Is blood pressure reduction a valid surrogate endpoint for stroke prevention? an analysis incorporating a systematic review of randomised controlled trials, a by-trial weighted errors-in-variables regression, the surrogate threshold effect (STE) and the biomarker-surrogacy (BioSurrogate) evaluation schema (BSES)

Trial inclusion and exclusion criteria

Randomised trial evidence of the relationship of blood pressure reduction and rate of stroke was reviewed from the published literature. Trial inclusion criteria were negatively (placebo or open-label) controlled trials that randomised patients that (i) were at least six months duration of pharmacologic treatment for primary or secondary prevention, (ii) used any anti-hypertensive regimen, (iii) reported baseline and on-trial blood pressure for treated and for control patients, and (iv) reported number of events for fatal and non-fatal stroke for treated and for control patients. A negatively controlled trial was a trial with no mandatory anti-hypertensive treatment requirement for patients in the control arm. However, discretionary treatment, for example, rescue medication, was permitted. Exclusion criteria were (i) trials that only recruited patients with chronic heart failure, diabetes or chronic renal failure, (ii) trials in patients with acute stroke or acute myocardial infarct, (iii) trials designed to assess blood pressure in responders rather than all randomised patients, (iv) trials using a second on-trial randomisation that re-assigned some active arm patients to placebo treatment, (v) trials that simultaneously evaluated multiple interventions targeting vascular risk (e.g. hypertension and hyperlipidaemia) and (vi) trials with fewer than five cerebrovascular (CVA) events per treatment arm [18]. We did not require elevated blood pressure at entry as an inclusion criterion.

Search strategy

Our first search strategy was a search of Medline (1950 to February 2009) for randomised trials of blood pressure using exp Hypertension/(174,452) OR exp Blood Pressure/(210,864) OR (blood pressure or hyperten* or systolic or diastolic).mp. (523,114) that identified 528,263 citations. These were limited to (humans AND clinical trial, all OR clinical trial, phase I OR clinical trial, phase II OR clinical trial, phase III OR clinical trial or controlled clinical trial OR multicentre study OR randomized controlled trial) yielding 50,780 unique citations, a random selection of which identified most as unsuitable for our objective and a systematic evaluation of all was not feasible. Therefore, an alternative strategy to identify trials that met our inclusion criteria was applied.

Our second strategy was a rapid review process to identify original trial reports that met our trial inclusion criteria by sourcing secondary data identified in meta-analyses of randomised trials of hypertension. We searched Medline (1950 to May 2009) using the search terms (exp Hypertension/(181,231) OR exp Blood Pressure/(216,603) OR (blood pressure or hyperten* or systolic or diastolic).mp. (538,084); limited to humans AND adults AND to meta-analysis OR reviews OR systematic reviews. This yielded 1199 citations. A search of the Cochrane Database identified 8 reviews that already had been identified in the Medline search. The abstracts of these 1199 citations were evaluated and 38 meta-analyses or systematic reviews reported trials that satisfied our inclusion criteria (see Additional file 2 reference list). The remaining meta-analyses did not contribute trials because they were meta-analyses of trials that (i) were of insufficient duration, (ii) did not address adult patients with hypertension, (iii) were derivative analyses of earlier meta-analyses with no new trials, or they were not meta-analyses at all. All randomised controlled trial reports identified from these 38 meta-analyses were obtained to determine whether they met our inclusion/exclusion criteria. One author (KJ) further hand-searched all citations of the randomised controlled trial reports to identify trials that may have been missed by the 38 meta-analyses.

