A systematic assessment of preclinical multilaboratory studies and a comparison to single laboratory studies

  1. Victoria T Hunniford
  2. Agnes Grudniewicz
  3. Dean A Fergusson
  4. Joshua Montroy
  5. Emma Grigor
  6. Casey Lansdell
  7. Manoj M Lalu  Is a corresponding author
  8. On behalf of The Canadian Critical Care Translational Biology Group
  1. Clinical Epidemiology Program, Blueprint Translational Research Group, Ottawa Hospital Research Institute, Canada
  2. Telfer School of Management, University of Ottawa, Canada
  3. Faculty of Medicine, University of Ottawa, Canada
  4. Department of Surgery, University of Ottawa, Canada
  5. School of Epidemiology and Public Health, University of Ottawa, Canada
  6. Department of Anesthesiology and Pain Medicine, The Ottawa Hospital, University of Ottawa, Canada
  7. Regenerative Medicine Program, The Ottawa Hospital Research Institute, Canada
  8. Department of Cellular and Molecular Medicine, University of Ottawa, Canada

Abstract

Background:

Multicentric approaches are widely used in clinical trials to assess the generalizability of findings, however, they are novel in laboratory-based experimentation. It is unclear how multilaboratory studies may differ in conduct and results from single lab studies. Here, we synthesized the characteristics of these studies and quantitatively compared their outcomes to those generated by single laboratory studies.

Methods:

MEDLINE and Embase were systematically searched. Screening and data extractions were completed in duplicate by independent reviewers. Multilaboratory studies investigating interventions using in vivo animal models were included. Study characteristics were extracted. Systematic searches were then performed to identify single lab studies matched by intervention and disease. Difference in standardized mean differences (DSMD) was then calculated across studies to assess differences in effect estimates based on study design (>0 indicates larger effects in single lab studies).

Results:

Sixteen multilaboratory studies met inclusion criteria and were matched to 100 single lab studies. The multicenter study design was applied across a diverse range of diseases, including stroke, traumatic brain injury, myocardial infarction, and diabetes. The median number of centers was four (range 2–6) and the median sample size was 111 (range 23–384) with rodents most frequently used. Multilaboratory studies adhered to practices that reduce the risk of bias significantly more often than single lab studies. Multilaboratory studies also demonstrated significantly smaller effect sizes than single lab studies (DSMD 0.72 [95% confidence interval 0.43–1]).

Conclusions:

Multilaboratory studies demonstrate trends that have been well recognized in clinical research (i.e. smaller treatment effects with multicentric evaluation and greater rigor in study design). This approach may provide a method to robustly assess interventions and the generalizability of findings between laboratories.

Funding:

uOttawa Junior Clinical Research Chair; The Ottawa Hospital Anesthesia Alternate Funds Association; Canadian Anesthesia Research Foundation; Government of Ontario Queen Elizabeth II Graduate Scholarship in Science and Technology

Editor's evaluation

This study provides new insights into the strengths of multi center laboratory studies in enhancing rigor and possibly more realistic effect sizes. These insights provide potential paths forward for future studies.

https://doi.org/10.7554/eLife.76300.sa0

Introduction

The impact of preclinical research using animal models is conditional on its scientific validity, reproducibility, and representation of human physiology and condition (Landis et al., 2012; Chalmers et al., 2014; van der Worp et al., 2010). Improving the quality of the design, conduct, and reporting of preclinical studies may lead to a reduction in research waste (Chalmers et al., 2014; Ioannidis et al., 2014), as well as increase their utility in informing the development of novel therapies (Begley and Ellis, 2012; Langley et al., 2017). One method to do so may be the application of multicenter experimentation in preclinical studies. This is analogous to what is done in clinical trials where positive findings from a single center study are usually evaluated and confirmed in a multicenter study (Chamuleau et al., 2018; Bath et al., 2009; Bellomo et al., 2009). Multicenter studies allow for the comparison of effects between centers, which provides insight into the generalizability of effects across institutions (Cheng et al., 2017). Thus, they inherently test reproducibility while also increasing efficiency in attaining sufficient sample sizes (Bath et al., 2009). In addition, rigorously designed and reported multicenter studies may enhance the confidence in study findings and increase transparency (Maertens et al., 2017). This approach has been adopted in other fields such as social and developmental psychology (Visser et al., 2022; Baumeister et al., 2022).

Multiple calls from the biomedical science community have been made to adopt and apply multicenter study design to preclinical laboratory-based research (Langley et al., 2017; Chamuleau et al., 2018; Maertens et al., 2017; O’Brien et al., 2013; Boltze et al., 2016; Dirnagl and Fisher, 2012). Some recent examples have been published that exemplify the successful implementation of this approach (Llovera et al., 2015; Jones et al., 2015; Maysami et al., 2016). Indeed, multilaboratory studies may offer a method to test issues of reproducibility that have been highlighted by several studies (Begley and Ellis, 2012; Errington et al., 2021b). As interest in preclinical multilaboratory studies grows, and major funders begin to invest in this approach (Federal Ministry of Education and Research, 2022), a systematic evaluation of this method is needed. This will inform and optimize future multicenter preclinical studies by producing a synthesis of current practices and outcomes, while also identifying knowledge gaps and areas for improvement (Dirnagl and Fisher, 2012; Llovera and Liesz, 2016; Fernández-Jiménez and Ibanez, 2015). Moreover, it is currently unknown how the results obtained from a preclinical multilaboratory study compare to a preclinical study conducted in a single laboratory. This comparison is of interest as multiple clinical meta-epidemiological studies have shown that single center clinical trials have a higher risk of bias and overestimate treatment effects compared to multicenter trials (i.e. smaller clinical trials at single sites have a higher probability of methodological shortcomings, lower inferential strength, and may provide inaccurately high estimates of treatment effects) (Unverzagt et al., 2013; Dechartres et al., 2011; Bafeta et al., 2012). For this reason, results from single center studies are generally used cautiously for clinical decision-making (Bellomo et al., 2009). Currently, there has been no empirical investigation into whether this trend occurs in the preclinical domain. This knowledge would provide greater insight into the potential value of the multilaboratory design in preclinical research.

The first objective of this systematic review was to identify, assess, and synthesize the current preclinical multilaboratory study literature. The second objective was to empirically determine if differences exist in the methodological rigor and effect sizes between single lab and multilaboratory studies.

Materials and methods

Synthesis of preclinical multilaboratory studies

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This systematic review was reported in accordance with the Preferred Reporting Items for Systematic Review and Meta-Analysis (PRISMA) guidelines (Moher et al., 2009; Page et al., 2020). A copy of the PRISMA checklist is provided in the supporting information (Reporting standard 1). The protocol was registered with the International Prospective Register of Systematic Reviews (PROSPERO CRD42018093986). All data can be accessed in supplementary files.

Preclinical multilaboratory eligibility criteria

Population

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The population of interest was preclinical, interventional, multilaboratory, controlled comparison studies. Preclinical was defined as research conducted using nonhuman models that involve the evaluation of potential therapeutic interventions of relevance to human health. Multilaboratory was defined as cooperative research formally conducted between multiple research centers (sites). Models were limited to in vivo experiments but were not limited by the clinical scope or domain of the preclinical study.

Intervention, comparators, outcomes

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Interventions were restricted to agents with potential effects when considering human health. There were no limitations to the comparator or outcomes of individual studies included.

Study design

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Eligible preclinical studies including in vivo, controlled, interventional studies of randomized and non-randomized designs. In vivo experiments needed to be conducted at two or more independent sites for the study to qualify as multicentric. The sites needed to also share more than just general study objectives to be considered multicentered. Features that met the ‘multicenter’ criteria included: shared design, specific hypothesis, a priori protocol, animal model, intervention protocol, method of analysis, primary endpoints tested with or without identical measurement apparatuses; separate centers for coordination, protocol development, and data analysis; and study objective, timelines, protocols, and dissemination strategies developed a priori. Veterinary clinical trials, in vitro and ex vivo studies (with no in vivo component), and retrospective data analysis from multiple sites were excluded.

Preclinical multilaboratory search strategy

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The search strategy was developed in collaboration with our institute’s information specialist (Risa Shorr MLS, The Ottawa Hospital). Embase (Embase Classic and Embase), and MEDLINE (Ovid MEDLINE Epub Ahead of Print, In-Process & Other Non-Indexed Citations, Ovid Medline Daily and Ovid Medline) were searched (last updated November 25, 2020). A second, independent librarian peer-reviewed the search strategy according to the Peer Review of Electronic Search Strategy (PRESS) framework (McGowan et al., 2016). No study scope, date, or language limits were imposed, though all search terms were in the English language. The search strategy is presented in the supporting information (Supplementary file 1), as well as the PRESS review (Supplementary file 2).

Preclinical multilaboratory screening and data extraction

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The results from the literature search were uploaded to Distiller Systematic Review Software (DistillerSR; Evidence Partners, Ottawa, Canada). DistillerSR is a cloud-based program that facilitates the review process by managing studies through customized screening, auditing, and reporting. Duplicate references were removed, and two reviewers (VTH and CL/EM/JM) independently screened titles and abstracts based on the eligibility criteria. Any disagreements were resolved by consensus. For the second stage of screening, two reviewers (VTH and MML/JM) independently screened the full-text reports of included references based on the eligibility criteria. Disagreements were solved via consensus.

Data were extracted using a standardized extraction form developed in DistillerSR that was piloted by the primary reviewer (VTH) on five studies and revised based on feedback from a senior team member (MML). Qualitative data included characteristics of the studies: publication details (authors, year published, journal), the country(ies) where the study was conducted, sources of funding, the number of centers involved (experimental and non-experimental), the disease model, animal species and sex, treatment/exposure, all study outcomes (primary, secondary, or undefined), the reported results, statements of barriers and facilitators, and statements of recommendations and suggestions for future testing of the specific therapy being investigated. Quantitative data included the measures of central tendency and dispersion, the sample sizes for the outcome used in the meta-analysis and for the control group, and the total number of animals analyzed. Numerical data were extracted from raw study data or using Engauge Digitizer (version 12.0 Mitchell et al., 2020) if data was presented in a graphical format.

Assessing preclinical multilaboratory study completeness of reporting and risk of bias

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Risk of bias and completeness of reporting in the preclinical multilaboratory studies were assessed independently by two reviewers (VTH and MML), and disagreements were resolved via consensus. For both assessments, the main articles along with the supporting information (when provided) were consulted. All randomized, interventional studies were assessed as high, low, or unclear for the 10 domains of bias adapted from the SYRCLE ‘Risk of Bias’ assessment tool for preclinical in vivo studies (Hooijmans et al., 2014). The ‘other sources’ of risk of bias domain was divided into four sub-domains (funding influences, conflicts of interest, contamination, and unit of analysis errors). An overall ‘other’ risk of bias assessment was given based on the following: overall high risk of bias if one or more of the four other sources were assessed as high; overall unclear risk of bias if two or more of the four other sources were assessed as unclear (and no high risk); and overall low risk of bias if three of the four other sources were assessed as low (and no high risk).

Completeness of reporting of the multilaboratory studies was assessed using a checklist modified from various sources: consolidated Standards of Reporting Trials (CONSORT Moher et al., 2010); the National Institutes of Health (NIH)’s principles and guidelines for reporting preclinical research Landis et al., 2012; and the Good Clinical Practice (GCP) Guidance Document: E6(R2) (Health Canada, 2016). The checklist is provided in the supporting information (Appendix 1—table 5) with details on the sources for each item.

Effect size comparison between preclinical multilaboratory and single lab studies

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We compared the effect sizes of the multilaboratory studies we identified with single lab studies that investigated the same intervention. We only performed comparisons for the multilaboratory studies that evaluated the efficacy of an intervention. Single lab studies for each of the included multilaboratory study comparisons were identified using rapid review methods, which consisted of the search of a single database, and having a single reviewer screen, extract, and appraise studies while an additional reviewer verified study exclusions, extracted data, and appraisals (Khangura et al., 2012; Varker et al., 2015). The protocol for the effect size comparison was developed a priori and posted on Open Science Framework (https://osf.io/awvs9/).

Single lab study eligibility criteria

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Population - We included all animal species used to model the disease of interest in the multilaboratory study. We only included studies modeling the exact human condition/disease of the multilaboratory study, but did not limit this to the method and timing of disease induction, nor by additional co-morbidities modeled in the animals.

Intervention – We included studies investigating the same intervention being evaluated in the multilaboratory study.

Comparator – We only included studies that had the same comparator to the multilaboratory study in terms of active versus placebo controls.

Outcome – We considered only the main outcome that was evaluated in the multilaboratory study.

Design – Eligible preclinical studies including in vivo, controlled, interventional studies of randomized, and non-randomized designs.

Date limitations – No date limitations were applied.

