis plan specifying which outcomes or contrasts were intended to support formal claims. The unadjusted p-values should consequently be treated as individual, exploratory summaries rather than as results with a reported family-wise error guarantee.

The record reports outcome-specific denominators, but does not describe the amount or reasons for missing outcome data, whether participants were excluded after randomization, or how missing pre- or post-modification scores were handled. It does not report imputation, sensitivity analyses, or a missing-data assumption. The absence of such details limits assessment of whether the observed counts could be affected by incomplete follow-up or differential availability of scores.

The registry also does not report the analysis populations, such as an intention-to-treat population or a per-protocol population. Although the study is labeled randomized, that design label alone does not establish how participants were included in each analysis. No formal analyses are listed in the registry record, and details of interim analyses are not reported. These gaps constrain interpretation of the posted comparisons and should be distinguished from evidence that a particular method was or was not used.

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 registry reports zero serious adverse events and zero other adverse events in each listed safety group. The groups are described separately for participants in the observation arm, treatment group, and control group, and for prosthetists in the treatment and control groups. The corresponding at-risk counts are 17, 16, 16, 8, and 9, respectively. These safety denominators are separate from the outcome-specific denominators for the comfort endpoint.

These entries mean that no events were recorded in the listed categories for the groups and periods represented in the registry. They do not establish that no event could occur, and they do not show whether all possible adverse outcomes were actively assessed or reported. The registry record does not provide further detail on adverse-event definitions, collection procedures, severity grading beyond the serious-versus-other categories, or the duration of safety follow-up. The safety figures should therefore be read as registry reporting, not as a comprehensive estimate of risk.

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

The registry results describe participant counts before and after socket modification and compare the frequency of a defined positive comfort change across study arms. In the experimental arm, the prosthetist could use bioimpedance information when considering modification; in the control arm, bioimpedance measurements were collected but withheld from the prosthetist. That contrast is the most direct comparison of interest for the proposed information-sharing approach.

The posted primary outcome does not establish that sharing bioimpedance data improves comfort, nor does it establish that it has no effect. The unadjusted treatment-versus-control p-value is 0.279, and the confidence interval is broad. The observation-arm comparison also has substantial uncertainty. The record therefore leaves meaningful uncertainty about the direction and size of the difference in the threshold-based comfort outcome.

The endpoint is not a direct measure of average comfort change. It counts participants who meet a specified positive-change rule and excludes those with a decrease or a score difference of less than 2. It does not show how much comfort changed for each participant, the average score in each arm, or whether other aspects of prosthesis use changed. The threshold may be useful as a simple classification, but it should not be confused with the full experience represented by a 0-to-10 rating.

The secondary outcomes offer additional perspectives, but their unadjusted nature and the lack of a reported multiplicity plan mean that isolated findings should not be treated as definitive. The registry record also lacks details about missing data and analysis populations, which further limits certainty. Overall, these are results from a completed study record that can inform further research questions; they are not a basis for individual clinical decisions or a substitute for a fuller report of methods and analyses.

17. Why This Trial Matters Statistically

This study raises a statistical question about information as part of an intervention. The bioimpedance device collects data, but the experimental strategy also involves communicating those data to the prosthetist. The relevant comparison is therefore not simply device versus no device: it is a decision process informed by bioimpedance information versus a process in which the information is collected but not shared. Distinguishing measurement from access to the measurement is important when defining the treatment contrast.

The outcome definition also illustrates a common trade-off. Turning a rating scale into a binary participant count makes a threshold-based result accessible, but sacrifices information about the size of score changes. Researchers and readers need to know precisely how “positive” or “significant” change is defined, because the term can otherwise be mistaken for a group-level statistical finding.

The study also illustrates why estimates and uncertainty matter more than a simple focus on whether a p-value crosses a threshold. With wide confidence intervals and modest outcome-specific denominators, the data do not tightly identify the size or direction of the primary contrast. A non-small p-value is not proof of no difference, and a nominal secondary p-value should be interpreted in the context of multiple outcomes.

Finally, the registry entry shows the value of transparent reporting. Details on masking, missing data, analysis populations, multiplicity, and the original sample-size rationale would help readers judge how the reported comparisons were produced and how firmly they can be interpreted. Their absence does not invalidate the posted counts, but it limits the strength of conclusions that can be drawn from them.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The outcome denominators are limited, and the primary confidence intervals are wide. This leaves substantial uncertainty about the treatment-versus-control contrast and makes the observed proportions sensitive to a small number of outcome classifications. The overall enrollment figure does not resolve this limitation because the primary endpoint has its own arm-specific denominators, and the record does not explain why they differ from the enrollment figure.

The primary endpoint is a thresholded count rather than a continuous summary of score change. It omits the magnitude of changes and treats participants near the cutoff differently, while grouping all qualifying positive changes together. The registry does not report the rationale or validation for the 2-point rule, or the distribution of the underlying comfort scores.

The trial has a sequential design with an observation component and a randomized component, but the registry provides limited detail about how the stages were linked and how conclusions drawn from Arm 1 informed the experimental arm. The record does not describe randomization procedures, masking implementation, baseline comparability, eligibility criteria, participant characteristics, or whether any differences in practitioner behavior affected the outcome.

Analysis limitations include the absence of a reported statistical analysis plan, multiplicity procedures, analysis populations, and missing-data methods. The record does not describe the extent of missing outcome data or provide sensitivity analyses. Although several secondary domains are listed, detailed numerical results are not available in the registry entry for every listed domain. These reporting gaps, together with the exploratory nature of unadjusted secondary comparisons, limit the breadth and firmness of interpretation.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Bioimpedance as a Diagnostic Tool for Assessing the Need for Socket Modification in Transtibial Amputees — NCT03164356.
• Registry record last updated 2023-05-03; status last verified 2023-04.
• Results first posted 2022-04-22.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed randomized, single-masked study with a sequential model, evaluating whether bioimpedance monitoring could inform socket-modification decisions for people with transtibial amputation. The primary outcome counts participants meeting a defined positive socket-comfort change after modification. Posted primary comparisons show substantial uncertainty, with wide confidence intervals and unadjusted p-values of 0.973 for Arm 1 versus control and 0.279 for treatment versus control.

The record also lists secondary outcomes across satisfaction, ambulation, residual-limb health, prosthesis-related measures, communication, and socket modification. One secondary comparison has an unadjusted p-value of 0.045; multiplicity handling is not reported. Safety entries list no serious or other adverse events in the reported groups. Missing-data methods, analysis populations, the original sample-size justification, and detailed analysis procedures are not reported in the registry record.