Compression Treatment Effects on Complications and Healing of Achilles Tendon Rupture: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Compression Treatment Effects on Complications and Healing of Achilles Tendon Rupture (NCT01317160), a randomized na study. The primary outcome is Venous Thromboembolic Events (VTE).

2. Clinical Question

The registry describes a prospective randomized study of postoperative care following acute Achilles tendon rupture. Its primary question concerns venous thromboembolism (VTE) at two weeks. The planned assessment used compression duplex ultrasound (CDU), with ultrasound assessors masked to treatment allocation. The endpoint description includes deep vein thrombosis (DVT), isolated calf muscle vein thrombosis, symptomatic DVT or isolated calf muscle vein thrombosis, and symptomatic pulmonary embolism detected by computer tomography.

The comparison is between two different approaches to early postoperative immobilization: IPC with an orthosis and routine plaster-cast treatment. The study description states that IPC ended after two weeks and that both groups were then immobilized in an orthosis until the six-week follow-up. A separate study objective concerned tendon healing, assessed at two weeks by microdialysis and markers for tendon repair. Functional outcomes were also planned for one year after surgery.

The registry record reports a primary VTE outcome at two weeks and a further VTE outcome at six weeks. The central statistical question is about the contrast between groups at the prespecified primary time point, while the later and other outcomes provide additional, distinct evidence. The registry record does not report a detailed protocol rationale for selecting the primary measure or the original assumptions used to plan the study size.

3. Trial Design

This was a completed, randomized, double-masked, parallel-group study sponsored by Karolinska University Hospital. The registry lists an enrollment of 150. The record gives a start date of 2011-03 and a primary completion date of 2015-08. Phase is listed as not applicable.

The brief study description allocates 75 patients to IPC and 75 to treatment as usual. In the IPC group, calf compression was used during two weeks of immobilization in an orthosis. The plaster-cast group received two weeks of conventional lower-limb plaster immobilization in 30 degrees of plantarflexion. The description states that after the first two weeks both groups were to use an orthosis until follow-up at six weeks. The registry identifies the IPC intervention as a device, specifically an Aircast VenaFlow Elite System, and identifies the orthosis as an Aircast XP Walker.

The study had several outcome domains. The first focused on VTE, with the primary assessment at two weeks and a further assessment at six weeks. The study description also identifies tendon-healing measurements at two weeks and functional outcomes at one year. Listed functional measures include the Achilles tendon Total Rupture Score, Physical Activity scale, Foot and Ankle Outcome Score, and EQ-5D. The registry lists additional secondary outcomes involving heel-rise muscular endurance, patient-reported outcomes, microdialysis, and time from injury to surgery.

The analyzed group sizes differ from the planned group sizes. For the primary two-week outcome, the posted results include 71 participants in the plaster-cast group and 67 in the IPC group. The primary endpoint description says that exposure to less than ten hours of IPC was defined as non-compliance and that two patients were withdrawn on this basis; it also states that the treatment group comprised 67 patients at final analysis. A complete account of participant flow and the analysis populations is not reported in the registry record.

The record identifies the allocation as randomized and masking as double, but further details of sequence generation, allocation concealment, and exactly which study roles were masked are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Non-compliance was defined by exposure to less than ten hours of IPC. Therefore, two patients were withdrawn on this basis and the treatment group comprised 67 patients at final analysis.

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 Venous Thromboembolic Events (VTE), measured over 2 weeks.

The primary endpoint is the number of participants with VTE events at two weeks after surgery. It is a binary outcome at the participant level: each participant is classified according to whether an event was detected, and the group results are presented as event counts and denominators. The registry endpoint description includes DVT detected by compression duplex ultrasound, isolated calf muscle vein thrombosis detected by CDU, symptomatic DVT or isolated calf muscle vein thrombosis detected by CDU, and symptomatic pulmonary embolism detected by computer tomography.

CDU screening is used in this study to identify thrombosis through imaging, including events that may not have been identified solely from symptoms. The registry description says the two ultrasonographers assessing the two-week scans were masked to treatment allocation. Masking of assessors is relevant because knowledge of group assignment could otherwise influence how an imaging assessment is interpreted. The registry record does not report further operational detail on how the event categories were combined or adjudicated.

