Infracalcaneal Peppering Injection Technique for Chronic Plantar Fasciitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Infracalcaneal Peppering Injection Technique for Chronic Plantar Fasciitis (NCT05868577), a randomized phase 1 study. The primary outcome is Visual Analog Scale Score - General Heel Tenderness.

2. Clinical Question

The central clinical question can be framed as whether the injection strategies are being compared in people with chronic plantar fasciitis, and what outcome is available to assess that comparison. The registry record identifies the two injection regimens and a randomized, double-blind, parallel-group design. However, the primary outcome result posted is at baseline. A baseline comparison describes the groups before the outcome could reflect effects of the assigned injections; it is not an estimate of a treatment effect over follow-up.

The registry’s brief summary notes that corticosteroid injection may be used for short-term pain relief and describes potential risks. Those statements provide context for the trial, but the posted primary result does not establish a benefit or harm attributable to either study injection. The registry record does not report a post-treatment primary endpoint result, a protocol rationale for choosing this baseline measure as the primary outcome, or a primary analysis plan.

3. Trial Design

The registry identifies this study as a randomized, double-blind, parallel-group clinical trial of infracalcaneal peppering injection techniques for chronic plantar fasciitis. The listed phase is Phase 1. Wake Forest University Health Sciences is named as the sponsor. Enrollment is listed as 41, and the status is completed.

The two arms differed in injectate. One received corticosteroid with local anesthetic (CSI/LA); the other received local anesthetic with saline (LA/Saline). Both arm descriptions refer to an infracalcaneal needle peppering approach. The procedural text available in the registry is cut off before the full description is complete, so additional details of delivery are not reported in the registry record.

The registry lists the study start as 2023-10-18 and primary completion as 2024-09-18. These dates describe the registered trial timeline; they do not establish when particular outcome assessments were completed. The primary outcome is listed at baseline, while the posted secondary Exit Survey Score is listed at Week 12.

The record lists 21 participants for the CSI/LA baseline primary outcome and 20 for the LA/Saline baseline primary outcome. These outcome counts match the listed enrollment of 41, but the registry does not provide a participant flow account or explain whether any participants were excluded from particular analyses. The Week 12 Exit Survey Score has 15 participants in each arm. Reasons for the lower outcome counts are not reported in the registry record.

Randomization and double masking are registered design features, but details such as sequence generation, allocation concealment, who was masked, and how masking was maintained are not reported in the registry record. The planned sample-size justification, original power assumptions, and detailed statistical analysis plan are also not reported in the registry record. The presence of posted outcome summaries should therefore be distinguished from a complete account of the trial’s prespecified design and analysis.

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:

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 Visual Analog Scale Score - General Heel Tenderness, measured over Baseline.

The primary endpoint is the Visual Analog Scale Score for General Heel Tenderness. The registry describes a paper scale on which a participant places a mark to rate general heel pain. It defines a range from 0 to 100 and gives anchors ranging from no pain through mild, moderate, and extreme pain to the worst pain imaginable. The measure is reported as a mean with a standard deviation, so the posted summary describes the average score and the spread of scores among participants in each arm.

A participant-rated scale is used to capture a person’s own assessment of pain, rather than relying only on an observer’s rating. General heel tenderness is relevant to the condition being studied, and a numerical scale can summarize responses across participants. In general, such a scale makes the outcome easier to describe and compare, while the individual mark still represents a subjective report.

The registry lists the primary measure at baseline. That timing matters for interpretation: a baseline score describes the starting measurement, not a response following injection. The posted means therefore characterize the groups at baseline. The registry record does not report a later primary VAS result, a change score, or a prespecified comparison of post-injection scores. It also does not report a rationale for selecting baseline general heel tenderness as the primary endpoint.

7. Results Posted in the Registry

• Local Anesthetic (LA)/Saline Injection: mean 47.50 versus 46.70 on control; difference 0.80 (95% CI -10.53 to 12.13), standardized effect d = 0.04; z-test p = 0.890.

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.

