Abstract
Context
Minimizing bias in randomized controlled trials (RCTs) includes intention-to-treat analyses. Hospice/palliative care RCTs are constrained by high attrition unpredictable when consenting, including withdrawals between randomization and first exposure to the intervention. Such withdrawals may systematically bias findings away from the new intervention being evaluated if they are considered nonresponders.
Objectives
This study aimed to quantify the impact within intention-to-treat principles.
Methods
A theoretical model was developed to assess the impact of withdrawals between randomization and first exposure on study power and effect sizes. Ten reported hospice/palliative care studies had power recalculated accounting for such withdrawal.
Results
In the theoretical model, when 5% of withdrawals occurred between randomization and first exposure to the intervention, change in power was demonstrated in binary outcomes (2.0%–2.2%), continuous outcomes (0.8%–2.0%), and time-to-event outcomes (1.6%–2.0%), and odds ratios were changed by 0.06–0.17. Greater power loss was observed with larger effect sizes. Withdrawal rates were 0.9%–10% in the 10 reported RCTs, corresponding to power losses of 0.1%–2.2%. For studies with binary outcomes, withdrawal rates were 0.3%–1.2% changing odds ratios by 0.01–0.22.
Conclusion
If blinding is maintained and all interventions are available simultaneously, our model suggests that excluding data from withdrawals between randomization and first exposure to the intervention minimizes one bias. This is the safety population as defined by the International Committee on Harmonization. When planning for future trials, minimizing the time between randomization and first exposure to the intervention will minimize the problem. Power should be calculated on people who receive the intervention.
Key Words
Introduction
The International Committee on Harmonization Statistical Principles for Clinical Trials (ICH E9) guideline has been adopted internationally as the authoritative document on the conduct and analysis of clinical trials.
1
Included in the ICH E9 guideline is a section on the study populations to be included in the analyses, and the reasons for choosing one population over another, depending on circumstances.1
For example, it outlines the times at which one should use an intention-to-treat (ITT) analysis and contrasts that with when it may be appropriate to use a per-protocol analysis.1
ITT analyses aim to evaluate the primary outcome in randomized controlled trials (RCTs) to minimize bias and ensure that the point estimate is as close to the truth as possible.
1
,2
With an ITT approach in mind, the sample size is calculated using the parameters related to the primary end point, attempting to only include the number of participants required to answer the question in the most robust way. This also ensures an ethical approach as studies should be no bigger than required to answer the question (as estimated from prespecified power) so that participants are not unnecessarily enrolled and exposed to harms or not offered benefits that may have already been defined by the study.Two time points are crucial when considering the design, conduct, and analysis of RCTs within an ITT context: randomization and first exposure to the intervention. The ICH E9 guideline recognizes that subgroups of people might withdraw from RCTs at different stages of study engagement, including eligible people who were randomized:
1
- 1.but
- a.were not exposed to the intervention; and
- b.provided no further postrandomization data; while
- c.participants, clinicians, and other research staff were still blinded to their allocated arm;
- a.
- 2.and were not exposed to the intervention but provided no further data;
- 3.and were exposed to the intervention, and provided further data, but withdrew before the primary end point.
The present study deals entirely with this first group where people withdrew between randomization and first exposure to the intervention.
For most RCTs, participants who withdraw between randomization and first exposure to the intervention constitute an extremely small proportion of participants, and their withdrawal consequently makes little difference to the power of the studies or its conclusions. By contrast, this proportion is appreciable in hospice/palliative care studies.
In hospice/palliative care RCTs, there are three issues that suggest a strict application of the ICP E9 guidance to be applied to ensure that this source of bias away from the new intervention is minimized:
- 1.Hospice/palliative care studies tend to seek a clinically significant difference between groups requiring a large delta between groups.3,4,5,6Because of this, sample sizes tend to be smaller, potentially leading to a greater loss of power when people withdraw.2
- 2.Withdrawal of study participants cannot be predicted at enrollment, or it would be unethical to enroll those persons in the first instance. A proportion of these people will withdraw between randomization and first exposure to the intervention.
