GUIDOR® Growth Factor Enhanced Bone Graft Substitute for the Treatment of Periodontal Defects 6-months Post-Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for GUIDOR® Growth Factor Enhanced Bone Graft Substitute for the Treatment of Periodontal Defects 6-months Post-Surgery (NCT01728844), a randomized na study. The primary outcome is Number of Participants That Met the Success Criteria of Radiographic and Clinical Measurements.

2. Clinical Question

The trial asked whether adding recombinant human basic fibroblast growth factor to beta-tricalcium phosphate would change the chance of meeting a combined clinical and radiographic success definition after periodontal surgery. It also compared three concentrations of the growth factor to help evaluate dose levels.

The endpoint required both parts of the composite to meet their thresholds: regain from baseline of clinical attachment level of at least 1.5 mm, and linear bone growth of at least 1 mm. The registry record does not report an overall statistical conclusion from the trial sponsor. The posted group counts therefore allow a descriptive comparison and unadjusted recalculations, but do not by themselves establish that one concentration is superior or identify an optimal dose.

3. Trial Design

This was a randomized, parallel-group, controlled, multicenter clinical trial. The registry record describes masking as quadruple. The study was completed, and its enrollment was 88. The record lists the phase as not applicable. The trial title describes a dose-verification study of GUIDOR growth factor enhanced bone graft substitute for periodontal defects, with assessment six months after surgery.

Participants were assigned to beta-tricalcium phosphate alone or to beta-tricalcium phosphate combined with recombinant human basic fibroblast growth factor at 0.1%, 0.3%, or 0.4%. The primary endpoint was binary: a participant counted as a success only if both radiographic linear bone growth and clinical attachment level met their respective criteria. The modified Intent-to-Treat population for this endpoint consisted of 83 subjects after two were removed for protocol noncompliance.

The registry record lists eight secondary outcomes, including clinical attachment level, linear bone growth, bone fill, pocket depth, and gingival recession at specified follow-up times. Numerical summaries are posted for three secondary outcomes: clinical attachment level at three months, clinical attachment level at six months, and linear bone growth at six months. For each of these, the posted comparisons use beta-tricalcium phosphate alone as the control.

The registry record does not report the original sample-size justification, the planned statistical analysis procedures, or details of any interim analyses. It also does not report sponsor-conducted analyses for the posted secondary summaries. The trial’s multicenter setting and masking are relevant design features, but the registry record does not provide site-level results or information that would permit assessment of how masking was maintained.

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

Analysis population for the primary outcome, as defined in the registry: The modified Intent-to-Treat population consisted of 83 subjects after two subjects were removed for lack of compliance with the study protocol.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants That Met the Success Criteria of Radiographic and Clinical Measurements, measured over 6 months post-surgery.

The primary endpoint is the number of participants who met a combined radiographic and clinical definition of success six months after surgery. The radiographic component is linear bone growth, assessed in vertical and horizontal directions using radiographs. The clinical component is regain from baseline of clinical attachment level. Clinical attachment level is defined in the registry record as the distance from the cemento-enamel junction, or another fixed reference point, generally along the tooth’s long axis to the deepest extent of the periodontal pocket.

Success required both components to meet the prespecified thresholds: at least 1.5 mm for change in clinical attachment level and at least 1 mm for linear bone growth. A participant meeting only one threshold did not meet the composite success definition. The endpoint thus summarizes two distinct dimensions of the measured response rather than treating either measurement alone as sufficient.

A composite endpoint can be useful when a trial aims to capture a broader clinical and radiographic outcome in one measure. It also has an interpretive trade-off: the overall success count does not show which component determined whether an individual participant met the definition. The registry record does not provide component-by-component success counts alongside the primary composite counts, so the contribution of each component to the group results cannot be assessed from these posted results.

7. Results Posted in the Registry

• GFeBGS 0.1%: 71.4% (15/21) versus 80.0% (16/20) on control; risk difference -8.6 percentage points (95% CI -34.7 to 17.5), risk ratio 0.89 (0.63–1.26); unadjusted two-proportion z-test p = 0.523.
• GFeBGS 0.3%: 90.5% (19/21) versus 80.0% (16/20) on control; risk difference 10.5 percentage points (95% CI -11.1 to 32.0), risk ratio 1.13 (0.87–1.47); unadjusted two-proportion z-test p = 0.343.
• GFeGBS 0.4%: 81.0% (17/21) versus 80.0% (16/20) on control; risk difference 1.0 percentage points (95% CI -23.3 to 25.2), risk ratio 1.01 (0.75–1.37); unadjusted two-proportion z-test p = 0.939.