Exit Survey 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:
  • Local Anesthetic (LA)/Saline Injection: mean 9.60 versus 8.80 on control; difference 0.80 (95% CI -0.18 to 1.78), standardized effect d = 0.59; z-test p = 0.109.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Local Anesthetic (LA)/Saline Injection and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists six secondary outcome measures, including an Exit Survey Score, exercise completion, heel pressure threshold scores, and heel tenderness scores for symptomatic and asymptomatic feet. Numerical results are posted for the Exit Survey Score at Week 12. Results for the other listed secondary outcomes are not reported in the registry record. The amount of outcome information available is therefore limited relative to the range of measures named.

The secondary outcome information should be considered separately from the primary baseline VAS comparison. The Exit Survey Score is a different measure and is assessed at a later time. It cannot be treated as a follow-up version of the primary endpoint, nor does it provide a post-treatment primary VAS result. The secondary results can add descriptive context about outcomes recorded in the trial, but they do not change what the primary result measures or when it was taken.

In general, secondary analyses are often less definitive than a prespecified primary analysis because they may involve multiple outcomes, time points, or comparisons. If many statistical tests are conducted, some results can appear noteworthy by chance even when there is no underlying difference. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Accordingly, unadjusted secondary results carry less weight than a clearly specified primary analysis, especially when the full analysis plan and results for other listed outcomes are not reported.

The overall pattern is best described as incomplete rather than as consistent or inconsistent across all secondary endpoints: most listed measures lack posted numerical results in the registry record. The available secondary outcome cannot resolve the absence of a post-injection primary heel-tenderness result. It also cannot support broad conclusions across all the secondary measures.

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

• Exit Survey Score
• Number of Completed Exercises
• Heel Pressure Threshold Score - Symptomatic Foot
• Heel Pressure Threshold Score - Asymptomatic Foot
• Heel Tenderness Score - Symptomatic Foot
• Heel Tenderness Score - Asymptomatic Foot

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports continuous outcomes as means and standard deviations. A mean describes the average observed score in an arm. A standard deviation describes how spread out individual scores are around that arm’s mean; it is not the same as the uncertainty around the mean or around a group difference. The baseline VAS is measured on a 0–100 scale, so the mean and standard deviation provide a compact description of participants’ reported heel tenderness in each group.

What does a mean difference describe?

For the primary baseline comparison, the reported contrast is LA/Saline minus CSI/LA. Its estimate is 0.8 points. A positive value means the LA/Saline group’s observed mean score is numerically higher in this contrast. Because the scale’s higher anchors indicate more severe pain, the numerical direction can be described, but this contrast remains a baseline difference, not a change after injection. The confidence interval runs from -10.53 to 12.13, so the data are compatible with both negative and positive baseline differences.

In general, a mean difference is expressed in the same units as the outcome. That makes it interpretable in relation to the scale, but interpretation still depends on timing and on whether a clinically meaningful difference has been defined. A threshold for clinical importance is not reported in the registry record. No new threshold should be inferred from the observed score or from the interval.

What does the standard deviation add?

The arm-level standard deviations describe variability among participants. In general, greater variation makes the group mean less precise when participant counts are limited, while a smaller standard deviation indicates scores are more tightly clustered around the mean. Standard deviations alone do not show the range of individual observations, the shape of the score distribution, or whether unusual values are present. Those details are not reported in the registry record.

The comparison also reports a pooled standard deviation and a standardized effect-size estimate. In general, standardizing a mean difference by a measure of spread expresses the contrast in standard-deviation units. That can help compare effects measured on different scales, but it removes the original score units and depends on the variability used. The reported standardized estimate is small in magnitude for the baseline comparison; it remains a summary of the baseline contrast, not a treatment effect. The registry record does not report a clinically meaningful threshold for this standardized measure.

How should the p-value be read?

The primary comparison has an unadjusted p-value of 0.89. In general, a p-value describes how unusual results at least as incompatible with a specified null model would be if that model and the analysis assumptions were correct. It does not give the probability that the null hypothesis is true, the probability that the result will replicate, or the size of a clinical effect. A p-value also does not repair limitations in endpoint timing or missing details about the analysis plan.

The term unadjusted means the reported p-value is not presented as corrected for multiple comparisons. It should be considered alongside the effect estimate, confidence interval, outcome timing, and analysis context rather than treated as a stand-alone verdict. The registry does not report a multiplicity strategy or a detailed primary analysis plan, so it is not possible to determine from the record whether this p-value reflects a prespecified analysis.

What does a confidence interval convey?