The endpoint matches the study's first stated objective: comparing VTE incidence after two postoperative treatment approaches. It should be interpreted as the observed proportion of participants meeting the endpoint definition in each analyzed group at the specified time, rather than as a direct measure of tendon healing or longer-term function. Those are separate study domains. The two-week time point also matters: the study description says the IPC intervention ended then, and both groups continued in an orthosis until the six-week follow-up.

7. Results Posted in the Registry

• Intermittent Pneumatic Compression (IPC): 20.9% (14/67) versus 36.6% (26/71) on control; risk difference -15.7 percentage points (95% CI -30.6 to -0.9), risk ratio 0.57 (0.33–1.00); unadjusted two-proportion z-test p = 0.042.

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.

Venous Thromboembolic Events (VTE)

• 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:
  • Intermittent Pneumatic Compression (IPC): 52.2% (36/69) versus 47.9% (34/71) on control; risk difference 4.3 percentage points (95% CI -12.3 to 20.8), risk ratio 1.09 (0.78–1.52); unadjusted two-proportion z-test p = 0.612.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intermittent Pneumatic Compression (IPC) and the control. The interval gives the range of effects that remain compatible with the data.

Patient-reported Outcome

• 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:
  • Intermittent Pneumatic Compression (IPC): mean 77.80 versus 78.00 on control; difference -0.20 (95% CI -6.76 to 6.36), standardized effect d = -0.01; z-test p = 0.952.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intermittent Pneumatic Compression (IPC) and the control. The interval gives the range of effects that remain compatible with the data.

Microdialysis

• 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:
  • Intermittent Pneumatic Compression (IPC): mean 3.47 versus 2.05 on control; difference 1.42 (95% CI 0.41 to 2.43), standardized effect d = 1.08; z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Intermittent Pneumatic Compression (IPC) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes span different domains and time points: later VTE assessment, patient-reported status, and a biological measure of tendon repair. They do not form a single common endpoint, and their values cannot be combined into one overall treatment effect. Taken together, the available results present a mixed pattern rather than a consistent direction across all measured outcomes. The two-week primary endpoint remains the main basis for interpreting the study's central VTE question; secondary findings address related but distinct questions.

The six-week VTE comparison is a later assessment of the same general event domain, but it does not reproduce the two-week pattern in the recalculated group contrast. The one-year patient-reported outcome and the two-week microdialysis result concern different constructs, measured on different scales and in smaller analysis groups. The registry lists functional muscular-endurance testing and time from injury to surgery among secondary outcomes, but numerical results for those outcomes are not reported in the registry record. The registry also names several instruments for one-year function, while the posted patient-reported result is presented as a single score; further scale-specific details are not reported in the registry record.

Unadjusted secondary comparisons carry less weight than a prespecified primary analysis for several reasons. Multiple outcomes and time points create more opportunities for apparently notable results to arise by chance. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary endpoints. Secondary analyses can also be more vulnerable to incomplete outcome data, especially when their analyzed sample sizes differ from the primary analysis. The posted results should therefore be treated as exploratory or supportive evidence unless a fuller analysis plan establishes a different role.

These secondary findings can help describe whether the study observed signals across distinct aspects of recovery, but they do not confirm or negate the primary result. The record does not report a single prespecified summary that combines VTE, tendon repair, and functional outcomes, so each domain should remain separately interpreted.

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

• Functional Outcome - Muscular Endurance Tests (Heel-rise)
• Venous Thromboembolic Events (VTE)
• Patient-reported Outcome
• Microdialysis
• Time From Injury to Surgery

9. Statistical Interpretation

10. Statistical Methods Explained

The analyses include binary comparisons for VTE and continuous comparisons for score and microdialysis outcomes. The registry reports chi-squared and logistic-regression analyses for the primary outcome, while the effect estimates labelled as recalculated are simple, unadjusted comparisons derived from the posted group summaries. The registry record does not report a complete statistical analysis plan or all details of the sponsor's models.

