## 1 Introduction

While individual studies are rarely used to inform scientific or medical decision making [1], multiple sources of evidence may be aggregated in order to offer more generalizable and precise comparisons between treatments [2, 3, 4, 5]. Meta-analysis, which is the statistical synthesis of multiple study results, is often considered the highest form of quantitative evidence due to its ability to combine all relevant information in the scientific literature. However, because of such issues as effect heterogeneity across study populations and methodology that does not necessarily account for all sources of bias, the status of meta-analysis as the “gold standard” of medical knowledge has been questioned [6].

Standard meta-analysis compares two treatments of interest (or, for instance, an active treatment and placebo). When many treatments for a common condition are tested and made available over time, the medical literature may then contain multiple randomized controlled trials (RCTs) with various treatment comparisons on potentially different populations. Without additional guidance, clinicians and patients are left to informally synthesize information in the available studies in order to determine an optimal treatment decision. A *network meta-analysis* statistically aggregates the results from the relevant RCTs in order to obtain an estimate of the contrast between each pair of treatments. In particular, this type of analysis can produce estimates of contrasts even when no RCT directly compared the two treatments of interest directly.

Each RCT in the network may be performed on populations that differ in terms of their baseline characteristics. These population-specific variables may affect the average response to treatment so that in order to combine inference involving the means, it might be beneficial to control for such variables [7]. Furthermore, it has been noted that if these characteristics not only differentially affect response to treatment, but also the initial study design choice of which treatments to compare, then these variables may confound the overall effect estimate [6, 8]. As an example, Jansen et al. [8],suggest that the baseline severity of patients recruited into a study can be related to the type of treatments investigated in the study and also affect the average outcome at the end of the study. As we demonstrate in this paper, such “study-level confounding” must be adjusted for in order to obtain consistent estimation of average treatment effects.

In this paper, we consider the setting where individual patient data are not available so that the observed data is limited to average covariate and outcome values in addition to study-level information (which we refer to as “aggregate” or study-level data). We begin by describing past parametric approaches to network meta-analysis where the parameter of interest is dependent on the model specification and where the absence of effect heterogeneity is often required a priori. Using the counterfactual framework, we propose a novel definition of a marginal and model-independent causal parameter of interest in network meta-analysis and delineate the assumptions required to estimate this parameter in the presence of measured study-level confounders. We are then able to clarify conditions under which a network meta-analysis is appropriate and when it might mislead decision making regardless of estimation method used. We describe several marginal estimation methods adapted from the single study causal inference setting, including a doubly robust and semiparametric locally efficient Targeted Maximum Likelihood Estimator, and then compare these methods in a simulation study. Finally, we perform a reanalysis of the systematic review by Bally et al. [9],to compare the efficacy of antibiotics on suspected or confirmed methicillin-resistant *Staphylococcus aureus* (MRSA) in hospitalized patients.

## 2 The observed data

Each RCT is assumed to randomly sample subjects from a wider population, called a *superpopulation*. Within the RCT, randomization assigns subjects to two or more groups, each one receiving a treatment. These groups are often referred to as *treatment arms*. Due to randomization and random sampling, each group is a representative sample from the superpopulation. Therefore, each arm can be thought of as a distinct study on the same superpopulation. The superpopulations targeted by the RCTs may differ in terms of their characteristics due to, for example, each trial’s physical and temporal location, the individual inclusion and exclusion criteria, and the recruitment sample size targets. Therefore, if effect heterogeneity exists (i. e. if the relative treatment effects at the subject level depend on baseline covariate values), one would not expect the average relative treatment effects to necessarily be equal across superpopulations.

