Point–counterpoint: The MERINO trial and what it should imply for future treatment of ESBL bacteremia

Background

There has been a long-standing controversy in the infectious diseases and microbiology community regarding the use of beta-lactam/beta-lactamase inhibitors (BLBIs) in the management of extended-spectrum beta-lactamase carrying organisms (ESBL). Existing observational literature has been contradictory for outcomes of patients treated with BLBIs compared with carbapenems in ESBL infections (1–4). A meta-analysis of the literature (5) has shown sufficient equipoise to warrant a randomized clinical trial comparing BLBIs with carbapenems—the MERINO trial. The trial aimed to show that piperacillin-tazobactam (PTZ) is non-inferior to meropenem for definitive treatment of bacteremia caused by ceftriaxone–non-susceptible E. coli or Klebsiella spp that test susceptible to PTZ. Study results were released at the ECCMID conference in 2018 and published in JAMA in September 2018 (6). In brief, the study showed that there was higher mortality in the PTZ group compared with the meropenem group (12.3% versus 3.7%) and that the study was stopped at its third interim analysis due to futility. The study’s authors conclude that their study “doesn’t support the use of PTZ for ceftriaxone resistant, PTZ sensitive organisms.” While intended to definitively answer the question of the role of BLBIs for ESBL organisms, the MERINO trial leaves the community divided as to what the results mean and how they should be used. In a point–counterpoint, we discuss the paper and its implications for management of ESBL bacteremia.

Randomization

Against MERINO: The study groups were not well balanced

Randomization is intended to assign patients to similar groups, on average. This works on the principle that, if you have a large enough sample, differences will be sorted evenly to different groups through a stochastic process. Unfortunately, as Gallup polls so frequently remind us, this works 19 times out of 20, but there is always the 1 time out of 20 when, by random chance, the groups are unbalanced. This is true in the MERINO trial, in which both clinical condition and severity of illness are biased against the PTZ group. Specifically, there were 24% more urinary tract infections (UTIs) in the meropenem study group (128 in the meropenem group versus 103 in the PTZ group) which are less likely to cause mortality (overall mortality 4.8%) and more pneumonias (9 in the PTZ versus 3 in the Meropenem group), mucositis (12 in the PTZ arm versus 7 in the meropenem arm), and intra-abdominal (34 in the PTZ arm versus 28 in the meropenem arm) and surgical site infections (8 in the PTZ arm versus 4 in the meropenem arm)—all of which are associated with higher mortality (15%). Severity of illness is likewise higher in the PTZ group: there were more central venous catheters (35 in the PTZ group versus 20 in the meropenem group), immune compromise (51 in the PTZ group versus 40 in the meropenem group), neutropenia (16 in the PTZ group versus 9 in the meropenem group), urinary catheters (51 in the PTZ group versus 37 in the meropenem group), and patients with a qSOFA score greater than 2 (86 in the PTZ group versus 77 in the meropenem group). While some factors—liver disease and diabetes—favoured meropenem, these factors were lower in number and frequency. The net result was that PTZ was going to perform more poorly as a result of group allocation, even if it performed similarly for a given severity of infection.

Certain other variables in this study were out of keeping with what is expected in a trial of sepsis, further supporting the assertion that patients in the PTZ group had more severe illnesses than those in the meropenem group. First, the mortality for the meropenem arm was extremely low at 3.7%. Predicted mortality was 14%, based on previous literature. While we would expect a lower mortality in any study for which physicians and patients must agree to participate, the very low mortality suggests that group allocation played a role in determining outcomes.

Second, the variables known to impact survival in sepsis were reversed in the study. The time to receiving appropriate antibiotics was much slower in the meropenem arm (9.6 hours versus 5.5 hours), yet there was increased survival. As well, appropriate initial antibiotic therapy showed a non-significant deleterious effect (OR 1.69, p = 0.24), while diabetes was protective (OR 0.61, p = 0.25). That multiple variables known to improve outcome were associated with the opposite effect suggests that there is some other variable explaining the results. These are all non-significant findings and any one of these elements in isolation could be attributed to random variation, but their systematic presence suggests that results are impacted by elements other than the course of infection.

Critics will argue that not all elements need to equal between groups in order for randomization to eliminate the risk of bias. We are not concerned about physician bias in this instance, but rather that outcomes are due to unequal group allocation. This assertion supports the thesis of Guyatt et al, who found that prognostic factors both known and unknown [emphasis added] overwhelm treatment effect (7). So, while we cannot comment on unknown factors, the known ones appear to cast doubt on the study’s results. Further, critics will argue that a large sample size will tend to result in equal groups. It is true, that if the sample size had been large enough, eventually these elements would have balanced, but the fact is that this study appears not to have achieved this goal on multiple factors—as documented earlier.