What does a risk difference describe?

A risk difference compares the proportions of participants with an event in two groups. It is expressed as the event proportion in the intervention group minus the event proportion in the comparator group. A negative value therefore indicates a smaller observed event proportion in the intervention group, while a positive value indicates a larger one. The recalculated primary estimate is a risk difference, so it is directly expressed on the absolute difference scale. It is not an adjusted estimate unless an adjustment is explicitly described; no such adjustment is part of the recalculated comparison.

The underlying data are counts of participants with events and the number assessed in each group. The number of events alone is not enough to compare groups fairly when their denominators differ. The denominators are therefore essential to interpreting the event proportions. The registry's primary result also includes an odds ratio from logistic regression. An odds ratio compares event odds, not event proportions, and its numerical value depends on which group is used as the reference and how the outcome is coded. It is not numerically interchangeable with a risk difference.

How should the chi-squared result be understood?

A chi-squared test evaluates whether the observed distribution of event and non-event counts differs between groups under the test's assumptions. Its p-value quantifies how unusual a result at least as discrepant as the observed one would be under a statistical model in which there is no group association. A p-value is not the probability that the null hypothesis is true, and it does not measure the size or importance of a difference. The registry reports this method for both the two-week and six-week VTE comparisons.

Logistic regression models the relationship between a binary outcome and group assignment on the log-odds scale. The registry reports an odds ratio and interval from a logistic-regression analysis for the primary endpoint. Whether the reported model adjusted for other variables, and which variables were used if it did, are not reported in the registry record. The differing group sizes and treatment-compliance information make it especially important not to assume that this reported model and the simple recalculation use identical analysis populations or specifications.

What do the continuous-outcome comparisons measure?

For a continuous outcome, a mean difference compares the average values in the two groups. The posted one-year patient-reported outcome and the two-week microdialysis measure are reported as means with standard deviations. A standard deviation describes the spread of individual observations around a group mean; it is not the uncertainty in the mean itself. The recalculated comparisons use the posted group means, standard deviations, and sample sizes. Their confidence intervals express uncertainty around a difference in means, not the range within which individual participant values fall.

In general, a continuous measure may be analyzed using a model that accounts for its distribution and design features. The registry does not report the sponsor's analyses for the posted continuous outcomes. The simple recalculations should therefore be read as descriptive, unadjusted comparisons, not as a reconstruction of an unavailable sponsor model.

Why do the confidence intervals matter?

In general, a confidence interval gives a range of effect estimates that are reasonably compatible with the observed data under the statistical method used. It describes uncertainty about an estimated group contrast. A narrow interval indicates greater precision than a wide interval, while an interval spanning the no-difference value indicates that the data are compatible with both a difference and no difference at the stated confidence level. This is not a probability statement about the true effect after observing the data.

For binary outcomes, the no-difference value on the risk-difference scale is zero. For a mean difference it is also zero; for a ratio measure such as an odds ratio it is one. The posted intervals should be read on their own scales. They do not account automatically for all uncertainty arising from missing observations, outcome measurement, analysis-population choices, or multiple testing.

What does recalculated mean?

A recalculated estimate is a simple unadjusted re-analysis from the posted summary statistics. It is useful for placing group counts or means on a common effect scale and for illustrating the precision of those summaries. It does not replace the sponsor's analysis. Here, the record flags a discrepancy for the primary result, so the sponsor's own analysis takes precedence. The numerical contrast between a recalculated risk difference and a sponsor-reported odds ratio should not be treated as proof that one can be transformed exactly into the other without the underlying model details.

Finally, statistical significance is not a synonym for clinical importance. A p-value can be affected by sample size and variability, and it does not capture the consequences of an outcome to participants. The registry record does not report a threshold for a clinically important difference, a complete account of model diagnostics, or the detailed methods used for handling all analysis decisions. Those omissions constrain how much can be inferred from the posted tests alone.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate is determined by the observed data. The primary two-week recalculated risk difference is -0.157, with a 95% confidence interval from -0.306 to -0.009. The interval is entirely below zero, but it extends from a relatively small negative difference to a much larger negative difference. Thus, the direction of the unadjusted estimate is more clearly determined than its exact magnitude. The sponsor's own analysis reports an odds ratio with a 95% confidence interval from 1.25 to 6.32. That interval is on a different scale and comes from the sponsor's logistic-regression analysis.