Data extraction

Two authors (KJ, MS) independently extracted the data from trial reports and uncertainty was further adjudicated (ML). Intention-to-treat extractions were applied throughout. We extracted the following for treated and control patients: treatments at trial entry; initial, on-trial and final diastolic and systolic blood pressure; fatal and non-fatal stroke events (CVAs), and any other interventions used. We also extracted all cardiovascular fatal events and all-cause fatal events if the trial reported fatal and non-fatal stroke events. Trials enrolling both primary and secondary prevention patients were coded as combined primary and secondary prevention. We also extracted, if reported, information on trial: demographics (age, gender), additional risk factors (e.g. smoking history, diabetes), trial year, trial size, trial duration, trial blinding, and the proportion of subjects that were blood pressure treatment naïve, had past treatment or were on current treatment at trial entry. We also recorded whether add-on treatment was permitted in either arm if protocol defined blood pressure targets were not met and the proportion that required that add-on treatment. No publication included individual level data for analysis.

Data analysis

The surrogate endpoint independent variables were two, diastolic blood pressure and systolic blood pressure. Each was a difference between arms of the differences over the trial for each arm. For diastolic blood pressure (DBP) the difference over the trial was defined as the mean baseline DBP in the treated patients minus the mean on-trial DBP (i.e., all measures from year 1 to end-of-trial) in the treated patients, and similarly for the control patients. The DBP independent variable was then the mean DBP difference in treated patients minus the mean DBP difference in control patients. The systolic blood pressure independent variable was defined similarly. Systolic and diastolic blood pressure differences were analysed separately. The dependent variable was the relative risk reduction (RRR) of fatal and non-fatal stroke, i.e., the stroke rate in the control arm minus the stroke rate in the test arm, divided by the stroke rate in the control arm. RRR was selected as the most intuitively understandable outcome metric for clinicians. All trial data are from intention-to-treat analysis. If a trial report pre-specified a comparison combining treatment arms, these were used. Otherwise, the comparison used from multiple arm trials was the comparison with the largest difference in BP changes. We used the BSES3 for the multidimensional quantitative evaluation of blood pressure reduction as a surrogate endpoint for stroke events.

Statistical analysis

The independent variable mean blood pressure difference is an estimated variable; therefore, its true value is not known with certainty in regression analysis. When both the independent variable as well as the dependent variable are measured with error, then the effect of the independent variable is biased, usually towards the null (underestimated) [19, 20]. There are several errors-in-variables regression methods that have been proposed to adjust for this bias [20]. One method adjusts for the bias by incorporating knowledge of the reliability, r, (where r = 1- (noise variance/total variance)) of the independent variable. Therefore we undertook a weighted (by trial size) errors-in-variables regression of relative risk reduction (RRR) of fatal and non-fatal stroke on systolic and diastolic blood pressure reduction respectively, incorporating sensitivity analyses with reliabilities of 0.6, 0.7, 0.8 and 0.9, where 1.0 indicates no measurement error. The weighting was applied to (i) estimates of the linear prediction, (ii) the standard error of the predicted expected value and (iii) the standard error of the point prediction for a single observation, commonly referred to as the standard error of the future or forecast value. We used data from the literature to inform these reliabilities as there have been many studies that report within and between individual, as well as within and between group variability of systolic and diastolic blood pressure, plus specific studies of sources of variability including measurement error of blood pressure observations. We used Tobit regression (assuming no uncertainty in the estimated surrogate) [21] because relative risk reduction is bounded at 1.0, representing 100% increase. We also used fractional polynomial regression [22] to confirm that a linear model was satisfactory. Other regression assumptions were evaluated using standard methods. The surrogate threshold effect (STE) is the minimum by-arm blood pressure reduction difference that predicts a by-arm stroke reduction benefit. Graphically, this is where the regression lower 95% prediction line [23] for an individual trial crosses the horizontal axis representing no stroke reduction benefit [9]. Other statistics reported are the R-squared at the trial level (R² _trial-level) of the weighted errors-in-variables regression model as well as the coefficient (slope) of the blood pressure reduction difference. No publication included individual level data therefore, we were unable to determine the patient-level association between both endpoints (R² _individual).

Given that reduction of blood pressure with antihypertensive drugs has a greater effect on stroke prevention than on reduction of cardiovascular mortality or on all-cause mortality [24, 25], we evaluated the construct validity of the STE by repeating all the statistical analyses with cardiovascular deaths and all-cause deaths as the patient-relevant clinical endpoints. We used Stata 11 for all analyses.

