Can You Condition on a Collider in an Rct

Epidemiology. Author manuscript; bachelor in PMC 2022 January i.

Published in final edited course equally:

PMCID: PMC5130591

NIHMSID: NIHMS818738

Biases in randomized trials: a conversation between trialists and epidemiologists

Mohammad Ali Mansournia

¹Department of Epidemiology and Biostatistics, School of Public Health, Tehran University of Medical Sciences, Tehran, Iran

Julian P. T. Higgins

²Schoolhouse of Social and Customs Medicine, University of Bristol, Bristol, UK

Jonathan A. C. Sterne

ⁱⁱSchool of Social and Customs Medicine, Academy of Bristol, Bristol, UK

Miguel A. Hernán

ⁱⁱⁱDepartments of Epidemiology and Biostatistics, Harvard School of Public Wellness, Boston, MA, U.s.a.

^ivHarvard-MIT Partition of Health Sciences and Technology, Boston, MA, USA

Abstract

Trialists and epidemiologists often use dissimilar terminology to refer to biases in randomized trials and observational studies, even though many biases accept a similar construction in both types of study. Nosotros apply causal diagrams to represent the structure of biases, as described by the Cochrane Collaboration for randomized trials, and provide a translation to the usual epidemiologic terms of confounding, selection bias, and measurement bias. This structural arroyo clarifies that an explicit description of the inferential goal—the intention-to-treat effect or the per-protocol upshot—is necessary to appraise risk of bias in the estimates. Existence aware of each other'southward terminologies volition enhance communication between trialists and epidemiologists when considering key concepts and methods for causal inference.

Keywords: bias, randomized trial, Cochrane bias domains, causal diagram

Introduction

Randomized controlled trials (RCTs) and observational studies are used to assess the causal effects of medical interventions.ⁱ By definition, treatment strategies are randomly assigned in RCTs but non in observational studies. Randomization, which prevents bias due to non-comparability betwixt groups, is exploited in total when the data assay follows the "intention-to-care for" principle.

Some other deviation between some RCTs and observational studies is masking (blinding) of trial participants and personnel, which can exist achieved past using a placebo that is duplicate from the agile treatment. Masking prevents differential intendance during follow-upward, accounts for nonspecific effects associated with receiving an intervention (placebo effects), may facilitate blinding of upshot assessors, and may better adherence.

Widespread use of masking and of intention-to-care for analyses became established by regulatory requirements, which privileged intention-to-care for analyses of double-blind placebo-controlled RCTs to assess the efficacy of drugs earlier licensing. Yet, masking is sometimes non viable (e.g., in surgical trials), and may not even be desirable (east.grand., in businesslike trials whose goal is estimating effects in existent-world weather). An intention-to-care for analysis is not feasible if trial participants are lost to follow-up and has disadvantages in safe and non-inferiority trials.²

Discussions nigh the differences between RCTs and observational studies can be complicated past the different terminology employed past trialists and epidemiologists.³ Trialists oft utilize the taxonomy of bias typified by the Cochrane tool for assessing chance of bias in RCTs: choice bias, operation bias, detection bias, attrition bias, reporting bias, and other bias.^four,5 Epidemiologists, on the other hand, tend to utilise the categories confounding, selection bias, and measurement (or data) bias.^1,six,7

Causal diagrams take been used extensively to represent biases in epidemiologic studies.^8-fourteen These diagrams, represented as directed acyclic graphs, comprise variables (nodes) and arrows (directed edges). The absenteeism of an pointer pointing from variable A to variable B indicates that variable A does not accept a direct causal event on B. A key advantage of causal diagrams is that they provide a mathematically rigorous nonetheless intuitive tool for deducing the statistical independencies implied by the lack of causal arrows.^1,8,9

Here we apply causal diagrams to represent the biases described in the Cochrane Adventure of Bias Tool, and provide a translation to the epidemiologic terms of confounding, selection bias, and measurement bias. For simplicity, we focus on individually randomized (not-cluster-randomized), parallel group (non-crossover) trials that compare ii time-fixed handling strategies. We commencement past reviewing the main types of causal effect that are of interest in RCTs.