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.

Change in Clinical Attachment Level at 3 Months

• 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:
  • GFeBGS 0.1%: mean 2.90 versus 3.10 on control; difference -0.20 (95% CI -1.15 to 0.75), standardized effect d = -0.13; z-test p = 0.680.
  • GFeBGS 0.3%: mean 3.10 versus 3.10 on control; difference 0.00 (95% CI -0.92 to 0.92), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GFeBGS 0.1% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GFeBGS 0.3% and the control. The interval gives the range of effects that remain compatible with the data.

Change in Clinical Attachment Level at 6 Months

• 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:
  • GFeBGS 0.1%: mean 2.50 versus 2.90 on control; difference -0.40 (95% CI -1.69 to 0.89), standardized effect d = -0.19; z-test p = 0.542.
  • GFeBGS 0.3%: mean 3.00 versus 2.90 on control; difference 0.10 (95% CI -1.00 to 1.20), standardized effect d = 0.06; z-test p = 0.858.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GFeBGS 0.1% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GFeBGS 0.3% and the control. The interval gives the range of effects that remain compatible with the data.

Linear Bone Growth at 6 Months

• 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:
  • GFeBGS 0.1%: mean 3.00 versus 3.10 on control; difference -0.10 (95% CI -1.04 to 0.84), standardized effect d = -0.07; z-test p = 0.835.
  • GFeBGS 0.3%: mean 3.70 versus 3.10 on control; difference 0.60 (95% CI -0.37 to 1.57), standardized effect d = 0.38; z-test p = 0.223.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GFeBGS 0.1% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GFeBGS 0.3% and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary summaries cover clinical attachment level at three and six months and linear bone growth at six months. Across these measures, the observed group means show some variation, but the pattern does not provide a uniform separation of every growth factor concentration from beta-tricalcium phosphate alone. The recalculated mean differences have confidence intervals that include zero. These summaries therefore do not provide precise evidence of a consistent difference across the posted secondary outcomes.

The secondary measures relate to the primary endpoint because clinical attachment level and linear bone growth are components of the primary success definition, although the secondary outcomes are reported as continuous measurements rather than as the combined success count. They can add descriptive context about each component, but they cannot directly explain which component led a participant to meet or miss the composite threshold. The registry record does not report component-level primary success counts.

Other secondary outcomes listed in the registry record include percent bone fill, pocket depth change, and gingival recession change at specified follow-up times. Numerical results for those measures are not reported in the registry record. The record lists eight secondary outcomes, while numerical summaries are posted for three. This limits any assessment of the full pattern across all planned secondary measures.

Secondary findings generally carry less weight than a prespecified primary analysis, particularly when many outcomes and comparisons are considered. Without a reported multiplicity strategy, the chance of apparently notable findings arising among many unadjusted comparisons is harder to assess. The secondary results are useful as exploratory context, but they should not override the uncertainty in the primary comparison or be treated as independent confirmation of a dose effect.

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

• Change in Clinical Attachment Level at 3 Months
• Change in Clinical Attachment Level at 6 Months
• Linear Bone Growth at 6 Months
• Percent Bone Fill at 6 Months
• Pocket Depth Change at 3 Months
• Pocket Depth Change at 6 Months
• Change in Gingival Recession at 3 Months
• Change in Gingival Recession at 6 Months

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a binary outcome: each participant either met both success criteria or did not. For this type of outcome, a risk is the fraction of participants meeting the endpoint in a group. A risk difference compares those group risks by subtracting the control risk from the intervention risk. A positive risk difference indicates a higher observed success proportion in the intervention group; a negative value indicates a lower observed proportion. This direction describes the comparison and is not, by itself, evidence of a reliable treatment effect.

What does a confidence interval add?