- 3.The proportion of subsequent withdrawals after intervention commencement at any point before the primary end point is also higher,7even when the trial measures the end point at the earliest clinically appropriate time for the intervention under study. In some hospice/palliative care RCTs, total withdrawals any time between randomization and the end point can be as high as 50%8and sufficient to introduce bias.7Importantly, most withdrawals will be unrelated to the intervention(s) being tested.2,7,9
An unnecessary bias may be avoided if withdrawals between randomization and first exposure to the intervention are excluded from the analysis. Currently, they are assumed to be nonresponders (a conventional view of ITT as they are postrandomization), potentially introducing a systematic bias away from the intervention being evaluated. However, ICH E9 directly addresses such a situation, offering an alternative. It states that: “The intention-to-treat principle would be preserved despite the exclusion of [people who withdraw between randomisation and first exposure to the intervention] provided, for example, that the decision of whether or not to begin treatment could not be influenced by knowledge of the assigned treatment.”
1
(p1929) Crucially, there is no indication that the interpretation and applicability of the ITT principle changes with such exclusions from the data sets. The ICH E9 considers such analyses to be unambiguously ITT; therefore, analyses that exclude the data of participants between randomization and first exposure to the intervention should not be seen as modified ITT.The unanswered question is whether applying the conventional interpretation of ITT to the primary analysis (which assumes withdrawals before exposure to the intervention are nonresponders) may introduce bias against the finding of effectiveness and therefore justify exclusion of these patients from the analysis. Conversely, if data from such participants are excluded, there will be a modest but at times appreciable loss of power and potential to underestimate the adverse event rates.
Given concerns about potentially higher rates of attrition between randomization and first exposure to the intervention, which contributes to attrition that occurs in hospice/palliative care RCTs, this article sought to explore this problem through three approaches:
- 1.Demonstrate theoretically how inclusion of the data from consented participants who withdraw between randomization and first exposure to intervention (with the assumption that they are nonresponders in primary analyses) reduces the power and effect size of a study using three different types of primary outcome measures (binary, continuous, and time-to-event data);
- 2.Quantify these rates in a convenience sample of 10 completed double-blind and placebo-controlled Phase III hospice/palliative care studies while evaluating the impact on the power and effect size on these selected 10 Phase III studies; and
- 3.Offer recommendations for future conduct and analyses of all hospice/palliative care Phase III studies.
If power is affected appreciably, a strong case could be made for a change to the approach to analyses without compromising the interpretation and applicability of the ITT principle as first outlined by ICH E9.
Methods
Phase 1: Theoretical Model
Illustrative hypothetical models were developed reflecting hypothetical studies with three different effect sizes (small, medium, and large) and three types of outcome measures (binary, continuous, and time-to-event). For the purpose of these theoretical models, the authors assumed that the hypothetical studies had already closed for recruitment, and all withdrawals were only between randomization and first exposure to the intervention. The sample size calculation package nQuery (Version 8.0; Statsols Ltd, Cork, Ireland) was used to generate these three theoretical models corresponding to the type of primary outcome measure:
- 1.Binary Outcome Data. The authors assumed that the proportion of responders in the theoretical control group was 30%, whereas in the intervention group, responders accounted for 40% (small effect size [10%]), 50% (moderate effect size [20%]), and 60% (large effect size [30%]) of participants. This corresponded to odds ratios of 1.56, 2.33, and 3.50 for small, medium, and large sizes, respectively.
- 2.Continuous Data. The SD was set at 1.0, and mean differences between groups of 0.2, 0.5, and 0.8 (to reflect small, medium, and large effect sizes, respectively) were used.
- 3.Time-to-event Data. Assuming hazard ratios of 0.8, 0.6, and 0.4 (for small, medium, and large effect sizes, respectively), event rates by the primary end point were 50% and 42% (in the control group) and 31.5% and 17.7% (in the intervention group).
Impact on Power
For each type of outcome measure, we first generated the sample size with appropriately fixed 0.05 significance level and 80% power reflecting levels most frequently used in hospice/palliative care trials to ensure that the models reflected current practice. We then calculated a revised sample size and power calculation based on the assumption that 5% of study participants withdrew between randomization and first exposure to the intervention and were excluded from the analysis.
Impact on Odds Ratio
Studies with binary primary outcomes were used to assess the theoretical impact of 5% withdrawals between randomization and first exposure to the intervention on the studies odds ratios. Assuming 0.05 significance level, 80% power and three study effect sizes (small, medium, and large), we first calculated the odds ratios of the studies assuming these withdrawals were included in the analysis as nonresponders. We then repeated the calculations assuming these withdrawals were excluded from the analysis.