Context of surrogacy and impact of secular change in study design, trial populations and treatment modalities

These STEs for systolic and diastolic blood pressure assume that the new trial measuring only the surrogate endpoint is otherwise similar to past trials used in the predictive model regarding intervention, population, trial design and pharmacologic therapy. These STEs were derived from negatively controlled antihypertensive randomised controlled trials of varying design, clinical populations and pharmacologic classes. Therefore, these STEs may not be applicable to trials that require subjects in all arms to be randomised to an anti-hypertensive drug, or to trials of homogeneous populations, for example, trials of only heart or renal failure patients. As our data-set of trials spans four decades, secular changes in standard of care of hypertension is to be expected and is reflected in changes in trial design and in relation to inclusion and exclusion criteria of risk populations. At one extreme, severe hypertension rapidly became incompatible with trials with no treatment controls. Another secular change is the large number of different pharmacologic classes of agents used singly and in combination. As the evidence for the benefits of blood pressure reduction accrued, equipoise for negatively controlled trials diminished, and as more pharmacologic classes of anti-hypertensive agents appeared, polypharmacy became the rule. Few patients were treatment-naïve, and trials increasingly used designs with provisions for add-on to established "background" regimens. Trial entry criteria changed as did the cut-off for mandatory discontinuation in the event of the on-trial development of severe, uncontrolled hypertension. Older patients and those with lower entry BP and improved risk profiles generally were increasingly enrolled in more recent trials. In seven trials, a proportion of enrolled patients (sometimes up to half) were already on antihypertensive drugs either for hypertension or other indications. We did not exclude these trials because they met our inclusion criteria. Also, to capture drug effects that may occur with BP lowering from a baseline high-normal range, we did not require elevated BP at baseline. Cross-over also occurred in some trials, although generally it was less than 15% and occurred from active to control arm as well as in the other direction. Only four trials recruited treatment-naïve patients exclusively, where one might expect greater BP and outcome responses compared to trials with treatment-experienced patients. Fourteen trials had varying proportions of treatment-naïve versus treatment-experienced patients which also might dilute or delay the effect on stroke reduction. These changes are likely to attenuate the relationship between blood pressure and stroke, impede the compilation of new data supporting surrogacy, and increase the size of the STE. It is likely that the STEs estimated from active-control randomised trials would be larger because subjects in all arms are randomised to hypertensive drugs. Furthermore, trials clinically of homogeneous populations, such as heart or renal failure populations may also have different STEs. These hypotheses, if substantiated, imply that the initial evaluation of all existing and new biomarkers should be in negatively controlled heterogeneous randomised trials; otherwise, the surrogacy potential of these biomarkers may be underestimated.

Regression modelling with measurement error in the independent variable: Application to blood pressure

