Cardiovascular Effects of Chronic Sildenafil in Men With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cardiovascular Effects of Chronic Sildenafil in Men With Type 2 Diabetes (NCT00692237), a randomized phase 4 study. The primary outcome is Left Ventricular Torsion Defined as Change in Ventricular Mid-wall Rotation (°) Measured by Cine-Cardiac Magnetic Resonance (CMR) Imaging With Tagging, Before and After Three Months of Treatment With Sildenafil and Placebo (100 mg/Day)..

2. Clinical Question

The clinical question is specifically about a cardiac imaging measure over the treatment period. It is not a direct test of clinical events or long-term health outcomes. The registry’s stated rationale is that diabetic cardiomyopathy and hypertrophy can involve increased cardiac torsion, and that a reduction in wall rotation can indicate improvement after removal of causes of hypertrophy. That rationale explains why torsion was selected for study; it does not establish that a change in the imaging measure necessarily leads to a change in symptoms, complications, or survival.

The record also describes ejection fraction as a secondary measure. Both cardiac measures were taken before and after three months of treatment. The primary comparison is the difference between groups in the change in torsion, rather than a comparison of the groups’ values at only one time point. The reported arm summaries and mean difference describe this change-based comparison.

3. Trial Design

This was a phase 4, randomized, double-masked, parallel-group trial sponsored by the University of Roma La Sapienza. The registry lists 59 participants enrolled and identifies sildenafil and placebo as the two interventions. The primary endpoint record states that 29 participants randomized to sildenafil and 25 randomized to placebo completed the trial. The record does not explain the status or endpoint data of the other enrolled participants, so the completed counts should not be treated as a complete account of every participant’s disposition.

The intervention was sildenafil 100 mg per day, with placebo as the comparison. Treatment and measurement were described over three months, with imaging at baseline and at the three-month time point. The primary endpoint was left ventricular torsion measured by cine-cardiac magnetic resonance imaging with tagging. Ejection fraction, also measured with cine-cardiac magnetic resonance imaging, was a secondary outcome.

The registry marks the study as completed. It lists a start date of 2008-01 and a primary completion date of 2009-09. These dates describe the registry record, not necessarily the timing of every analysis or report. The record lists two outcome measures, one primary and one secondary, and reports no registered analyses. It does not report a detailed account of randomization procedures, concealment, adherence, protocol deviations, the analysis population, or how missing measurements were handled.

The primary endpoint description includes a design statement: an overall sample size of 32 subjects, with 16 in each group, was described as giving 90% power to detect the specified minimum detectable difference of 3° at a two-sided significance level of 0.01. It also reports that 59 patients were enrolled and gives the completed group counts. This statement records the endpoint’s stated design rationale, but it does not supply a full account of the assumptions or methods behind that planning calculation. In particular, the planning illustration based on the observed results uses assumptions distinct from the original study design.

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.

Before assignment: Overall 66 patients were eligible and enrolled; Seven were then excluded due to evidence of aneurysm of ascending aorta (1) on stress-Echo and of ischemic heart disease (6) at the first CMR. Fifty-nine patients were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: An overall sample size of 32 subjects (16 for each group) would thus have given a 90% power to detect the specified minimum detectable difference (3°) at a 2-sided significance level of 0.01; 59 patients were enrolled: 29 randomized to Sildenafil and 25 randomized to Placebo completed the trial. Analysis was per primary efficacy outcome (LV-q).

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 Left Ventricular Torsion Defined as Change in Ventricular Mid-wall Rotation (°) Measured by Cine-Cardiac Magnetic Resonance (CMR) Imaging With Tagging, Before and After Three Months of Treatment With Sildenafil and Placebo (100 mg/Day)., measured over 0 and + 3 months.

The primary endpoint is left ventricular torsion, described as a change in ventricular mid-wall rotation and measured in degrees using cine-cardiac magnetic resonance imaging with tagging. Measurements were planned at baseline and after three months of sildenafil or placebo treatment. The reported outcome is a continuous measure, summarized as a mean and standard deviation for each group.