For continuous or time-to-event analyses, withdrawal between randomization and first exposure to the intervention does not allow imputation given the lack of data. If the study includes such people in the overall a priori recruitment total, the study will again be at risk of being underpowered.
Phase 2: Assessing the Model Using Phase III Hospice/Palliative Care Studies
A convenience sample of 10 RCTs published in the hospice/palliative care literature between 2003 and 2018 was used to evaluate the problem. The selected trials were led by four clinical research teams from around the world and were double-blind and placebo-controlled randomized trials testing pharmacological interventions for symptom control in people with advanced life-limiting illnesses. Crossover and parallel-arm studies were included.
Study characteristics retrieved from study protocols and published articles included the following: study design (randomization, blinding, and treatment/control intervention), the primary outcome, number of sites involved, days between successful screening and first exposure to the study intervention, sample size, number of participants randomized, and number of participants withdrawn before first intervention.
Study characteristics were summarized using counts, percentages, medians, interquartile ranges, SD, and means as appropriate. Descriptive statistics were used to present the types of withdrawal.
For each study, we calculated the proportion of participants who withdrew between randomization and first exposure to the intervention. We then calculated changes in the power that would have occurred if these people's data were excluded from the analysis. For studies with binary primary outcomes, the impact on changes in odds ratio was also examined for these same exclusions.
Results
Results of the Theoretical Modeling
Impact on Power
For hypothetical studies with binary outcomes, a 5% rate of withdrawal between randomization and first exposure to the intervention leads to 2.0%–2.2% difference in power depending on the inclusion or exclusion of these data from the analysis (Table 1). For studies with continuous outcomes, a 5% attrition caused 0.8%–2.0% power loss, depending on the study effect sizes; greater power loss was observed in studies with smaller effect sizes. For studies with time-to-event outcomes, the power loss associated with 5% attrition ranged from 1.6% to 2.0%; again, greater loss of power was observed in studies with smaller effect sizes.
Table 1The Impact of Withdrawals Between Randomization and First Exposure to the Intervention in ITT Analyses on Losing Study Power
| Type of Study Outcomes | Small Effect Size | Medium Effect Size | Large Effect Size | |||
|---|---|---|---|---|---|---|
| No Withdrawals | 5% Withdrawals | No Withdrawals | 5% Withdrawals | No Withdrawals | 5% Withdrawals | |
| Binary outcomes (e.g., response rate, etc.) | ||||||
| Proportion in control group (%) | 30 | 30 | 30 | 30 | 30 | 30 |
| Proportion in intervention group (%) | 40 | 40 | 50 | 50 | 60 | 60 |
| Effect size (%) | 10 | 10 | 20 | 20 | 30 | 30 |
| Odds ratio | 1.556 | 1.556 | 2.333 | 2.333 | 3.500 | 3.500 |
| N per group | 356 | 338 | 93 | 88 | 42 | 40 |
| Power (%) | 80 | 77.9 | 80 | 77.8 | 80 | 78.0 |
| Power loss (%) | 2.1 | 2.2 | 2.0 | |||
| Continuous outcomes (e.g., quality of life, etc.) | ||||||
| Mean difference | 0.2 | 0.2 | 0.5 | 0.5 | 0.8 | 0.8 |
| SD | 1.0 | 1.0 | 1.0 | 1.0 | 1.0 | 1.0 |
| Effect size | 0.2 | 0.2 | 0.5 | 0.5 | 0.8 | 0.8 |
| N per group | 394 | 374 | 64 | 61 | 26 | 25 |
| Power (%) | 80 | 78.0 | 80 | 78.2 | 80 | 79.2 |
| Power loss (%) | 2.0 | 1.8 | 0.8 | |||
| Time-to-event outcomes (e.g., overall survival, etc.) | ||||||
| Event rate at primary end point in control group (%) | 50 | 50 | 50 | 50 | 50 | 50 |
| Event rate at primary end point in intervention group (%) | 42 | 42 | 31.5 | 31.5 | 17.7 | 17.7 |
| Hazard ratio | 0.8 | 0.8 | 0.6 | 0.6 | 0.4 | 0.4 |
| N per group | 589 | 560 | 106 | 101 | 33 | 31 |
| Power (%) | 80 | 78.0 | 80 | 78.1 | 80 | 78.4 |
| Power loss (%) | 2.0 | 1.9 | 1.6 | |||
ITT = intention-to-treat.