Intention-to-treat issue and per-protocol outcome

The intention-to-care for upshot is the upshot of treatment assignment (or allotment).¹⁵ Consider an RCT in which HIV-positive individuals are assigned to either initiating a new handling Z=1 or to continuing on their existing treatment Z=0, and are followed until death or the end of follow-up at 5 years. The effect of involvement is 5-year mortality Y (ane: aye, 0: no). The intention-to-care for effect is unbiasedly estimated by an intention-to-treat assay that compares the hateful outcome betwixt those assigned to Z=1 and Z=0. For example, the intention-to-treat issue on the causal run a risk deviation calibration is unbiasedly estimated past the difference of the risks in the groups Z=1 and Z=0, which are readily computed from the written report data.

The magnitude of the intention-to-treat effect in a particular study depends on the magnitude and type of adherence to the assigned treatment strategies. To see this, consider two RCTs with identical eligibility criteria and that compare the same two strategies. In the first RCT, but half of the patients assigned to the new treatment (Z=1) stop upward really taking it (A=ane); the other half do not take it (A=0). In the second RCT, all patients assigned to treatment accept it (that is, patients with Z=i also have A=1). In both studies all patients assigned to Z=0 cannot accept the new treatment considering it is non bachelor outside the study (that is, patients with Z=0 also have A=0). Even if the event of the new treatment is identical in both studies, the intention-to-treat event will more often than not differ between the two studies. For case, the intention-to-treat outcome will exist closer to the aught in the first RCT than in the second 1 if the event of handling goes in the aforementioned direction (beneficial or harmful) for all patients, and more beneficial in the offset RCT than in the second one if adherers tend to be those for whom treatment has a benign upshot and not-adherers tend to be those for whom handling has a harmful result.¹ If the in a higher place RCTs were caput-to-head trials that assigned participants to two active treatments, then the intention-to-treat outcome in the first RCT might too be either closer or further from the cipher than that in the second RCT.²

An alternative to the intention-to-care for effect that is non affected by the study-specific adherence to treatment is the per-protocol effect, that is, the causal result that would take been observed if all patients had adhered to the protocol of the RCT. Unfortunately, valid estimation of the per-protocol result in the presence of imperfect adherence generally requires untestable assumptions.^xvi

Two common approaches to guess the per-protocol effect are (i) comparison the outcomes of those who took handling A=1 and treatment A=0 (regardless of the treatment they were assigned to), e.chiliad., Pr[Y=ane|A=ane] − Pr[Y=i|A=0], and (ii) comparing the outcomes of those who took treatment A=one among those assigned to Z=1 and handling A=0 amongst those assigned to Z=0, eastward.g., Pr[Y=one|A=1, Z=one] − Pr[Y=1|A=0, Z=0].) Arroyo (i) is often referred to as an "equally treated" analysis and approach (ii) as a "per protocol" analysis.^2,8 Neither approach is by and large valid to estimate the per-protocol consequence, equally we discuss below. (1000-estimation and instrumental variable methods tin sometimes be used to approximate some form of per-protocol effects fifty-fifty in the presence of unmeasured confounders in Figures 1c and ​ 1d.^16,17)

Per-protocol effect: Cochrane selection bias/ Epidemiologic choice bias in a per-protocol analysis

Per-protocol effect: Cochrane selection bias/ Epidemiologic misreckoning in an as-treated assay

Although "every bit treated" and "per-protocol" analyses are potentially biased, the per-protocol result may be of greater interest to patients and their clinicians than the intention-to-treat consequence. We at present discuss how the potential for bias in effects estimated from RCTs depends on whether the goal is to approximate the per-protocol or the intention-to-care for outcome.

Cochrane bias domains and causal diagrams

The Cochrane Risk of Bias Tool for randomized trials covers six domains of bias.^4,5 In the next sections, we use causal diagrams to show the structure of most of these biases, and hash out their correspondence to the epidemiologic terms of confounding, option bias, and measurement bias. Because all these biases can occur under the null, we draw the causal diagrams nether the causal null hypothesis, unless otherwise specified. (Any causal construction that results in bias nether the null will also cause bias under the alternative that treatment has an effect on the event, just the converse is not true.) For each bias, we explain whether it affects the intention-to-treat result or the per-protocol upshot. Our definition of bias is the same equally in Affiliate 10 of reference 1 under either a randomization model or a correct population model.^eighteen,19

Option bias

In its Risk of Bias Tool, Cochrane defines pick bias as the upshot of "systematic differences betwixt baseline characteristics of the groups that are compared."⁴ The presence of "systematic differences between baseline characteristics" means that the distribution of prognostic factors varies between the groups being compared. The bias may affect the estimate of the intention-to-care for outcome and/or the estimate of the per-protocol issue, depending on the definition of "groups that are compared."