Torsion is used in the registry’s rationale because diabetic cardiomyopathy and hypertrophy are characterized by increased cardiac torsion. The description says normal rotation values are < 12° and that values in a hypertrophic heart can rise to 20-25°. It further notes that reduced left ventricular wall rotation can be a sign of improvement after removal of known causes of hypertrophy. On that basis, the registry identifies a reduction of 3° as clinically significant.

These statements explain the proposed interpretation of the imaging measure. They do not make torsion a direct measure of a patient’s symptoms, cardiovascular events, or long-term prognosis. Nor does a group mean establish the response of every participant. The result should be understood as a comparison of average change in a cardiac imaging measure between randomized groups over the stated treatment interval.

7. Results Posted in the Registry

• Sildenafil: mean -3.89 versus 2.13 on control; difference -6.02 (95% CI -7.48 to -4.56), standardized effect d = -2.16; z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Ejection Fraction (EF) Defined as the Volume of Blood Ejected With Each Beat Was Measured on Cine-Cardiac Magnetic Resonance (CMR) Images Before and After Three Months Treatment With Sildenafil and Placebo (100 mg/Day).

• 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:
  • Sildenafil: mean 2.77 versus 3.14 on control; difference -0.37 (95% CI -3.17 to 2.43), standardized effect d = -0.07; z-test p = 0.795.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sildenafil and the control. The interval gives the range of effects that remain compatible with the data.

Ejection fraction is the single secondary outcome listed in the registry. It is an imaging measure of the volume of blood ejected with each beat, assessed by cine-cardiac magnetic resonance imaging at baseline and after three months. The observed group means are close, and the recalculated contrast is uncertain, with a confidence interval that includes zero. This differs from the primary torsion comparison, whose interval is separated from zero. Taken together, the posted outcomes show a clearer between-group separation for the primary imaging measure than for the secondary one.

The results should not be treated as interchangeable evidence about a single underlying construct. Torsion describes ventricular rotation, while ejection fraction describes the proportion of ventricular volume ejected with each beat. A change in one does not necessarily imply a corresponding change in the other. The registry does not report a combined endpoint or a planned rule for interpreting the measures jointly.

Secondary results generally carry less weight than a primary result when the study’s main question is defined by the primary outcome. They may be exploratory, and testing multiple outcomes can increase the chance of at least one apparently notable result by chance. The registry does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. The ejection-fraction comparison is therefore best read as additional descriptive evidence, not as an independent confirmatory test.

The available information does not establish whether this outcome was fully prespecified beyond its listing as secondary, whether additional secondary outcomes were collected but not posted, or how missing measurements were handled. The registry lists one secondary outcome and no registered analyses. Those reporting limits make it difficult to assess selective reporting or to know whether the posted secondary result represents the complete set of analyses considered by the investigators.

Across the posted endpoints, the statistical pattern is not uniform: the primary torsion estimate is more distinctly separated between groups, while the secondary ejection-fraction estimate remains compatible with no difference and with differences in either direction. This contrast informs the strength and scope of the evidence in the registry record. It does not show whether any imaging change results in a meaningful change in health outcomes.

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

• Ejection Fraction (EF) Defined as the Volume of Blood Ejected With Each Beat Was Measured on Cine-Cardiac Magnetic Resonance (CMR) Images Before and After Three Months Treatment With Sildenafil and Placebo (100 mg/Day).

9. Statistical Interpretation

10. Statistical Methods Explained

The primary measure is continuous: it records change in ventricular rotation in degrees. A common way to summarize a continuous outcome is to report a group mean and a measure of spread. The mean describes the group’s average change, while the standard deviation describes how dispersed individual changes are around that average. Neither alone describes every participant’s result. A group mean can be influenced by variation among participants, and the standard deviation helps readers see that the estimate comes from observations that are not all identical.

What does the mean difference represent?

The primary mean difference is calculated as the sildenafil group mean minus the placebo group mean. With this ordering, a negative contrast means that the reported change was lower in the sildenafil group. The estimate of -6.02° is the difference between the posted group means, not a separate measurement in an individual participant. It summarizes how far apart the two group averages were in this comparison.