Ordinary linear regression has several assumptions, one being that all variation is in the dependent variable and that as long as these measurement errors are uncorrelated and unbiased the results are not influenced. However, the independent variable must be measured without error. In the presence of random measurement error in the independent variable coefficients are biased towards the null. In our analysis both stroke relative risk reduction and mean blood pressure reduction are trial-level estimations. Therefore, a priori, they are measured with error. Unfortunately, trials did not report the within arm standard deviation of blood pressure reduction. Individual blood pressure readings are highly variable, because of position, rest, etc, and measurement errors due to the instrument and observer [44, 45]. Systematic bias, such as white coat hypertension [46], is generally less problematic in the setting of a randomised controlled trial. Hebel [47] evaluated within-person variability of diastolic BP. Within occasion variability was 3.1 mmHg for patients on medication and 2.4 mmHg for normotensive controls. Reliability coefficients of 0.6 to 0.9 have been reported [48–52]. Skirton [53] recently undertook a systematic review of variability and reliability of manual and automated blood pressure readings, but none of the results were reported as reliability coefficients. The importance of blood pressure variability as a predictor of vascular events is a new direction of research [54]. The underestimation of risk association due to regression dilution in long-term prospective studies has also been well described in studies of hypertension [55, 56]. Therefore, our linear regression model is influenced by several sources of variation all of which, assuming no systematic variation, underestimate the slope of the relationship between stroke relative risk reduction and blood pressure reduction. Therefore, our results are conservative, and we illustrate the effect of adjusting for the error in the independent variable by sensitivity analysis using several reliability coefficients. Using errors-in-variables regression systolic STEs vary from 7.4 mmHg (assuming no uncertainty around the estimated effects on the independent variable) to 5.9 (assuming a reliability coefficient as low as 0.6). The diastolic STEs vary from 2.6 mmHg (assuming no uncertainty around the estimated effects on the independent variable) to as little as1.2 (again assuming a reliability coefficient as low as 0.6). Interestingly, the difference in STEs across these different reliability coefficients was only 1.5 and 1.4 mmHg for systolic and diastolic blood pressure respectively, a indicator of the robustness of STE and the STEP as a method of evaluating surrogacy. There was a much greater impact of different reliability coefficients on the R-squared trial-level association. These almost doubled for both systolic and diastolic blood pressure (R-squared 0.37 to 0.61 and 0.58 to 0.96) with increasing correction for measurement error. We used the reliability coefficient errors-in-variables regression (as provided by Stata statistical software), however, several other methods have been proposed [19, 20] and comparing the results of different methods would be worthy of further research.

Statistical measures of surrogacy

Surrogacy is a complex construct and requires several qualitatively different statistical (and substantive) metrics for its evaluation. We were limited to the STE, the STEP and trial-level linear regression to statistically evaluate blood pressure's surrogacy status. We did not have access to any patient-level data, therefore, were unable to evaluate surrogacy status on an individual-level. Other approaches have been proposed, including a mixed models analysis [7] that combine time, surrogate, clinical endpoint, treatment, trial and individual subject variables into a single analysis for estimation of a mixed model trial-level association, a mixed model individual-level association and a mixed model STE. Other new methods are those based on principal stratification [57]. The STEP is useful because it identifies the relative position of the STE within the model of data used to determine the STE by converting a unit-specific STE, e.g. mmHg of blood pressure, to a proportion. It is similar to the coefficient of determinations in that it can take a value from 0.0 to 1.0 (or 0% to 100%). The STEP serves to compare STEs across different contexts. We have already shown that the STE is more robust to measurement error than the R-squared trial-level association; therefore, the STEP may also be a more robust method of comparing different surrogate endpoints.

Our trial-level association for systolic blood pressure may be considered low (R-squared 0.37 assuming no uncertainty). The results for diastolic blood pressure were somewhat better (R-squared 0.58 assuming no uncertainty). Trial-level associations of reported surrogate endpoints that are considerably higher (> 0.8) are those that evaluate progression-free survival, disease-free survival and event-free survival as a surrogate endpoint for overall survival, where survival is included in the surrogate [58–60]. Analyses of time to progression or response rate surrogate endpoints, measures that do not include a survival in the surrogate, report more modest trial-level associations. In metastatic colon disease the trial-level association of time to progression was 0.33 [10]. Biomarkers in non-oncological chronic disease also have trial-level associations that are modest. In negatively-controlled randomised trials of statins the trial-level association of LDL-cholesterol reduction and cardiovascular mortality reduction assuming no uncertainty was 0.41 [11].

Previously published models and meta-analyses of stroke and other vascular outcomes