More formally, the superpopulation is the conceptual group of essentially infinite size from which the study sample is selected [10]. A measure of some outcome (

Let

Because we are interested in summarizing effects across multiple superpopulations, we are arguably attempting to estimate effects in a *metapopulation* that contains the individual superpopulations from each study. For the purpose of this paper, we define the metapopulation as the union of possible study superpopulations and define our parameters of interest with respect to this metapopulation. In particular, we assume that the individual

## 3 Past approaches to network meta-analysis

Standard approaches in network meta-analysis where only aggregate data are observed place a hierarchical model on either the study-specific contrasts (e. g. the difference in means,

The effect targeted in a hierarchical model depends on the contrast-type chosen and the parametrization of the model, and may or may not correspond to a marginal effect as we define further on. For binary outcomes, due to the non-collapsibility of the logistic regression model [19] in particular, adjustment for covariates in such a model changes the true value of the “effect” parameter being estimated. This type of modeling strategy may therefore be biased for the estimation of a marginal effect. Even in linear models, the inclusion of treatment interactions with covariates can also bias the value of the coefficient of treatment relative to the marginal effect. Zhang et al. [12],and Zhang et al. [20],take a missing data perspective and model the arm-specific outcomes using a Bayesian hierarchical model to estimate marginal parameters. While neither approach has yet been extended to incorporate covariates, the former paper assumes that treatments are applied to studies at-random while the latter allows for estimation in a not-at-random context by explicitly specifying the unobservable selection mechanism.

While adjustment for covariates is rare in practice, Jansen et al. [8],introduced the notion of adapting Pearl’s causal directed acyclic graphs (DAGs) to this setting [21] in order to assist in covariate selection. As a general rule, Jansen et al. [8],advocate for the adjustment of all modifiers of the relative treatment effects across comparisons. They also discourage adjustment for covariates that are not effect modifiers due to the fact that they may *induce* bias in the meta-analysis.

## 4 The counterfactual approach

Let

For two treatments,

The patient sample in any given study arm may not be representative of the metapopulation, for which the effect of interest is defined. In addition, because treatment was not randomly allocated across different RCTs, the collection of mean outcomes observed under a given treatment

### 4.1 A causal directed acyclic graph (DAG) for network meta-analysis

Similar to Alonso et al. [22], we assume that heterogeneity in the different superpopulations targeted in the individual RCTs implies that each RCT estimates a different causal effect. Like Zhang et al. [12], we take an “arm-based” approach to the problem. Like Jansen et al. [8], we draw a causal DAG in order to conceptualize the relationship between treatment, study results, and population-specific characteristics. We arbitrarily choose to intervene on the arm labeled

Many of the assumptions presented in detail in Section 4.3 are drawn explicitly using the study-level DAGs in Figure 1(a). The nodes of the DAG represent variables measured at the level of the RCT and the arrows between them represent the effect of the parent on the child node. For example, the absence of an arrow from

The sample size node

Causal DAGs can be used as a tool to identify which variables must be controlled for in the meta-analysis in order to estimate the treatment-specific metapopulation mean outcome. Depending on some underlying statistical assumptions that we will investigate in detail in the following sections, these DAGs may simplify to Figure 1(b). This happens because we can ignore the mediation path through

Note that the recommendations based on this DAG differ from those of Jansen et al. [8], who say that the analysis must adjust exclusively for effect modifiers. The assumptions that we list in Section 4.3 are explicitly required in the steps we take in Section 4.2 in order to obtain identifiability of the meta-analysis parameter of interest.

### 4.2 The G-formula and nonparametric identifiability

Suppose we observe the aggregate data

### 4.2.1 The observed data generation

At the study design stage for RCT

The second stage operates at the individual level once subjects are recruited and randomly assigned treatment. Suppose each subject

Let

Assuming no interference between arms and that the distribution of

The probability density function

where

### 4.2.2 The counterfactual distribution

Define an intervention as the assignment of treatment strategy

where

### 4.2.3 Identifiability for conditionally independent $\stackrel{\u02c9}{Y}$ and $S$

Suppose we have that

Identifiability without assuming this structural independence is possible, and we describe the additional causal assumptions required for this setting in Appendix A.2.

### 4.2.4 Identifiability for binary outcomes

If the original study outcomes are binary (such that

### 4.3 Assumptions

For convenience, here we list the assumptions needed for the identification of

*No interference*. The use of the above counterfactual notation presupposes that the treatment assigned to one study does not affect the counterfactual outcome of another study [25]. A secondary level of interference within an individual study involves the treatment in one study *arm* affecting the outcomes in another study arm. This means that the estimates

*Unconfoundedness*. (Weak) unconfoundedness [26] is required for the identification of

*Consistency*. The consistency assumption in this context states that the counterfactual mean of a study arm under a given treatment is the same as the observed result. With notation, this is equivalent to stating that

*Positivity*. Finally, we need to evaluate both theoretical and practical positivity. Theoretical positivity is the assumption that, *conditional only on variables required for unconfoundedness*, all studies had a positive probability of being assigned each treatment under investigation. Practical positivity is the condition that for every level of the characteristics *estimated* positive probability of receiving treatment.

