Build Better Bones With Exercise: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Build Better Bones With Exercise (NCT01761084), a randomized na study. The primary outcome is Feasibility of Recruitment and Retention.

2. Clinical Question

The central question is about feasibility, not a definitive test of whether exercise changes health outcomes. The registry identifies recruitment and retention as the primary outcome, with success criteria of 20 recruited per site and at least 75% retained. It also describes a target adherence rate of 60% in the study’s primary hypothesis. These criteria relate to whether a larger study could be conducted; they are not themselves estimates of exercise effects.

The trial was designed as a pilot randomized controlled study in women with vertebral fracture. Its intervention was intended to be performed at home thrice-weekly for one year, with physiotherapists making 6 home visits. The control condition was designed to provide equal attention through general health or social discussion. The registry describes the longer-term motivation as assessing whether tailored home exercise could be evaluated in a larger multicentre study.

Secondary questions concern outcomes that matter to participants and researchers, including falls, fractures, posture, physical performance, balance, pain, and quality of life. These outcomes offer exploratory information alongside the feasibility question. They do not replace the primary focus on whether recruitment and retention targets were achieved.

3. Trial Design

This was a randomized, parallel-group pilot trial with single masking. The registry does not identify who was masked. It lists an enrollment of 141 and a completed study, with a start date of 2013-01 and primary completion in 2016-12. The trial phase is recorded as NA. The sponsor was the University of Waterloo.

Participants were assigned to exercise and behaviour-change strategies or general health or social discussion. The exercise program was tailored to participants’ abilities and included strength training, balance training, and cardiovascular exercise. The physiotherapist was also to use behaviour-change strategies; the registry mentions documenting progress in a log, but the available description ends before all strategies are specified. The control group received equal attention, but no prescribed exercise or exercise counselling, and the physiotherapist discussed general health topics.

The registry describes the intervention as thrice-weekly home exercise for one year and the physiotherapist’s role as conducting 6 home visits. These are features of the planned intervention, rather than evidence about how consistently participants completed it. The primary hypothesis included recruitment, retention, and adherence targets. The number of sites and site-specific recruitment results are not reported in the registry record, so the criterion of 20 recruits per site cannot be evaluated from the posted information.

Recruitment and retention were the primary feasibility outcome. The registry describes monthly records up to 12 months and defines success as recruiting 20 participants per site and retaining at least 75%. Secondary outcomes include the number of fallers, participants with multiple falls, fractures, physical performance, balance, posture, quality of life, pain, and falls-related confidence. The registry lists 24 outcome measures and 26 analyses, while 22 secondary outcomes are posted. Details of allocation concealment, the identity of the masked party, and the original statistical analysis plan 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

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 Feasibility of Recruitment and Retention, measured over Monthly records up to 12 months..

The primary endpoint is titled feasibility of recruitment and retention. It measures the number of participants recruited and retained, with monthly records up to 12 months. The stated criteria for success are 20 recruits per site and retention of at least 75%. The study’s primary hypothesis also describes an adherence target of 60%, although the posted primary endpoint is recruitment and retention rather than adherence.

Feasibility outcomes are useful in a pilot because they address whether a larger study can enroll and keep participants under the proposed approach. Recruitment indicates whether the intended population can be reached; retention indicates whether participants remain available through follow-up. These measures help assess whether the study procedures and participant commitment are workable. They do not directly establish an effect on fractures, falls, pain, or other clinical outcomes.

The posted arm values are 66 for exercise and 64 for general health or social discussion, with reported arm sizes of 71 and 70. The registry does not make clear in the posted result whether each value represents recruitment, retention, or a specific combined interpretation of the endpoint. Nor does it provide the site-level counts needed to assess the recruitment criterion. The reported primary comparison should therefore be read as the posted feasibility measure, not as a complete demonstration that each stated success criterion was met.

7. Results Posted in the Registry

• General Health or Social Discussion: 91.4% (64/70) versus 93.0% (66/71) on control; risk difference -1.5 percentage points (95% CI -10.4 to 7.3), risk ratio 0.98 (0.89–1.08); unadjusted two-proportion z-test p = 0.735.