For six-week VTE, the recalculated risk difference is 0.043, with a 95% confidence interval from -0.123 to 0.208. This interval spans zero and includes estimates in either direction. It therefore indicates substantial uncertainty about the direction and size of the group contrast. The registry's chi-squared p-value is also reported separately; the record does not explain the difference between that test and the recalculated test result.

For the one-year patient-reported outcome, the recalculated mean difference is -0.2, with a 95% confidence interval from -6.759 to 6.359. The interval includes zero and permits a range of possible differences in either direction. For the two-week microdialysis outcome, the recalculated mean difference is 1.42, with a 95% confidence interval from 0.409 to 2.431. The interval is above zero, but the measurement is based on a smaller analyzed group than the VTE comparison.

Confidence intervals do not resolve differences in study design, endpoint interpretation, or analysis population. They also do not show whether an effect is clinically important; the registry record does not report a clinical-importance threshold for these comparisons. Precision is affected by the amount of information in the analysis, including the number of participants and the variability or frequency of the measured outcome. Results with different endpoints and time points should not be compared solely by the widths of their intervals.

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 calculations are planning illustrations based on the observed effect, not the study's original design calculation. For the binary VTE outcomes and continuous outcomes presented in the planning section, the figures are participants per arm. The general calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect equal to the stated fraction of the observed effect. The trial's own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect if that effect were the true one, under the listed planning assumptions. The 90% power column gives the corresponding per-arm planning number for a 90% chance. These are design targets, not guarantees that a study of that size will produce a statistically significant result.

Rows that plan for 75% or 50% of the observed effect use smaller target effects than the row based on 100% of the observed effect. Smaller effects are harder to distinguish from random variation and therefore require more participants under the same assumptions. The very different planning figures across endpoints reflect differences in the estimated effects and, for continuous outcomes, the observed variability. A particularly small observed effect can imply a very large planning requirement when a future study is intended to detect a similarly small difference.

These figures are not observed power. They are forward-looking planning illustrations and should not be read as a retrospective measure of whether the completed study was adequately powered. For time-to-event tables, the planning values would represent total events, but the outcomes presented in this registry record are not time-to-event tables; the listed planning figures are per arm.

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 = 0.366; treatment proportion p₁ = 0.209; average p̄ = 0.288.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6401 = 1.2546.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6304 = 0.5305.
4. n = (1.2546 + 0.5305)² / (-0.1572)² = 128.9, rounded up to 129 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 <- 0.366197183098592                          # control proportion
p1 <- 0.208955223880597                          # 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(1317160)
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 = 129 (80% power), 173 (90% power)
 75% of observed effect: n per arm = 240 (80% power), 320 (90% power)
 50% of observed effect: n per arm = 558 (80% power), 746 (90% power)
power.prop.test: 128.9 
Simulated power at n = 129 per arm: 0.810 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports two sponsor analyses for the primary two-week VTE outcome: a chi-squared test with p = 0.042 and a logistic-regression odds ratio of 2.81, with a 95% confidence interval from 1.25 to 6.32 and p < 0.05. A simple unadjusted recalculation from the posted event counts gives a risk difference of -0.157 for IPC relative to routine plaster-cast care, with a 95% confidence interval from -0.306 to -0.009 and p = 0.042.

These estimates use different effect scales: a risk difference compares event proportions, while an odds ratio compares odds. The reported odds ratio also appears in the opposite numerical direction from the IPC-relative risk difference, but the registry record does not give sufficient coding and reference-group details to resolve that orientation or establish the exact reason for the discrepancy. It does not report whether the logistic model included covariates.