Let usa first consider the case in which the "groups that are compared" are the randomized groups Z=1 and Z=0. There are at least iii reasons why differences in the distribution of risk factors may ascend.

(i) The assignment of patients to a group is influenced by knowledge of which treatment they volition receive

This bias can occur if the assignment that was not properly randomized or the randomized consignment was not sufficiently concealed, and and so the person enrolling participants was enlightened of allocation sequence and influenced which patients were assigned to each group based on their prognostic factors. This situation is depicted past the causal diagram in Figure 1a that includes the prognostic factors 50 (e.thousand., CD4 count, viral load) as mutual causes of the outcome Y and the assignment Z. The arrow from L to Z may be due to the improperly randomized or insufficiently curtained resource allotment sequence. There are other causal diagrams that stand for common causes of Z and Y (see, for example, Affiliate 7 of Reference 1); we chose the simplest.

Intention-to-treat effect: Cochrane option bias/Epidemiologic misreckoning in an intention-to-treat analysis

Epidemiologists refer to biases that arise from the presence of mutual causes as confounding. The being of common causes L_Z of consignment Z and effect Y introduces confounding bias for the intention-to-treat effect in an intention-to-care for analysis that compares individuals in groups Z=1 and Z=0, and for the per-protocol outcome in a per-protocol analysis that compares individuals in groups Z=1 and Z=0 with A=Z. In both cases, the Cochrane Risk of Bias Tool refers to this bias as selection bias; run into Table.

Tabular array

Translation of Cochrane bias in randomized trials domains into common epidemiologic terms

Cochrane bias domain	Epidemiologic term	Bias in intention-to-treat consequence	Bias in per-protocol effect
Selection bias	Confounding or selection bias	Yep	Yeah
Operation bias	Biased straight effect or confounding	No	Yes
Detection bias	Measurement bias	Yes	Yes
Attrition bias	Selection bias	Yes	Yes
Reporting bias	Non-structural bias that cannot be represented in our causal diagrams	Yep	Yep

Appropriate randomization, generation, and concealment of the allotment sequence, or adjustment for the prognostic factors 50 removes the 50 →Z pointer and therefore the confounding bias.

Even under perfect randomization procedures, random imbalances in prognostic factors may bias intention-to-treat effect estimates. This then-called chance misreckoning²⁰ (sometimes referred to every bit allocation bias^xixor accidental bias^18,21,22) is quantitatively addressed by frequentist confidence intervals and is mitigated by adjusting for measured prognostic factors that are imbalanced.^1,10 Dissimilar the structural misreckoning depicted in Effigy 1a, hazard misreckoning is expected to go smaller equally sample size increases.

(ii) The decision to recruit a patient is influenced by noesis of which treatment the patient will receive. ^19,21

This bias can occur if an investigator is aware of the random sequence and decides to enroll patients with certain prognostic factors simply if they are known to be assigned to a item handling strategy. The Cochrane Adventure of Bias Tool describes this problem: "Knowledge of the side by side assignment […] can crusade selective enrolment of participants on the basis of prognostic factors. Participants who would have been assigned to an intervention accounted to be 'inappropriate' may be rejected."⁴

The causal diagram in Effigy 1b represents this scenario. The node S is the option into the trial (one: yes, 0: no), which depends on the values of consignment Z and prognostic factors L. The box around Southward indicates that the assay is restricted to those with South=ane. This bias arises from the selection of a subset of the potential report population into the analysis and, because South is a common effect of consignment and prognostic factors, both intention-to-care for and per-protocol analyses may be biased fifty-fifty if both effects are truly zip. Epidemiologists¹⁰ and Cochrane refer to this bias every bit selection bias (Table 1).

Intention-to-treat issue: Cochrane selection bias/Epidemiologic selection bias in an intention-to-care for analysis

The elimination of this selection bias requires removing the Z →S arrow through appropriate concealment of the allotment sequence, or adjustment for the prognostic factors Fifty.

(iii) The decision to adhere to the assigned treatment is influenced by prognostic factors

This may result in an imbalance between the groups A=one and A=0, but not between the groups Z=one and Z=0. Therefore, this imbalance will not bias the intention-to-treat judge, just will generally bias the per-protocol approximate of a naïve per-protocol analysis. This tertiary case is not addressed by the Cochrane Risk-of-Bias Tool.