The comparison is described as an unadjusted recalculation from posted summary statistics. An unadjusted comparison does not incorporate additional covariates or a more complex analysis model. The registry lists no analyses, so it does not report whether the original investigators used an adjusted model, how they handled baseline values, or whether the displayed contrast matches a prespecified analysis. The recalculation is consequently useful for interpreting the available summaries, but it should not be presented as a registry-reported adjusted treatment effect.

How should the p-value be read?

The primary unadjusted comparison has p < 0.001. In general, a p-value describes how unusual results at least as incompatible with a stated null hypothesis would be if that hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. Here, the p-value accompanies the recalculated comparison of the group means. The registry does not report an analysis plan or a multiplicity adjustment, so the result should not be described as a prespecified, adjusted test.

For ejection fraction, the unadjusted p-value is 0.795. A large p-value does not demonstrate that the groups are the same or equivalent. It says that the observed summaries do not provide strong evidence against a zero difference under the unadjusted comparison. The confidence interval is important alongside the p-value because it shows the range of differences compatible with the data and method, rather than reducing the result to a threshold decision.

What does the confidence interval add?

A confidence interval conveys uncertainty around an estimated contrast. In general, a narrower interval indicates greater precision, while a wider interval leaves more plausible values open. The primary torsion interval runs from -7.479 to -4.561. The ejection-fraction interval runs from -3.165 to 2.425. The former stays on one side of zero, while the latter spans zero. These intervals describe uncertainty under the unadjusted method used for the recalculations; they do not account for unreported analytic choices or potential missing-data mechanisms.

Confidence intervals are not guarantees that the true effect lies inside a particular interval, nor do they show the range of individual participants’ outcomes. The intervals concern the estimated group contrast. Individual-level variability is described separately by the group standard deviations, which are 3.11 and 2.35 for torsion and 4.36 and 5.87 for ejection fraction.

Why can outcome variability matter?

In general, more variability makes it harder to estimate a group difference precisely when the sample size is unchanged. The spread in the ejection-fraction groups is substantial relative to the observed contrast, and its confidence interval is broad enough to include negative and positive values. Torsion has a larger separation between the group means relative to its reported spread, and its interval is more clearly separated from zero. These are descriptions of the posted summaries, not a claim that the trial was powered or designed to establish every possible effect on either measure.

Over-dispersion is a general concern when observed variation exceeds what an assumed statistical model allows. If that occurs, standard errors and confidence intervals based on a model that understates variation can be too small, making results look more precise than they are. The registry record does not report an over-dispersion assessment or a model-based analysis for these outcomes. Since the outcomes are summarized as continuous measures with standard deviations, the relevant interpretive point is that observed spread affects precision; no additional model assumption can be confirmed from the record.

What does randomization contribute?

Random allocation is intended, in general, to make treatment groups comparable at the time of allocation and to reduce systematic differences in prognostic factors. Double masking is intended to limit expectations or knowledge of assignment from influencing care, measurement, or reporting. Those design labels are reported for this trial, but the record does not describe allocation concealment, how masking was implemented, or whether masking remained intact. Randomization does not eliminate chance imbalances, missing outcomes, or bias arising after assignment.

The parallel-group design means that participants were assigned to one intervention group rather than being described as crossing over between treatments. The reported comparison is between the two groups’ average changes over three months. The record does not provide the analysis population or a participant flow account detailed enough to establish how all randomized participants contributed to the endpoint estimates.

What are the planning illustrations?

The sample-size illustrations use observed effects as planning inputs, with alternative rows considering 100%, 75%, and 50% of the observed effect. In general, planning calculations estimate how many participants would be needed under specified assumptions to have a chosen chance of detecting a target effect at a specified significance level. They are not estimates of how likely this completed trial was to produce a statistically significant result. Smaller target effects generally require more participants because they are harder to distinguish from random variation.

The registry separately states that an overall sample size of 32 subjects, 16 in each group, would give 90% power to detect a 3° difference at a two-sided significance level of 0.01. The full basis for that original planning statement is not reported in the registry record. It is distinct from the later planning illustrations, which use the observed effect and assumptions listed with those illustrations. Neither type of planning statement establishes the actual probability that the trial’s result is correct.