It is important to note that treatment comparisons are based on the same

It is furthermore important to note that the positivity assumption is not the same as requiring that all studies could have realistically been assigned each treatment. In particular, certain treatments may not have been available when some older trials were carried out. If year of study is not required to unconfound the analysis, then the *unconditional* probability may still be non-zero.

## 5 Estimation of the treatment-specific metapopulation mean outcome

### 5.1 G-Computation

G-Computation procedures based on the G-formula in Section 4.2 can be used to estimate the target parameter. Here we define a simple procedure resulting from the data requirement that the sample mean and standard deviation are independent within a study arm. This procedure allows for simple frequentist estimation of the mean effect of treatment.

This procedure requires estimates for the conditional expectation

Because

A model for the regression on

The standard error for the G-Computation estimate is usually computed through nonparametric bootstrap methods [29]. Bootstrap resampling must be done by resampling studies, rather than arms, similar to what is done in a study with clustering [30].

### 5.2 Inverse probability of treatment weighting

Likelihood methods, such as G-Computation, require correct parametric specification of the outcome model, which may be difficult to specify. An alternative approach is to utilize propensity score methods, which require the estimation of a model for the treatment received by the arm. For a given treatment type

Despite the small sample size in standard network meta-analysis, one might attempt inverse probability of treatment weighting (IPTW) for the estimation of the marginal parameter. Let

Intuitively, this estimator takes a mean of

The consistency of this estimator can be shown as follows.

### 5.3 Targeted minimum loss-based estimation

Targeted Minimum Loss-based Estimation (TMLE) [31, 32] is a framework for the construction of semi-parametric estimators generally applied to the estimation of causal quantities. The TMLE procedure is carried out by first fitting a model for the expected value of the arm-based means,

This TMLE is consistent under correct specification of the propensity score model or the model for the expected value of the mean outcome (the property of *double robustness*). If both of these models are correct, then TMLE is asymptotically efficient in the class of regular, asymptotically linear estimators in the semiparametric model space [32]. More details and a proof of consistency are included in Appendix A.3.

## 6 Simulation study

In this section we demonstrate that we can obtain consistent estimation of the target parameter

While the proposed estimators do not restrict the number of study arms, we fix all simulated studies to have exactly two treatment arms for simplicity. We are interested in estimating the mean outcome of the metapopulation under treatment for each of four treatments of interest. For each study

Simulation study: data generation.

Variable | Study design: for each |
---|---|

Number of arms | |

Study-level covariate | |

Treatments | |

Sample size | |

(study recruitment) where | |

Within-study: for each | |

Subject-level covariate | |

Subject-level outcome | |

where | |

Observed data: for each | |

Study-level information |

The sample statistics from each study arm are calculated by taking the mean and standard deviation of

We tested the three methods described in the text (G-Computation, IPTW and TMLE) for

The unadjusted estimator was greatly biased for the first and third contrasts, indicating that those two contrasts were highly confounded by the simulated study-level covariate. The correctly specified G-Computation estimator had the lowest bias throughout, the smallest standard errors, and near optimal confidence interval coverage. This is to be expected as G-Computation is a function of maximum likelihood parameter estimates with correct parametric specification of the necessary component of the likelihood (namely, the conditional mean of the outcome). However, with an incorrectly specified outcome model, the estimator was biased which caused the coverage to suffer for the third contrast.

IPTW was the most biased estimator and also had the largest variance. The bias largely dissipated when the sample size was increased to

TMLE with correct outcome model specification had bias comparable to G-Computation but slightly higher for

Simulation: quality of treatment contrast estimation with a Gaussian outcome (two-arm studies, 1,000 simulated datasets).