The causal diagram in Figure 1c represents this scenario. The node U_A stands for common causes (e.1000., symptoms resulting from severe immunosuppression) of adherence to treatment A and outcome Y.² The node Southward is the variable selection into the per-protocol population (1: yeah, 0: no), which depends on the values of Z and A (Southward=1 if Z=A, South=0 if Z≠A), and the analysis is restricted to those with S=1.

Epidemiologists may refer to this bias equally choice bias because it arises from the selection of a subset (the per-protocol population) of the study population into an analysis that compares Z=1 vs. Z=0. However, note that this selection bias for the per-protocol effect merely arises when there is misreckoning of the effect of A due to mutual causes U_A of A and Y.

Regardless of whether we refer to this bias as misreckoning or selection bias, reducing information technology requires either a masked design or a non-naïve, more realistic per-protocol analysis that adjusts for the variables U_A or their proxies. Because a per-protocol analysis compares groups not entirely defined by randomization, the analysis is subject to the biases usually associated with observational studies.

Finally, let us consider the case in which the "groups that are compared" are the not-randomized groups A=1 and A=0, i.eastward., an equally-treated assay. Considering as-treated analyses are finer observational analyses, their estimates of the per-protocol effect will be confounded in the presence of common causes of treatment A and the outcome Y. The structure of the bias is shown by the causal diagram in Effigy 1d. In subsequent diagrams we will omit the common causes of A and Y to avoid clutter and to focus the attention on the other sources of bias.

Performance bias

The Cochrane Risk of Bias Tool defines performance bias as the result of "systematic differences between groups in the intendance that is provided, or in exposure to factors other than the interventions of interest."^three These differences may occur due to knowledge of the assigned handling Z past study participants and thus will be less likely in masked trials.

Again let us start consider the case in which the "groups that are compared" are the randomized groups Z=1 and Z=0. Consider the causal diagram in Figure 2a, where O represents medical interventions that are forbidden by the study protocol (e.g., an intensive monitoring and treatment of cardiovascular take a chance factors) and U_O represents unmeasured common causes of O and Y (east.g., gamble factors for cardiovascular affliction). The arrow from Z to O indicates that awareness of the assigned treatment might lead to changes in the beliefs of study participants or their doctors, which in turn may affect the outcome, hence an arrow from O to Y. The interventions O are a result of assignment Z itself, and therefore just mediators of the effect of Z.

Intention-to-care for effect: Cochrane RCT performance bias is non a bias in intention-to-treat analyses

Considering the intention-to-treat result is the effect of assignment and office of the effect of assignment is mediated through O, then O cannot be viewed every bit a source of bias. The intention-to-treat effect naturally incorporates the effects of deviations from protocol, including the interventions O. That is, in an intention-to-treat analysis whose goal is to judge the intention-to-treat effect, performance bias cannot occur. In epidemiologic terms, there is no confounding or selection bias.

Still, the Cochrane literature appears to propose that performance bias tin can occur even in intention-to-treat analyses. To explore this issue, consider two types of departures from intended interventions

(i) Departures from intended interventions that might happen in real life

When trial participants receive interventions O that are prohibited by the protocol only that they would have also received outside of the trial, we believe that most people would agree with the conclusion that no operation bias exists in intention-to-treat analyses.

(ii) Departures from intended interventions that arise only considering of the randomized trial context

When trial participants receive interventions O that are prohibited by the protocol and that they would take non received outside of the trial, the intention-to-treat effect estimated from the trial is relatively unhelpful for patients outside the trial. This may be a reason why Cochrane uses the operation bias label for randomized trials. However, the use of the word "bias" in this context needs to be carefully qualified.

In the absenteeism of whatever of the other biases discussed hither, an intention-to-treat assay of a trial in which interventions O occur is an unbiased estimator of the intention-to-treat effect in that detail trial context and population. The presence of interventions O, like other trial-specific characteristics (east.g., eligibility criteria, monitoring) do not affect the estimates' internal validity just that may affect their external validity (due east.thou, if the judge cannot be transported to clinical contexts outside of the trial in which the interventions O are less frequent). In this case, it might exist more appropriate to say that the intention-to-treat effect from the trial is not generalizable or transportable to other settings rather than proverb that it is "biased".