Single lab study screening and data extraction

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We first searched for preclinical systematic reviews of the therapies being tested and disease modeled in the multilaboratory studies. If no systematic review was identified, we searched for single lab studies through a formal literature search. Search strategies using the eligibility criteria outlined above were developed with our institute’s information specialist. The references of previous single lab studies cited in the multilaboratory studies were retrieved and used to refine the searches. The database MEDLINE (Ovid MEDLINE Epub Ahead of Print, In-Process & Other Non-Indexed Citations, Ovid Medline Daily, and Ovid Medline) was searched from inception (1946). A validated animal filter limited results to animal studies (Hooijmans et al., 2010). A single database was used as per rapid review methods (Haby et al., 2016).

The results of the searches were uploaded to DistillerSR. Duplicate references were removed, and one reviewer screened titles, abstracts, and full-text based on eligibility criteria. If after the screening, there were greater than 10 eligible single lab studies identified (either through a systematic review or through a literature search), we selected the 10 single lab studies most similar to the respective multilaboratory study (in terms of animal species, timing and dose of intervention, time of measurement/humane killing, publication year). Given the large number of searches required, we chose to compare a maximum of 10 single lab studies for feasibility reasons. If more than 10 eligible studies were equally similar to the multilaboratory study, then 10 were randomly selected using a random-number generator (https://www.random.org/).

Data from the eligible single lab studies were extracted by one reviewer (VTH) and audited by a second reviewer (JM). Any disagreements were resolved through further discussion. Extracted data included: the first author, year of publication, the quantitative outcome data along with the measures of variation (e.g. means, standard error/deviation, and sample size) for the shared outcome with the multilaboratory study, the animal species and sex, the study sample sizes (intervention and control groups). Numerical data were extracted from reported study data or using Engauge Digitizer if data was presented in a graphical format.

Data analysis

Multilaboratory and single lab study quality

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Study quality for both multilaboratory and single lab studies was assessed by one reviewer (VTH) and confirmed by a second (JM); disagreements were resolved by consensus (Jadad et al., 1996). Specifically, for each study, we evaluated five key practices that are recognized to reduce bias in laboratory experiments: randomization to treatment groups, low risk of bias methods of randomization (Reynolds and Garvan, 2021), blinding of personnel (O’Connor and Sargeant, 2014), blinding of outcome assessor (Bello et al., 2014; Macleod et al., 2008), and complete reporting of all outcome data (Holman et al., 2016). Each practice was assessed as ‘0’ for not performed/reported, or a ‘1’ for having performed the practice. We used a Mann-Whitney U test to compare the total quality estimates between multilaboratory and single lab studies. We did not individually compare the five key practices between multilaboratory and single lab studies.

Statistical analysis - effect size comparison

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The multilaboratory study’s effect size (i.e. treatment effect) of their respective primary/shared outcome was compared to the pooled effect size of the corresponding set of single lab studies. We extracted quantitative outcome effect measures and measures of variation from each single lab study (e.g. means, standard error/deviation, and sample size). We used Engauge Digitizer if data was presented in a graphical format. Summary effect sizes (ES) were calculated for the multilaboratory and single lab studies using Comprehensive Meta‐Analysis (version 3; Biostat Inc, USA). The effect size ratio (ESR) for the multilaboratory versus single lab studies was obtained by dividing the single lab summary effect size by the effect size of the corresponding multilaboratory study. This was expressed as a percentage. For each meta-analysis i, this was calculated as:

ESRi=ES(singlelabstudies)iES(multilaboratorystudy)i

This quantified the difference between the effect size of matched multilaboratory and single lab studies, regardless of the metric used to demonstrate the outcome effect. An ESR of 1 indicates no difference, an ESR greater than 1 indicates single lab studies produce a larger summary effect size compared to multilaboratory studies, and an ESR less than one indicates that the single lab studies produce a smaller summary effect size compared to multilaboratory studies. To obtain a more metric-relevant comparison, and for cases where the single lab studies measure the effect of the same outcome in different ways, we also calculated the difference of standardized mean difference (DSMD). Because all multilaboratory outcomes were continuous, standardized mean differences were calculated using a random effects inverse‐variance model and presented with accompanying 95% confidence intervals. Standardized mean differences were used due to the variety of measurement methods reported for the outcomes of interest. We calculated the standardized mean difference for all single lab studies, collective, and for the multilaboratory study. These values, indicated as d, were used to calculate the DSMD as follows:

DSMDi=d(singlelabstudies)id(mutlilaboratorystudy)i

Synthesis of preclinical multilaboratory qualitative data and assessments

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Descriptive data of the multilaboratory study was synthesized and presented through tabulation of textual elements (Popay et al., 2006). A synthesis of any statements and examples pertaining to barriers and facilitators in conducting a multilaboratory study was also performed. Studies were arranged in tables based on study design, basic characteristics, and risk of bias assessments.

Synthesis of multilaboratory and single lab data

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Study quality estimates and effect size comparison assessments from each of the sets of the selected single lab studies and corresponding multilaboratory studies were synthesized and presented independently in a tabular format. Forest plots were used to compare the effect sizes of individual single lab studies with the respective corresponding multilaboratory study.

Deviations from protocol

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The original protocol submitted to PROSPERO indicated that the degree of collaboration would be evaluated. After expert feedback, it was decided not to evaluate the degree of collaboration as the methods for this assessment were not feasible to apply to the preclinical setting.

The protocol to evaluate the effect sizes of multilaboratory and single lab studies was posted on Open Science Framework. This protocol indicated that we would use SYRCLE’s Risk of Bias tool (Hooijmans et al., 2014) to evaluate the studies’ quality estimate. After expert feedback, it was decided to focus on elements with empirical evidence supporting their importance in the lab setting (i.e. randomization Reynolds and Garvan, 2021, blinding O’Connor and Sargeant, 2014; Bello et al., 2014; Macleod et al., 2008, and complete reporting of all outcome data Holman et al., 2016).

Peer reviewers requested additional analysis to qualitatively assess identified single laboratory studies that were conducted by the same authors of matched multilaboratory studies.

Results

Preclinical multilaboratory search results and study characteristics

The database searches identified a total of 3793 papers after duplicates were removed (Figure 1). There were no non-English articles identified in the search. Sixteen articles met eligibility criteria following title, abstract, and full-text screening (Tables 1 and 2).

Preferred reporting items for systematic reviews and meta-analysis (PRISMA) flow diagram for study selection.
Table 1
Basic study characteristics of preclinical multilaboratory studies.
Author, YearCenter locationJournalFundingCenters PerformingIn Vivo WorkNon-Experimental Centers*Animal, SexSample size
Reimer et al., 1985USCirculation ResearchGovernment (NHLBI)31Dog, both51
Crabbe et al., 1999Canada, USScienceGovernment30Mouse, both384
Alam et al., 2009USJournal of Trauma: Injury, Infection and Critical CareGovernment (US army)30Swine, F60
Spoerke et al., 2009USArchives of SurgeryGovernment (US army)20Swine, NA32
Jones et al., 2015USCirculation ResearchGovernment (NHLBI)33Mouse, M
Rabbit, M
Swine, F
47
23
26
Llovera et al., 2015France, Germany, Italy, SpainScience Translational MedicineGovernment, academic and charitable51Mouse, M315
Maysami et al., 2016Finland, France, Germany, Hungary, UK, SpainJournal of Cerebral Blood Flow & MetabolismGovernment (FP7/
2007–2013, INSERM), academic
51Mouse, M241
Bramlett et al., 2016USJournal of NeurotraumaGovernment (US army)31Rat, M140
Browning et al., 2016USJournal of NeurotraumaGovernment (US army)31Rat, M130
Dixon et al., 2016USJournal of NeurotraumaGovernment (US army)31Rat, M135
Gill et al., 2016USDiabetesGovernment, charitable40Mouse, FNR
Mountney et al., 2016USJournal of NeurotraumaGovernment (US army)31Rat, M128
Shear et al., 2016USJournal of NeurotraumaGovernment (US army)31Rat, M142
Arroyo-Araujo et al., 2022Netherlands, Switzerland, USScientific ReportsGovernment (FP7/2007–2013), industry (EFPIA), charitable30Rat, M72
Jha et al., 2020USJournal of NeurotraumaGovernment (US army)31Rat, M111
Kliewer et al., 2020Australia, Germany, UKBritish Journal of PharmacologyGovernment (NHMRC, NIH), NGO30Mouse, M108
  1. Legend: EFPIA - European Federation of Pharmaceutical Industries and Associations; FP7/2007-2013 – European Union Commission seventh Funding Program; INSERM - Institut national de la santé et de la recherche médicale; NGO – Non-government organization; NHLBI – National Heart, Lung, and Blood Institute; NHMRC – National Health and Medical Research Council; NIH – National Institutes of Health; NR - not reported; UK – United Kingdom; US – United States.

  2. *

    Non-experimental center: A site/lab not involved with the in vivo experiment (data processing, coordinating, biomarker, or pathology centers).

  3. Center that was both an experimental center and a coordinating center.

Table 2
Study design characteristics of preclinical multilaboratory studies.
Author, YearDisease modelInterventionStudy OutcomesSecondary OutcomesReported ResultsRecommendations for Future Research
Reimer et al., 1985Myocardial infarctionVerapamil and ibuprofenInfarct sizeMortality, hemodynamic measures, pathological/histological features, regional blood flowNullNot reported
Crabbe et al., 1999Stimulant exposureCocaineLocomotor activityMixedFurther preclinical testing
Alam et al., 2009PolytraumaBlood transfusionHemodynamic parametersMortalityMixed across resuscitation productsFurther preclinical testing
Spoerke et al., 2009PolytraumaLyophilized plasmaResidual clotting activityMortality, hemodynamic measures, total blood loss, coagulation profiles, inflammatory measuresPositiveFurther preclinical testing
Jones et al., 2015Myocardial infarctionIschemic preconditioningInfarct sizeHemodynamic measures, regional blood flow, heart weight, troponin I, mean arterial pressurePositiveFurther preclinical testing
Llovera et al., 2015StrokeAnti-CD49d antibodyInfarct sizeFunctional outcome, invasion of leukocytes to brainMixed across models (positive, null)First-in-human clinical trial
Maysami et al., 2016StrokeInterleukin-I receptor antagonistInfarct sizeOdema, functional outcome, mortalityPositiveExtensive clinical trial
Bramlett et al., 2016Traumatic brain injuryErythropoietinCognitive outcomes, biomarkers, motor outcomes, neuropathologyNullNo further preclinical study
Browning et al., 2016Traumatic brain injuryLevetiracetamCognitive outcomes, biomarkers, motor outcomes, neuropathologyPositiveFurther preclinical testing and first-in-human clinical trial
Dixon et al., 2016Traumatic brain injuryCyclosporineCognitive outcomes, biomarkers, motor outcomes, neuropathologyNullNo further preclinical testing
Gill et al., 2016DiabetesCombined
anti-CD3 +IL-1 blockade
Blood glucoseNullPause clinical trial
Mountney et al., 2016Traumatic brain injurySimvastatinCognitive outcomes, biomarkers, motor outcomes, neuropathologyNullNo further preclinical study
Shear et al., 2016Traumatic brain injuryNicotinamideCognitive outcomes, biomarkers, motor outcomes, neuropathologyNullNo further preclinical study
Arroyo-Araujo et al., 2019Autism spectrum disordermGluR1 antagonist (JNJ16259685)Behavioural activityPositiveNot reported
Jha et al., 2020Traumatic brain injuryGlibenclamideCognitive outcomes, biomarkers, motor outcomes, neuropathologyGlucose level, drug levelsMixed across models and outcomes (positive, null, and negative)Further preclinical testing
Kliewer et al., 2020Opioid-induced respiratory depressionMorphineRespiratory rateConstipationNullNot reported

The identified studies fell into seven clinical domains: traumatic brain injury (n=6), myocardial infarction (n=2), stroke (n=2), traumatic injury (n=2), effects of stimulants/neuroactive medication (n=2), diabetes (n=1), and autism spectrum disorder (n=1). Twelve of 16 studies were published in 2015–2020. Five studies were international (studies with labs located in multiple countries), and eleven studies were conducted solely in the USA (all labs located in the USA). The median number of total labs involved per multilaboratory study was four (range: 2–6), and the median number of experimental labs performing in vivo work was three (range:2-5). Nine studies (56%) reported having non-experimental centers involved, such as a coordinating center, data processing center, biomarker core, or pathology core. Five different species of animals were used in the studies: rats (n=7), mice (n=6), swine (n=3), rabbits (n=1), and dogs (n=1). One study used three species of animals for their experiments. The median sample size was 111 (range 23–384 animals), and a total of 2145 animals were used across the sixteen studies, 91% of which were lab rodents (mice and rats).