In general, a confidence interval gives a range of values that are reasonably compatible with the observed data under the method used. Its width reflects precision: a narrower interval indicates more precision, while a wider interval indicates less. The primary interval spans negative and positive differences and includes zero. That means the posted data do not isolate a single direction of baseline difference with precision. It does not mean that all values in the interval are equally likely or that values outside it are impossible.

The interval’s interpretation also depends on the model and calculation used. The registry record does not report all implementation details of the primary analysis. The arm summaries and comparison are sufficient to describe the posted result, but they do not replace a full statistical analysis plan, participant-level data, or details of how missing observations were handled.

Why does over-dispersion matter in general?

Over-dispersion occurs when observed variability is greater than the model assumes. In general, if a model underestimates variability, standard errors may be too small and confidence intervals too narrow, making results appear more precise than they are. If a model accounts for variability appropriately, uncertainty estimates are better aligned with the data. This general issue can matter for outcomes that do not follow a simple normal pattern or for counts with more variability than expected. The posted primary outcome is continuous, and the registry does not report an over-dispersion assessment or a distributional diagnostic. No claim about over-dispersion in this trial can be made from the registry record.

For the sample-size planning illustration, the registry states that the calculation uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It uses a stated fraction of the observed effect as the effect to detect. In general, this kind of calculation estimates how many participants per arm would be needed under those assumptions to achieve a chosen probability of detecting an effect if that effect were present. It is not evidence about the design assumptions originally chosen for this trial, which are not reported in the registry record.

The planning calculations use the observed effect as their reference. Because an observed effect from a small trial can be uncertain, planning directly from it is only illustrative. The calculations do not establish that the trial was adequately powered, and they are not observed power. The registry record does not report the original sample-size justification, a target effect, or the rationale for enrollment of 41 participants.

11. Confidence Intervals and Precision

The primary baseline mean difference is 0.8 points for LA/Saline versus CSI/LA. Its confidence interval is -10.53 to 12.13. The interval includes zero and extends to differences in either numerical direction. It therefore does not precisely identify a single direction of baseline imbalance. The interval should be read as uncertainty around the baseline contrast, not as an interval for an effect of injection over follow-up.

In general, a confidence interval is a range generated by a statistical method to communicate uncertainty in an estimate. A narrower interval indicates greater precision; a wider interval indicates less precision. The primary interval is wide relative to the point estimate. It allows for baseline mean differences that are meaningfully separated from the point estimate, but the registry does not report a threshold for what size difference would be clinically important. It would be inappropriate to label values inside the interval clinically meaningful or unimportant without such a benchmark.

The two arm summaries are based on 21 and 20 participants, respectively. With limited participant counts, the estimate can remain uncertain even when the observed group means are close. The confidence interval is more informative about that uncertainty than the p-value alone. Still, it does not describe individual participants’ scores, account for unreported features of the data, or show the result of an adjusted model.

The interval is also tied to the analysis and outcome as posted. Since the primary endpoint is listed at baseline, precision around this contrast does not answer how precisely a post-injection treatment effect was estimated. A post-treatment primary comparison or a change-from-baseline analysis is not reported in the registry record. The interval cannot be repurposed to answer that missing question.

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 planning figures are participants per arm, not total events. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The original trial design assumptions and its own sample-size justification are not reported in the registry record; these figures are a planning illustration based on the observed comparison.

The 80% power column represents the number of participants per arm estimated to give an 80% chance of detecting the specified effect under the stated assumptions, if that effect is present. The 90% power column uses a higher target chance of detection and therefore calls for more participants per arm under the same planning framework. These are planning probabilities, not probabilities that the trial result is correct and not a measure of the chance that a treatment works.

