EHRs and RCTs: Outcome Prediction vs. Optimal Treatment Selection

Frank Harrell
Professor of Biostatistics
Vanderbilt University School of Medicine

Laura Lazzeroni
Professor of Psychiatry and, by courtesy, of Medicine (Cardiovascular Medicine) and of Biomedical Data Science
Stanford University School of Medicine
Revised July 17, 2017

It is often said that randomized clinical trials (RCTs) are the gold standard for learning about therapeutic effectiveness. This is because the treatment is assigned at random so no variables, measured or unmeasured, will be truly related to treatment assignment. The result is an unbiased estimate of treatment effectiveness. On the other hand, observational data arising from clinical practice has all the biases of physicians and patients in who gets which treatment. Some treatments are indicated for certain types of patients; some are reserved for very sick ones. The fact is that the selection of treatment is often chosen on the basis of patient characteristics that influence patient outcome, some of which may be unrecorded. When the outcomes of different groups of patients receiving different treatments are compared, without adjustment for patient characteristics related to treatment selection and outcome, the result is a bias called confounding by indication.

To set the stage for our discussion of the challenges caused by confounding by indication, incomplete data, and unreliable data, first consider a nearly ideal observational treatment study then consider an ideal RCT. First, consider a potentially optimal observational cohort design that has some possibility of providing an accurate treatment outcome comparison. Suppose that an investigator has obtained $2M in funding to hire trained research nurses to collect data completely and accurately, and she has gone to the trouble of asking five expert clinicians in the disease/treatment area to each independently list the patient characteristics they perceive are used to select therapies for patients. The result is a list of 18 distinct patient characteristics, for which a data dictionary is written and case report forms are collected. Data collectors are instructed to obtain these 18 variables on every patient with very few exceptions, and other useful variables, especially strong prognostic factors, are collected in addition. Details about treatment are also captured, including the start and ending dates of treatment, doses, and dose schedule. Outcomes are well defined and never missing. The sample size is adequate, and when data collection is complete, analysis of covariance is used to estimate the outcome difference for treatment A vs. treatment B. Then the study PI discovers that there is a strong confounder that none of the five experts thought of, and a sensitivity analysis indicates that the original treatment effect estimate might have been washed away by the additional confounder had it been collected. The study results in no reliable knowledge about the treatments.

The study just described represents a high level of observational study quality, and still needed some luck to be useful. The treatments, entry criteria, and follow-up clock were well defined, and there were almost no missing data. Contrast that with the electronic health record (EHR). If questions of therapeutic efficacy are so difficult to answer with nearly perfect observational data how can they be reliably answered from EHR data alone?

To complete our introduction to the discussion, envision a well-conducted parallel-group RCT with complete follow-up and highly accurate and relevant baseline data capture. Study inclusion criteria allowed for a wide range of age and severity of disease. The endpoint is time until a devastating clinical event. The treatment B:treatment A covariate-adjusted hazard ratio is 0.8 with 0.95 credible interval of [0.65, 0.93]. The authors, avoiding unreliable subgroup analysis, perform a careful but comprehensive assessment of interaction between patient types and treatment effect, finding no evidence for heterogeneity of treatment effect (HTE). The hazard ratio of 0.8 is widely generalizable, even to populations with much different baseline risk. A simple nomogram is drawn to show how to estimate absolute risk reduction by treatment B at 3 years, given a patient's baseline 3y risk.

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There is an alarming trend in advocates of learning from the EHR saying that statistical inference can be bypassed because (1) large numbers overcome all obstacles, (2) the EHR reflects actual clinical practice and patient populations, and (3) if you can predict outcomes for individual patients you can just find out for which treatment the predicted outcomes are optimal. Advocates of such "logic" often go on to say that RCTs are not helpful because the proportion of patients seen in practice that would qualify for the trial is very small with randomized patients being unrepresentative of the clinical population, because the trial only estimates the average treatment effect, because there must be HTE, and because treatment conditions are unrepresentative. Without HTE, precision medicine would have no basis. But evidence of substantial HTE has yet to be generally established and its existence in particular cases can be an artifact of the outcome scale used for the analysis. See this for more about the first two complaints about RCTs. Regarding (1), researchers too often forget that measurement or sample bias does not diminish no matter how large the sample size. Often, large sample sizes only provide precise estimates of the wrong quantity.