Reported preclinical multilaboratory outcomes

Five of the studies (31%) reported that the treatment showed statistically significant, positive results (i.e. favoring the hypothesis); seven studies reported that the treatment showed non-significant or null results; four studies reported that the results were mixed across different treatment specifics (Alam et al., 2009), animal models of the disease of interest (Llovera et al., 2015), or outcome measures (Wahlsten et al., 2003; Jha et al., 2020; Table 2). Based on their respective results, thirteen studies made explicit statements of recommendations or future directions for the intervention tested. Seven studies stated that they would conduct further testing or recommended that further preclinical testing be done. Four studies indicated they would not continue testing or recommended that no further preclinical testing be done. Three studies recommended to proceed with clinical trials. Brief synopses of the sixteen studies can be found in supporting information (Appendix 1), along with sample statements of their future recommendations (Appendix 1—table 1).

Risk of bias of preclinical multilaboratory studies

None of the 16 studies (0%) were considered low risk of bias across all ten domains (Table 3). Fifteen studies randomized animals to experimental groups and four of these reported the method of random sequence generation – one of which used pseudo-randomization methods at one of the participating labs (thus was given a high risk of bias assessment). Thirteen studies had a low risk of detection bias by blinding of outcome assessors. Eleven studies were at low risk of performance bias by blinding personnel administering interventions. All but one study were unclear if animals were randomly housed during the experiments. Six studies from the same research consortium (Operation Brain Trauma Therapy) had a high risk of bias for ‘other sources’ of bias due to potential industry-related influences (Table 3). The four ‘other sources’ of risk of bias assessments for each study can be found in the supporting information (Appendix 1—table 2).

Table 3
Risk of bias assessment of preclinical multilaboratory studies.
StudySequence generation §Baseline characteristicsAllocation concealment§Random housingBlinding of personnelRandom outcome assessmentBlinding of outcome assessmentIncomplete outcome data*, §Selective outcome reportingOther sources of bias §
Reimer et al., 1985U*ULUHULULU
Crabbe et al., 1999U*LULUUULLH
Alam et al., 2009U*LUUULULLU
Spoerke et al., 2009U*LUUULULLU
Jones et al., 2015LLUULLLLLL
Llovera et al., 2015LLUULLLLLL
Maysami et al., 2016H HLULLLLHH
Bramlett et al., 2016U*UUULLLULH
Browning et al., 2016U*UUULLLULH
Dixon et al., 2016U*UUULLLULH
Gill et al., 2016HLUUULLUUL
Mountney et al., 2016U*UUULLLULH
Shear et al., 2016U*UUULLLULH
Arroyo-Araujo et al., 2019LLUULULLLH
Jha et al., 2020U*UUULLLULH
Kliewer et al., 2020U*UUULULULL
  1. Legend: H=High risk of bias (red), L=Low risk of bias (green), U=Unclear risk of bias (yellow).

  2. Baseline Characteristics: Low risk = Relevant baseline characteristics equal between experimental groups or controlled for. Unclear = Relevant baseline characteristics are unreported. High risk = Relevant baseline characteristics unbalanced between experimental groups and not controlled.

  3. Random Housing: Low risk = Animal cages were randomly placed within an animal room/facility, Unclear = Housing placement unreported, High risk = Animals placed in a non-random arrangement in animal room/facility.

  4. Blinding of Outcome Assessment: Low risk = Outcome assessors were blinded to the study groups when assessing endpoints/animals Unclear = Insufficient information to determine if outcome assessors were blinded during an assessment. High Risk = Outcome assessors not blinded to the study groups.

  5. Incomplete Outcome Data: Low risk = N values were consistent between methods and results for the outcomes. Unclear = N value was either not presented in the methods or in the results, and therefore there is insufficient information to permit judgment. High risk = N values were not consistent between methods and results for the outcomes.

  6. Selective Reporting: Low risk = The methods section indicated pre-specified outcome measures. Unclear: Was not clear about the pre-specified primary endpoints and outcome results. High risk = The outcome was presented in the results but not pre-specified in the methods section.

  7. *

    Method of randomization not specified.

  8. Assessed as high because one arm of the study was inadvertently unblinded.

  9. Some labs used appropriate randomization where others used pseudo-randomization.

  10. §

    Items in agreement with the Cochrane Risk of Bias tool.

  11. other sources include funding influences, conflicts of interest, contamination, a unit of analysis errors.

Completeness of reporting in preclinical multilaboratory studies

Overall, the completeness of reporting of checklist items across all sixteen studies was high (median 72%, range 66–100%). The domains with the highest completeness of reporting included replicates (biological vs. technical), statistics, blinding, and discussion (Appendix 1—table 3). The domains for standards, randomization, sample size estimation, and inclusion/exclusion criteria were variably reported. The introduction and abstract domain had the lowest completeness of reporting, as 8 of the 16 studies did not report that the study was multicentered in the title (or use a synonym) and less than half indicated the number of participating labs in the abstract. Reporting assessment for all 29 items across the 16 studies can be found in the supporting information (Supplementary file 3).

Single lab study rapid review search results

We next identified single lab studies that were matched to fourteen of the identified multilaboratory studies (these fourteen were used since they evaluated the efficacy of an intervention). Systematic reviews were identified for two interventions (Wever et al., 2015; Peng et al., 2014), thus systematic searches were designed and undertaken for the remaining twelve studies. In total, 978 articles were screened for eligibility, and data from 100 eligible single lab studies were extracted. Full details of the identification and selection process can be found in Supporting Information, Appendix 1—table 4.

Single lab characteristics

Across the single lab studies, the median number of animals used (number of animals used for all experiments) was 19 (range: 10–72 animals) and the total number of animals used across all studies was 2166. Studies were published between 1980 and 2019. The disease model, treatment, and comparator group were the same in the single lab studies and the respective corresponding multilaboratory studies. Seventy-three percent of the comparisons were made with single lab studies using the same species in the multilaboratory study. Summary characteristics of the included single lab studies are presented in Table 4.

Table 4
Comparison of characteristics between single lab and multilaboratory studies.

Multilaboratory studies (n=16)Single lab studies (n=100)
Median sample size (range)111 (23–384)19 (10–72)
Total animals used2,1452,166
Publication date range1985–20201980–2019
Disease modeln (%)n (%)
TBI6 (38)46 (46)
Myocardial infarction2 (13)20 (20)
Stroke2 (13)16 (16)
Traumatic injury2 (13)10 (10)
Stimulant exposure2 (13)NA
Diabetes1 (6)2 (2)
Autism spectrum disorder1 (6)6 (6)
Animal speciesn (%)n (%)
Rat7 (44)42 (42)
Mouse6 (38)31 (31)
Swine3 (19)12 (12)
Rabbit1 (6)3 (3)
Dog1 (6)9 (9)
Monkey02 (2)
Cat01 (1)
Animal sexn (%)n (%)
Male10 (63)69 (69)
Female2 (13)13 (13)
Both3 (19)12 (12)
Not reported1 (6)6 (6)
Quality domainPercent of studies that performed each measure (%)
Randomization9457
Randomization methods197
Blinding of personnel6924
Blinding of outcome assessment7553
Complete outcome data3838

Study quality assessments

Study quality was significantly higher in multilaboratory studies versus single lab studies (p<0.001; Mann-Whitney U test). Across all quality domains, the median score of the multilaboratory studies was assessed as three (range: 1–5), while single lab studies were assessed as two (range: 0–4). Sixty-nine percent of multilaboratory studies compared to 22% of single lab studies had total scores of three and above. Percentage of multi- and single lab studies performing each element assessed are presented in Table 4; assessments for each multilaboratory and single lab study can be found in the supplemental information (Supplementary file 4).

Differences in the intervention effect size between single lab and multilaboratory studies

In 13 of 14 comparisons, the intervention effect size (i.e. treatment effect) was larger in single lab studies than in multilaboratory studies. In the pooled analysis of all 14 comparisons, the effect size was significantly larger in single lab studies compared to multilaboratory studies (combined DSMD, 0.72 [95%CI, 0.43–1]; p<0.001) (Figure 2). A scatterplot of the study effect sizes for each comparison is presented in Figure 3; and the forest plots of each of the 14 comparisons can be found in the supplemental information (Figure 2—source data 2). Of note, 8 of the 14 multilaboratory studies had 95% confidence intervals that fell outside of the pooled single laboratory 95% confidence intervals.

Difference in standardized mean difference between single lab and multilaboratory preclinical studies.
Figure 2—source data 1

Source data for comparision of single lab and multilaboratory studies.

https://cdn.elifesciences.org/articles/76300/elife-76300-fig2-data1-v2.xlsx
Figure 2—source data 2

Standardized mean differences for all 14 singlevs multilaboratory comparisons and sub-groups by total quality score.

https://cdn.elifesciences.org/articles/76300/elife-76300-fig2-data2-v2.pdf
Standardized mean differences of single lab and multilaboratory preclinical studies.

Effect size ratio

The ESR was greater than 1 (i.e. the single lab studies produced a larger summary effect size) in 10 of the 14 comparisons. The median effect size ratio between multilaboratory and single lab studies across all 14 comparisons was 4.18 (range: 0.57–17.14). The ESRs for each comparison along with the mean effect sizes and the ratio of the mean effect sizes are found in the supplemental information (Supplementary file 4).

For 10 multilaboratory studies, researchers also had authored 11 matched single lab studies. Median effect size ratio of this smaller matched cohort was 2.50 (mean 4.10, range 0.35–17.63). Median quality assessment score for this cohort of 10 multilaboratory studies was three (range 1–5); median quality score of the 11 single laboratory studies matched by authors was one (range 1–4).

Reported barriers and enablers to preclinical multilaboratory studies

Five of the 16 studies (31%) explicitly reported on the barriers and facilitators to conducting a multilaboratory study. The most frequently reported barrier identified in all five studies was the establishment of a consistent protocol, with attention to exact experimental details across research labs (Llovera et al., 2015; Jones et al., 2015; Maysami et al., 2016; Reimer et al., 1985; Gill et al., 2016). In addition to the challenge of the initial protocol development, studies reported difficulty in labs strictly adhering to the established protocol throughout the entirety of the study. One study (Maysami et al., 2016) had considerable issues in adhering to the protocol, and in effect had to modify its methods through the course of the study.

Three studies (Llovera et al., 2015; Jones et al., 2015; Maysami et al., 2016) reported differences in equipment and resources across labs as a barrier that made it difficult to conduct a collaborative project and to communicate what measurements and endpoints would be assessed. Specific experimental conditions that investigators were unable or unwilling to harmonize across all participating laboratories included animal models of the disease, animal housing conditions, the separate labs’ operating and measurement procedures, equipment, and institutional regulations. There was also inconsistent funding across research labs. Different labs had separate budgets with different amounts of funding that could be allocated to the study. If the protocol was to be harmonized, then it had to be adapted to fit each lab’s budget accordingly (e.g. the lab with the smallest budget set the spending limit in Maysami et al., 2016). Alternatively, labs developed a general protocol but adapted it to fit their own respective budget with what resources they had. Of note, recent work has suggested that harmonization reduces between-lab variability, however, systematic heterogenization did not reduce variability further (Arroyo-Araujo et al., 2022); this may suggest that, even in fully harmonized protocols, enough uncontrolled heterogeneity exists that further purposeful heterogenization has little effect. Another barrier identified was ethics approval for animal experiments at all the labs (Llovera et al., 2015). This was especially significant when labs were located in multiple countries, as each country had different regulations for ethical approval (Llovera et al., 2015; Maysami et al., 2016).

Jones et al., 2015 suggested collaborative protocol development was facilitated by employing pilot testing through all the labs. Developing a defined experimental protocol also included establishing an agreed-upon timeline, laboratory setup, and method of analysis and measurement. Maysami et al., 2016 and Reimer et al., 1985 suggested that a similar approach might have enhanced the conduct of both of their studies. Another study reported that the use of a centralized core for administration and data processing was a facilitator (Llovera et al., 2015; Jones et al., 2015). The validity of reports depends on the control of statistical and data management, and having one lab coordinate these operations reduces the chances of error or bias in the analysis. Other facilitators were related to the interpersonal aspect of collaboration. These included having investigator leadership through regular conferences and check-ins from the beginning to the end of the project (Mondello et al., 2016) and building upon previously established personal/professional relationships between investigators (Jones et al., 2015).

Discussion

Multiple calls for the use of multilaboratory study design in preclinical research have been published (O’Brien et al., 2013; Dirnagl and Fisher, 2012; Llovera and Liesz, 2016; Fernández-Jiménez and Ibanez, 2015; Mondello et al., 2016). Here, we have synthesized characteristics and outcomes from all interventional preclinical multilaboratory studies published in our search period. Our results suggest that this is an emerging, novel, and promising area of research. The sixteen identified multilaboratory studies had investigated a broad range of diseases, promoted collaboration, adopted many methods to reduce bias, and demonstrated high completeness of reporting. In addition, we found that multilaboratory studies had higher methodological rigor than single lab studies, demonstrated by the greater level of implementation of several key practices known to reduce bias. We observed that multilaboratory studies showed significantly smaller intervention effect sizes than matched single lab studies. This approach addresses pressing issues that have been recently highlighted such as reproducibility, transparent reporting, and collaboration with data and resource sharing (Errington et al., 2021b; Kane and Kimmelman, 2021; Errington et al., 2021a).