Rows using smaller fractions of the observed effect require more participants because smaller differences are harder to distinguish from random variation. For the primary comparison, the planning figures rise as the assumed effect fraction is reduced. The same relationship is represented by the sample-size curve: smaller effects require a larger planned sample under these assumptions. The planning figures do not show that this trial enrolled enough participants for a particular target or that its original design used these assumptions. This is not observed power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.800; pooled standard deviation σ = 18.538.
2. n = 2 × (1.96 + 0.842)² × 18.538² / 0.800² = 8,428.9, rounded up to 8,429 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.799999999999997                      # observed difference in means
sigma <- 18.5377715586036                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(5868577)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 8,429 (80% power), 11,284 (90% power)
 75% of observed effect: n per arm = 14,985 (80% power), 20,061 (90% power)
 50% of observed effect: n per arm = 33,716 (80% power), 45,136 (90% power)
power.t.test: 8429.9 
Simulated power at n = 8,429 per arm: 0.803 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcomes, with 21 outcome measures noted overall and six secondary outcomes named. When a study assesses multiple outcomes or makes multiple comparisons, the chance of obtaining at least one apparently notable result by chance can increase. Statistical approaches can address this, for example by controlling a family-wise error rate or by specifying a hierarchy in which certain outcomes are tested before others. These are general approaches; the registry record does not report which approach, if any, was planned for this trial.

The posted p-values are described as unadjusted. The record does not report a multiplicity adjustment, a prespecified outcome hierarchy, or a detailed analysis plan that would establish which tests were primary and which were exploratory. Without those details, secondary results should be interpreted cautiously and not as independent confirmation of a treatment effect. The registry does not report whether any interim analyses were planned or conducted.

Missing-data handling is also not reported in the registry record. The primary baseline outcome has 21 and 20 participants in the two arms, while the Week 12 Exit Survey Score has 15 participants in each arm. The record does not explain why the Week 12 counts differ from enrollment, whether all randomized participants were expected to complete the measure, or whether an imputation method or other missing-data strategy was used. The registry does not provide participant flow details that would clarify exclusions, withdrawals, or outcome availability.

The analysis population is not reported in enough detail to identify whether the posted summaries are based on all randomized participants, participants who received the assigned injection, or a subset with available outcome data. In general, intention-to-treat analysis retains participants in their randomized groups, whereas per-protocol or as-treated analyses use other membership rules. These choices can affect interpretation, particularly if participants do not complete follow-up or do not receive assigned procedures. No such analysis population can be assumed from the posted summaries.

These gaps do not invalidate the descriptive statistics, but they limit evaluation of whether the posted analyses followed a prespecified plan and how representative the analyzed participants are of all enrolled participants. The registry record does not report the original sample-size rationale, missing-data plan, interim analysis plan, or full multiplicity strategy.

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.

Most frequent non-serious adverse event terms

The registry reports serious adverse events in 0 of 21 participants in the CSI/LA arm and 0 of 20 participants in the LA/Saline arm. Deaths are listed as 0 in both arms. These figures describe the recorded serious adverse event and death counts for the reported groups; they do not show that the risk of serious events is zero.

The record also lists other adverse events affecting 2 of 21 participants in the CSI/LA arm and 2 of 20 participants in the LA/Saline arm. The registry does not provide event terms for these entries in the information summarized, so their nature, severity, timing, and relation to the injections are not reported in the registry record. No serious adverse event terms are listed.

In general, adverse-event counts are interpreted in light of how events were defined, collected, and attributed. The registry record does not report those details. With the listed group sizes, the counts are descriptive and do not establish that the arms have equal safety profiles or that an event cannot occur. The safety figures should not be taken as a prediction for an individual or as medical advice.

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

The posted primary result shows similar average general heel-tenderness VAS scores between the two groups at baseline: 46.7 in the CSI/LA arm and 47.5 in the LA/Saline arm. The estimated baseline mean difference is 0.8 points, with a confidence interval from -10.53 to 12.13 and an unadjusted p-value of 0.89. These statistics describe the observed baseline groups and the uncertainty around their difference.

They do not show whether either injection strategy changed heel pain, whether one strategy was better after injection, or whether the strategies were equivalent. The primary endpoint is listed at baseline, and a post-injection primary outcome result or change-from-baseline comparison is not reported in the registry record. A baseline similarity result is not a treatment-effect result.

The posted Week 12 Exit Survey Score is a secondary measure, not the primary heel-tenderness VAS. Other listed secondary outcomes do not have numerical results reported in the registry record. The secondary information therefore cannot be used to make a comprehensive judgment about all outcomes or to compensate for the missing post-injection primary result.

The registered design is randomized, double-blind, and parallel-group, but some implementation and analysis details are not reported. In general, randomization is intended to support comparisons between assigned groups, while masking can reduce some forms of bias. These design labels alone do not resolve missing outcome information or establish that every analysis followed a prespecified plan.