Others have found similar relationships using different regression methods relating BP differences and expected outcome differences, but none calculated prediction bands to estimate an STE. Staessen et al [16] was the first to publish a blood pressure trial level regression. Using data from hypertension outcome trials of at least 2-years duration and at least 100 patients, they reported trial-level regression models of the odds ratio of cardiovascular mortality and all cardiovascular events versus systolic blood pressure difference. Graphically, a systolic BP difference of 5 mmHg corresponded to a cardiovascular mortality reduction of about 10%. In our data-set of trials, designed to identify stroke outcomes, a systolic blood pressure reduction of 10 mmg was associated with a 9% reduction of cardiovascular mortality, but the result was not statistically significant. Law et al [18] published a meta-analysis of stroke in 45 trials (including trials in conditions other than essential hypertension) demonstrating a 5 mmHg diastolic blood pressure or 10 mmHg SBP reduction corresponded to a 41% reduction in stroke. However, among the 45 trials were studies in patients with coronary heart disease that reported no BP data at all, and for these trials BP changes were imputed from results from an earlier study of short term BP studies [61]. We found, in our trial-dataset, a 5 mmHg DBP reduction or 10 mmHg SBP reduction corresponded to a 22.5% and 20% reduction in stroke respectively, assuming a no measurement error model. Boissel et al [62] in the INDANA data set that included individual patient data reported a Cox proportional hazard model of stroke in the five trials (28,997 patients, 808 events). They found a hazard ratio for stroke of 0.79, a risk reduction of 21%. In this study about one-half of the benefit was accounted for when adding an adjustment made for on-treatment BP and BP measurement error, a result interpreted by the authors as suggesting that only half of the stroke benefit is "explained by" the effect of treatment on blood pressure. We found that baseline blood pressure was not a significant predictor of stroke events, a result confirmed by others [63].

Others have also found that the relationship for stroke reduction is stronger than that for cardiovascular mortality or all-cause mortality reduction [24]. We therefore would expect the STE for mortality reduction to be larger than the STE for stroke reduction. All trials in our data reported all-cause fatal events and all but one (PREVENT [35]) reported cardiovascular fatal events. Trial-level associations for both systolic and diastolic blood pressure reduction and cardiovascular mortality and all-cause mortality relative risk reduction were extremely poor, less than 0.15 for systolic and 0.05 for diastolic blood pressure, assuming no measurement uncertainty. We were surprised to find that the relationship between blood pressure reduction and mortality reduction in our stroke dataset was too poor for an STE to be estimated. In our stroke data-set, there was no blood pressure reduction that predicted a mortality benefit. Although these findings provide additional support for the validity of the stroke-specific STEs, we cannot conclude that there is no STE for mortality reduction. Our dataset a required at least 5 stroke outcomes per treatment arm. To determine the STEs for cardiovascular mortality and all-cause mortality, a search strategy specific to this research question is needed. A less conservative statistical analysis using mixed models and individual-level data may also prove necessary before we conclude that blood pressure is not a valid surrogate endpoint for mortality endpoints.

Potential limitations and further qualifications of the STE and other conclusions

Are there any caveats that may bias the STE and our conclusions towards non-conservative results? We propose that the STE, STEP and trial-level associations we have reported are conservative. As we only had access to trial level data we could not undertake a full hierarchical mixed model regression. Our model could also be vulnerable to ecological bias. Our preliminary unpublished simulation work in SAS on comparing ordinary least squares (OLS) regression with a joint hierarchical linear mixed model has indicated that OLS regression STE is almost always larger therefore conservative compared to the STE obtained from the linear mixed model. In fact, the exceptional simulation scenarios seem to be clinically highly implausible ones; for example, models with very few (5) trials, very small (50 patients) trials, or very small between-trial outcome variance compared to the patient-level outcome variance. Furthermore, these scenarios presented computational problems when fitting a linear mixed model, while the by-trial model is computationally straightforward. In fact, because of its ability to incorporate both trial and patient-level variances, the mixed model may be expected to produce narrower prediction bands.

Our simulation work also suggests that the OLS STE is not influenced by individual-level correlation between surrogate and true endpoints. Therefore, the STE may be less subject to ecological bias. Individual-level correlation is usually first explored in observation cohort studies, as was the case in blood pressure, and is often the basis for subsequent evaluation in randomised controlled trials.