The differences between single and multilaboratory preclinical studies observed here have also been noted in clinical studies. Several comparisons between clinical single-and multilaboratory RCTs have been performed, all finding that single center RCTs demonstrate larger effect sizes (Bellomo et al., 2009; Unverzagt et al., 2013; Dechartres et al., 2011; Bafeta et al., 2012). These studies also found that multicenter clinical RCTs had larger sample sizes and greater adherence to practices such as allocation concealment, randomization, and blinding. This difference in sample size and methodological quality, which we have also observed, may explain the discrepancy in effect sizes. It has been shown that smaller studies included in meta-analyses provide larger intervention effects than larger studies (Zhang et al., 2013; Fraley and Vazire, 2014). Furthermore, preclinical studies with a high risk of bias (i.e. low methodological quality) may produce inflated estimates of intervention effects (Landis et al., 2012; Collins and Tabak, 2014). Interestingly, the discrepancy in methodological quality between single and multilaboratory studies was larger in our preclinical comparison than in previous clinical comparisons. This could be explained by the fact that practices such as blinding and randomization are better established in clinical research, thus, even small single center clinical trials are more likely to adhere to them.

A second, somewhat less intuitive issue that may have contributed to larger effect sizes in single lab studies is the smaller sample sizes that may lead to skewed results. It has been suggested that, even in the absence of other biases, under-powered studies have a greater likelihood of effect inflation and generate more false positives than high-powered studies; a lower probability that any observed differences reach the minimum threshold for asserting the findings reflect a true effect; and have a greater likelihood of effect inflation (Button et al., 2013). Perhaps the low power of these single lab studies, combined with well-recognized issues of publication bias (Sena et al., 2010), contributed to the larger effect sizes we observed.

Completeness of reporting in the multilaboratory studies was also noted to be high across many domains. This is in stark contrast to previous preclinical systematic reviews of single lab studies by our group and others that have found significant deficiencies in reporting (Landis et al., 2012; Fergusson et al., 2019; Avey et al., 2016). Within our sample of multilaboratory studies, replicates, statistics, and blinding were overall transparently reported in the majority of studies. Items specific to multilaboratory designs, such as indicating the number of participating centers in the abstract and identifying as a multilaboratory study in the title were less frequent. One potential explanation for this finding is that guidelines and standards for multilaboratory preclinical studies are just emerging, and there have yet to be any reporting recommendations specific to a preclinical multilaboratory design.

The difference in observed methodological quality and high completeness of reporting in preclinical multilaboratory studies could be explained by the routine oversight and quality control that were employed by some of the multilaboratory studies included in our sample. Though not all multilaboratory studies reported routine oversight, we expect that this is inherent in collaborative studies between multiple independent research groups. As reported by several studies, the coordination of a successful preclinical multilaboratory study requires greater training, standardization of protocols, and study-level management when compared to a preclinical study within a single laboratory. Another barrier was the issue of obtaining adequate funding for a multilaboratory study. As a consequence of limited funding, we would speculate that these studies may have undergone more scrutiny and refinement by multiple investigators, funders, and other stakeholders. Indeed, comparison of single lab studies that had been conducted by authors of multilaboratory studies suggested differences in the conduct and outcomes of these studies (despite having the some of the same researchers involved in both). However, this post hoc analysis was qualitative with a limited sample; thus, future studies will need to explore these issues further.

Due to the greater methodological rigor and transparent reporting, the inferred routine oversight, and larger sample sizes, we speculate that preclinical multilaboratory studies may provide a more precise evaluation of the intervention’s effects than do single lab studies. As research groups globally consider adopting this approach, the biomedical community may benefit by emulating successful existing networks of multicenter studies in social psychology (https://psysciacc.org/), developmental psychology (https://manybabies.github.io), and special education research (https://edresearchaccelerator.org/). Moreover, identified barriers and enablers to these studies should be further explored from a variety of stakeholder perspectives (e.g. researchers, animal ethics committees, institutes, and funders) in order to maximize future chances of success.

Strengths and limitations

A strength of this systematic review is the in-depth synthesis of published preclinical multilaboratory studies that summarizes and assesses the state of this field of research, along with a quantitative comparison between single and multilaboratory studies. The application of rigorous inclusion criteria limited the eligible studies to interventional, controlled-comparison studies, which could omit valuable information that may have come from the excluded studies of non-controlled and/or observational designs, or studies focused on mechanistic insights. Another limitation is that our assessment of the risk of bias relies on complete reporting; reporting, however, can be influenced by space restrictions in some journals, temporal trends (e.g. better reporting in more recent studies), as well as accepted norms in certain fields of basic science. However, with the increasing prevalence of reporting checklists and standards in preclinical research (Percie du Sert et al., 2020), future assessments will be less susceptible to this information bias (Ramirez et al., 2020). We also note that our quantitative analysis included only 16 studies, and thus our results might be better regarded as a preliminary analysis that will require future confirmation when more multilaboratory studies have been conducted. We would note, however, that despite the diversity of included multilaboratory studies, overall trends were quite similar across these 16 studies (e.g. more complete reporting, lower risk of bias, and smaller effect size than comparable single laboratory studies).

An additional limitation is that we calculated the effect sizes of the comparable single lab studies using standardized mean differences. We acknowledge that using mean difference would provide a more readily interpretable comparison, however, the use of standardized mean difference allowed us to compare the same outcomes between studies irrespective of the unit of measurement reported. Another limitation is the restriction to a maximum of 10 studies for each multicenter comparison in order to maintain the feasibility of this study. However, we do not expect that this would influence the results or trends we observed.

Conclusion

This review demonstrates the potential value of multicentric study designs in preclinical research, an approach that has been richly rewarding in clinical research. Importantly, this review provides evidence that preclinical multilaboratory studies report smaller treatment effect sizes and appear to have greater methodological rigor than preclinical studies performed in a single laboratory. This suggests that the preclinical multilaboratory design may have a place in the preclinical research pipeline; indeed, this approach may be a valuable means to evaluate the potential of a promising intervention prior to its consideration in an early-phase clinical trial.

Appendix 1

Supporting information

Overviews of preclinical multicenter studies

  1. In a study by Reimer et al., 1985, three independent laboratories collaborated to develop models to test potential ischemic myocardium protection therapies, using two standardized, well-characterized canine models of myocardial infarction. Using the two different dog models (conscious model of coronary occlusion, and unconscious model of 3-hr ischemia in open-chest), the researchers tested the effects of verapamil and ibuprofen (therapies) on infarct size. The pooled results from all three centers demonstrated that neither drug limited infarct size in either model. It was later published that the participating laboratories discovered through statistical and hard evidence that a fourth participating lab initially involved in the study had generated fraudulent data, in the sense that data had been completely fabricated by a researcher at one of the centers (Bailey, 1991). The data from this lab was not included in the multicenter study paper. The detection of the fraudulent data would not have been possible if not for the design of a multicenter study. The fraud was detected by the large discrepancies in outcome data between the offending center and the other centers involved in the study.

  2. Crabbe et al., 1999 performed a large study across three laboratories. The main objective was to test the behavioural variability in mice of different genetic strains, sexes, and laboratory environments. The evaluation was done with identical methods and protocols across all three labs. The potentially clinically relevant portion of this study was an assessment of cocaine’s effect on behavior (i.e. locomotor activity). The study found that cocaine effects on locomotor activity had a strong relationship with genetic differences on the laboratory giving the tests but was negligible for sex differences and source of mice (i.e. shipped from a supplier or bred locally).

  3. Alam et al., 2009 conducted a three-phase severe traumatic injury protocol to model trauma-induced coagulopathy, acidosis, and hypothermia on Yorkshire swine across three experimental centers. Animals were treated with four different blood products: fresh whole blood (FWB), hetastarch, fresh frozen plasma/packed RBCs (FFP: PRBC), and FFP, to determine which, if any, were effective in reversing trauma-associated coagulopathy. Treatment with FFP and FFP: PRBC corrected the coagulopathy as effectively as FWB, whereas hetastarch worsened coagulopathy.

  4. Spoerke et al., 2009 tested whether lyophilized plasma (LP) is as safe and effective as fresh frozen plasma (FFP) for resuscitation after severe trauma. They used a swine model of severe injury across animal laboratories of two level 1 trauma centers, to test the lyophilized plasma for factor levels and clotting activity before lyophilization and after reconstitution. The swine model was developed and performed at one of the centers and was learned and performed at a second center. They found that LP decreased clotting factor activity and was equal to FFP in terms of efficacy.

  5. Jones et al., 2015 aimed to develop a multicenter, randomized controlled clinical-like infrastructure for preclinical evaluation of cardioprotective therapies using mice, rabbit and pig models. The researchers established the Consortium for preclinicAl assESsment of cARdioprotective therapies – called CAESAR - to test the effect of ischemic preconditioning (IPC) on infarct size following a myocardial infarction. IPC involves short episodes of blood restriction to the heart – which is an experimental technique for producing resistance to longer durations of ischemia. Six centers (two centers/animal model) tested the therapy in the three animal models with shared protocols, and found the results were similar across centers and that IPC significantly reduced infarct size in all three species.

  6. Llovera et al., 2015 performed a preclinical randomized controlled multicenter trial to test the potential of anti-CD49d antibodies as a treatment for stroke. These antibodies had shown promise as a form of therapy in individual laboratories by inhibiting the migration of leukocytes into the brain following induction of stroke. Six independent European research centers tested the antibody using two mouse models of stroke. The results demonstrated that the antibody significantly reduced leukocyte invasion and infarct size in the less severe model of stroke. In contrast, these beneficial effects were not noted in the more severe model of stroke.

  7. Maysami et al., 2016 conducted a cross-laboratory study in five centers (four experimental, one coordinating) to test an interleukin receptor antagonist as a drug therapy for stroke. The coordinating center developed and distributed the standard operating procedure to all centers. Stroke was induced both by permanent and transient occlusion in mice. Drug effects on stroke outcome were evaluated by several measures: lesion volume, edema, neurological deficit scoring and post-treatment mortality. The results across all centers supported the therapeutic potential of the cytokine receptor antagonist in experimental stroke.

  8. Six separate studies (2016-2020) that were coordinated by Operation Brain Trauma Therapy (OBTT) consortium (Kochanek et al., 2016). Three independent centers collaborated to test 6 different therapies for severe traumatic brain injury (TBI). The consortium was supported by the United States Army and had an overall approach of testing promising therapies in three-well established models of TBI in rats with a rigorous design. The end goal of the consortium was to test the 6 initial therapies in rats prior to considering further testing in a swine model of TBI. Based on the results, four of the six drugs preformed below or well below what was expected based on the previously published literature. It was reported that levetiracetam would advance to testing in the swine model, and that glibenclamide showed benefit only in the cortical contusion injury model.

  9. Gill et al., 2016 assessed the efficacy of combined anti-CD3 plus interleukin-1 blockade to reverse new-onset autoimmune diabetes in non-obese diabetic (NOD) mice. Their consortium was supported by the National Institutes of Health Immune Tolerance Network and the Juvenile Diabetes Research Foundation. Four academic centers shared models and operating procedures. They found that the combined antibody treatment did not show reversal of diabetes across all sites. They did, however, conclude that intercenter reproducibility is possible with the NOD mouse model of diabetes.

  10. Arroyo-Araujo et al., 2019 evaluated the potential of the metabotropic Glutamate Receptor 1 (mGluR1) antagonist JNJ16259685, as a treatment for autism spectrum disorder (ASD). Three centers used Shank2 knockout (KO) rats as a model for ASD, which mimics autistic-like hyperactivity and repetitive behaviour. They found that the results were reproducible across the three centers, and that KO rats treated with the mGluR1 antagonist demonstrated reduced hyperactivity and repetitive behaviour as compared to placebo treated KO rats.

  11. Kliewer et al., 2020 investigated whether β-arrestin2 signaling plays a role in opioid-induced respiratory depression. Three independent laboratories injected β-arrestin2 knockout (KO) mice and control wild-type mice with morphine and monitored the respiratory rate of both groups of mice. The authors found that the KO mice did develop respiratory depression across all three sites, thus, they suggested that β-arrestin2 signaling does not play a key role in opioid-induced respiratory depression.