To illustrate this problem, suppose that one is interested in estimating and testing the treatment effect, B-A, of a certain blood pressure lowering medication (drug B) when compared to another drug (A). Assume a relevant subset of the EHR can be extracted in which patients started initial monotherapy at a defined date and systolic blood pressure (SBP) was measured routinely at useful follow-up intervals. Suppose that the standard deviation (SD) of SBP across patients is 8 mmHg regardless of treatment group. Suppose further that minor confounding by indication is present due to the failure to adjust for an unstated patient feature involved in the drug choice, which creates a systematic unidirectional bias of 2 mmHg in estimating the true B-A difference in mean SBP. If the EHR has m patients in each treatment group, the variance of the estimated mean difference is the sum of the variances of the two individual means or 64/m + 64/m = 128/m. But the variance only tells us about how close our sample estimate is to the incorrect value, B-A + 2 mmHg. It is the mean squared error, the variance plus the square of the bias or 128/m + 4, that relates to the probability that the estimate is close to the true treatment effect B-A. As m gets larger, the variance goes to zero indicating a stable estimate has been achieved. But the bias is constant so the mean squared error remains at 4 (root mean squared error = 2 mmHg).

Now consider an RCT that is designed not to estimate the mean SBP for A or the mean SBP for B but, as with all randomized trials, is designed to estimate the B-A difference (treatment effect). If the trial randomized m subjects per treatment group, the variance of the mean difference is 128/m and the mean squared error is also 128/m. The comparison of the square root of mean squared errors for an EHR study and an equal-sized RCT is depicted in the figure below. Here, we have even given the EHR study the benefit of the doubt in assuming that SBP is measured as accurately as would be the case in the RCT. This is unlikely, and so in reality the results presented below are optimistic for the performance of the EHR.

EHR studies have the potential to provide far larger sample sizes than RCTs, but note that an RCT with a total sample size of 64 subjects is as informative as an EHR study with infinitely many patients. Bigger is not better. What if the SBP measurements from the EHR, not collected under any protocol, are less accurate than those collected under the RCT protocol? Let’s exemplify that by setting the SD for SBP to 10 mmHg for the EHR while leaving it as 8 mmHg for the RCT. For very large sample sizes, bias trumps variance so the breakeven point of 64 subjects remains, but for non-large EHRs the increased variability of measured SBPs harms the margin of error of EHR estimate of mean SBP difference.

We have addressed estimation error for the treatment effect, but note that while an EHR-based statistical test for any treatment difference will have excellent power for large n, this comes at the expense of being far from preserving the type I error, which is essentially 1.0 due to the estimation bias causing the two-sample statistical test to be biased, .

Interestingly, bias decreases the benefits achieved by larger sample sizes to the extent that, in contrast to an unbiased RCT, the mean squared error for an EHR of size 3000 in our example is nearly identical to what it would be with an infinite sample size. While this disregards the need for larger samples to target multiple treatments or distinct patient populations, it does suggest that overcoming the specific resource-intensive challenges associated with handling huge EHR samples may yield fewer advances in medical treatment than anticipated by some, if the effects of bias are considered.

There is a mantra heard in data science that you just need to "let the data speak." You can indeed learn much from observational data if quality and completeness of data are high (this is for another discussion; EHRs have major weakness just in these two aspects). But data frequently teach us things that are just plain wrong. This is due to a variety of reasons, including seeing trends and patterns that can be easily explained by pure noise. Moreover, treatment group comparisons in EHRs can reflect both the effects of treatment and the effects of specific prior patient conditions that led to the choice of treatment in the first place - conditions that may not be captured in the EHR. The latter problem is confounding by indication, and this can only be overcome by randomization, strong assumptions, or having high-quality data on all the potential confounders (patient baseline characteristics related to treatment selection and to outcome--rarely if ever possible). Many clinical researchers relying on EHRs do not take the time to even list the relevant patient characteristics before rationalizing that the EHR is adequate. To make matters worse, EHRs frequently do not provide accurate data on when patients started and stopped treatment. Furthermore, the availability of patient outcomes can depend on the very course of treatment and treatment response under study. For example, when a trial protocol is not in place, lab tests are not ordered at pre-specified times but because of a changing patient condition. If EHR cannot provide a reliable estimate of the average treatment effect how could it provide reliable estimates of differential treatment benefit (HTE)?