Impact on Odds Ratio
For hypothetical studies with binary outcomes, the impact of counting withdrawals as nonresponders on odds ratios ranged from 0.06 to 0.17 (Table 2). Excluding the withdrawals changed the odds ratios; greater loss of power was seen with larger effect sizes.
Table 2The Impact of Counting Withdrawals Between Randomization and First Exposure to the Intervention as Nonresponders on Changing Odds Ratio
| Effect of Response Rate | Binary Outcomes (e.g., Response Rate, etc.) | |||||
|---|---|---|---|---|---|---|
| Small Effect Size | Medium Effect Size | Large Effect Size | ||||
| No Withdrawals | 5% Withdrawals | No Withdrawals | 5% Withdrawals | No Withdrawals | 5% Withdrawals | |
| Responders in control group (%) | 30 | 25 | 30 | 25 | 30 | 25 |
| Responders in intervention group (%) | 40 | 35 | 50 | 45 | 60 | 55 |
| Odds ratio | 1.556 | 1.615 | 2.333 | 2.455 | 3.500 | 3.667 |
| Odds ratio difference | 0.059 | 0.122 | 0.167 | |||
Assessing the Model Using Phase III Hospice/Palliative Care Studies
Study Characteristics
Ten studies were conducted across 85 sites in Australia, Norway, and the U.K. (Table 3). The total number of participants randomized to the studies was 1710. The median time to primary end point was seven days (interquartile range 4–16). In seven studies,
11
, 12
, 13
, 14
, 15
, 16
, 17
median time from screening to first exposure to the study intervention was one day, whereas for three studies,18
, 19
, 20
these data were not available). In three studies,12
,14
,17
there was a run-in period before receiving the first study intervention for a median of one day. The a priori power calculations for seven studies were set at 80%,11
, 12
, 13
, 14
, 15
,17
,19
one study was powered to 85%,16
and two studies were powered to 90%.18
,20
Table 3The Impact of Withdrawals Between Randomization and First Exposure to the Intervention on Potential Power Loss and Odds Ratio Changes for 10 RCTs in Hospice/Palliative Care
| Study | Primary Outcome | Sample Size (Per Arm) | Median Days: Successful Screen to Receiving First Exposure to the Intervention | Withdrawals Between Randomization and First Exposure to the Intervention, n (%) | Corresponding Power Loss (%) | Corresponding Odds Ratio Difference |
|---|---|---|---|---|---|---|
| Binary outcomes | ||||||
| Currow et al. 13 | Treatment response | 190 in total; megestrol acetate (n = 61) or dexamethasone (n = 67) or placebo (n = 62) | 1 | 5/190 (2.6) | 1.2 | 0.22 |
| Hardy et al. 16 | Response rate | 187 in total; ketamine (n = 93) or placebo (n = 92); deleted from analysis (n = 2) | 1 | 4/185 (2.2) | 0.5 | 0.06 |
| Fallon et al. 14 | Treatment response | 233 in total; pregabalin & radiotherapy (n = 116) or placebo & radiotherapy (n = 117) | 1 | 2/233 (0.9) | 0.3 | 0.01 |
| Currow et al. 12 | Treatment response | 223 in total; sertraline (n = 112) or placebo (n = 111) | 2 | 0/223 (0) | 0 | 0 |
| Continuous outcomes | ||||||
| Klepstad et al. 18 | Time needed to achieve pain relief | 40 in total; immediate-release morphine (n = 19) or sustained-release morphine (n = 21) | Not available | 4/40 (10) | 2.2 | Not applicable |
| Oxberry et al. 19 | NRS breathless severity score | 39 in total; crossover: oramorph/oxynorm/placebo (n = 39) | Not available | 2/39 (5.1) | 1.8 | Not applicable |
| Paulsen et al. 20 | Pain intensity | 50 in total; methylprednisolone (n = 26) or placebo (n = 24) | Not available | 1/50 (2) | 1.0 | Not applicable |
| Currow et al. 17 | Breathlessness change | 287 in total; morphine (n = 146) or placebo (n = 141) | 1 | 8/287 (2.8) | 0.7 | Not applicable |
| Agar et al. 11 | NuDESC score | 249 in total; risperidone (n = 82) or haloperidol (n = 81) or placebo (n = 86) | 0 | 11/249 (4.4) | 0.1 | Not applicable |
| Time-to-event outcomes | ||||||
| Fallon et al. 15 | Duration of analgesic benefit | 214 in total; ketamine (n = 107) or placebo (n = 107) | 1 | 3/214 (1.4) | 0.6 | Not applicable |
The total number of participants who were randomized but were not exposed to the intervention was 40, which was 2.34% of the 1710 patients randomized in all 10 studies.