Appendix 1—table 1
Statements of future recommendations.
Author, YearRecommendation statements
Reimer et al., 1985Nothing reported
Crabbe et al., 1999Relatively small genetic effects should first be replicated locally before drawing conclusions... genotypes should be tested in multiple labs and evaluated with multiple tests of a single behavioral domain
Alam et al., 2009Based upon the findings of the current study that demonstrated the impressive hemostatic properties of plasma, we have proceeded to successfully develop and test (in the same model) lyophilized [freeze dried plasma].
Spoerke et al., 2009The species-specific differences in factor activities will require ongoing investigation to ensure full safety and efficacy. Our future investigations will include a comprehensive evaluation of the effects of the lyophilization process on coagulation properties of the LP.
Jones et al., 2015other investigators can adopt the protocols [for measuring infarct size in mice, rabbits, and pigs in a manner that is rigorous, accurate, and reproducible] in their own laboratories.
Llovera et al., 2015future clinical trials testing immunotherapeutic drugs for stroke will need to ensure that the included study population feature a substantial neuroinflammatory reaction to the brain injury
Maysami et al., 2016interleukin 1 receptor antagonist should be evaluated in more extensive clinical stroke trials
Bramlett et al., 2016Although we cannot rule out the possibility that other doses or more prolonged treatment could show different effects, the lack of efficacy of EPO reduced enthusiasm for its further investigation in OBTT.
Browning et al., 2016need for OBTT to study LEV further. This includes studies of dose response, therapeutic window, mechanism, and testing in our large animal FPI model in micropigs… consider a randomized controlled trial examining early administration in patients
Dixon et al., 2016Our findings reduce enthusiasm for further investigation of this therapy in OBTT and suggest that if this strategy is to be pursued further, alternative CsA analogs with reduced toxicity should be used.
Gill et al., 2016pause in proceeding with clinical trials without further preclinical testing.
Mountney et al., 2016the current findings do not support the beneficial effects of simvastatin… it will not be further pursued by OBTT.
Shear et al., 2016The marginal benefits achieved with nicotinamide, however, which appeared sporadically across the TBI models, has reduced enthusiasm for further investigation by the OBTT Consortium.
Arroyo-Araujo et al., 2019Nothing reported
Jha et al., 2020Optimizing [GLY] treatment regimens (dose, duration, timing), surrogate markers for edema subtypes on MRI, pathway-specific biomarkers, and genetic risk stratification may facilitate precision medicine and patient selection for future clinical trials.
Kliewer et al., 2020Nothing reported
  1. Legend: FDP – Freeze-dried plasma; LP – Lyophilized plasma; EPO – Erythropietin; OBTT – Operation Brain Trauma Therapy; LEV – Levetiracetam; FPI – Fluid percussion brain injury; CsA – cyclosporin-A; cyclosporine; TBI – Traumatic Brain Injury; GLY - Glibenclamide.

Appendix 1—table 2
Risk of bias for other sources of bias.
  1. *

    financial disclosure, no statement of other conflicts provided.

Appendix 1—table 3
Frequency of reported preclinical multilaboratory checklist items.
Domain#Item Description% of studies that reported
Intro/ abstract1Identification as a multicenter/multilaboratory study in title38
2Abstract states number of participating centers50
Standards3Community based reporting guidelines listed13
4Names of each participating center listed100
5List roles of participating centers (central coordinating center, experimental site)88
6No changes, or if applicable major changes to study protocol after commencement are documented94
Replicates (biological vs. technical)7Results substantiated by repetition under a range of conditions at each site100
8Number of subjects per outcome100
9Number of measurements per subject for one experimental outcome stated75
10Number of subjects per lab81
Statistics11List of the total number of subjects used in each experimental group81
12List of all statistical tests used100
13Definition of the measure of central tendency100
14Definition of the measure of dispersion100
Randomization15Random group assignment reported100
16Description of the method of random group assignment31
Blinding17Experimenters blinded to group allocation during conduct of the experiment75
18Experimenters blinded to group allocation during result assessment75
Sample Size Estimation19Description of an a priori primary outcome94
20Sample size for each site computed during study design31
21Description of the method of sample size determination31
Inclusion and Exclusion Criteria22Total number of animals for the experiment reported88
23Description of the criteria used for the exclusion of any data or subjects50
24List losses and exclusions of animals at the end of experiment50
25All outcomes described, or description of any outcomes that were measured and not reported in the results section100
26Previous or pilot/preliminary studies performed and listed88
27Results were significant, or if not, null or negative outcomes included in the results100
Discussion28Limitations of the study are documented75
29Discrepancies in results across labs expected or absent, or if not, they discussed100
  1. Legend: Coloured cells indicate the frequency (%) of item reported over all included studies. Frequency (%) ranges: 0-37 = red; 38-76 = yellow; 77-100 = green.

Appendix 1—table 4
Preclinical single lab studies selection process for the comparison.

Reimer et al., 1985Spoerke et al., 2009Alam et al., 2009Llovera et al., 2015Maysami et al., 2016Gill et al., 2016Bramlett et al., 2016Browning et al., 2016Dixon, 2016Mountney et al., 2016Shear et al., 2016Arroyo-Araujo et al., 2019Jha et al., 2020
Records identified/
abstracts screened
71189615233391773119745282629
Full-texts assessed
for eligibility
29221814211157154830181210
Records considered eligible135561021 SR4891265
Records
used for comparison
105561021 SR4891065
Appendix 1—table 5
Multilaboratory reporting checklist with item domain and source(s).
Domain#Item DescriptionSource(s)
Intro/abstract1Identification as a multicenter/multilaboratory study in titleCONSORT
2Abstract states number of participating centersCONSORT
Standards3Community based reporting guidelines listedNIH
4Names of each participating center listedGCP E6(R2)
5List roles of participating centers (central coordinating center, experimental site)GCP E6(R2)
6No changes, or if applicable major changes to study protocol after commencement are documentedCONSORT
Replicates (biological vs. technical)7Results substantiated by repetition under a range of conditions at each siteNIH, CONSORT
8Number of subjects per outcomeNIH, CONSORT
9Number of measurements per subject for one experimental outcome statedNIH, CONSORT
10Number of subjects per labGCP E6(R2)
Statistics11List of the total number of subjects used in each experimental groupNIH, CONSORT
12List of all statistical tests usedNIH, CONSORT
13Definition of the measure of central tendencyNIH
14Definition of the measure of dispersionNIH
Randomization15Random group assignment reportedNIH, CONSORT
16Description of the method of random group assignmentNIH, CONSORT
Blinding17Experimenters blinded to group allocation during conduct of the experimentNIH, CONSORT
18Experimenters blinded to group allocation during result assessmentNIH, CONSORT
Sample Size Estimation19Description of an a priori primary outcomeCONSORT
20Sample size computed during study designNIH, CONSORT
21Description of the method of sample size determinationNIH, CONSORT
Inclusion and Exclusion Criteria22Total number of animals for the experiment reportedGCP E6(R2)
23Description of the criteria used for the exclusion of any data or subjectsNIH, CONSORT
24List losses and exclusions of animals at the end of experimentCONSORT
25All outcomes described, or description of any outcomes measured but not reported in resultsNIH, CONSORT
26Previous or pilot/preliminary studies performed and listedNIH
27Results were significant, or if not, null or negative outcomes included in the resultsNIH
Discussion28Limitations of the study are documentedCONSORT
29Discrepancies in results across labs expected or absent, or if not, they discussedCONSORT

Data availability

The protocol for the effect size comparison was developed a priori and posted on Open Science Framework (https://osf.io/awvs9/).Supplementary documents contains the search strategies, risk of bias assessments, reporting checklists, quality scores, effect sizes, effect size ratios, and standardized mean differences to generate the figures and tables.

The following previously published data sets were used
    1. Lalu M
    2. Hunniford V
    (2020) Open Science Framework
    ID awvs9. Study Protocol: Quantitative comparison between the effect sizes of preclinical multicenter studies and single center studies.

References

  1. Report
    1. Health Canada
    (2016)
    E6(R2) Good Clinial Practice: Integrated Addendum to ICH E6(R1) - Guidance for Industry
    US Food and Drug Administration.

Decision letter

  1. Carlos Isales
    Reviewing Editor; Augusta University, United States
  2. Mone Zaidi
    Senior Editor; Icahn School of Medicine at Mount Sinai, United States
  3. David Mellor
    Reviewer; Center for Open Science, United States
  4. Andrew SC Rice
    Reviewer; Imperial College London, United Kingdom

In the interests of transparency, eLife publishes the most substantive revision requests and the accompanying author responses.

Decision letter after peer review:

Thank you for submitting your article "A systematic assessment of preclinical multicenter studies and a comparison to single laboratory studies" for consideration by eLife. Your article has been reviewed by 3 peer reviewers, and the evaluation has been overseen by a Reviewing Editor and Mone Zaidi as the Senior Editor. The following individuals involved in the review of your submission have agreed to reveal their identity: David Mellor (Reviewer #1); Andrew SC Rice (Reviewer #3).

The reviewers have discussed their reviews with one another, and the Reviewing Editor has drafted this to help you prepare a revised submission.

Essential revisions:

1) Introduction: I believe that your audience reach would be expanded, and your intended audience would be even more interested in your work, by noting how this method of multi-lab collaborations is appropriate beyond preclinical research. I will not suggest changing your inclusion criteria for the study already conducted, but it would be worth noting how efforts in social psychology* and human development** have seen similar results as those you describe. Likewise, existing networks in psychology (https://psysciacc.org/), development biology (https://manybabies.github.io/), and special education research (https://edresearchaccelerator.org/) would be worth mentioning as models for emulation when discussing how these practices could be scaled to more communities within preclinical research (perhaps mention this in the Conclusion).

2) Line 123: Can you please define "interventional" and clarify your definition of "Preclinical" so as to make it clear to readers outside of your domain of focus why psychological or developmental biology was not included (as these do have human health implications). (Just to be clear, I am not being sarcastic or suggesting that these should have been included, I just know that these terms get blurry when going from the preclinical to the basic sciences).

3) I appreciate that the calculations for the effect size ratio and the difference of standardized mean difference were specified a priori. Even though they were straightforward calculations, there is room for divergence or selective reporting and it appears that those analyses were reported as pre-specified.

4) The sample size is rather limited. While I do not doubt that the authors invested a lot of work into finding multi-centre studies fulfilling their inclusion criteria, they ended up with a list of only 16 studies. Multi-centre studies are tedious to perform and more expensive, so it is not surprising that the authors could not find more. However, given an N=16 for a rather diverse collection of studies, spanning 35 years, different model species (mice, rats, dogs, pigs, and rabbits) and investigating rather different interventions, this might be better regarded as a preliminary analysis.

5) There is one question that cannot be answered but which is nevertheless rather important. Is the difference in effect size estimates (with the multi-lab studies presumably providing more accurate effect size estimates) due to the multi-lab setting itself or due to the fact that researchers willing to go the extra length of conducting a multi-lab study are stricter and more rigorous (and more aware) than the average researcher? If the latter is the case, then this would be a confounding factor and one could not conclude that the observed difference is due to the multi-lab approach itself.

6) As the authors noted themselves, sample sizes of single-lab and multi-lab differed substantially (median 19 vs. 111) and this difference in sample size might itself lead to more accurate effect size estimates (closer to the meta-analytic estimate). I am, therefore, missing an analysis, of whether this effect alone could explain the discrepancy. That is – would single-lab studies using the same number of animals be equally accurate as a multi-lab study?

7) I have some minor methodological issues regarding the evaluation of the risk of bias and specifically its interpretation as a measure for the quality of scientific rigor. This is more of a general critique of the use of 'risk of bias' in systematic reviews and is not specific to this study, but it nevertheless means that the results of this part of the study should be taken with a grain of salt and be interpreted with care. The risk of bias questionnaire is focusing on what is reported in the publication. As it is visible in table 3, even for the multi-lab studies-where risk of bias was considerably lower than for the single-lab studies-a substantial proportion of questions was answered with unclear-i.e., it was, for example, not reported whether allocation concealment was done or not. This could mean that it was not done or it can mean that it was done, but researchers didn't find it noteworthy to report it. Reporting practice slightly differs between fields, it differs between journals (due to space restriction, editorial guidelines, and also the rigor of the editors), and it very strongly changes over time – due to the current discussion about replicability editors and reviewers are now asking for more details than they did a decade ago. So, any analysis of the risk of bias using those criteria should consider journal and year of publication as co-variates. In the present case the authors mentioned, that they tried to match single-lab studies with multi-lab studies also according to age, though a quick look at publication years suggests that this was not always achieved.

8) There seem to be some inconsistencies between Table 3 and Table S11. For example, in the column "Blinding of outcome assessment" in Table S3 there are 4 studies with "unknown" (Crabbe, Alam, Spoerke, Gill), while in Table S11 in the column "Blinding of outcome assessment" there are 4 study scoring 0, but here Arroyo-Araujo scores also 0, while Gill scores 1. How does this fit together?

9) Methods: maybe I have missed that: have you described, whether for the reporting scores you checked only the main article or also the electronic supplementary (supporting information)?

10) Language limits: In the methods description you wrote "No language limits were imposed" (line 147). In the Results section, I could, however, not find any information, on if any non-English papers were found and whether they were included in the analysis. There is also no mention of what you would have done if you encountered a paper in a language you were not capable of. When would this have been an exclusion criterion? In any case, in the methods section where you wrote "no language limits were imposed", please add the information that all search terms were in English. (Or were they also translated into other languages?)