8. Secondary Efficacy Endpoints

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

Number of Fallers

• 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:
  • General Health or Social Discussion: 51.4% (36/70) versus 67.6% (48/71) on control; risk difference -16.2 percentage points (95% CI -32.2 to -0.2), risk ratio 0.76 (0.58–1.01); unadjusted two-proportion z-test p = 0.050.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between General Health or Social Discussion and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Multiple Falls

• 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:
  • General Health or Social Discussion: 31.4% (22/70) versus 43.7% (31/71) on control; risk difference -12.2 percentage points (95% CI -28.1 to 3.6), risk ratio 0.72 (0.47–1.11); unadjusted two-proportion z-test p = 0.134.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between General Health or Social Discussion and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several domains, including falls, fractures, physical performance, balance, posture, quality of life, pain, exercise confidence, and falls-related confidence. This breadth is useful for describing what was measured in the pilot, but it also means the results address many different questions. The overall pattern should be read as exploratory rather than as a single confirmatory test.

The posted faller counts differ between groups, while the registry’s reported risk-ratio interval includes one. The comparison for participants with multiple falls has no reported analysis. The registry also lists other secondary outcome measures, but the record summarized in the posted results does not establish a consistent pattern of effects across all those domains. Outcomes that were measured but do not have a posted inferential result should not be treated as showing no effect.

Secondary outcomes complement the primary feasibility result; they do not answer the same question. Recruitment and retention assess whether a larger study may be practicable. Falls, function, quality of life, and other outcomes concern possible effects on participants. A pilot’s secondary estimates can help identify which outcomes warrant further study, but they cannot by themselves establish that the intervention changes those outcomes.

Unadjusted secondary results carry less weight because multiple outcomes and analyses create more opportunities for chance findings. The registry lists 26 analyses, but a multiplicity strategy and the full analysis plan are not reported in the registry record. Without that information, it is not possible to know which comparisons were designated in advance or how the overall error from testing multiple outcomes was addressed. Secondary findings should therefore be considered alongside their uncertainty, the pilot context, and the primary feasibility purpose—not as independent confirmation of effectiveness.

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

• Number of Fractures.
• Number of Fallers
• Occiput to Wall Distance
• Scores on the Short Physical Performance Battery (SPPB)
• Scores on Balance Outcome Measure for Elder Rehabilitation (BOOMER).
• Quality of Life (QoL) and Pain Scores Measured Through the EuroQOL Instrument (EQ5D5L) and the Osteoporosis Quality of Life Questionnaire (OQLQ) and a Visual Analog Scale (VAS).
• Scores on Exercise Self-efficacy Scales.
• Score on Short-form Falls Efficacy Scale International (FES-I).

9. Statistical Interpretation

10. Statistical Methods Explained

The registry describes a randomized, parallel-group comparison. Random allocation is intended to make the groups comparable on average, although it cannot guarantee balance in every feature, especially in a pilot. The record identifies single masking but does not say who was masked. The intervention and discussion conditions differ in their content, and the registry does not provide enough detail to assess how masking was implemented.

What does a risk difference describe?

General statistical explanation: a risk difference compares the proportion with an outcome in one group with the proportion in another. A value of zero represents no difference in the proportions; values on either side indicate different directions of the comparison. The posted binary outcomes count participants with an event, rather than recording how many times each person experienced it. For example, the number of fallers is a participant-level measure and is not the same as the total number of falls.

The posted comparisons use risk differences. The primary comparison’s estimate is close to zero, and its interval includes zero. The sign of an estimate depends on the order of the groups in the comparison, so it should be read with the group counts and labels. The registry also reports a risk ratio for the number of fallers. General statistical explanation: a risk ratio compares the event proportions as a ratio, with one representing equal proportions. A ratio above or below one indicates a relative difference whose direction depends on the group order.

What does a confidence interval add?

General statistical explanation: a confidence interval describes a range of estimates compatible with the data and the statistical procedure. It conveys precision as well as direction. An interval that includes the value for no difference does not rule out no difference at the stated confidence level. A wide interval indicates that materially different effects may remain compatible with the observations. An interval is not a guarantee that the true effect lies within its limits, and it does not measure the probability that a particular hypothesis is true.