SE-MC | SE-BS( | ||||||
---|---|---|---|---|---|---|---|

15 | 50 | 15 | 50 | 15 | 50 | ||

Correctly specified models | |||||||

G-Comp | 0 | 0 | 0.04 | 0.02 | 0.04(91) | 0.02(94) | |

IPTW | 40 | 9 | 0.57 | 0.46 | 0.61(89) | 0.41(92) | |

TMLE | 4 | 0 | 0.27 | 0.03 | 0.44(96) | 0.05(92) | |

G-Comp | 1 | 0 | 0.04 | 0.02 | 0.04(91) | 0.02(95) | |

IPTW | –2 | 0 | 0.10 | 0.04 | 0.25(99) | 0.05(97) | |

TMLE | –1 | –1 | 0.17 | 0.04 | 0.29(96) | 0.04(93) | |

G-Comp | 0 | 0 | 0.04 | 0.02 | 0.04(89) | 0.02(93) | |

IPTW | 81 | 3 | 0.76 | 0.74 | 0.62(63) | 0.80(68) | |

TMLE | –9 | 0 | 0.81 | 0.11 | 0.74(94) | 0.21(95) | |

Misspecified outcome model | |||||||

No adjustment | 101 | 103 | 0.65 | 0.35 | 0.61(75) | 0.34(52) | |

G-Comp | 2 | 12 | 0.20 | 0.13 | 0.24(98) | 0.11(94) | |

TMLE | –8 | –2 | 0.33 | 0.09 | 0.46(97) | 0.11(96) | |

No adjustment | 5 | –7 | 0.37 | 0.20 | 0.38(92) | 0.20(93) | |

G-Comp | –1 | 7 | 0.20 | 0.12 | 0.18(99) | 0.11(95) | |

TMLE | 0 | 0 | 0.15 | 0.05 | 0.28(99) | 0.05(96) | |

No adjustment | 126 | 125 | 0.69 | 0.38 | 0.61(51) | 0.36(18) | |

G-Comp | 36 | 33 | 0.53 | 0.29 | 0.48(88) | 0.24(80) | |

TMLE | 44 | –24 | 0.86 | 0.38 | 0.75(87) | 0.36(75) |

## 7 Application: Antibiotic use on methicillin-resistant **Staphylococcus aureus** infection

**Staphylococcus aureus**

We illustrate this causal inference approach and the adapted estimation methods in network meta-analysis with an example from infectious disease research. An increase in MRSA has spurred investigation of comparative efficacy of different antibiotic treatment options. While the antibiotic vancomycin has been the standard treatment for decades, treatment failures have been noted in patients with serious infections [37]. Interest therefore lies in whether alternative antibiotics are as effective as the standard. Bally et al. [9] performed a systematic review and Bayesian network meta-analyses of RCTs of parenteral antibiotics used for treating hospitalized adults with complicated skin and soft-tissue infections (cSSTIs) and hospital-acquired or ventilator-associated pneumonia.

We consider the target population of interest to be the population of clinical trial participants with suspected or confirmed MRSA cSSTIs or pneumonia, with corresponding studies published until May 2012. The site of infection and confirmation of MRSA represent important differences in the entrance criteria of the various studies. 24 studies were found. Patients were randomized based on suspicion of MRSA in all but three studies for which the protocol specified confirmation of presence of MRSA at baseline. 14 studies enrolled subjects with cSSTIs, 7 studies enrolled subjects with hospital-acquired or ventilator-associated pneumonia, and 3 studies allowed for either indication. The original network meta-analysis of Bally et al. [9],analyzed each infection site in separate analyses and therefore obtained stratified estimates. Based on the theory we developed, we can account for the potentially different treatment effects in each subpopulation by controlling for subpopulation type as a covariate in the analysis. By doing so, we ask a higher-level yet still clinically interesting question: “Are the alternative therapies as effective as the standard antibiotic for the treatment of suspected or confirmed MRSA?” Because infection site, MRSA confirmation, and study year can potentially affect the choice of investigated therapies and the outcomes, these three covariates (labeled

The outcome of interest is clinical test of cure for all subjects who received at least one dose of treatment (a standard measure in infectious disease research). Four papers evaluated the outcome only on a subset of patients selected post-randomization; as this does not conform to our definition of the RCT-specific parameter of interest, we considered these outcomes missing. For our analysis, we chose to compare vancomycin with the two most prevalent alternatives: telavancin and linezolid. In total, 47 study arms evaluated one of these three treatments and 36 had an observed outcome. Of the remaining treatments, tigecycline, daptomycin, and ceftaroline were each evaluated in three study arms, and a regime of quinupristin/dalfopristin was evaluated in one arm. All of this information is available in the data extraction Table 3.