Because the record flags a discrepancy, the sponsor's own analysis takes precedence over the simple unadjusted recalculation. The recalculated result remains useful as a transparent comparison based on the posted counts, but it should not be presented as a correction to or replacement for the sponsor's reported analysis. For six-week VTE, the sponsor reports a chi-squared p-value of 0.737, while the simple recalculation gives p = 0.612; the record does not provide enough methodological detail to explain the difference.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcome domains and follow-up times, including VTE at two and six weeks, microdialysis at two weeks, and patient-reported outcomes at one year. It also lists heel-rise muscular endurance and time from injury to surgery as secondary outcomes. Testing several outcomes creates a multiplicity issue: even when no true differences exist, the chance of at least one apparently unusual result can increase as more comparisons are made. A multiplicity adjustment, prespecified hierarchy, or clearly stated exploratory strategy can help define how secondary findings should be interpreted. Such procedures are not reported in the registry record.

The record identifies a primary VTE endpoint at two weeks, but a complete statistical analysis plan is not reported in the registry record. Details about the prespecified test, covariate adjustment, subgroup analyses, interim analyses, and handling of protocol deviations are not reported in the registry record. The registry's double-masked designation and description of masked ultrasound assessors do not establish which other study personnel or analysts were masked.

Missing-data methods are also not reported in the registry record. The analyzed denominators vary by outcome: the primary two-week VTE result uses 71 participants in routine care and 67 in IPC; the six-week result uses 71 and 69; one-year patient-reported results use 64 and 55; and microdialysis results use 19 and 14. Differences in denominators indicate that the outcome analyses do not all include the same number of participants, but the reasons for all differences, the handling of missing outcomes, and any imputation procedures are not reported in the registry record.

The primary endpoint description states that exposure to less than ten hours of IPC was defined as non-compliance and that two patients were withdrawn on that basis, with 67 patients in the treatment group at final analysis. The registry does not provide a complete participant flow diagram or clearly identify all analysis populations. It is therefore not possible to determine from the registry record whether analyses followed intention-to-treat, per-protocol, or another population definition. These uncertainties matter because exclusions and missing observations can affect comparability between randomized groups.

16. Safety Results

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

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 adverse-event information lists zero serious adverse events among 71 participants at risk in the plaster-cast group and zero among 71 at risk in the IPC group. The registry does not list serious adverse-event terms. These entries describe the posted serious-event counts; they do not establish that every possible safety outcome was systematically assessed or reported in the same way.

For other adverse events, the registry reports 5 affected participants among 71 at risk in the plaster-cast group and 3 among 69 at risk in the IPC group. The record does not provide event descriptions or severity detail for these other events. Deaths are not reported in the registry record. The adverse-event denominators also differ from the primary VTE analysis denominators, so they should not be assumed to represent precisely the same analysis population.

Adverse-event counts are descriptive and do not, on their own, establish whether the groups differ in safety. The registry record does not report a statistical comparison for these figures, detailed event definitions, or the duration and completeness of adverse-event surveillance.

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

The posted results describe a randomized comparison of two postoperative treatment approaches and include a primary VTE assessment at two weeks. The unadjusted comparison based on the posted counts shows a lower observed event proportion in the IPC group at that time, and the registry's own primary analyses also report p-values below 0.05. However, the record flags a discrepancy between the sponsor's analysis and the simple recalculation. The sponsor's own analysis takes precedence, and the available registry entries do not fully explain the difference in effect measures or model specifications.

The findings do not establish that the same pattern continued at six weeks. The six-week comparison is imprecise and its interval includes differences in either direction. Other outcomes address patient-reported status and tendon-repair markers, not the primary VTE question. Their results should not be treated as direct confirmation of the primary endpoint, and the unadjusted secondary analyses warrant caution because multiplicity procedures are not reported.

Statistical evidence about a group contrast is not the same as evidence about clinical importance. The registry record does not report thresholds for a clinically important difference, nor does it provide enough detail to assess all potential sources of bias or uncertainty. The participant counts differ across outcome analyses, while full information about missing data and analysis populations is not reported in the registry record.

The results therefore support a limited statistical description: a two-week primary comparison with a reported group difference in the sponsor's analyses, alongside a flagged discrepancy with the simple recalculation; no similarly clear pattern in the later VTE comparison; and separate secondary results that require cautious interpretation. They do not by themselves establish a complete account of benefits, harms, tendon healing, or longer-term function.