11) Line 166: Primary and secondary research outcomes. According to my own experience, one sees many papers, where the authors report outcomes of several analyses and do not clearly define what the primary and the secondary outcomes are. In fact, I only rarely read that an author writes "this is our primary outcome" and "this was a secondary outcome". Did you encounter such cases and which criteria did you use to decide what counted as a primary and secondary outcome?

12) Line 196: Rapid review method. Please describe in one or two sentences what that is.

13) Line 259: were the effect sizes just pooled or were they weighted by study size or variance?

14) Line 267: I think giving a ratio (without multiplication by 100) might be better

15) Line 345: potentially industry-related influences are considered a risk of bias. Is there actually any study clearly showing that papers with authors from industry are more biased than papers from authors from academia? I know that this is an item on the SYRCLE list of bias tools, but is this prejudice against industry justified – i.e., based on evidence? Just recently there have been several cases of spectacular fraud (data fabrication) by authors in academia (behavioural ecology). Specifically for early career researchers in academia publication pressure for securing tenure or a faculty position is often described as extremely high, creating incentives for "beautifying" results which are then easier to publish. If you are, however, aware of any publication or data showing that bias in industry is more of an issue than in academia then it would be good to cite it here.

16) Line 388: As mentioned in the public review: I would be very careful with equating low reporting scores with "quality of research"

17) Analysis (Meta-analysis, Figure S12): It would be really interesting to add publication year as a covariate in the models. I would assume that estimates get closer to zero the younger the publication.

18) The list of references seems incomplete or incorrect with errors in text citation numbers. There are far more citations in the text (up to 82, whereas only 17 are on the list).

19) It would be good to know more about the training/qualification/validation criteria for the interviewers.

20) page 3 the sentence starting "we found that the…..rigorous manner" did not quite make sense to me.

21) I was curious as to why the group considered that testing of efficacy was the major use of such studies (rather than testing a new mechanism or fundamental finding) and that evaluation of a new method, model, or outcome measure was not even mentioned. That would not have been my view had I been interviewed. It would be nice to see a critical discussion about this.

22) I wonder if a more forensic discussion of what the authors see as the probable barriers to funders, peer scientists, and other stakeholders would be informative. Perhaps even a more extensive discussion of potential solutions may have been informative.

23) The main area of disagreement between interviewees was the issue of harmonisation of protocols- a strong contrast to the clinical multi-centre practice where harmonisation is the norm. This interesting response could perhaps have been discussed more?

Ebersole, C. R., Atherton, O. E., Belanger, A. L., Skulborstad, H. M., Allen, J. M., Banks, J. B., Baranski, E., Bernstein, M. J., Bonfiglio, D. B. V., Boucher, L., Brown, E. R., Budiman, N. I., Cairo, A. H., Capaldi, C. A., Chartier, C. R., Chung, J. M., Cicero, D. C., Coleman, J. A., Conway, J. G., … Nosek, B. A. (2016). Many Labs 3: Evaluating participant pool quality across the academic semester via replication. Journal of Experimental Social Psychology, 67, 68-82. https://doi.org/10.1016/j.jesp.2015.10.012

Klein, R. A., Ratliff, K. A., Vianello, M., Adams, R. B., Bahník, Š., Bernstein, M. J., Bocian, K., Brandt, M. J., Brooks, B., Brumbaugh, C. C., Cemalcilar, Z., Chandler, J., Cheong, W., Davis, W. E., Devos, T., Eisner, M., Frankowska, N., Furrow, D., Galliani, E. M., … Nosek, B. A. (2014). Investigating Variation in Replicability: A "Many Labs" Replication Project. Social Psychology, 45(3), 142-152. https://doi.org/10.1027/1864-9335/a000178

Klein, R. A., Vianello, M., Hasselman, F., Adams, B. G., Adams, R. B., Alper, S., Aveyard, M., Axt, J. R., Babalola, M. T., Bahník, Š., Batra, R., Berkics, M., Bernstein, M. J., Berry, D. R., Bialobrzeska, O., Binan, E. D., Bocian, K., Brandt, M. J., Busching, R., … Nosek, B. A. (2018). Many Labs 2: Investigating Variation in Replicability Across Samples and Settings. Advances in Methods and Practices in Psychological Science, 1(4), 443-490. https://doi.org/10.1177/2515245918810225

Byers-Heinlein, Tsui, A. S. M., K., Bergmann, C., …, Wermelinger, S. (2021). A multi-lab study of bilingual infants: Exploring the preference for infant-directed speech. Advances in Methods and Practices in Psychological Science. PsyArXiv PrePrint

Byers-Heinlein, K., Tsui, R. K. Y., van Renswoude, D., Black, A. K., Barr, R., Brown, A., … Singh, L. (2020). The development of gaze following in monolingual and bilingual infants: A multi-lab study Infancy, Advance online publication. PsyArXiv Preprint

ManyBabies Consortium (2020). Quantifying sources of variability in infancy research using infant-directed speech preference. Advances in Methods and Practices in Psychological Science, 3, 24-52. PsyArXiv Preprint

Frank, M. C., Bergelson, E., Bergmann, C., Cristia, A., Floccia, C., Gervain, J., Hamlin, J. K., Hannon, E. E., Kline, M., Levelt, C., Lew-Williams, C., Nazzi, T., Panneton, R., Rabagliati, H., Soderstrom, M., Sullivan, J., Waxman, S., Yurovsky, D. (2017). A collaborative approach to infant research: Promoting reproducibility, best practices, and theory-building. Infancy, 22, 421-435. PsyArXiv Preprint

Reviewer #1:

This paper provides two important benefits to the field. First is the clear data showing the risk of bias assessments and effect size differences between single and multi-lab studies. This provides more clear evidence about the problematic process of single study science. Second, and I believe more important, is the qualitative information provided through the interviews with participating labs that describe the barriers and recommendations from participating labs (eg timelines, pilot periods, budget limitations set by the least well-resourced lab, ethics approval processes, centralized data processing, and even interpersonal lab coordination suggestions). Summarizing these qualitative findings in specific recommendations or a set of proposed guidelines would expand the relevance of this paper.

Below are my recommendations for improvement, which are not substantial but will hopefully help the authors widen their audience and convince their peers that these methods are not limited to their own community.

Introduction: I believe that your audience reach would be expanded, and your intended audience would be even more interested in your work, by noting how this method of multi-lab collaborations is appropriate beyond preclinical research. I will not suggest changing your inclusion criteria for the study already conducted, but it would be worth noting how efforts in social psychology and human development have seen similar results as those you describe. Likewise, existing networks in psychology (https://psysciacc.org/), development biology (https://manybabies.github.io/), and special education research (https://edresearchaccelerator.org/) would be worth mentioning as models for emulation when discussing how these practices could be scaled to more communities within preclinical research (perhaps mention this in the Conclusion).

Line 123: Can you please define "interventional" and clarify your definition of "Preclinical" so as to make it clear to readers outside of your domain of focus why psychological or developmental biology was not included (as these do have human health implications). (Just to be clear, I am not being sarcastic or suggesting that these should have been included, I just know that these terms get blurry when going from the preclinical to the basic sciences).

I appreciate that the calculations for the effect size ratio and the difference of standardized mean difference were specified a priori. Even though they were straightforward calculations, there is room for divergence or selective reporting and it appears that those analyses were reported as pre-specified.

Reviewer #2:

This paper reports results of a systematic review comparing single-lab with multi-lab studies with regard to reported effect size and risk of bias. The main outcome was that risk of bias was lower in multi-lab studies and so was the reported effect size. The authors argue, that the higher effect sizes observed in the single lab studies are presumably over-estimates and that, hence, the multi-lab studies provide more accurate effect size estimates. They, thus, conclude that this meta-analysis demonstrates the potential value of multi-centre studies in pre-clinical research. While I do agree that multi-centre studies are valuable, I have certain reservations as to what extent this is actually shown in the current study. Here are my concerns.

1) The sample size is rather limited. While I do not doubt that the authors invested a lot of work into finding multi-centre studies fulfilling their inclusion criteria, they ended up with a list of only 16 studies. Multi-centre studies are tedious to perform and more expensive, so it is not surprising that the authors could not find more. However, given an N=16 for a rather diverse collection of studies, spanning 35 years, different model species (mice, rats, dogs, pigs, and rabbits) and investigating rather different interventions, this might be better regarded as a preliminary analysis.

2) There is one question that cannot be answered but which is nevertheless rather important. Is the difference in effect size estimates (with the multi-lab studies presumably providing more accurate effect size estimates) due to the multi-lab setting itself or due to the fact that researchers willing to go the extra length of conducting a multi-lab study are stricter and more rigorous (and more aware) than the average researcher? If the latter is the case, then this would be a confounding factor and one could not conclude that the observed difference is due to the multi-lab approach itself.

3) As the authors noted themselves, sample sizes of single-lab and multi-lab differed substantially (median 19 vs. 111) and this difference in sample size might itself lead to more accurate effect size estimates (closer to the meta-analytic estimate). I am, therefore, missing an analysis, of whether this effect alone could explain the discrepancy. That is-would single-lab studies using the same number of animals be equally accurate as a multi-lab study?

4) I have some minor methodological issues regarding the evaluation of the risk of bias and specifically its interpretation as a measure for the quality of scientific rigor. This is more of a general critique of the use of 'risk of bias' in systematic reviews and is not specific to this study, but it nevertheless means that the results of this part of the study should be taken with a grain of salt and be interpreted with care. The risk of bias questionnaire is focusing on what is reported in the publication. As it is visible in table 3, even for the multi-lab studies – where the risk of bias was considerably lower than for the single-lab studies-a substantial proportion of questions was answered with unclear – i.e., it was, for example, not reported whether allocation concealment was done or not. This could mean that it was not done or it can mean that it was done, but researchers didn't find it noteworthy to report it. Reporting practice slightly differs between fields, it differs between journals (due to space restriction, editorial guidelines, and also the rigor of the editors), and it very strongly changes over time – due to the current discussion about replicability editors and reviewers are now asking for more details than they did a decade ago. So, any analysis of the risk of bias using those criteria should consider journal and year of publication as co-variates. In the present case the authors mentioned, that they tried to match single-lab studies with multi-lab studies also according to age, though a quick look at publication years suggests that this was not always achieved.

Overall, I think this study provides evidence that multi-centric preclinical studies do report effect size estimates that might be more trustworthy than those provided by single-lab studies. I can therefore fully agree with the authors' conclusion about the value of such studies. Yet, why exactly multi-center studies fare better (whether it is because of the larger sample sizes, the different mindset of the experimenters, or the necessity to coordinate protocols), remains an open question.

Reviewer #3:

This is a well-written and clear manuscript covering an important and emerging area, albeit one that has not yet significantly penetrated into scientific practice. The authors were attempting to ascertain professional attitudes to multi-centre studies in pre-clinical biomedical research by using a semi-structured interview method. I am not an expert in the methods used and defer to expert reviewers in this regard; my expertise is in multi-centre animal studies.

A potential limitation is that only 16 participants were included in the interviews, although this is a sample size justified by reference to norms in the literature. Furthermore, in the results, the authors suggest that data saturation had been reached by the 13th interview, so perhaps this is sufficient. Ten out of 16 interviewees were US-based, the remainder European. A further potential bias may be that the interviewees had all participated in pre-clinical multicentre research, so were perhaps likely to be enthusiasts of the approach.

I was curious as to why the group considered that testing of efficacy was the major use of such studies (rather than testing a new mechanism or fundamental finding) and that evaluation of a new method, model, or outcome measure was not even mentioned. That would not have been my view had I been interviewed. It would be nice to see a critical discussion about this.

I wonder if a more forensic discussion of what the authors see as the probable barriers to funders, peer scientists, and other stakeholders would be informative. Perhaps even a more extensive discussion of potential solutions may have been informative.

The main area of disagreement between interviewees was the issue of harmonisation of protocols – a strong contrast to the clinical multi-centre practice where harmonisation is the norm. This interesting response could perhaps have been discussed more?

[Editors' note: further revisions were suggested prior to acceptance, as described below.]

Thank you for resubmitting your work entitled "A systematic assessment of preclinical multicenter studies and a comparison to single-laboratory studies" for further consideration by eLife. Your revised article has been evaluated by Mone Zaidi (Senior Editor) and a Reviewing Editor.

The manuscript has been improved but there are some remaining issues that need to be addressed, as outlined below:

Reviewer #1 (Recommendations for the authors):

The authors have sufficiently addressed the comments I made in the first submission.