A confidence interval expresses uncertainty around an estimated effect. The risk-difference intervals are broad in these comparisons, reflecting that the observed group counts do not pin down the underlying difference precisely. When an interval includes zero, the posted data are compatible with no difference as well as with differences in either direction at the stated confidence level. It is important not to interpret the interval as a range containing every plausible value with certainty, or as proof that the groups are equivalent.

The registry record also includes unadjusted p-values for the primary comparisons. A p-value measures how unusual data at least as incompatible with a specified no-difference model would be, if that model and the test assumptions were true. It is not the probability that the treatment has no effect, and it does not measure the size or clinical importance of an effect. These p-values are labelled unadjusted; the registry record does not report a correction for multiple comparisons or the sponsor’s analysis procedure.

How should the continuous outcomes be read?

The posted secondary results report group means and standard deviations for changes in clinical attachment level and for linear bone growth. A mean is a group average, while the standard deviation describes the spread of individual measurements around that average. The unadjusted recalculations compare the intervention-group mean with the control-group mean. Their confidence intervals describe uncertainty in the estimated mean difference under the recalculation approach. They are not adjusted for other variables, and they are not a substitute for a sponsor-reported model or analysis.

Statistical methods for continuous outcomes often rely on assumptions about the distribution of measurements and their variability. A standard deviation is one way to describe variability, but it does not reveal the full distribution, potential outliers, or whether the assumptions of a particular analysis are suitable. Those diagnostic details and the sponsor’s planned analysis are not reported in the registry record.

Why can over-dispersion matter?

Over-dispersion is a general issue for count or binary data when outcomes vary more than a simple statistical model expects. If a model underestimates that variation, its uncertainty estimates can be too narrow and statistical evidence can appear stronger than warranted. The posted primary comparisons are simple unadjusted recalculations from group counts; the registry record does not report a model-based analysis or an assessment of over-dispersion. The concern is therefore a general methodological point, not a finding that over-dispersion occurred in this trial.

The distinction between a registry result and a recalculation matters. The primary estimates and p-values discussed in the interpretation are unadjusted recalculations from the posted summary counts. The record does not report sponsor analyses for these comparisons. The registry’s posted counts remain the descriptive basis for interpretation, while recalculated inferential quantities should be understood as supplementary rather than as a replacement for any original analysis that is not reported.

Finally, the primary definition is a composite. Because success required both components to pass, its binary analysis compresses information from the radiographic and clinical measurements. A composite may be straightforward to interpret as an overall success count, but its components can behave differently. Component-level distributions and the number meeting each component separately are not reported in the registry record, limiting interpretation of what drove the combined endpoint.

11. Confidence Intervals and Precision

Precision concerns how tightly the data estimate a group difference. The confidence intervals for all three primary risk differences are wide relative to the point estimates. For GFeBGS 0.1%, the interval is -0.347 to 0.175; for GFeBGS 0.3%, it is -0.111 to 0.320; and for GFeGBS 0.4%, it is -0.233 to 0.252. Each includes zero and spans values on both sides of it. The observed estimates therefore do not sharply distinguish a lower success proportion, little difference, or a higher success proportion.

A point estimate is the single value calculated from the observed data, not a guarantee of the underlying effect. In particular, the positive estimate for the 0.3% group should not be read in isolation: its interval also includes zero and negative values. Likewise, a p-value above a conventional threshold does not demonstrate equivalence. Establishing equivalence or non-inferiority would require an appropriate design and analysis with a prespecified margin, which the registry record does not report.

The posted secondary mean-difference intervals are also broad. For example, the six-month linear bone growth comparison for GFeBGS 0.3% has an estimated mean difference of 0.6 mm and a confidence interval from -0.365 to 1.565. The interval includes zero, so the estimate does not precisely establish a difference. These are unadjusted recalculations, and the registry record does not report sponsor analyses for the secondary outcomes.

Confidence intervals are most useful when considered alongside the endpoint definition, group sizes, analysis population, and multiplicity. They communicate uncertainty in estimated effects; they do not express the probability that a treatment is beneficial, nor do they resolve questions about clinical importance. The record does not state a threshold for a clinically meaningful difference in the risk difference or the secondary measures.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these comparisons, the figures are participants per arm. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect. The original sample-size justification and assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if the assumptions and effect are correct. The 90% power column gives the corresponding illustration for a 90% chance. These are planning targets, not claims about what the completed trial could detect with a particular probability. This is not observed power.