Another reason why Cochrane uses the performance bias label for intention-to-treat analysis of randomized trials is that the implicit research question may not be about the pure intention-to-care for consequence, but rather an intention-to-treat upshot where the only deviation in protocol is non-adherence to the assigned treatment i.e., the research question is neither intention-to-care for effect nor per-protocol effect. Thus, dissimilar enquiry questions might atomic number 82 to different categorizations of bias.

Performance bias may occur when estimating the per-protocol effect via either a per-protocol or an as-treated analysis. There are at least two distinct reasons for the bias to arise.

Figure 2b depicts a setting in which deviations from protocol O are affected by the received treatment (e.1000., because the use of certain therapies prompts doctors conduct tests for cardiovascular gamble factors that were forbidden past the protocol). The per-protocol event is then the straight outcome of treatment in the absence of those deviations from protocol O (e.g., if no tests for cardiovascular factors had been conducted). Unfortunately, per-protocol and as-treated analyses will yield a biased direct effect (per-protocol) estimate whether they practice or do non adjust for O (Tabular array ane). Lack of adjustment will upshot in bias considering the effect estimate will include the indirect effect also; adjustment for O but not also for all confounders of the effect of O on the effect (east.k., U_O ),^eleven volition generally result in option bias (in graph theoretic terms, O is a collider).

Per-protocol effect: Cochrane performance bias/ Biased direct effect in a per-protocol or as-treated assay

Operation bias for the per-protocol effect may besides take the same structure every bit misreckoning. Figure 2c represents a setting in which O operates as a confounder of the effect of A on Y. The arrow from O to A indicates that interventions not specified in the protocol (e.g., intensive monitoring of cardiovascular chance factors) may alter handling received during the follow-up (e.one thousand., the presence of cardiovascular hazard factors leads doctors to prescribe a different type of antiretroviral therapy). With fourth dimension-varying variables A and O, the structures represented in Figures 2b and ​ 2c tin can occur simultaneously.

Per-protocol effect: Cochrane performance bias / Epidemiologic misreckoning a in per-protocol or as-treated analysis

Detection bias

The Cochrane Hazard-of-Bias Tool defines detection bias as the consequence of "systematic differences between groups in how outcomes are determined".⁴ This bias (besides called observer, observation, or assessment bias) occurs if knowledge of a patient's assigned strategy influences upshot assessment. Figure 3a represents detection bias for the intention-to-treat event. In this graph the true outcome Y remains unmeasured and Y* represents the mismeasured issue. The arrows from Z and Y to Y* correspond that event measurement depends on both the truthful outcome Y and the treatment assignment Z. An intention-to-care for judge of the effect of Z on Y* from Figure 3a will exist biased for the intention-to-treat effect of Z on Y; the bias is a consequence of mismeasurement of Y, and is usually referred to as "measurement bias" or "information bias" in epidemiology (Table 1).^1,six,12 The type of measurement error represented in Figure 3a is differential with respect to handling consignment^1,five and therefore, like all other biases discussed previously, leads to bias even if Z has no effect on Y.

Intention-to-care for effect: Cochrane detection bias/ Measurement bias due to outcome misclassification in an intention-to-treat assay

Detection bias may affect per-protocol issue estimates either directly if A affects Y*, as in Figure 3b, or indirectly, equally in Figure 3c, if Z is a common crusade of A and Y*. Measurement bias in Figures 3a-​ c can be avoided by masking of consequence assessors, because it removes the Z→Y* arrow or the A→Y* arrow.

Per-protocol effect: Cochrane detection bias/ Measurement bias due to outcome misclassification in a per-protocol or every bit-treated analysis

Per-protocol effect: Cochrane detection bias/ Measurement bias due to outcome misclassification in a per-protocol or equally-treated analysis

Compunction bias

The Cochrane Take a chance of Bias Tool defines compunction bias as the upshot of "systematic differences between groups in withdrawals from a study".⁴ The source of bias is differential loss-to-follow-up (e.m., drop out) or other forms of exclusions from the analysis. Figure 4a includes the censoring indicator C, which takes value 1 for individuals excluded from the analysis. The box around C=0 indicates that the analysis is restricted to those who were not excluded from the assay. The arrow from Z to C indicates that withdrawal from the analysis is influenced by noesis of the participant's group assignment, e.g., patients assigned to less potent combination antiretroviral therapy are more probable to not attend hereafter visits if they were aware of their assigned handling. The pointer from 50 to C indicates that individuals with worse prognosis (Fifty=1) are more likely to be excluded than the others (with L=0), because the severity of their disease prevents them from attending hereafter written report visits. In graph-theoretic terms, the intention-to-treat effect estimate is biased because, even under the null, the path Z→C←L→Y is open when conditioning on the collider C. This bias is some other example of what epidemiologists refer to as selection bias (Table one).^1,x