Table 3 presents the impact of withdrawals between randomization and first exposure to the intervention on power loss and odds ratio changes for all Phase III studies. Primary outcomes were binary (four studies),
12
, 13
, 14
,16
continuous (five studies),11
,18
, 19
, 20
or time-to-event (one study).15
Only one study had no withdrawals between randomization and first exposure to the intervention.
12
For all other studies, this proportion ranged from 0.9% to 10.0%, which corresponded to 0.1%–2.2% power loss reflecting increasing loss of power with and increasing proportion of such withdrawals.13
, 14
, 15
, 16
, 17
, 18
, 19
, 20
The exception to this was the study by Agar et al.,11
where a 4.4% rate corresponded to a 0.1% loss of power; with the power loss being mitigated because of the baseline and follow-up outcome, correlation was considered in the sample size calculation.For studies with binary outcomes,
12
, 13
, 14
,16
withdrawal between randomization and first exposure to the intervention ranged from 0.9% to 2.6%, with corresponding 0.01–0.22 changes in odds ratios when the withdrawals were excluded from analysis.Discussion
Our theoretical model demonstrated that an ITT population that excluded participants who withdrew between randomization and first exposure to the intervention resulted in a loss of power of approximately 2% compared with an analysis that included these participants, irrespective of the primary outcome measures used. Effect size did not impact on this loss of power in studies with binary outcomes although, as expected from first principles, power loss was relatively less in trials with continuous or time-to-event outcomes with moderate or large effect sizes. In studies with binary outcomes, excluding withdrawals changed the odds ratio; the loss of power was greater with larger effect sizes. In studies with large effect sizes, the odds ratio changed by approximately 17%.
Across 10 trials conducted in people with advanced life-limiting illnesses, 2.34% of consented participants withdrew between randomization and first exposure to the intervention. One study experienced no withdrawals, and one study had a withdrawal rate of 10%. The loss of power paralleled the rate of withdrawal and was similar to the theoretical model, ranging between 0.1% and 2.2%. The expected power loss was not seen in the study by Agar et al.,
11
in which 4.4% rate of withdrawals led to only 0.1% loss of power because the method of sample size calculation mitigated the impact of withdrawals. By contrast, in the studies that used a binary outcome, excluding withdrawals between randomization and first exposure to the intervention changed the odds ratio by as much as 22%.Although attrition between randomization and first exposure to the intervention represents a relatively small proportion of participants in studies in general, the phenomenon is relevant to RCTs in people with advanced life-limiting illnesses given that overall sample sizes in symptom control studies are often relatively small because of the large delta required for clinically relevant differences of effect size between groups. This impact is further amplified because most hospice/palliative care RCTs are powered to 80% (including seven of the 10 studies in our convenience sample). The smaller the trial, the greater the loss of power with withdrawals as each individual carries more power.
Withdrawals between randomization and first exposure to the intervention from binary outcome trials affect the odds ratio if included in the analysis as nonresponders, especially in the typically large effect size trials in palliative care. A 22% change in odds ratio represents a clinically relevant difference potentially. Participants who withdraw between randomization and first exposure to the intervention from trials using continuous or time-to-event outcome as their primary powered end point will not contribute to the analysis unless missing data are imputed. Yet, they provide no data for imputation as they have not been exposed to the intervention. Including the population who have no exposure to the intervention (or control) and treating their data in the same way as any participants who has been exposed to the intervention does not help to minimize a potential bias.
Implications for Trial Conduct and Analysis
Excluding people who withdraw between randomization and first exposure to the intervention effectively means that the population described for the primary analysis in hospice/palliative care RCTs (subject to certain caveats) would be both not only the ITT population but also the safety population—that is those who have had exposure to the intervention and can exhibit treatment emergent adverse events. The theoretical model and its application to our convenience sample of 10 studies suggest that this use of the safety population (defined as “[…] those … who received at least one dose of the investigational drug”
1
(p1934)) may pose advantages for RCTs in hospice/palliative care and other frail populations.However, for this argument to be valid, there are four criteria that must be met. To exclude study participants who withdraw between randomization and first exposure to the intervention from an ITT analysis data set, criteria include the following:
- 1.As noted in the ICH E9 guideline, the study must still be blinded at the time of withdrawal.1This is to ensure that any decisions about the start of the intervention are not influenced by knowledge of the assigned intervention.1This may preclude some cluster-randomized studies that are single blinded or unblinded.