For MERINO: Randomization corrects for known and unknown confounders

As Guyatt et al identified over 2 decades ago, the severity of illness, comorbidities, and a whole host of other prognostic factors—both known and unknown—often overwhelm any treatment effect (7). My colleague rightly points out the importance of randomization in producing groups of patients who are, on average, similar for all the known and unknown prognostic factors. The critique that MERINO failed to balance study groups is flawed.

It is a misunderstanding of randomized controlled trials that complete balance will be achieved for all confounding prognostic factors. A properly executed randomization process ensures that any residual differences between study groups is due to chance and not physician choice. While differences in potential confounders will exist after randomization, with sufficient sample size, their impact on the treatment effect is reduced (8,9). Furthermore, controlling for potential confounders can also be done after trial completion by incorporating a multivariate analysis of potential confounders to adjust the treatment effect (8).

The randomization methodology employed by the MERINO trial was sound. Randomization itself was stratified into a high-risk and a low-risk stratum separately for E. coli and Klebsiella spp. High risk was defined as a non-urinary source of bacteremia with a Pitt score greater than 4. Random permuted blocks of two and four patients would prevent study personnel from ascertaining treatment group and introducing selection bias. At least for patients who were referred for enrolment in MERINO, we can be reasonably certain that physician bias did not impact randomization.

The randomization methodology in MERINO also sufficiently reduced the impact of potential confounders on treatment effect. A list of differences in baseline characteristics between the PTZ and meropenem groups were provided earlier. These were described as biasing for or against a treatment group. Fortunately, we can use the trial data itself to ascertain what, if any, imbalance may exist between the groups.

The largest difference between groups was in the urinary tract (UT) source of bacteremia (54.8% in the PTZ group versus 67% in the meropenem group). Having a UT source was indeed protective for 30-day mortality: 4.8% for the UT source versus 12.8% in the non-UT source (OR 0.34, p = 0.006). So, did this fatally bias the results? No. By exploring treatment outcome stratified by UT versus non-UT source, it is clear that both strata favour meropenem (Table 1).

Table 1:

30-day mortality stratified by UT versus non-UT source

Source	30-day mortality No./total no. (%)		Risk difference (%)
	PTZ	Meropenem
UT	7/102 (6.9)	4/128 (3.1)	−3.8
Non-UT	16/85 (18.8)	3/63 (4.8)	−14.0

UT = urinary tract; PTZ = piperacillin-tazobactam

Immune compromise had a smaller difference between treatment groups (27.1% in the PTZ group versus 20.9% in the meropenem group). Being immune compromised showed a non-statistically significant trend toward higher 30-day mortality (OR 1.93, p = 0.10). Exploring treatment effect stratified by the presence or absence of immune compromise once again favours meropenem in both strata (Table 2).

Table 2:

30-day mortality stratified by immune compromise

Immune compromise	30-day mortality No./total no. (%)		Risk difference (%)
	PTZ	Meropenem
Present	10/51 (19.6)	1/40 (2.5)	−17.1
Absent	13/136 (9.6)	6/151 (4.0)	−5.6

PTZ = piperacillin-tazobactam

Lastly, multivariate adjustment incorporating UT source and Charlson Comorbidity Index was nearly identical to the unadjusted analysis (adjusted OR 3.41, one-sided 97.5% CI 0 to 8.38 versus unadjusted OR 3.69, one-sided 97.5% CI 0 to 8.82). Every reasonable subgroup and adjustment analyzed consistently favoured meropenem.

Study drug effect

Against MERINO: The influence of the study drug is too diminished to be interpretable in the results

The study design necessarily had patients on empiric therapy prior to randomization. Patients were allowed to be randomized as late as 72 hours following initial blood culture collection, to allow for the identification of resistant phenotype and study enrolment. This delay resulted in patients receiving about 2.2 days of antibiotics prior to randomization (53.6 hours for the PTZ group, 52.5 hours for the meropenem group). Empiric therapy was a drug other than a study drug 66% of the time and was only appropriate in 60% of cases. To be included in the per-protocol analysis, the patient had to be on the study drug for 4 days and then could be changed to the physician’s choice of drug, based on clinical criteria (e.g., discharge home). The flexibility of therapy following the required drug resulted in most patients (56%) receiving no antibiotics after day 5 of enrolment, 20% in both groups receiving a carbapenem, and only 3.5% continued a BLBI (Figure 1). The practicality of this approach cannot be impeached; however, the result is that patients spent as little as 4 days on the study drug with a mean of 7.4 days on the study drug compared with 6.1 days on some other regimen, or no drug at all. This equivalent time on study and non-study drug occurred approximately 83% of the time, with only 17% (15% meropenem, 20% PTZ arms) of patients on concordant therapy for empiric and study treatment (Figure 2). We argue that this serves only to bias toward the null hypothesis. An alternative interpretation is that non-study treatment would have an equivalent or greater impact on outcomes, and thus, it is impossible to know to what extent the study drug had a causal relationship with outcomes.