11. Confidence Intervals and Precision

Precision is best considered through the confidence intervals alongside the point estimates. For torsion, the unadjusted recalculated mean difference is -6.02°, and its 95% confidence interval ranges from -7.479 to -4.561. The interval is entirely negative, indicating that the data and calculation are compatible with negative contrasts across that range, rather than with a zero contrast. The estimate is also more precise than the ejection-fraction contrast in the sense that its interval is narrower on the reported measurement scale.

For ejection fraction, the mean difference is -0.37 percentage points, with a 95% confidence interval from -3.165 to 2.425. This interval includes zero and spans potentially negative and positive group differences. It therefore leaves considerable uncertainty about the direction and size of the difference. The result is not proof of no difference; a lack of evidence against zero in this comparison is not the same as evidence of equivalence.

These intervals concern estimated group means, not the range of individual responses. The standard deviations show substantial participant-level variation: 3.11 and 2.35 for torsion, and 4.36 and 5.87 for ejection fraction. The confidence intervals and standard deviations answer different questions. The standard deviations describe spread among observed measurements, while the confidence intervals describe uncertainty in the estimated difference between group means.

The intervals are based on unadjusted recalculations from the posted summaries. The registry record does not report a model, an adjustment strategy, or a missing-data method, so those intervals cannot reflect analytic choices that are not documented. They also do not address multiplicity across outcomes. Readers should therefore interpret them as precision summaries for the comparisons calculated from the posted results, not as a complete account of every uncertainty affecting the trial.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. The outcome is continuous, so the figures describe the number of participants needed in each group under the planning assumptions. The 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 to a stated fraction of the observed effect. Time-to-event planning displays use total events, but that convention does not apply to these continuous outcomes.

The 80% power column means the illustrated number of participants per arm for a design that, under the calculation assumptions, would have an 80% chance of detecting the target effect at the stated significance level if that effect were the true one. The 90% power column gives the corresponding planning target for a 90% chance. These are design concepts, not guarantees about a future study’s result. The figures are participants per arm, so they should not be read as the combined number across both groups.

The effect rows use 100%, 75%, and 50% of the observed effect. For torsion, the figures for 80% power are 4, 6, and 14 participants per arm across those rows; for 90% power they are 5, 8, and 18. For ejection fraction, the corresponding figures are 2,998, 5,329, and 11,990 for 80% power, and 4,013, 7,134, and 16,050 for 90% power. Smaller effects need more participants because a smaller group difference is more difficult to distinguish from random variation.

These illustrations are based on the observed effects and the stated calculation assumptions, rather than the trial’s original design. They are not observed power. The registry separately reports a design statement for the primary endpoint: 32 subjects overall, with 16 per group, for 90% power to detect 3° at a two-sided significance level of 0.01. The full assumptions behind that original statement are not reported in the registry record.

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 = -6.020; pooled standard deviation σ = 2.785.
2. n = 2 × (1.96 + 0.842)² × 2.785² / -6.020² = 3.4, rounded up to 4 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 <- -6.02                      # observed difference in means
sigma <- 2.78512118228274                     # 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(692237)
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 = 4 (80% power), 5 (90% power)
 75% of observed effect: n per arm = 6 (80% power), 8 (90% power)
 50% of observed effect: n per arm = 14 (80% power), 18 (90% power)
power.t.test: 4.6 
Simulated power at n = 4 per arm: 0.725 (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

Multiplicity arises when more than one outcome or statistical comparison is examined. In general, the more tests that are considered, the greater the chance that at least one result will appear unusual by chance, unless the analysis plan accounts for the number and structure of the tests. This trial lists a primary outcome and one secondary outcome, but the registry record does not report a multiplicity strategy, a testing hierarchy, or adjusted p-values. The p-values accompanying the recalculated comparisons are therefore unadjusted and should not be read as controlling the overall false-positive risk across outcomes.

The registry reports no analyses. It does not identify a prespecified statistical analysis plan, explain whether the primary comparison was adjusted for baseline values, or state whether other covariates were considered. It also does not report whether the analysis followed intention-to-treat principles, used a per-protocol population, or used another analysis population. The completed counts for the primary endpoint are reported, but an account of all randomized participants and their follow-up is not.