- 2.Access to each arm must happen simultaneously.2There can be no delay to the access to one arm, or unblinding will have occurred. (This was a principle that led to the ITT principle being articulated in the first place.)
- 3.As a check on reverting to the original ITT principles, the drop-out rate per arm should be of the same order of magnitude.2This is to ensure that the withdrawal is due to natural disease progression or sudden death, rather than the study intervention.2
- 4.The impact of excluding the data from such participants should be evaluated as a sensitivity analysis.2
Recognizing that attrition between randomization and first exposure to the intervention is a potential problem in hospice/palliative care RCTs suggests that the design of such studies should be reconsidered. The following is a proposed hierarchy of changes that may help investigators to reduce this risk.
Closed Studies
If the conditions for excluding participants between randomization and first exposure to the intervention are met, it is reasonable to consider excluding these data from the primary analysis. The requirements for ITT will be maintained (and therefore the resultant analysis should not be labeled a modified ITT), and the effect of the new intervention will not be underestimated. This will, however, lead to a loss of power.
Studies Currently Open to Recruitment
Additional recruitment to reach the original sample size may be possible if participants withdraw between randomization and first exposure to the intervention (and this is stipulated in the protocol). The withdrawals should not be counted toward the proposed optimal study recruitment.
Designing Future Studies
Ideally, participants should not be randomized until they are ready to be exposed to the intervention, although this is not always practical. If there is a run-in period, randomization should occur at the end of that period. Alternative sample size calculation can also be used, such as the one in the study by Agar et al.,
11
which seems to mitigate against loss of power because of withdrawals between randomization and first exposure to the intervention.Implications for Future Research
Prediction of eligible participants most likely to withdraw before any exposure to the intervention would enable refinement of eligibility criteria. End-of-study attrition rates in supportive/palliative oncology studies have been shown to be associated with higher baseline symptom burden (among other factors).
21
Determining any relationship between participants' overall performance status, disease status, and comorbidities at baseline and their withdrawal before they can be exposed to the intervention may help to refine recruitment strategies in future hospice/palliative care studies and aid generalizability.Limitations
A priori estimates of withdrawal proportion were neither available nor detailed breakdowns of withdrawal between first exposure to the intervention and the primary end point for the 10 included Phase III studies. Understanding in more detail study withdrawal rates in Phase III hospice/palliative care studies between randomization and each study's primary end point will further develop this work.
Conclusions
Excluding withdrawals between randomization and first exposure to the intervention from the primary analysis in hospice/palliative care RCTs still fully honors the principles of ITT, formed from the population that is best described as the safety population—those people who have been exposed to the intervention at least once. Although the loss of power may be modest, the impact of withdrawals between randomization and first exposure to the intervention can be minimized or even eliminated by attention to trial design for new studies and managing loss of power by additional recruitment for studies currently open. Exclusion of data from these participants would minimize one small but appreciable bias in reporting clinical trial outcomes.
Disclosures and Acknowledgments
The authors acknowledge the extreme selflessness of participants in symptom control studies in the hospice/palliative care setting and thank them for volunteering to participate. This provides an amazing legacy for future generations for which the whole community is grateful. The authors also thank Ms. Debbie Marriott for her expertise in manuscript formatting and generous assistance with the manuscript submission.
This study was funded from discretionary funds held by the university teams involved in the study. The authors declare no conflicts of interest.
Ethical approval: The use of secondary deidentified data did not require additional ethics approval. Approvals for primary data collection were obtained from all relevant Human Ethics Research Committees before each study commenced.
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Publication history
Published online: November 08, 2019
Accepted:
October 25,
2019
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- Intention-to-Treat Analyses for Randomized Controlled Trials in Hospice/Palliative Care Enhanced by Principled Methods to Handle Missing DataJournal of Pain and Symptom ManagementVol. 60Issue 4
- PreviewKochovska et al.1 raised an important issue, namely how to handle missing outcome data in a trial. They focus on the scenario of dropout before initiating treatment in the context of palliative care; a context where patient dropout is particularly high and sample sizes are small. The authors focus on two ways of handling missing outcome data, namely assuming that participants with missing data were nonresponders and excluding these participants from the analysis.
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