Figure 1:

Time on study drug compared with non-study drug

Stacked column graph showing the types of antimicrobials used for empiric, study and post study/discharge periods. Mean duration of each period is included in white at top.

Figure 2:

Schematic of antimicrobial therapy through MERINO trial stages

Schematic of therapies provided to patients in the MERINO trial empirically, during the study period and following the study period. Duration of study drug is shown below study arm box. Total duration of antibiotics in the meropenem arm is depicted above the image; the PTZ arm is depicted below the image.

For MERINO: The only difference between study arms is study drug and differences are attributable to study arm

The MERINO trial can only attempt to answer the question for which it was designed. The impact of empiric therapy, by the very nature of the study design, was not assessable. Furthermore, as a pragmatic trial accepting a wide range of infectious sources, the trial protocol could not stipulate a clearly defined treatment duration. More than half of the antibiotic exposure for patients in MERINO was defined by the group to which they were randomized: mean of 7.4 days of study drug out of 13.5 days of total antibiotic treatment. Furthermore, the choice of step-down therapy was similar between the PTZ and meropenem groups, suggesting that its impact on treatment effect between groups is minimal. While a non-study drug will impact the treatment effect, the greatest difference between groups in terms of antibiotic exposure remains the study drug to which they were randomized.

Cause of death

Against MERINO: The primary outcome is not attributable to the study drug

The primary outcome of 30-day mortality is objective and clear-cut. However, whether it reflects the efficacy of either antibiotic is questionable and 30 days is an arbitrary time, since most infections are treated by 7 days of antibiotics and given the end-stage disease in the patients who died, other factors may have intervened after effective treatment of the infection. Further, according to Harris et al (Supplement 2, eTable 6: Details of Fatal Serious Adverse Events), none of the deaths were attributable to the study drug. Some deaths are clearly unrelated to study drug (e.g., norovirus infection, leiomyosarcoma), while others could be argued to be the physiologic results of less well-treated sepsis. This is a hard argument to counter without having a very detailed look at the patient charts. However, much of the mortality occurs later in the follow-up, apparently from the underlying disease. It is very unlikely that any antibiotic choice would have altered the course of disease in end-stage metastatic cancer. Given the imbalance in groups, substantial time on non-study drugs and poor empiric therapy, it is unclear how much altering antibiotic therapy would have changed these outcomes.

For MERINO: Mortality is an accepted and clear-cut endpoint

All-cause mortality is the single most objective outcome measure. It completely removes all bias and subjective interpretation. While 30 days is an arbitrary time, one must be selected in order to conduct a clinical trial. Choosing a time that is too short risks missing relevant treatment effect; while choosing a time that is too long risks overwhelming the treatment effect by other confounding factors. The observational literature exploring definitive therapy for ESBL bacteremia predominantly used 30-day mortality as the primary outcome, further supporting the endpoint used by MERINO (1,4).

While none of the deaths were directly attributable to study drug, this is itself a narrowly defined concept. The treatment effect for antibiotic therapy involves clinical cure of the infection, as well as minimizing adverse impacts of antibiotic therapy on host physiology and microbiome. A treatment that cures the infection at the cost of destabilizing comorbid illness or microbiome consequences (such as C. difficile infection) should not be ignored. Furthermore, reviewing the causes of death in Harris et al (Supplement 2, eTable 6), the rates of malignancy-associated mortality were nearly identical between PTZ and meropenem groups at 55% and 50%, respectively. If the groups were prognostically unbalanced due to underlying malignancy, one would expect to see a higher proportion of malignancy-associated mortality in the PTZ group.