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 generally require more participants to distinguish them from random variation under the same planning assumptions. The estimates can become very large when the observed difference is small, as happens for some comparisons. That is a feature of the arithmetic behind planning from a small observed effect, not evidence that such a study is feasible or that the observed effect will recur.

These calculations are not a reconstruction of the trial’s design. They use the posted results as planning inputs, and the observed effect in a small study may itself be imprecise. The registry record does not report the trial’s original power target, target effect, or sample-size calculation.

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 = 0.800; treatment proportion p₁ = 0.714; average p̄ = 0.757.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6064 = 1.1886.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6034 = 0.5078.
4. n = (1.1886 + 0.5078)² / (-0.0857)² = 391.7, rounded up to 392 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 <- 0.8                          # control proportion
p1 <- 0.714285714285714                          # 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(1728844)
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 = 392 (80% power), 524 (90% power)
 75% of observed effect: n per arm = 676 (80% power), 905 (90% power)
 50% of observed effect: n per arm = 1,473 (80% power), 1,971 (90% power)
power.prop.test: 391.7 
Simulated power at n = 392 per arm: 0.803 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several treatment comparisons, outcomes, or time points. Each additional statistical test creates another opportunity for a result to appear notable by chance. This is a general statistical concern and does not show that a particular posted result is false. It does mean that isolated unadjusted p-values should be interpreted cautiously when the analysis includes multiple comparisons.

This trial compares three growth factor concentrations with a common control and lists multiple secondary outcomes and follow-up times. The posted p-values are unadjusted. A multiplicity adjustment or a prespecified hierarchy of tests is not reported in the registry record. The original statistical analysis plan, including how the primary and secondary comparisons were to be handled, is also not reported in the registry record. Consequently, the unadjusted p-values cannot be interpreted as family-wise error-controlled confirmatory tests.

The primary population is described as a modified Intent-to-Treat population of 83 subjects, after two subjects were removed for lack of compliance with the study protocol. The registry record does not provide enough detail to evaluate the reasons and timing of all exclusions, the handling of any missing measurements, or whether missing data were imputed. The posted arm-level denominators for the endpoint are also reported separately. A reader should not infer that all randomized participants contributed to every outcome.

Missing outcome data can affect both the estimated group differences and their uncertainty, especially if the likelihood of missingness is related to outcomes or treatment assignment. The registry record does not report a missing-data sensitivity analysis. It also does not report sponsor analyses for the posted secondary summaries. These gaps limit assessment of robustness, but they do not establish that missingness or multiplicity changed the results in a particular direction.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: basal cell carcinoma basal (4.8%), bunion (4.5%), chronic lymphocytic leukemia (4.5%), coma (4.5%).

The registry reports serious adverse events and other adverse events by group, with separate numbers at risk and affected. In the beta-tricalcium phosphate alone group, 2 participants were reported with serious adverse events and 4 with other adverse events; one death is listed. For GFeBGS 0.1%, the corresponding counts are 1 and 6, with no deaths listed. For GFeBGS 0.3%, they are 1 and 2, with no deaths listed. For GFeGBS 0.4%, no serious adverse events and 10 other adverse events are listed, with no deaths listed. The record gives the group-specific numbers at risk as 22, 21, 22, and 23, respectively.

These are descriptive registry counts, not estimates of causal safety differences. The record does not report a statistical comparison of adverse events or enough detail to assess event timing, duration, severity beyond the serious classification, or relatedness to treatment. The listed top serious event terms and percentages are not a substitute for a complete event-by-event clinical assessment. Differences in reported counts should not be treated as proof that one group is safer or less safe.

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

The posted data describe a randomized comparison of beta-tricalcium phosphate alone with three concentrations of a growth factor enhanced substitute. For the primary composite endpoint, observed success counts differed across groups, and the unadjusted recalculated confidence intervals are broad and include zero for each comparison with control. The results are therefore uncertain about the direction and size of any group differences.

This does not mean that the groups have been shown to be equivalent. A study can fail to distinguish a difference from no difference when estimates are imprecise. Nor does the largest observed success proportion in one group establish that its concentration is optimal. The registry record does not report a formal dose-response analysis, a clinically meaningful difference threshold, or a sponsor-reported inferential conclusion for the primary endpoint.