However, one of their additions in response to another reviewer's comments may not be sufficient. The question is "Is the difference in effect size estimates (with the multi-lab studies presumably providing more accurate effect size estimates) due to the multi-lab setting itself or due to the fact that researchers are willing to go the extra length of conducting a multi-lab study are stricter and more rigorous (and more aware) than the average researcher?" I agree that the cause and effect cannot be addressed by this review and that only an experimental manipulation could start to truly answer that question (which would be a very tough experiment). However, the authors' response is also a bit limited and does add some additional questions from me. They state: "For ten multilaboratory studies, researchers had authored at least one of the matched single lab studies." I am now curious as to whether or not those ~10 single lab studies were in some way different than the ~90 other single lab studies (which would suggest that it's the person instead of the process that makes the difference). HOWEVER- I do not suggest that the authors go down that rabbit hole. No matter what is found from such digging, the root question ("is it the multi-lab process or the better scientist that makes the better studies?") will not be well addressed through this process simply because it will be an exercise in chasing smaller and smaller sub-samples with too much noise to make any reasonable conclusion. Instead, I have to disagree with the authors' first response to this comment and rather just recommend that they note these two possible explanations and state that this observational study cannot determine if it is the method or the authors that explain the differences reported.

All other changes and comments seem appropriate to me.

Reviewer #2 (Recommendations for the authors):

Overall the authors answered the questions coming up during the first review and changed the text accordingly.

There is, however, one point, where I would love to see a bit more. This regards the rather central question of whether multi-lab (ML) and single-lab (SL) differ because of the procedure or because they were done by a different 'population' of authors or with a different objective in mind.

The authors responded:

"We found that for the majority of the multilaboratory studies (i.e. ten), researchers had previously authored single lab studies on the same topic. " and then " This has now been addressed in the manuscript. Results: "For ten multilaboratory studies, researchers had authored at least one of the matched single lab studies." "

I would ask the authors, not only to mention in the results that for 10 ML studies, but researchers had also authored SL studies but also to describe how those 10 pairs compared. I don't advocate a statistical analysis, however, a descriptive summary (in how many of those 10 cases were the ML closer to the meta-analytic outcome than the SL?) and maybe these 10 SL studies could also be highlighted in figure 3 (if they were included there, though I presume they were).

https://doi.org/10.7554/eLife.76300.sa1

Author response

Essential revisions:

1) Introduction: I believe that your audience reach would be expanded, and your intended audience would be even more interested in your work, by noting how this method of multi-lab collaborations is appropriate beyond preclinical research. I will not suggest changing your inclusion criteria for the study already conducted, but it would be worth noting how efforts in social psychology* and human development** have seen similar results as those you describe. Likewise, existing networks in psychology (https://psysciacc.org/), development biology (https://manybabies.github.io/), and special education research (https://edresearchaccelerator.org/) would be worth mentioning as models for emulation when discussing how these practices could be scaled to more communities within preclinical research (perhaps mention this in the Conclusion).

These are excellent points we have now addressed in our introduction:

“…This approach has been adopted in other fields such social and developmental psychology (12, 13).”

In addition, we have mentioned the influential networks in our Discussion. We hope this will allow interested readers to seek out additional information easily.

“…. As research groups globally consider adopting this approach, the biomedical community may benefit by emulating successful existing networks of multicenter studies in social psychology (https://psysciacc.org/), developmental psychology (https://manybabies.github.io) and special education research (https://edresearchaccelerator.org/).”

2) Line 123: Can you please define "interventional" and clarify your definition of "Preclinical" so as to make it clear to readers outside of your domain of focus why psychological or developmental biology was not included (as these do have human health implications). (Just to be clear, I am not being sarcastic or suggesting that these should have been included, I just know that these terms get blurry when going from the preclinical to the basic sciences).

We agree these terms have various meanings depending on field of study. They are often a source of debate even with our closest collaborators as there are no consensus definitions. We have now clarified our intentions with these terms in the first paragraph of the methods:

Preclinical multilaboratory eligibility criteria

Population – The population of interest was preclinical, interventional, multilaboratory, controlled comparison studies. Preclinical was defined as research conducted using nonhuman models that involves the evaluation of potential therapeutic interventions of relevance to human health…

Intervention, comparators, outcomes – Interventions were restricted to agents with potential effects when considering human health.

3) I appreciate that the calculations for the effect size ratio and the difference of standardized mean difference were specified a priori. Even though they were straightforward calculations, there is room for divergence or selective reporting and it appears that those analyses were reported as pre-specified.

Thank-you for providing this supportive comment.

4) The sample size is rather limited. While I do not doubt that the authors invested a lot of work into finding multi-centre studies fulfilling their inclusion criteria, they ended up with a list of only 16 studies. Multi-centre studies are tedious to perform and more expensive, so it is not surprising that the authors could not find more. However, given an N=16 for a rather diverse collection of studies, spanning 35 years, different model species (mice, rats, dogs, pigs, and rabbits) and investigating rather different interventions, this might be better regarded as a preliminary analysis.

We would point out that, although the publication dates of included studies spanned 35 years, the majority have been published since 2015. In addition, despite the diversity of studies noted by reviewers, the overall trends are similar across studies (more complete reporting, lower risk of bias, and much smaller effect sizes than those seen in single-laboratory studies). Finally, we would note that our comparative approach emulates similar landmark clinical meta-research studies; the first highly cited landmark study on this issue in clinical research investigated only five topics (Ref #9, Bellomo 2009). Nonetheless, we agree with the reviewers that we have much to learn still and that our study is an important starting point. In our discussion we have now explicitly stated this:

“Strengths and limitations

… In addition, our quantitative analysis included only sixteen studies, and thus our results might be better regarded as a preliminary analysis that will require future confirmation when more multilaboratory studies have been conducted. We would note, however, that despite the diversity of included multilaboratory studies, overall trends were quite similar across these sixteen studies (e.g. more complete reporting, lower risk of bias, and smaller effect size than comparable single-laboratory studies).”

5) There is one question that cannot be answered but which is nevertheless rather important. Is the difference in effect size estimates (with the multi-lab studies presumably providing more accurate effect size estimates) due to the multi-lab setting itself or due to the fact that researchers willing to go the extra length of conducting a multi-lab study are stricter and more rigorous (and more aware) than the average researcher? If the latter is the case, then this would be a confounding factor and one could not conclude that the observed difference is due to the multi-lab approach itself.

In order to address this interesting question raised by the reviewers we compared authorship of the multilaboratory studies to matched single lab studies. We found that for the majority of the multilaboratory studies (i.e. ten), researchers had previously authored single lab studies on the same topic. This suggests that the multilaboratory approach itself is perhaps more rigorous.

Of interest, we would speculate that may in part due to the shared mental models that may develop in the multilaboratory approach. Of note, this is actually the topic of an ongoing funded study by our group (published protocol: DOI: 10.1371/journal.pone.0273077).

This has now been addressed in the manuscript.

Results:

“For ten multilaboratory studies, researchers had authored at least one of the matched single lab studies.”

6) As the authors noted themselves, sample sizes of single-lab and multi-lab differed substantially (median 19 vs. 111) and this difference in sample size might itself lead to more accurate effect size estimates (closer to the meta-analytic estimate). I am, therefore, missing an analysis, of whether this effect alone could explain the discrepancy. That is – would single-lab studies using the same number of animals be equally accurate as a multi-lab study?

We agree that larger sample size would lead to a more accurate effect size estimate, with smaller confidence intervals. However, as shown in Figure S12, the majority of the multi-laboratory studies effect sizes fall outside the upper limits of the 95% confidence interval of the overall single-lab studies effect size. Simply increasing the sample size would only increase precision of the estimates, but we would still anticipate the effects would fall into the confidence interval 95% of the time.

This indicates that the true value of the overall single-lab effect size does not overlap with the true effect size of multi-laboratory studies in a majority of cases. We have now mentioned this issue in the Results:

“…A scatterplot of the study effect sizes for each comparison is presented in Figure 3; and the forest plots of each of the 14 comparisons can be found in the supplemental information (S12 Figure). Of note, 8 of the of the 14 multilaboraotry studies had 95% confidence intervals that fell outside of the pooled single-laboratory 95% confidence intervals.”

7) I have some minor methodological issues regarding the evaluation of the risk of bias and specifically its interpretation as a measure for the quality of scientific rigor. This is more of a general critique of the use of 'risk of bias' in systematic reviews and is not specific to this study, but it nevertheless means that the results of this part of the study should be taken with a grain of salt and be interpreted with care. The risk of bias questionnaire is focusing on what is reported in the publication. As it is visible in table 3, even for the multi-lab studies-where risk of bias was considerably lower than for the single-lab studies-a substantial proportion of questions was answered with unclear-i.e. it was, for example, not reported whether allocation concealment was done or not. This could mean that it was not done or it can mean that it was done, but researchers didn't find it noteworthy to report it. Reporting practice slightly differs between fields, it differs between journals (due to space restriction, editorial guidelines, and also the rigor of the editors), and it very strongly changes over time – due to the current discussion about replicability editors and reviewers are now asking for more details than they did a decade ago. So, any analysis of the risk of bias using those criteria should consider journal and year of publication as co-variates. In the present case the authors mentioned, that they tried to match single-lab studies with multi-lab studies also according to age, though a quick look at publication years suggests that this was not always achieved.

This is a valid point raised by the reviewers. We have now acknowledged this in the Discussion:

“…Another limitation is that our assessment of risk of bias relies on complete reporting; reporting, however, can be influenced by space restrictions in some journals, temporal trends (e.g. better reporting in more recent studies), as well as accepted norms in certain fields of basic science. However, with the increasing prevalence of reporting checklists and standards in preclinical research, (62) future assessments will be less susceptible to this information bias (63).”

8) There seem to be some inconsistencies between Table 3 and Table S11. For example, in the column "Blinding of outcome assessment" in Table S3 there are 4 studies with "unknown" (Crabbe, Alam, Spoerke, Gill), while in Table S11 in the column "Blinding of outcome assessment" there are 4 study scoring 0, but here Arroyo-Araujo scores also 0, while Gill scores 1. How does this fit together?

Thank you for pointing this out – the inconsistencies were noted and have been corrected. Studies Gill and Arroyo-Araujo both blinded the outcome assessment, thus, in Table 3 the “unknown” was changed to “low” for Gill, 2016 under "Blinding of outcome assessment"; and in Table S10 the “0” was changed to “1” for Arroyo-Araujo, 2019 under "Blinding of outcome assessment". Additionally, the Results section has been adjusted accordingly – changed from “Twelve studies” to “Thirteen studies”.

9) Methods: maybe I have missed that: have you described, whether for the reporting scores you checked only the main article or also the electronic supplementary (supporting information)?

Indeed, we did consult the supporting information in addition to the main article for evaluating the reporting scores. This has now been clarified in the methods:

“For both assessments, the main articles along with the supporting information (when provided) were consulted.”

10) Language limits: In the methods description you wrote "No language limits were imposed" (line 147). In the Results section, I could, however, not find any information, on if any non-English papers were found and whether they were included in the analysis. There is also no mention of what you would have done if you encountered a paper in a language you were not capable of. When would this have been an exclusion criterion? In any case, in the methods section where you wrote "no language limits were imposed", please add the information that all search terms were in English. (Or were they also translated into other languages?)

We did not impose any language limits in the search and no non-English articles were found. For other meta-research projects we have typically had the article translated by members in our research institute familiar with the language.

We have added the following to clarify in the Results:

“There were no non-English articles identified in the search.”

11) Line 166: Primary and secondary research outcomes. According to my own experience, one sees many papers, where the authors report outcomes of several analyses and do not clearly define what the primary and the secondary outcomes are. In fact, I only rarely read that an author writes "this is our primary outcome" and "this was a secondary outcome". Did you encounter such cases and which criteria did you use to decide what counted as a primary and secondary outcome?

This is an important point and reflects differences in approach and language used by lab researchers (versus clinical trialists, for instance). Thus, we have now further clarified in the Methods:

“Qualitative data included… all study outcomes (primary, secondary, or undefined) …” and “Quantitative data included… sample sizes for the outcome used in the meta-analysis and for the control group.”

The heading in Table 2 was changed from “Primary Outcome” to “Study Outcomes”.

12) Line 196: Rapid review method. Please describe in one or two sentences what that is.

Thank you for this suggestion. We added a more detailed description to the Methods:

“…, which consisted of the search of a single database, and by having a single reviewer screen, extract, and appraise studies while an additional reviewer auditing all information.”

13) Line 259: were the effect sizes just pooled or were they weighted by study size or variance?

Pooled effect sizes (i.e. for single lab studies) were weighted (inverse variance).

For the effect size ratio calculation, there was no weighting of the two data points used (i.e. multilab effect size, pooled single lab effect size). We recognized a priori the potential drawbacks of this, and this is why several measures to compare effect sizes of multilaboratory vs. single lab studies were prespecified and reported.

14) Line 267: I think giving a ratio (without multiplication by 100) might be better

Point taken. We have modified the effect size ratio calculation to be a simple ratio without multiplying by 100%. The has been adjusted in the methods, results, and supporting information Table S11.

15) Line 345: potentially industry-related influences are considered a risk of bias. Is there actually any study clearly showing that papers with authors from industry are more biased than papers from authors from academia? I know that this is an item on the SYRCLE list of bias tools, but is this prejudice against industry justified – i.e., based on evidence? Just recently there have been several cases of spectacular fraud (data fabrication) by authors in academia (behavioural ecology). Specifically for early career researchers in academia publication pressure for securing tenure or a faculty position is often described as extremely high, creating incentives for "beautifying" results which are then easier to publish. If you are, however, aware of any publication or data showing that bias in industry is more of an issue than in academia then it would be good to cite it here.