Enzyme type and microbiologic techniques

Against MERINO: The role of ESBL compared with other enzymes is not clear

The authors discuss ESBL as being the target of their study, and this enzyme group is the predominant group; however, a substantial minority of resistant enzymes are AmpC rather than ESBL and would not be predicted to respond to a BLBI. Unfortunately, the publication does not address the distribution of AmpC enzymes with respect to mortality, specifically for PTZ which would be expected to fail for organisms carrying these enzymes. Also, the missing 20% of organisms that were not tested phenotypically are not well explained. If, for example, they all came from a specific site that had high mortality (e.g., Turkey), there may be excess deaths explained by differences in epidemiology. Looking at the mortality rate of 12.3% in the PTZ arm of the study and the AmpC prevalence of 12.2% (alone or in combination) it is at least mathematically possible that all deaths were due to failure to treat an AmpC carrying organism. Further, the role and distribution of OXA-1 enzymes were not reported. It is known that OXA-1 can increase minimum inhibitory concentration (MIC) values to PTZ (9) and so an examination of its role in mortality may (or may not) explain differences in outcomes between groups, and may serve to inform what the role of PTZ might be in the future in the presence or absence of OXA-1 enzymes.

In addition, the choice of microbiologic technique raises questions. The use of gradient strips as the definitive test of resistance to PTZ raises the potential question of inaccurate results—as evidenced by the high number of AmpC carrying organisms. The European Committee on Antimicrobial Susceptibility Testing (EUCAST) has a long-standing warning about under-detection of resistance in all available gradient strips for PTZ, which applied during the entire study duration (10). The coordinating lab should have used a reference method (e.g., broth microdilution), rather than gradient strips. Also, since the technology necessary for detection of ESBL is easy and cheap to perform (by disk, gradient strip, or automated system), it would have been preferable to include this testing at the time of enrolment.

For MERINO: The enzyme distribution and testing methods reflect real-world medicine

For pragmatic reasons, MERINO did not specifically focus on ESBL-producing organisms. Instead, they used ceftriaxone–non-susceptible and PTZ-susceptible as a proxy: all labs will routinely report susceptibility results, but not all labs specifically test for the presence of ESBL. It is admittedly troubling that only 80.7% of isolates were available at the reference lab for further testing; it is not clear why not all isolates were available. Nevertheless, of those isolates tested, 86% were phenotypically confirmed ESBL-producing—a clear majority. The 12% carrying AmpC genes is of concern, although no mention is made of the relative distribution between treatment groups. Therefore, inferring the potential confounding impact of AmpC is not justifiable. Moreover, the relative prevalence of OXA-1 is common—a similar distribution is present in Canadian ESBL isolates (11).

Conclusions

How do we move forward?

While we applaud MERINO trial authors, concerns remain about the validity and applicability of the study conclusions. As this point–counterpoint has shown, MERINO has not been the definite trial to answer the question of whether BLBIs are safe and effective in ESBL infections. Like all good science, the MERINO trial raises new questions and offers the opportunity to refine our methods.

The pragmatic trial design, by its very nature, enrolled a more heterogeneous population of patients. Adding to this, the early cessation of the study during interim analysis and the resultant sample size left serious doubts about an adequate balance of the confounding factors. Furthermore, enrolling a substantial number of patients with malignancies and other end-stage diseases—while pragmatically relevant—makes the conclusions difficult to interpret.

Given the aforementioned uncertainties, the most concerning outcome would be that we close the book on this important question. Certainly, the data do not support the use of a BLBI on very ill patients until there is further information; however, failure to revisit this question could result in the premature rejection of a useful carbapenem-sparing option. In addition, based on personal observations, the MERINO trial has been used to alter empiric therapy regimes favouring carbapenems, a decision that is supported neither by the trial design nor its outcomes.

Future studies would do well to focus more narrowly in order to better control the trial conditions. Lower risk sources of infection supported by the trial subgroup data and observational data, such as UTIs, would be a good start (1,4). Duration of therapy in UTIs is also well established, allowing for a well contained and controlled trial (12). Biliary sources of bacteremia are another potential patient population with a low risk of mortality. Conversely, conducting a trial in immune-compromised patients in the absence of further safety data is likely unjustifiable. In the bigger picture, having high-quality efficacy and safety data for UTIs and biliary infections would go a long way to support carbapenem-sparing strategies.

In trials of bacteremic patients, it is likely impossible that the time to randomization and study drug administration can be brought down to zero. However, newer rapid diagnostic techniques can shorten the time to randomization dramatically (13). This would maximize treatment duration under the study drug, and therefore minimize confounding factors.

Competing Interests:

The authors have nothing to disclose.

Ethics Approval:

N/A

Informed Consent:

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Registry and the Registration No. of the Study/Trial:

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Animal Studies:

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Funding:

No funding was received for this work.

Peer Review:

This article has been peer reviewed.