The primary outcome combines a clinical measurement and a radiographic measurement, and requires both to meet criteria. That gives the endpoint a broad definition of success, but the composite counts do not show the separate contribution of each component. The secondary summaries add some information about component measurements, yet are also imprecise and do not cover every listed secondary outcome.

The trial results should be understood in the context of the registry record: the analysis population was modified, the original sample-size justification and statistical plan are not reported, and the posted comparisons are unadjusted recalculations. These limitations affect how confidently the effects can be interpreted. The results describe the observations in this completed trial; they do not alone establish a general conclusion about treatment benefit, lack of benefit, or comparative safety.

17. Why This Trial Matters Statistically

This trial illustrates several statistical issues common to multi-arm clinical research. Comparing several concentrations with one control can be useful for dose exploration, but creates multiple comparisons that require a clear analysis strategy. The registry record lists several arms and outcomes, while the posted inferential comparisons are unadjusted. Without the planned multiplicity approach, individual p-values provide only a partial view of the evidence.

The endpoint also demonstrates the interpretive trade-off in composite outcomes. Combining a clinical measurement with a radiographic measurement yields a single success count, but obscures whether both components show similar patterns. Reporting component-level distributions and the number meeting each threshold separately would help readers understand how the composite result arose; those details are not reported in the registry record.

Small group counts can produce wide confidence intervals even when the point estimates differ. In this trial, the recalculated intervals are compatible with effects in either direction. The sample-size illustrations show why planning from a small observed difference can imply very large future studies, but they are not substitutes for a design based on clinically meaningful targets and justified assumptions.

Finally, the record distinguishes the primary endpoint population from the overall enrollment and records exclusions for protocol noncompliance. Transparent reporting of analysis populations, missing-data methods, sponsor analyses, and the original statistical plan is important for judging whether estimates are robust. These are not merely technical details: they shape how readers should weigh a descriptive pattern against uncertain comparisons.

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.

Several trial-specific limitations constrain interpretation. First, the primary endpoint is a composite requiring both clinical attachment level and linear bone growth to meet threshold criteria. The registry record does not report separate primary success results for the two components, so it is not possible to determine which measure contributed most to the combined outcome.

Second, the modified Intent-to-Treat population excludes two subjects for protocol noncompliance. The registry record does not provide further detail about the exclusions or report a sensitivity analysis using alternative populations. This leaves uncertainty about the robustness of the primary analysis population definition.

Third, the primary comparisons are based on modest group counts, and their confidence intervals are wide. The unadjusted recalculations are not a replacement for an original sponsor analysis, which is not reported in the registry record. The record also does not report the prespecified statistical plan, multiplicity handling, original sample-size justification, or missing-data procedures.

Fourth, the registry lists eight secondary outcomes, but numerical summaries are posted for three. This incomplete outcome reporting restricts assessment of whether findings across all listed clinical and radiographic measures support a coherent pattern. The registry record does not report site-specific estimates, so variation across the multicenter trial cannot be evaluated from these results.

These limitations do not establish that the trial was conducted improperly or that its results are biased in a particular direction. They identify information needed to assess precision, robustness, and completeness of the reported evidence.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: GUIDOR® Growth Factor Enhanced Bone Graft Substitute for the Treatment of Periodontal Defects 6-months Post-Surgery — NCT01728844.
• Registry record last updated 2020-09-17; status last verified 2020-08.
• Results first posted 2020-08-21.
• 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

NCT01728844 is a completed randomized, quadruple-masked, parallel-group, multicenter trial of beta-tricalcium phosphate alone versus three concentrations of GUIDOR growth factor enhanced bone graft substitute for periodontal defects. Enrollment was 88. The primary endpoint was the number of participants meeting both clinical attachment level and radiographic linear bone growth criteria six months after surgery.

The registry reports primary success counts for the control and three intervention groups, with an analysis population described as modified Intent-to-Treat. Unadjusted recalculations show broad confidence intervals that include zero for all primary comparisons. Numerical secondary summaries are posted for three outcomes; results for the other listed secondary outcomes are not reported in the registry record. The original statistical plan, sample-size justification, and multiplicity approach are also not reported.