Missing data can affect a trial result when the chance of an outcome being unavailable is related to treatment assignment or participant characteristics. In general, complete-case comparisons may be biased if the people with observed outcomes differ systematically from those without them. Imputation methods can address some missing-data situations, but they require assumptions that should be explained. The registry record does not say whether measurements were missing, how any missing values were handled, or whether sensitivity analyses were performed.

The record also does not describe protocol deviations, treatment adherence, or withdrawals by reason. The enrollment figure is 59, while the primary endpoint description reports 29 sildenafil and 25 placebo participants as having completed the trial. Without a participant flow account, the reason for the difference between enrollment and the endpoint completion counts is not reported in the registry record. This limits assessment of attrition and of the population represented by the posted summaries.

These gaps do not establish that the results are biased, but they restrict how confidently the comparisons can be interpreted as the result of a prespecified analysis applied to all randomized participants. The unadjusted recalculations are informative summaries of the reported group data; they cannot resolve undocumented choices about multiplicity, missing data, or analysis populations.

15. 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 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: portal vein thrombosis (3.4%).

The serious adverse event counts are reported for 30 participants at risk in the sildenafil group and 29 in the placebo group. No serious adverse events were recorded in the sildenafil group; one was recorded in the placebo group. The registry lists Portal Vein Thrombosis as a serious adverse event term at 3.4%, but the posted term summary does not attribute that term to a treatment group. The registry’s group counts should not be used to infer an attribution that is not reported.

No other adverse events are listed in either group in the posted counts. Death counts are not reported in the registry record. The risk denominators for the safety summaries differ from the primary endpoint completion counts, and the registry does not explain the relationship between those populations.

These figures are descriptive counts from a trial with a limited number of participants. They can report what was recorded during the study, but they do not establish the frequency of uncommon events in a broader population or allow a precise comparison of safety risks. The absence of a recorded event in a group is not proof that the event cannot occur. Interpretation is also limited by the lack of detail about event collection, follow-up duration for safety, severity grading, and attribution procedures in the registry record.

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

The posted primary results show a difference in average change in left ventricular torsion between the sildenafil and placebo groups over three months. The unadjusted recalculated mean difference is -6.02°, with a 95% confidence interval from -7.479 to -4.561 and p < 0.001. The interval is separated from zero, and the result is consistent with a more negative average change in the sildenafil group in this comparison. The registry identifies a 3° reduction as clinically significant, but it does not report a formal test of the group contrast against that threshold.

The secondary ejection-fraction result is less precise. Its mean difference is -0.37 percentage points, with a 95% confidence interval from -3.165 to 2.425 and p = 0.795. The interval includes zero and allows for differences in either direction. This is not evidence that the groups are equivalent, nor does it establish that ejection fraction was unaffected. It shows that the available comparison does not precisely determine the direction or size of the difference.

Both outcomes are cardiac imaging measures. The registry’s explanation connects torsion to cardiac remodelling and describes why a reduction in rotation was considered relevant. The trial does not report clinical events, symptoms, or long-term outcomes as endpoints in the posted results. Consequently, the imaging comparisons do not establish a benefit or harm in terms of how participants feel, function, or experience later cardiovascular events.

The study was randomized and double-masked, which are design features intended in general to limit confounding and measurement or performance bias. However, the registry does not detail allocation concealment, the implementation of masking, adherence, participant flow, or missing-data methods. It also does not list analyses. Those omissions mean the recalculated comparisons should be interpreted as unadjusted summaries, not as a complete reconstruction of the original statistical analysis.

The results apply to the participants and follow-up described in the record: men with type 2 diabetes, treatment over three months, and cardiac magnetic resonance measurements. They do not by themselves establish what would happen with different doses, longer treatment, different populations, or other outcomes. The registry’s safety counts are also limited in their ability to characterize uncommon events, and the record does not report deaths. The appropriate meaning is therefore narrow: the posted summaries show a difference in the primary imaging measure, while the secondary imaging estimate remains uncertain; neither result alone resolves broader clinical questions.