Intention-to-treat effect: Cochrane attrition bias/ Selection bias due to differential loss-to-follow-up in an intention-to-care for assay

The per-protocol upshot estimate is likewise subject area to attrition bias. The bias may arise straight if A affects censoring C (e.g., subjects receiving A=1 are at a greater adventure of experiencing side effects, which could atomic number 82 them to dropout), as in Figure 4b, or indirectly, as in Effigy 4c, if Z is a common cause of A and C. In Figures 4a and ​ 4c, masking of participants and doctors providing care tin prevent attrition bias for intention-to-treat and per-protocol effect estimates past removing the Z→C pointer, and thus blocking the biasing paths Z→C←L→Y and A←Z→C←L→Y, respectively. Adjustment for 50 too in Figures 4a-​ c as well adjusts for selection bias.

Per-protocol effect: Cochrane compunction bias/ Selection bias due to differential loss to follow-up in a per-protocol or as-treated analysis

Per-protocol effect: Cochrane attrition bias/ Option bias due to differential loss to follow-upwardly in a per-protocol or as-treated analysis

Reporting bias

The Cochrane Risk of Bias Tool defines reporting bias as the result of "systematic differences between reported and unreported findings".⁴ Consequence reporting bias may occur because and so-called statistically significant effect estimates are more likely to be reported than nonsignificant effect estimates. Then the boilerplate published event will exist further from the null than the true average result, which will bias meta-analyses and systematic reviews.²³ A similar bias, "stepwise option", results in inflated estimated for weak furnishings, sometimes known as testimation (interpretation after testing) bias.^24-26 Reporting bias, which applies to both intention-to-treat and per-protocol effects, is negligible when treatment has a potent upshot on the outcome or the trial size is huge.^24,25

Epidemiologists have long warned confronting the issues resulting from corruption of significance testing and selective reporting after multiple comparisons.^27,28 Because reporting bias of private studies is not a structural bias, it cannot be generally represented using the causal diagrams.

Give-and-take

Nosotros described how the terminology used to depict similar biases differs between trialists and epidemiologists, and why an explicit specification of the causal target of each randomized trial is beneficial when discussing the adventure of bias. For example, making the intention-to-treat the target allows trialists to end worrying about some forms of "performance bias". On the other mitt, making the per-protocol effect the target makes it clear that adjustment for pre- and post-randomization confounding is needed, which has implications for the pattern and analysis of RCTs.²⁹

We encourage trialists and epidemiologists to be more explicit about their inferential goals. In detail, an open question is whether trialists conducting intention-to-treat analyses are actually interested in the intention-to-treat effect. The widespread preference for masked studies suggests that the per-protocol event, which is not affected past differential implementation of the treatment strategies existence compared, may be the ultimate target.

Causal diagrams help reduce confusion created by ambiguous terminology.³⁰ For example, the term selection bias is used with unlike meanings by trialists and epidemiologists. Drawing the corresponding causal diagram helps resolve these confusions. The structural approach to bias using causal diagrams also shows that some biases that are described using different terms in the RCT literature have the same construction. For example, Figures 1b and ​ 4a are substantially the aforementioned autonomously from the time and reason for choice.

Our simplistic graphical presentations of the Cochrane option, performance, detection and compunction biases cannot perhaps encompass all possibilities. Specifically, in trials with time-varying treatments and attrition, Robins's thousand-methods (g-formula, changed-probability weighting, g-estimation) are more often than not needed to properly arrange for fourth dimension-varying confounding and choice bias when estimating intention-to-care for and per-protocol effects.^sixteen

Acknowledgments

Funding: This work was funded by NIH grant R01 AI102634, and a Methods Innovation Fund grant from the Cochrane Collaboration. Jonathan Sterne is funded by National Found for Health Research Senior Investigator award NF-SI-0611-10168.

Footnotes

Conflicts of Interest: The authors declare no conflict of involvement.

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