The registry’s background description mentions potential short-term relief from corticosteroid injection and possible risks. The posted data do not establish that either injection works or does not work, and they do not support medical advice. They establish only the reported baseline summaries, the available secondary outcome information, and the adverse-event counts recorded in the registry. Readers should distinguish that limited descriptive record from a complete account of treatment outcomes.

17. Why This Trial Matters Statistically

This trial is statistically notable because its primary endpoint is recorded at baseline. That timing makes the posted primary comparison a description of starting scores rather than a direct test of the injection strategies after assignment. Recognizing the distinction between baseline balance and a treatment-effect estimate is essential when reading randomized-trial results.

The comparison also illustrates why point estimates, confidence intervals, and p-values should be considered together. The mean difference is small in relation to the scale, but its interval includes zero and extends in both directions. The p-value alone cannot establish that groups are equivalent, and the confidence interval does not show how participants’ scores changed after injection. Interpretation depends first on whether the outcome answers the clinical question.

The record includes a registered randomized, double-blind, parallel-group design and a completed status, but does not report a full statistical analysis plan, the original sample-size rationale, missing-data handling, or multiplicity procedures. Those omissions make it harder to assess how the posted summaries relate to the prespecified trial aims. They also show why registration fields and posted results should be read with attention to what is and is not documented.

Finally, the secondary outcome list is broader than the numerical results available in the registry record. The reported Week 12 Exit Survey Score supplies some additional information, but the other listed secondary measures have no results reported. This is a reminder that a list of planned or registered outcomes is not the same as a full set of interpretable results. Statistical conclusions should be proportionate to the data actually posted.

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.

A central limitation is that the primary outcome result is reported at baseline. The registry does not report a post-injection primary VAS score or a change-from-baseline analysis. Consequently, the primary comparison does not estimate the outcome of the assigned injection strategies over follow-up.

The registry lists enrollment as 41, and the primary outcome summaries include 21 participants in one arm and 20 in the other. The Week 12 Exit Survey summaries include 15 participants in each arm. Reasons for the different counts, participant flow, and missing-data handling are not reported in the registry record. This limits assessment of follow-up completeness and the population represented by the secondary results.

The registry names six secondary outcomes, but numerical results are reported for the Exit Survey Score only. Results for the other listed measures are not reported in the registry record. The record also does not report a multiplicity strategy, detailed statistical analysis plan, analysis population, interim analysis plan, or original sample-size justification. These omissions restrict evaluation of prespecification and the uncertainty attached to the secondary findings.

The procedural descriptions for both arms are incomplete in the registry record. The record identifies the injection approach and injectates, but does not provide the complete technique description. It also does not report participant characteristics that would permit assessment of how closely the enrolled group represents particular clinical populations. These are limits on the detail available for interpreting and reproducing the trial.

Safety reporting is limited to counts: serious adverse events and deaths are listed as zero in both groups, and other adverse events are listed as two in each group. Event terms and attribution details are not reported in the registry record. The available counts therefore do not permit a detailed characterization of the events or a strong comparison of safety between arms.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Infracalcaneal Peppering Injection Technique for Chronic Plantar Fasciitis — NCT05868577.
• Registry record last updated 2025-10-30; status last verified 2024-03.
• Results first posted 2025-10-30.
• 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

NCT05868577 is a completed, randomized, double-blind, parallel-group Phase 1 trial sponsored by Wake Forest University Health Sciences. The registry lists 41 participants enrolled and identifies chronic plantar fasciitis as the condition. The study compares infracalcaneal peppering injections of corticosteroid with local anesthetic against local anesthetic with saline.

The primary outcome is a baseline 0–100 Visual Analog Scale Score for General Heel Tenderness. The posted baseline mean difference for LA/Saline versus CSI/LA is 0.8, with a 95% confidence interval from -10.53 to 12.13 and an unadjusted p-value of 0.89. Because the endpoint is recorded at baseline, the result is not a post-injection treatment comparison.

The registry posts a Week 12 Exit Survey Score as a secondary outcome; results for the other listed secondary measures are not reported in the registry record. Serious adverse events and deaths are listed as zero in both arms. The original sample-size justification, detailed analysis plan, and missing-data handling are not reported in the registry record.