The registry’s reported faller analysis gives a risk ratio of 1.32 with a 95% confidence interval from .99 to 1.74. Because the interval includes one, it does not exclude equal proportions at that confidence level. The posted p-value for this reported analysis is absent. A separate unadjusted recalculation from posted summary statistics gives p = 0.05. That calculation is not an adjusted model and should be distinguished from the registry’s reported risk-ratio analysis.

Why does the pilot context matter?

This study’s primary purpose is feasibility. A pilot can provide information about recruitment, retention, and delivery, while also producing exploratory outcome data. The trial’s enrollment and arm counts do not by themselves demonstrate that it had adequate precision for each secondary clinical outcome. The original design assumptions and a formal sample-size justification are not reported in the registry record.

The statistical plan, including any planned adjustment for covariates, handling of repeated monthly records, and analysis population, is not reported in the registry record. The record lists 26 analyses, but the methods for all analyses are not specified. Interim analyses are not reported in the registry record. It is therefore not possible to determine from the record whether the posted comparisons follow a prespecified primary analysis plan or how missing observations were handled.

What does over-dispersion mean in general?

General statistical explanation: over-dispersion occurs when observed variation is greater than a statistical model assumes. It is relevant to some count outcomes, where a simple model may underestimate uncertainty if events vary more across participants than expected. The posted primary and specified secondary results in this record are participant counts for binary outcomes, such as whether a person was a faller. These are not event-rate models, so over-dispersion is not the central interpretation for the comparisons. The registry does not provide enough detail to assess any models used for other outcomes.

The planning figures are illustrations based on fractions of the observed effect and stated statistical assumptions. They are not the trial’s original design calculation. The registry’s own sample-size assumptions are not reported in the registry record. Planning calculations can indicate how a future study’s required size changes under specified assumptions, but they cannot validate the observed estimates or replace a design based on a clinically justified target effect.

11. Confidence Intervals and Precision

Precision is best judged from the confidence intervals, not from whether an estimate is described as statistically significant. For the primary feasibility comparison, the reported interval includes no difference between groups. This means the posted data are compatible with no difference as well as with differences in either direction. The interval does not support a precise claim that the groups had identical outcomes.

The registry’s reported analysis for the number of fallers gives a risk ratio of 1.32, with a 95% confidence interval from .99 to 1.74. The range includes one and extends to values indicating a potentially larger relative difference. The interval therefore leaves uncertainty about the size and direction of the underlying contrast. The unadjusted recalculation gives p = 0.05, but that single value does not describe the range of plausible effects and is not the registry’s reported risk-ratio result.

Small pilot trials generally yield less precise estimates than larger studies when outcome frequencies and other conditions are similar. General statistical explanation: fewer observations usually mean that random variation has a greater influence on an estimate, widening its confidence interval. The posted arm sizes are 71 and 70. The record does not report a design intended to estimate each secondary effect with high precision, and the trial’s stated purpose is feasibility.

For the number of participants with multiple falls, the registry posts arm counts and an unadjusted comparison, but no reported analysis. The absence of a reported analysis does not mean that the outcome had no effect; it means the record does not provide a sponsor-reported inferential result for that comparison. More broadly, the registry does not report a complete analysis plan or missing-data methods, limiting how fully the precision and robustness of estimates can be assessed.

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 a reconstruction of the trial’s original design. They give participants per arm for binary outcomes such as the posted participant-count outcomes. 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 the stated fraction of the observed effect. The original trial’s design assumptions and sample-size justification are not reported in the registry record.

The column for 80% power gives the planned participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect is real and the assumptions hold. The 90% power column uses a higher chance of detecting that same specified effect, which requires more participants per arm. For the faller comparison, the planning figures range from 144 participants per arm for 80% power and 192 for 90% power when planning for 100% of the observed effect, to 555 and 742 when planning for 50% of the observed effect. For multiple falls, the corresponding figures are 245 and 328 for 100% of the observed effect, and 1,011 and 1,353 for 50%.

Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants. The figures for 75% of the observed effect fall between the displayed 100% and 50% scenarios. These calculations are not observed power: they are prospective illustrations under stated assumptions, not a measure of what the completed trial achieved. They should not be interpreted as evidence that the observed effects are stable estimates of what a larger trial would find.