This is an important point. Dr. Lisa Bero and colleagues have investigated this issue in several studies and demonstrated that the relationship is complicated. For studies investigating statins on atherosclerosis and bone outcomes they found that non-industry studies were more likely to demonstrate efficacy than industry sponsored studies (i.e. larger effect size in non-industry studies; PMID 25880564 and 24465178). However, in animal studies assessing the effect of atrazine exposure, industry sponsored studies were less likely to demonstrate harm than non-industry sponsored studies (i.e. smaller effect size in non-industry studies; PMID 26694022). In our group’s work (not-published yet) we found that industry sponsored animal studies of hydroxyethyl starch intravenous fluids were more likely to demonstrate efficacy than non-industry sponsored studies (i.e. smaller effect size in non-industry studies). This is notable since these (very expensive) fluids were subsequently pulled from markets with a black-box warning from the FDA.

These data demonstrate that there is no straightforward/easy approach to understanding the relationship between industry/non-industry sponsorship and risk of bias in preclinical studies.

We agree that perhaps the SYRCLE risk of bias tool should reevaluate this issue in the future and we have brought it to their attention through an email communication with Dr. Kimberly Wever, who is a member of their leadership. Ultimately, this remains a question that needs to be investigated further and addressed by future iterations of the SYRCLE risk of bias tool.

16) Line 388: As mentioned in the public review: I would be very careful with equating low reporting scores with "quality of research"

We agree and have adjusted our terminology throughout (i.e. “completeness of reporting”).

17) Analysis (Meta-analysis, Figure S12): It would be really interesting to add publication year as a covariate in the models. I would assume that estimates get closer to zero the younger the publication.

In order to address this question we have explored the relationship between absolute effect size vs. year of publication (all single lab studies plotted in Author response image 1). There is no clear relationship between the two variables (r2 = 0.002).

Author response image 1

18) The list of references seems incomplete or incorrect with errors in text citation numbers. There are far more citations in the text (up to 82, whereas only 17 are on the list).

Thanking for pointing this out. There was an error in the continuation of the references/citations for the interview study that was appended. This has now been corrected.

19) It would be good to know more about the training/qualification/validation criteria for the interviewers.

This is an important issue in qualitative research and reflects on reflexivity. As such, it is a mandatory aspect of the COREQ reporting guideline we used (found in the appendix for that paper).

20) Page 3 the sentence starting "we found that the…..rigorous manner" did not quite make sense to me.

Thank you for pointing this out in the appended interview study. We have adjusted the sentence to, “We found that the multicenter studies undertaken to date have been conducted using more rigorous methodology and quality control”.

21) I was curious as to why the group considered that testing of efficacy was the major use of such studies (rather than testing a new mechanism or fundamental finding) and that evaluation of a new method, model, or outcome measure was not even mentioned. That would not have been my view had I been interviewed. It would be nice to see a critical discussion about this.

Indeed, we agree that multilaboratory studies could be used for other purposes (e.g. mechanistic/fundamental). However, the majority of studies using this method have been interventional/therapeutic. We have now discussed this in the Discussion:

Discussion:

“…The application of rigorous inclusion criteria limited the eligible studies to interventional, controlled-comparison studies, which could omit valuable information that may have come from the excluded studies of non-controlled and/or observational designs, or studies focused on mechanistic insights.”

22) I wonder if a more forensic discussion of what the authors see as the probable barriers to funders, peer scientists, and other stakeholders would be informative. Perhaps even a more extensive discussion of potential solutions may have been informative.

As we had only interviewed the scientists involved, and not other stakeholders, we are hesitant to speculate on solutions from their viewpoints. Although we are hesitant to further lengthen our discussion (which we feel is already quite long), we have now included a statement that further studies will need to investigate this important issue. We believe a stakeholder response should be:

Discussion:

“…Moreover, identified barriers and enablers to these studies should be further explored from a variety of stakeholder perspectives (e.g. researchers, animal ethics committees, institutes and funders) in order to maximize future chances of success.”

23) The main area of disagreement between interviewees was the issue of harmonisation of protocols- a strong contrast to the clinical multi-centre practice where harmonisation is the norm. This interesting response could perhaps have been discussed more?

This is an excellent point and we have now elaborated on this issue in the Results:

“If the protocol was to be harmonized, then it had to be adapted to fit each lab’s budget accordingly (i.e. the lab with the smallest budget set the spending limit (19)). Alternatively, labs developed a general protocol but adapted it to fit their own respective budget with what resources they had. Of note, recent work has suggested that harmonization reduces between-lab variability, however, systematic heterogenization did not reduce variability further (52); this may suggest that, even in fully harmonized protocols, enough uncontrolled heterogeneity exists that further purposeful heterogenization has little effect.”

[Editors' note: further revisions were suggested prior to acceptance, as described below.]

Reviewer #2 (Recommendations for the authors):

Overall the authors answered the questions coming up during the first review and changed the text accordingly.

There is, however, one point, where I would love to see a bit more. This regards the rather central question of whether multi-lab (ML) and single-lab (SL) differ because of the procedure or because they were done by a different 'population' of authors or with a different objective in mind.

The authors responded:

"We found that for the majority of the multilaboratory studies (i.e. ten), researchers had previously authored single lab studies on the same topic. " and then " This has now been addressed in the manuscript. Results: "For ten multilaboratory studies, researchers had authored at least one of the matched single lab studies." "

I would ask the authors, not only to mention in the results that for 10 ML studies, but researchers had also authored SL studies but also to describe how those 10 pairs compared. I don't advocate a statistical analysis, however, a descriptive summary (in how many of those 10 cases were the ML closer to the meta-analytic outcome than the SL?) and maybe these 10 SL studies could also be highlighted in figure 3 (if they were included there, though I presume they were).

The following text has been added:

Methods:

“Peer reviewers requested additional analysis to qualitatively assess identified single-laboratory studies that were conducted by the same authors of matched multilaboratory studies.”

Results:

“The ESR was greater than 1 (i.e. the single lab studies produced a larger summary effect size) in 10 of the 14 comparisons. The median effect size ratio between multilaboratory and single lab studies across all 14 comparisons was 4.18 (range: 0.57 to 17.14). The ESRs for each comparison along with the mean effect sizes and ratio of the mean effect sizes is found in the supplemental information (Appendix 11 – table 7).

For 10 multilaboratory studies, researchers also had authored 11 matched single lab studies. Median effect size ratio of this smaller matched cohort was 2.50 (mean 4.10, range 0.35-17.63). Median quality assessment score for the 10 multilaboratory studies was 3 (range 1-5); median quality score of the 11 single-laboratory studies matched by authors was 1 (range 1-4).”

Discussion:

“The difference in observed methodological quality and high completeness of reporting in preclinical multilaboratory studies could be explained by the routine oversight and quality control that were employed by some of the multilaboratory studies included in our sample. Though not all multilaboratory studies reported routine oversight, we expect that this is inherent of collaborative studies between multiple independent research groups. As reported by several studies, the coordination of a successful preclinical multilaboratory study requires greater training, standardization of protocols, and study-level management when compared to a preclinical study within a single-laboratory. Another barrier was the issue of obtaining adequate funding for a multilaboratory study. As consequence of limited funding, we would speculate that these studies may have undergone more scrutiny and refinement by multiple investigators, funders, and other stakeholders Indeed, comparison single-laboratory studies that had been conducted by authors of multilaboratory studies suggested differences in the conduct and outcomes of these studies (despite having the some of the same researchers involved in both). However, this post hoc analysis was qualitative with a limited sample; thus, future studies will need to explore these issues further.”

We chose not to highlight the studies in Figure 3 to avoid distracting from our a priori planned analysis.

https://doi.org/10.7554/eLife.76300.sa2

Article and author information

Author details

  1. Victoria T Hunniford

    1. Clinical Epidemiology Program, Blueprint Translational Research Group, Ottawa Hospital Research Institute, Ottawa, Canada
    2. Telfer School of Management, University of Ottawa, Ottawa, Canada
    Contribution
    Conceptualization, Formal analysis, Investigation, Methodology, Writing – original draft, Writing – review and editing
    Competing interests
    No competing interests declared
  2. Agnes Grudniewicz

    Telfer School of Management, University of Ottawa, Ottawa, Canada
    Contribution
    Supervision, Writing – review and editing
    Competing interests
    No competing interests declared
  3. Dean A Fergusson

    1. Clinical Epidemiology Program, Blueprint Translational Research Group, Ottawa Hospital Research Institute, Ottawa, Canada
    2. Faculty of Medicine, University of Ottawa, Ottawa, Canada
    3. Department of Surgery, University of Ottawa, Ottawa, Canada
    4. School of Epidemiology and Public Health, University of Ottawa, Ottawa, Canada
    Contribution
    Conceptualization, Supervision, Methodology, Writing – review and editing
    Competing interests
    No competing interests declared
  4. Joshua Montroy

    Clinical Epidemiology Program, Blueprint Translational Research Group, Ottawa Hospital Research Institute, Ottawa, Canada
    Contribution
    Formal analysis, Writing – review and editing
    Competing interests
    No competing interests declared
  5. Emma Grigor

    1. Clinical Epidemiology Program, Blueprint Translational Research Group, Ottawa Hospital Research Institute, Ottawa, Canada
    2. Faculty of Medicine, University of Ottawa, Ottawa, Canada
    Contribution
    Investigation, Writing – review and editing
    Competing interests
    No competing interests declared
  6. Casey Lansdell

    Clinical Epidemiology Program, Blueprint Translational Research Group, Ottawa Hospital Research Institute, Ottawa, Canada
    Contribution
    Investigation, Writing – review and editing
    Competing interests
    No competing interests declared
  7. Manoj M Lalu

    1. Clinical Epidemiology Program, Blueprint Translational Research Group, Ottawa Hospital Research Institute, Ottawa, Canada
    2. School of Epidemiology and Public Health, University of Ottawa, Ottawa, Canada
    3. Department of Anesthesiology and Pain Medicine, The Ottawa Hospital, University of Ottawa, Ottawa, Canada
    4. Regenerative Medicine Program, The Ottawa Hospital Research Institute, Ottawa, Canada
    5. Department of Cellular and Molecular Medicine, University of Ottawa, Ottawa, Canada
    Contribution
    Conceptualization, Resources, Supervision, Methodology, Writing – review and editing
    For correspondence
    mlalu@toh.ca
    Competing interests
    No competing interests declared
    ORCID icon "This ORCID iD identifies the author of this article:" 0000-0002-0322-382X

Funding

QEII Scholarship (Graduate Student Scholarship)

  • Victoria T Hunniford

Canadian Anesthesia Research Foundation (Career Scientist Award)

  • Manoj M Lalu

The funders had no role in study design, data collection and interpretation, or the decision to submit the work for publication.

Acknowledgements

VTH was supported by a Government of Ontario Queen Elizabeth II Graduate Scholarship in Science and Technology. MML was supported by The Ottawa Hospital Anesthesia Alternate Funds Association, a University of Ottawa Junior Clinical Research Chair in Innovative Translational Research, and the Canadian Anesthesiologists’ Society Career Scientist Award (Canadian Anesthesia Research Foundation). We would like to thank Risa Shorr (Information Specialist, The Ottawa Hospital) for providing assistance with the generation of the systematic search strategies and article retrieval. We would also like to thank Dr. Alison Fox-Robichaud from the Canadian Critical Care Translational Biology Group for providing critical feedback on the manuscript.

Senior Editor

  1. Mone Zaidi, Icahn School of Medicine at Mount Sinai, United States

Reviewing Editor

  1. Carlos Isales, Augusta University, United States

Reviewers

  1. David Mellor, Center for Open Science, United States
  2. Andrew SC Rice, Imperial College London, United Kingdom

Version history

  1. Preprint posted: March 27, 2019 (view preprint)
  2. Received: December 12, 2021
  3. Accepted: March 8, 2023
  4. Accepted Manuscript published: March 9, 2023 (version 1)
  5. Version of Record published: May 9, 2023 (version 2)

Copyright

© 2023, Hunniford et al.

This article is distributed under the terms of the Creative Commons Attribution License, which permits unrestricted use and redistribution provided that the original author and source are credited.

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  1. Victoria T Hunniford
  2. Agnes Grudniewicz
  3. Dean A Fergusson
  4. Joshua Montroy
  5. Emma Grigor
  6. Casey Lansdell
  7. Manoj M Lalu
  8. On behalf of The Canadian Critical Care Translational Biology Group
(2023)
A systematic assessment of preclinical multilaboratory studies and a comparison to single laboratory studies
eLife 12:e76300.
https://doi.org/10.7554/eLife.76300

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https://doi.org/10.7554/eLife.76300