Other potential methodological weaknesses that may bias the STE towards a non-conservative value deserve mention. Even though some individual patient analyses suggest the hazard ratio for stroke varies over time [64], we assume the hazard is constant; individual patient data are needed to study this question. Incorporating patient-level variability could increase the STE, but, to date, we have not found that patient-level variability is as great an influence on the STE as number of trials and between-trial outcome variance in our simulations. Nevertheless, patient-level data would facilitate greater exploration of differences in trial populations over time and may generate more precise context-specific STEs. Although expecting that all patient level data on all trials to be available through publication is unrealistic, analysis informed by a incorporating a random subset of patient level data may prove useful and deserves further investigation. Another issue we considered is whether it is necessary to calculate a confidence interval around the STE. This was discussed at a recent international workshop on biomarkers as surrogate endpoints (Sydney Bio-Surrogates Workshop, February 2011, unpublished), and most workshop participants did not think it appropriate to calculate a confidence interval around a prediction interval.

Concepts to define surrogacy evaluation and qualification past, present and future: Lessons learned from the evaluation of blood pressure

It is important that the concepts that define surrogate validity are developed in a properly conceived context. Formal statistical, rather than anecdotal, evaluation of rigorously defined populations and other context-determined heterogeneity is needed to systematically explore and compare surrogacy status of biomarkers and patient-reported instruments. Our results support that diastolic blood pressure reduction is a very good surrogate for stroke prevention. Systolic blood pressure performs less well. Our analysis of mortality endpoints indicates that the surrogacy of blood pressure is more context specific than generally appreciated. The context could be drug-class specific, clinical endpoint specific and clinical population specific (i.e., by age, gender, ethnicity and comorbidity). How much is the effect on cardiovascular mortality mediated by blood pressure reduction, and how much by other drug class effects? Once the clinical endpoint is broadened to all-cause mortality, the effect of blood pressure is further diluted by other drug class effects, including drug class toxicity. Recently it has been shown that different drug classes mediate a heterogeneous effect on stroke through variable effects of blood pressure visit-to-visit variability [65] and visit-to-visit variability is an independent risk factor for vascular events. It is likely that risk predictions that include a composite surrogate endpoint of mean blood pressure reduction and reduced blood pressure variability and instability might estimate different STEs and provide stronger evidence of surrogacy for blood pressure [66] across a variety of clinical endpoints.

Using the BSES the surrogacy status of different biomarkers and patient-reported instruments can be compared within these specified contexts. The STE, a trial-level metric, is a useful measure because it provides information on the surrogate endpoint in the units of the surrogate and therefore could be used to inform drug registration and drug reimbursement decisions that are based on surrogate endpoints. Moreover, the STE is needed to determine the STEP, which we have shown is a robust relative metric of surrogacy. We should emphasise that we have not analysed data nor do we report a metric that provide decisions regarding individual patients, for example, how much to decrease an individual patient DBP or what is the optimal final DBP target to use. For those claims to be data-driven would require, for example, an RCT to demonstrate that lowering DBP to, say, 80 mmHg is superior (fewer strokes) than lowering the DBP to 85 mmHg. Undertaking such 'target' trials is feasible but difficult as evidenced by the experience of the Hypertension Optimal Treatment (HOT) Study [67, 68]. The epidemiology of BP seems to indicate that even very small BP differences result in difference in vascular event rates, so, in theory, trials could be designed to demonstrate a benefit from even very small BP differences. Policy recommendations would then need to be made on a numbers-needed-to-treat basis and, of course, integrated into the other risk factors for any given patient [69]. These issues are quite distinct from the strength of evidence of a surrogate, the aim of the STE and BSES.

Formal evaluation of surrogacy status using a standardised framework, such as the BSES3, can be used to begin discussions on a surrogate biomarkers qualification process [2]. However, surrogacy applications in the real world of patient-care or policy decisions take into account other factors that are not included in the BSES3. These factors of risk-benefit such as public health, drug safety, disease rarity or diseases that are serious or life-threatening and where there are no alternative therapies, do not directly impact the internal validity of surrogacy but nevertheless are important considerations for regulators and payors [12]. Nonetheless, the BSES3 provides clinicians and others a simple hierarchical framework that can now be used for critically appraising studies of biomarkers and surrogate endpoints.