Data extraction table for the network meta-analysis of antibiotic use on methicillin-resistant *Staphylococcus aureus* infection.

Publication | Events | Ni | Ai | StudyID | Year | Infection | Confirmed MRSA |
---|---|---|---|---|---|---|---|

at baseline | |||||||

Katz et al., 2008 | 42 | 48 | vancomycin | 1 | 2007 | cSSTI | 0 |

36 | 48 | daptomycin | 1 | 2007 | cSSTI | 0 | |

Arbeit et al., 2004 | 162 | 266 | vancomycin | 2 | 2001 | cSSTI | 0 |

165 | 264 | daptomycin | 2 | 2001 | cSSTI | 0 | |

235 | 292 | vancomycin | 3 | 2000 | cSSTI | 0 | |

217 | 270 | daptomycin | 3 | 2000 | cSSTI | 0 | |

Breedt et al., 2005 | 216 | 250 | vancomycin | 4 | 2003 | cSSTI | 0 |

212 | 253 | tigecycline | 4 | 2003 | cSSTI | 0 | |

Sacchidanand et al., 2005 | 196 | 255 | vancomycin | 5 | 2003 | cSSTI | 0 |

203 | 268 | tigecycline | 5 | 2003 | cSSTI | 0 | |

Stryjewski et al., 2008 | 307 | 429 | vancomycin | 6 | 2006 | cSSTI | 0 |

309 | 426 | telavancin | 6 | 2006 | cSSTI | 0 | |

360 | 489 | vancomycin | 7 | 2006 | cSSTI | 0 | |

348 | 472 | telavancin | 7 | 2006 | cSSTI | 0 | |

Stryjewski et al., 2006 | 81 | 95 | vancomycin | 8 | 2004 | cSSTI | 0 |

82 | 100 | telavancin | 8 | 2004 | cSSTI | 0 | |

Corey et al., 2010 | 297 | 347 | vancomycin | 9 | 2007 | cSSTI | 0 |

304 | 351 | ceftaroline | 9 | 2007 | cSSTI | 0 | |

Wilcox et al., 2010 | 289 | 338 | vancomycin | 10 | 2007 | cSSTI | 0 |

291 | 342 | ceftaroline | 10 | 2007 | cSSTI | 0 | |

Talbot et al., 2007 | 26 | 32 | vancomycin | 11 | 2005 | cSSTI | 0 |

59 | 67 | ceftaroline | 11 | 2005 | cSSTI | 0 | |

Weigelt et al., 2005 | 402 | 573 | vancomycin | 12 | 2003 | cSSTI | 0 |

439 | 583 | linezolid | 12 | 2003 | cSSTI | 0 | |

Stevens et al., 2002 | 54 | 87 | vancomycin | 13 | 1999 | cSSTI | 0 |

64 | 99 | linezolid | 13 | 1999 | cSSTI | 0 | |

16 | 32 | vancomycin | 14 | 1999 | pneumonia | 0 | |

20 | 39 | linezolid | 14 | 1999 | pneumonia | 0 | |

Wunderinket al., 2003 | 128 | 302 | vancomycin | 15 | 2000 | pneumonia | 0 |

135 | 321 | linezolid | 15 | 2000 | pneumonia | 0 | |

Rubenstein et al., 2001 | 73 | 192 | vancomycin | 16 | 1999 | pneumonia | 0 |

85 | 203 | linezolid | 16 | 1999 | pneumonia | 0 | |

Rubenstein et al., 2011 | 221 | 374 | vancomycin | 17 | 2007 | pneumonia | 0 |

214 | 372 | telavancin | 17 | 2007 | pneumonia | 0 | |

228 | 380 | vancomycin | 18 | 2007 | pneumonia | 0 | |

227 | 377 | telavancin | 18 | 2007 | pneumonia | 0 | |

Fagon et al., 2000 | 67 | 148 | vancomycin | 19 | 1996 | pneumonia | 0 |

65 | 150 | quinupristin/ dalfopristin | 19 | 1996 | Pneumo nia | 0 | |

Lin et al., 2008 | NA | 33 | linezolid | 20 | 2005 | cSSTI | 0 |

NA | 29 | vancomycin | 20 | 2005 | cSSTI | 0 | |

NA | 38 | linezolid | 21 | 2005 | pneumonia | 0 | |

NA | 40 | vancomycin | 21 | 2005 | pneumonia | 0 | |

Kohno et al., 2007 | NA | 51 | linezolid | 22 | 2004 | cSSTI | 0 |

NA | 26 | vancomycin | 22 | 2004 | cSSTI | 0 | |

NA | 31 | linezolid | 23 | 2004 | pneumonia | 0 | |