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 = 0.930; treatment proportion p₁ = 0.914; average p̄ = 0.922.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3794 = 0.7436.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3792 = 0.3192.
4. n = (0.7436 + 0.3192)² / (-0.0153)² = 4,830.5, rounded up to 4,831 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 <- 0.929577464788732                          # control proportion
p1 <- 0.914285714285714                          # 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(1761084)
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 = 4,831 (80% power), 6,467 (90% power)
 75% of observed effect: n per arm = 8,396 (80% power), 11,239 (90% power)
 50% of observed effect: n per arm = 18,456 (80% power), 24,706 (90% power)
power.prop.test: 4830.5 
Simulated power at n = 4,831 per arm: 0.801 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 26 analyses and 24 outcome measures, with 22 secondary outcomes posted. These counts indicate that the study covered multiple questions, but do not show how the analyses were organized or prioritized. A plan for controlling the chance of false-positive findings across multiple tests is not reported in the registry record. No multiplicity adjustment is described in the posted results.

General statistical explanation: when researchers test many outcomes, the chance that at least one result looks unusual by chance can rise. A prespecified hierarchy, adjustment method, or clear exploratory designation can help readers interpret that situation. Without a reported approach, an isolated secondary p-value should not carry the same evidential weight as a clearly specified primary result. This matters in a pilot with several outcomes spanning falls, fractures, function, balance, posture, and quality of life.

Missing-data methods are not reported in the registry record. The record does not describe whether participants with incomplete follow-up were included in particular analyses, how missing values were handled, or whether sensitivity analyses were conducted. It also does not report the analysis population, such as whether analyses followed the randomized assignment regardless of adherence. These omissions make it difficult to assess how incomplete follow-up or deviations from assigned conditions might affect the results.

The registry does not report an interim-analysis plan, stopping criteria, or a detailed prespecified statistical analysis plan. The record lists a single-masked randomized parallel design, but does not identify who was masked. These details matter because planned analysis choices can shape interpretation, especially when many outcomes are available. Their absence should be understood as a limitation of the registry record, not as evidence that no such plans existed.

For a feasibility trial, it is also important to distinguish the stated success criteria from a formal statistical test. The recruitment criterion is expressed per site, while site-specific recruitment is not reported. The retention criterion is stated as at least 75%, but the record does not clearly explain how the posted primary values map to that criterion. As a result, the published information does not allow a complete audit of each feasibility threshold.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fracture (5.6%), pneumonia (2.9%), stroke (2.9%), chronic obstructive pulmonary disease (1.4%), adverse reaction to forteo (1.4%).

The adverse-event record lists serious adverse events in 17 participants at risk in the exercise group and 12 at risk in the general health or social discussion group. Other adverse events are listed for 43 and 34 participants, respectively. Deaths are recorded as 0 in both groups. These are the posted counts; the registry does not provide an adjusted comparison of adverse events.

The most frequently listed serious-event terms include fracture at 5.6%, pneumonia at 2.9%, stroke at 2.9%, chronic obstructive pulmonary disease at 1.4%, adverse reaction to Forteo at 1.4%, and elevated blood pressure at 1.4%. The registry does not give the denominator or further detail for each term in the posted summary, so these percentages should be read as reported rather than used to infer additional counts.

Adverse-event listings describe events observed during the study; they do not by themselves establish that an event was caused by an assigned intervention. The record does not provide enough detail to assess event timing, severity beyond the serious classification, participant-level overlap, or attribution. The counts are useful for understanding what was recorded, but should not be treated as a comparative safety conclusion.

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

The main contribution of this trial is information about a pilot study of tailored home exercise in women with osteoporotic vertebral fracture. Its primary focus was feasibility: recruitment and retention, alongside the study’s stated adherence target. The posted primary values are similar in scale across the two groups, and the unadjusted comparison is imprecise enough to include no difference. The record does not provide the site-level recruitment information or a clear mapping of the reported values needed to judge all feasibility criteria.

The secondary outcomes describe possible differences in falls and other domains, but those results are exploratory. The reported risk-ratio interval for fallers includes one, and no reported analysis is listed for multiple falls. The trial’s purpose and posted information do not support a definitive conclusion about effects on fractures, falls, function, pain, or quality of life. A p-value or a difference in observed counts alone cannot establish a causal or clinically important effect.