Regarding the problem with signal vs. noise in "let the data speak", we envision a clinician watching someone playing a slot machine in Las Vegas. The clinician observes that a small jackpot was hit after 17 pulls of the lever, and now has a model for success: go to a random slot machine with enough money to make 17 pulls. Here the problem is not a biased sample but pure noise.

Observational data, when complete and accurate, can form the basis for accurate predictions. But what are predictions really good for? Generally speaking, predictions can be used to estimate likely patient outcomes given prevailing clinical practice and treatment choices, with typical adherence to treatment. Prediction is good for natural history studies and for counseling patients about their likely outcomes. What is needed for selecting optimum treatments is an answer to the "what if" question: what is the likely outcome of this patient were she given treatment A vs. were she given treatment B? This is inherently a problem of causal inference, which is why such questions are best answered using experimental designs, such as RCTs. When there is evidence that the complete, accurate observational data captured and eliminated confounding by indication, then and only then can observational data be a substitute for RCTs in making smart treatment choices.

What is a good global strategy for making optimum decisions for individual patients? Much more could be said, but for starters consider the following steps:

• Obtain the best covariate-adjusted estimate of relative treatment effect (e.g., odds ratio, hazards ratio) from an RCT. Check whether this estimate is constant or whether it depends on patient characteristics (i.e., whether heterogeneity of treatment effect exists on the relative scale). One possible strategy, using fully specified interaction tests adjusted for all main effects, is in Biostatistics for Biomedical Research in the Analysis of Covariance chapter.
• Develop a predictive model from complete, accurate observational data, and perform strong interval validation using the bootstrap to verify absolute calibration accuracy. Use this model to handle risk magnification whereby absolute treatment benefits are greater for sicker patients in most cases.
• Apply the relative treatment effects from the RCT, separately for treatment A and treatment B, to the estimated outcome risk from the observational data to obtain estimates of absolute treatment benefit (B vs. A) for the patient. See the first figure below which relates a hazard ratio to absolute improvement in survival probability.
• Develop a nomogram using the RCT data to estimate absolute treatment benefit for an individual patient. See the second figure below whose bottom axis is the difference between two logistic regression models. (Both figures are from BBR Chapter 13)
• For more about such strategies, see Stephen Senn's presentation.

Statistical Errors in the Medical Literature

Updated 2017-07-13

1. Misinterpretation of P-values and Main Study Results
2. Dichotomania
3. Problems With Change Scores
4. Improper Subgrouping
5. Serial Data and Response Trajectories

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As Doug Altman famously wrote in his Scandal of Poor Medical Research in BMJ in 1994, the quality of how statistical principles and analysis methods are applied in medical research is quite poor.  According to Doug and to many others such as Richard Smith, the problems have only gotten worse.  The purpose of this blog article is to contain a running list of new papers in major medical journals that are statistically problematic, based on my random encounters with the literature.

One of the most pervasive problems in the medical literature (and in other subject areas) is misuse and misinterpretation of p-values as detailed here, and chief among these issues is perhaps the absence of evidence is not evidence of absence error written about so clearly by Altman and Bland.   The following thought will likely rattle many biomedical researchers but I've concluded that most of the gross misinterpretation of large p-values by falsely inferring that a treatment is not effective is caused by (1) the investigators not being brave enough to conclude "We haven't learned anything from this study", i.e., they feel compelled to believe that their investments of time and money must be worth something, (2) journals accepting such papers without demanding a proper statistical interpretation in the conclusion.  One example of proper wording would be "This study rules out, with 0.95 confidence, a reduction in the odds of death that is more than by a factor of 2."  Ronald Fisher, when asked how to interpret a large p-value, said "Get more data."

Adoption of Bayesian methods would solve many problems including this one.  Whether a p-value is small or large a Bayesian can compute the posterior probability of similarity of outcomes of two treatments (e.g., Prob(0.85 < odds ratio < 1/0.85)), and the researcher will often find that this probability is not large enough to draw a conclusion of similarity.  On the other hand, what if even under a skeptical prior distribution the Bayesian posterior probability of efficacy were 0.8 in a "negative" trial?  Would you choose for yourself the standard therapy when it had a 0.2 chance of being better than the new drug? [Note: I am not talking here about regulatory decisions.]  Imagine a Bayesian world where it is standard to report the results for the primary endpoint using language such as:

• The probability of any efficacy is 0.94 (so the probability of non-efficacy is 0.06).
• The probability of efficacy greater than a factor of 1.2 is 0.78 (odds ratio < 1/1.2).
• >The probability of similarity to within a factor of 1.2 is 0.3.
• The probability that the true odds ratio is between [0.6, 0.99] is 0.95 (credible interval; doesn't use the long-run tendency of confidence intervals to include the true value for 0.95 of confidence intervals computed).