NA | 17 | vancomycin | 23 | 2004 | pneumonia | 0 | |

Florescu et al., 2008 | NA | 70 | tigecycline | 24 | 2005 | cSSTI | 0 |

NA | 23 | vancomycin | 24 | 2005 | cSSTI | 0 | |

Itani et al., 2010 | 223 | 276 | linezolid | 25 | 2007 | cSSTI | 1 |

196 | 266 | vancomycin | 25 | 2007 | cSSTI | 1 | |

Wunderink et al., 2008 | NA | 30 | linezolid | 26 | 2005 | pneumonia | 1 |

NA | 20 | vancomycin | 26 | 2005 | pneumonia | 1 | |

Wunderink et al., 2012 | 102 | 186 | linezolid | 27 | 2010 | pneumonia | 1 |

92 | 205 | vancomycin | 27 | 2010 | pneumonia | 1 |

We ran four methods to obtain estimates of the counterfactual relative risk of both contrasts with the comparator vancomycin. The methods are 1) a ratio of the unadjusted mean outcomes using all available arms (called “No Adjust”), 2) a random effects regression for the arm-specific study outcomes using a log-link and a study-specific intercept (“RE Arm”), 3) G-Computation where a random effects logistic regression weighted by the inverse standard errors is used to predict the conditional mean outcomes, and 4) TMLE with a weighted logistic random effects model for the outcome and LASSO-penalized logistic regressions (to handle the sparse data) for the propensity score and a missing data model using the R library glmnet Friedman et al. [38] The missing outcomes required that the TMLE algorithm include fitting a model to estimate the probability of a missing outcome in each study; the TMLE update step was therefore modified to use a product of the propensity score and the probability of observing the outcome in place of

The results of the network meta-analysis are presented graphically in Figure 2 (and numerically in the Appendix Figure 4). We also included the results of the studies that contrasted the two treatments directly. For the comparison of telavancin versus vancomycin, all estimators include the null in the confidence interval. The random effect regression and G-Computation produce estimates of the relative risk close to one, indicating near equivalence of treatments while the point estimate of TMLE was further from the null (in the direction of the superiority of vancomycin). Notably, the confidence interval for the TMLE in the first contrast is much wider than the others. The unadjusted method produced a point estimate in the direction of the superiority of telavancin, demonstrating that the correction for study-level confounding impacted the analysis. For the comparison of linezolid versus vancomycin, the random effects regression, G-Computation and TMLE agree on the superiority of linezolid. The original study by Bally et al. [9],also found some suggestion of a superior effect of linezolid compared to vancomycin but for both subpopulations the confidence intervals were large and spanned the null.

We can also easily obtain estimates of the contrast between telavancin and linezolid. The G-Computation and TMLE produce risk ratios for clinical success of 0.94 (