17. Why This Trial Matters Statistically

This trial is statistically interesting because its primary and secondary imaging outcomes tell different precision stories. The primary torsion estimate is separated from zero, while the ejection-fraction estimate has a confidence interval that spans zero. Considering both outcomes highlights why a result on one measure should not automatically be generalized to another, even when both relate to cardiac function and were assessed over the same treatment period.

The registry also gives a stated clinical threshold for the primary endpoint: a reduction of 3° is described as clinically significant. This creates a useful distinction between statistical evidence of a group difference and the interpretation of the size of that difference. The recalculated group contrast is large relative to the stated threshold, but the registry does not report a formal test against that threshold or a prespecified analysis plan. The result therefore illustrates why a clinical benchmark should be discussed alongside, but not substituted for, the statistical estimate and its uncertainty.

The record is also a reminder that a randomized design does not by itself fill in every detail needed for statistical interpretation. The registry identifies randomization, masking, and a parallel-group structure, but does not report the analysis population, missing-data approach, or multiplicity strategy. Such details affect how readers judge whether an unadjusted comparison answers the study’s intended question and how much confidence to place in the reported evidence.

Finally, the sample-size illustrations based on observed effects are useful for understanding how target effect size relates to planning requirements. They are distinct from the original design statement and should not be mistaken for observed power. The contrast between a larger observed effect and smaller target effects also emphasizes that planning depends on the effect a study is intended to detect, not only on the result eventually observed.

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 registry’s account of participant disposition is incomplete. It reports enrollment of 59 and gives completed primary endpoint counts of 29 for sildenafil and 25 for placebo, but does not explain the status of every enrolled participant. Safety denominators are also reported separately, and their relationship to the endpoint population is not described. This prevents a full assessment of attrition, exclusions, and the population contributing to each result.

The primary and secondary comparisons available for interpretation are unadjusted recalculations from posted summary statistics. The registry reports no analyses, so it is not possible to determine whether the trial’s original analysis used baseline adjustment, a repeated-measures approach, covariate adjustment, or another method. The record also does not report whether the stated primary contrast was the prespecified estimand or whether alternative analyses were conducted.

Multiplicity is another limitation. The record lists one primary and one secondary outcome, but does not state how the investigators planned to handle multiple testing or whether any other outcomes were examined. The reported p-values are unadjusted. Without a prespecified hierarchy or adjustment plan, the strength of confirmatory interpretation is uncertain, especially for secondary findings.

Missing-data handling, adherence, protocol deviations, and reasons for non-completion are not reported in the registry record. The listed study period and three-month measurement timeframe do not establish whether every participant contributed both measurements or whether all participants had the same follow-up. The registry also does not describe how imaging measurements were read, whether readings were blinded to treatment assignment, or how measurement reliability was assessed.

The outcome scope is narrow: the posted efficacy results are cardiac imaging measures over three months. The record does not provide clinical event outcomes or longer-term results. The serious adverse event data are counts, with limited detail on event ascertainment, attribution, and duration of safety follow-up. Death counts are not reported. These limitations restrict the conclusions that can be drawn from the registry record and do not establish that any unreported analysis or procedure was absent from the full study.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Cardiovascular Effects of Chronic Sildenafil in Men With Type 2 Diabetes — NCT00692237.
• Registry record last updated 2013-05-08; status last verified 2013-05.
• Results first posted 2012-05-15.
• 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.

22. Record Summary

NCT00692237 is a completed phase 4 randomized, double-masked, parallel-group trial sponsored by the University of Roma La Sapienza. It enrolled 59 participants and compared sildenafil 100 mg per day with placebo over three months in men with type 2 diabetes. The primary endpoint was change in left ventricular torsion measured by tagged cine-cardiac magnetic resonance imaging; ejection fraction was the secondary outcome.

The primary unadjusted recalculated comparison was -6.02°, with a 95% confidence interval from -7.479 to -4.561 and p < 0.001. The secondary ejection-fraction comparison was -0.37 percentage points, with a 95% confidence interval from -3.165 to 2.425 and p = 0.795. The registry reports no analyses, and does not report a multiplicity plan, missing-data approach, or analysis population. Serious adverse event counts were zero for sildenafil and one for placebo; deaths are not reported in the registry record.