The trial also does not establish whether a larger multicentre study would be feasible at the same recruitment, retention, or adherence levels. The registry describes those as goals, but site-specific achievement and adherence results are not reported in the registry record. Likewise, the record does not state the original sample-size rationale or provide enough analytic detail to verify how all outcomes were handled.

General statistical explanation: results from a pilot are often most useful for informing procedures and generating hypotheses, while estimates of clinical effects may remain uncertain. Here, the posted results should be read in that spirit. They describe the observations and their uncertainty, rather than proving that exercise works or does not work. Further conclusions would require appropriately designed research and fuller reporting, rather than extrapolation from these pilot comparisons.

17. Why This Trial Matters Statistically

This trial illustrates why a pilot’s primary question can differ from its most visible clinical outcome. Recruitment and retention address whether a larger study might be workable, while falls and other secondary outcomes address potential participant effects. Keeping those questions separate prevents an exploratory result from being mistaken for the main purpose of the study.

It also shows why uncertainty matters. The primary comparison does not clearly distinguish the groups, and the reported risk-ratio interval for fallers includes the value representing no relative difference. A point estimate alone can appear more decisive than the full interval warrants. Reporting both the estimate and its uncertainty helps readers see which conclusions remain open.

The trial raises practical statistical issues common to pilot studies: outcome selection, the interpretation of multiple secondary analyses, and the distinction between planning calculations and the original trial design. The registry lists many outcomes and analyses, but does not report a complete multiplicity approach, missing-data methods, or the original sample-size justification. These details affect how confidently readers can interpret results and use them to plan future work.

Finally, feasibility criteria need results at the level at which they are defined. Recruitment was specified per site, but site-specific data are not reported. A group-level count cannot fully answer a site-level target. Clear reporting that links each criterion to its observed measure would make it easier to judge whether the processes intended for a larger study were achieved.

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 limitations are specific to the information available for this trial. The registry defines recruitment success per site, but the number of sites and site-specific recruitment counts are not reported in the registry record. The primary outcome values are posted as 66 and 64, yet the record does not clearly identify how each value maps to recruitment, retention, or their combined endpoint. This limits assessment of the stated feasibility criteria.

The intervention description is incomplete in the registry record: its description of behaviour-change strategies ends mid-sentence. The record also does not report how much exercise participants completed or the posted result for adherence, despite the stated adherence target. Without those details, the delivered intervention and adherence cannot be fully characterized from the registry information.

Although the study was single-masked, the masked party is not identified. Allocation concealment and the statistical analysis plan are not reported in the registry record. Missing-data methods, analysis populations, covariate adjustments, and interim analyses are also not reported. The absence of these details limits assessment of potential bias and analytic robustness.

The secondary-outcome record is broad, but the multiplicity approach is not reported. The registry gives a reported risk-ratio analysis for fallers and no reported analysis for multiple falls, while many other outcome measures are listed. This uneven reporting makes it difficult to assess the full pattern of results. As a pilot, the study’s outcome estimates also remain uncertain; the record does not establish that the trial was designed to provide precise estimates of clinical effects.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Build Better Bones With Exercise — NCT01761084.
• Registry record last updated 2019-11-14; status last verified 2017-03.
• Results first posted 2019-11-14.
• 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

NCT01761084, Build Better Bones With Exercise, is a completed randomized, parallel-group pilot trial sponsored by the University of Waterloo. It enrolled 141 women with osteoporotic vertebral fracture and compared tailored home exercise plus behaviour-change strategies with general health or social discussion. The intervention was described as thrice-weekly exercise for one year, supported by 6 physiotherapist home visits.

The primary focus was recruitment and retention, with stated success criteria of 20 recruits per site and at least 75% retained. The posted primary values are 66 and 64, but the registry does not clearly map those values to the criteria. Secondary outcomes include falls, fractures, function, balance, posture, quality of life, and pain. The reported faller analysis has a risk ratio of 1.32 with a 95% confidence interval from .99 to 1.74; the interval includes one. The record does not report a complete analysis plan, missing-data methods, or multiplicity approach, so clinical conclusions from the secondary results remain exploratory.