If we are to interpret the summary statistics as estimates of the relative causal effects of antibiotic choice on successful treatment, the causal assumptions in Section 4.3 need to be satisfied. Each of the studies evaluated the clinical efficacy of the treatments, which is defined on patients who had received at least one dose of the study drug. Because randomized treatment was first-line therapy (administered intravenously in-hospital) and the success of treatment was determined clinically, each trial estimated the relative effect under full adherence. *No interference*: No interference is credible in this case because all subjects were already suspected or confirmed to have MRSA upon entry to the study. Therefore, the choice of treatment in the other arm wouldn’t have an effect on existing infections nor the success of treatment. *Unconfoundedness*: The unconfoundedness assumption relies on whether year, infection type, and whether MRSA was confirmed were sufficient to control for confounding at the study-level. This assumption could be violated if prognostic demographic variables were involved in the study design stage. However, prognostic markers such as diabetes and peripheral vascular disease (for cSSTI) and mechanical ventilation, APACHE II score, clinical markers of severity, and presence of organ dysfunction [for pneumonia) are unlikely to determine the choice of initial therapy [39], Niederman [40]. *Consistency*: The dosage regimens varied somewhat across studies but were all considered to be at therapeutic levels. However, the length of time to the evaluation time point for each treatment type varied within and between studies (e. g. 7–14 days for telavancin versus 12–28 days for linezolid]. If this corresponds to meaningfully different treatment durations (and/or periods of time lapsed before evaluation), this would indicate different definitions of interventions across studies, and thus a violation of the consistency assumption. *Positivity*: All subjects in the study were indicated to receive any of the treatments evaluated.

## 8 Summary

In this paper, we nonparametrically define the parameter of interest in a network meta-analysis with direct and indirect comparisons using the counterfactual framework often employed in causal inference. This definition of the parameter of interest is model-independent and is interpretable on what we define as a metapopulation, the union of all superpopulations. Such an approach allows for a straight-forward description of what is being estimated, which is accessible even without an understanding of the estimation methods being used. In particular, we can interpret the marginal effects defined in this paper as the relative mean outcome had all subjects in the metapopulation been assigned to each treatment versus another. If a specific population is of interest and not represented by the metapopulation, with some conditions it may also be possible to more generally transport effect estimation, as described by Bareinboim and Pearl [41].

We have presented a set of conditions under which identifiability of the parameter of interest is possible. Identifiability allows for a clear description of when the parameter of interest can and cannot be estimated. For instance, the non-interference requirement casts doubt on the synthesis of studies that allow for treatment switching, crossover, or group contamination. The assumptions that we made allowed for the simplification of the relevant components of the observed data likelihood so that arm-based inference is possible.

One might alternatively specify the RCT-estimated contrast as the “outcome of interest” (rather than use the arm-specific outcome as we did). However, under this alternative, the propensity score would then be defined as the probability of a trial directly contrasting a given treatment pair. For standard network meta-analysis sample sizes, this would most often produce practical positivity problems, indicating the need for extrapolation using the outcome model (and thereby creating estimators that are very sensitive to model misspecification). In particular, two treatments that had never been directly compared would have no data support in this model.

If all treatments are selected completely at random into studies (or if only two treatments have ever been available to compare) then a standard unadjusted analysis using those arms assigned the desired treatments would be consistent. If we weaken this assumption and replace it with conditional exchangeability, then the estimators introduced in this paper are appropriate in that they allow for the adjustment of study-level covariates.

Our methods also allow for a wider inclusion criteria of studies in a systematic review. It is often the case that systematic reviews will exclude studies because they do not evaluate the exact desired clinical endpoint. Using our proposed methods, we can avoid selection bias due to studies excluded only for this reason. To do so, we would artificially censor the outcomes of studies that do not estimate the desired outcome-type of interest. The censored outcomes of these studies might then be considered “missing at random” conditional on the study baseline information which should still be included in the analysis (both in the propensity score model and the missing data model).

For the analysis of continuous individual-level outcomes, we assumed independence between the sample mean and standard deviation within each study arm. While we chose to present our identifiability argument under this assumption, it is not ultimately necessary. However, it is not straight-forward to propose a valid Monte Carlo or Bayesian estimation approach to the setting with dependent sample means and standard deviations. In some cases, it may be possible to transform the individual-level data to remove the skew, but this relies on access to each study’s raw data, in which case an individual patient data analysis would be preferable.

In the simulation study, we show that certain estimators adopted from the causal inference literature can produce valid estimates of effect contrasts under the identifiability conditions described. In particular, G-Computation and TMLE might lend themselves well to network meta-analysis, which is characterized by small sample sizes and low prevalence for certain treatments. IPTW was seen to be sensitive to rare treatment assignment and G-Computation and TMLE were seen to be somewhat sensitive to model misspecification. Some general benefits of using TMLE are that it is double robust and can incorporate nonparametric (or machine learning) estimation of the propensity score and outcome model which can help avoid bias from model misspecification vander Laan and Rose [32]. More methods development and investigations are needed to address extremely rare treatments and how (or whether) TMLE can be adapted to be robust in this setting.