18. Why This Trial Matters Statistically

This trial is statistically informative because it places an objectively assessed postoperative event outcome alongside a randomized treatment comparison. The primary endpoint uses imaging-based detection, and the registry describes masked ultrasound assessors. Those features are relevant to measurement: when outcome assessment is less influenced by knowledge of treatment assignment, the comparison may be less vulnerable to observer expectations. The record does not report all procedural details needed to judge the extent of that protection.

The study also illustrates why effect scale and analysis specification matter. The registry's sponsor-reported logistic-regression odds ratio and the simple recalculated risk difference address the same underlying outcome but are not interchangeable summaries. Their apparent discrepancy cannot be resolved from the information in the registry record. Reporting both the group counts and an effect estimate with an interval helps readers see the underlying data, while the flagged difference highlights the need for transparent analysis details.

The multiple time points and outcome domains make a further statistical lesson visible: a primary endpoint should be distinguished from secondary measures, and a later result should not automatically be treated as a replication of an earlier one. VTE, microdialysis, and patient-reported scores answer different questions. Their analysis groups also differ in size, so precision and potential missing-data concerns vary across outcomes.

Finally, planning calculations based on observed effects demonstrate how strongly future sample-size requirements depend on the effect targeted. Smaller target effects require larger studies under the same assumptions. Such calculations are useful for planning illustrations, but they are not the original study's design justification and are not a retrospective measure of power. The original assumptions are not reported in the registry record.

19. Limitations

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

Several trial-specific limitations affect interpretation of the posted results. First, the primary analysis presents a discrepancy: the sponsor-reported logistic-regression odds ratio and the simple unadjusted risk-difference recalculation are on different scales and cannot be reconciled fully from the registry record. The record does not provide the coding, reference-group, covariate, or model details needed to explain the difference. The sponsor's own analysis takes precedence, but the reporting limits independent evaluation of the estimate.

Second, the analysis denominators vary across the primary, later VTE, microdialysis, patient-reported, and adverse-event results. The endpoint description reports withdrawal of two IPC participants for exposure below ten hours and a final IPC analysis group of 67, but it does not explain all differences between planned enrollment and outcome-specific denominators. A complete account of participant flow, analysis populations, reasons for missing outcomes, and missing-data handling is not reported in the registry record.

Third, the registry record does not report the original sample-size assumptions, detailed statistical analysis plan, multiplicity procedures, or whether interim analyses were conducted. This limits assessment of whether the reported analyses correspond to the original plan and how secondary findings should be weighted. Numerical results for some listed secondary outcomes, including heel-rise muscular endurance and time from injury to surgery, are not reported in the registry record.

Finally, the brief study description is truncated after its account of one-year functional measures, and the posted patient-reported result is not accompanied by instrument-specific details. The record does not report a clinical-importance threshold for the posted outcomes. These limitations do not negate the posted observations, but they restrict interpretation of their precision, completeness, and practical meaning.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Compression Treatment Effects on Complications and Healing of Achilles Tendon Rupture — NCT01317160.
• Registry record last updated 2024-03-07; status last verified 2024-03.
• Results first posted 2016-03-15.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT01317160 is a completed randomized, double-masked, parallel-group study sponsored by Karolinska University Hospital. It compared two weeks of calf intermittent pneumatic compression during orthosis use with routine two-week plaster-cast treatment following surgery for acute Achilles tendon rupture. The registry lists an enrollment of 150 and identifies VTE at two weeks as the primary outcome.

The posted primary counts are 26 of 71 in routine care and 14 of 67 in IPC. The sponsor reports a chi-squared p-value of 0.042 and a logistic-regression odds ratio of 2.81, with a 95% confidence interval from 1.25 to 6.32. The record flags a discrepancy with the simple unadjusted recalculation, so the sponsor's analysis takes precedence. Later VTE, patient-reported outcome, and microdialysis results are also posted, with differing analysis group sizes. The registry record does not report a full analysis plan, multiplicity procedure, complete missing-data account, or original sample-size assumptions.