The application we presented compared the results of random effects regression, G-Computation, and TMLE in a network meta-analysis of the relative efficacy of treatment options for MRSA infection. The random effects regression and G-Computation produced small confidence intervals relative to the direct contrasts of the individual RCTs though TMLE only did for one comparison investigated. In contrast to the analysis in the original article that used unadjusted contrast-based hierarchical Bayesian modeling on the separate subpopulations of infection types, our analyses concluded that there is evidence to support the superiority of linezolid over vancomycin. We also noted the poor stability of IPTW in this example and generally do not recommend this estimator when the data support for certain treatment levels is sparse. Finally, using this data example, we demonstrated how the causal assumptions should be listed and critiqued in order to stimulate discussion about the appropriateness of causal interpretations in specific contexts.

The framework we present formally assumes that we are restricting our analyses to studies evaluating a common parameter-type. If there was only partial-adherence in the RCTs, our framework does not allow for the mixing of intent-to-treat parameter estimates with adherence-adjusted parameter estimates. [Estimation of the adherence-adjusted parameters in RCTs is described in [42]. The same restriction applies to the results of observational studies if the parameter type estimated in the observational study is not the same as in the clinical trials. Specifically, treatment adherence and outcome need to be defined identically across studies, and all studies whose endpoints are included must estimate the same mean treatment-specific counterfactual outcome. Although it is common practice to include different parameter types in a meta-analysis, our formalization of the target parameter reveals that a causal interpretation of the resulting effect estimate may be quite challenging.

In addition to the issues we describe, there are many other concerns about aggregating study results in various settings. For instance, one might question the independence between RCTs happening close in time, or the systematic review inclusion criteria. We believe our framework provides additional structure to the ongoing discussion about the validity of network meta-analysis and will help stimulate solutions to the remaining challenges.

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The joint counterfactual distribution can be decomposed as

Let

where the integral for

because we assume that the study size has no effect on the individual-level outcome. It follows that

It may not be plausible to assume conditional independence between

The target parameter can be estimated as a multiple integral over each

Since each component of this density is estimable from the data, we have identifiability of the target parameter in this case as well.

The local semiparametric efficiency and estimation consistency of the TMLE we describe can be derived very similarly to the standard observational data setting (with a single categorical exposure variable) for the estimation of the average treatment effect [32]. To give more insight into how this extends to the network meta-analysis case, we present some additional details and a proof of double robustness.

The efficient influence function for parameter of interest

Note that the TMLE update step produces values of

so that it follows that the TMLE is a locally efficient estimator [43, 44]. Specifically, the logistic regression update step with single covariate

First suppose that for increasing values of

Now suppose that

Therefore, if either of the models for

*infection*

**Staphylococcus aureus**Table 3 presents the full study list from the systematic review of Bally et al. [9] and the data that we used in the analysis in Section 7. Table 4 presents the numerical results that we obtained from our analyses, corresponding with Figure 2. The full reference list is below.

Risk ratio estimates, standard errors and 95 % confidence intervals for relative effects of antibiotics telavancin (TEL), linezolid (LIN), and mainstay therapy vancomycin (VAN)

TEL vs VAN | LIN vs VAN | TEL vs LIN | |||||||||
---|---|---|---|---|---|---|---|---|---|---|---|

Method | Est | SE | 95 % CI | EST | SE | 95 % CI | |||||

No Adjust | 1.04 | 0.028 | (0.99,1.10) | 0.92 | 0.027 | (0.87,0.97) | 1.13 | 0.045 | (1.05,1.22) | ||

RE Arm | 1.00 | 0.010 | (0.98,1.02) | 1.08 | 0.012 | (1.05,1.10) | 0.92 | 0.014 | (0.89,0.95) | ||

G-Comp (RE) | 1.00 | 0.003 | (1.00,1.00) | 1.06 | 0.006 | (1.06,1.09) | 0.94 | 0.005 | (0.92,0.94) | ||

TMLE (RE) | 0.89 | 0.106 | (0.75,1.19) | 1.05 | 0.012 | (1.03,1.07) | 0.85 | 0.102 | (0.71,1.12) |

## References for the MRSA application

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