In a so-called "negative" trial we frequently see the phrase "treatment B was not significantly different from treatment A" without thinking out how little information that carries.  Was the power really adequate? Is the author talking about an observed statistic (probably yes) or the true unknown treatment effect?  Why should we care more about statistical significance than clinical significance?  The phrase "was not significantly different" seems to be a way to avoid the real issues of interpretation of large p-values.

Since my #1 area of study is statistical modeling, especially predictive modeling, I pay a lot of attention to model development and model validation as done in the medical literature, and I routinely encounter published papers where the authors do not have basic understanding of the statistical principles involved.  This seems to be especially true when a statistician is not among the paper's authors.  I'll be commenting on papers in which I encounter statistical modeling, validation, or interpretation problems.

Misinterpretation of P-values and of Main Study Results

One of the most problematic examples I've seen is in the March 2017 paper Levosimendan in Patients with Left Ventricular Dysfunction Undergoing Cardiac Surgery by Rajenda Mehta in the New England Journal of Medicine.  The study was designed to detect a miracle - a 35% relative odds reduction with drug compared to placebo, and used a power requirement of only 0.8 (type II error a whopping 0.2).  [The study also used some questionable alpha-spending that Bayesians would find quite odd.]  For the primary endpoint, the adjusted odds ratio was 1.00 with 0.99 confidence interval [0.66, 1.54] and p=0.98.  Yet the authors concluded "Levosimendan was not associated with a rate of the composite of death, renal-replacement therapy, perioperative myocardial infarction, or use of a mechanical cardiac assist device that was lower than the rate with placebo among high-risk patients undergoing cardiac surgery with the use of cardiopulmonary bypass."   Their own data are consistent with a 34% reduction (as well as a 54% increase)!  Almost nothing was learned from this underpowered study.  It may have been too disconcerting for the authors and the journal editor to have written "We were only able to rule out a massive benefit of drug."  [Note: two treatments can have agreement in outcome probabilities by chance just as they can have differences by chance.]  It would be interesting to see the Bayesian posterior probability that the true unknown odds ratio is in [0.85, 1/0.85].

The primary endpoint is the union of death, dialysis, MI, or use of a cardiac assist device.  This counts these four endpoints as equally bad.  An ordinal response variable would have yielded more statistical information/precision and perhaps increased power.  And instead of dealing with multiplicity issues and alpha-spending, the multiple endpoints could have been dealt with more elegantly with a Bayesian analysis.  For example, one could easily compute the joint probability that the odds ratio for the primary endpoint is less than 0.8 and the odds ratio for the secondary endpoint is less than 1 [the secondary endpoint was death or assist device and and is harder to demonstrate because of its lower incidence, and is perhaps more of a "hard endpoint"].  In the Bayesian world of forward directly relevant probabilities there is no need to consider multiplicity.  There is only a need to state the assertions for which one wants to compute current probabilities.

The paper also contains inappropriate assessments of interactions with treatment using subgroup analysis with arbitrary cutpoints on continuous baseline variables and failure to adjust for other main effects when doing the subgroup analysis.

This paper had a fine statistician as a co-author.  I can only conclude that the pressure to avoid disappointment with a conclusion of spending a lot of money with little to show for it was in play.

Why was such an underpowered study launched?  Why do researchers attempt "hail Mary passes"?  Is a study that is likely to be futile fully ethical?   Do medical journals allow this to happen because of some vested interest?

Similar Examples

Perhaps the above example is no worse than many.  Examples of "absence of evidence" misinterpretations abound.  Consider the JAMA paper by Kawazoe et al published 2017-04-04.  They concluded that "Mortality at 28 days was not significantly different in the dexmedetomidine group vs the control group (19 patients [22.8%] vs 28 patients [30.8%]; hazard ratio, 0.69; 95% CI, 0.38-1.22;P > = .20)."  The point estimate was a reduction in hazard of death by 31% and the data are consistent with the reduction being as large as 62%!

Or look at this 2017-03-21 JAMA article in which the authors concluded "Among healthy postmenopausal older women with a mean baseline serum 25-hydroxyvitamin D level of 32.8 ng/mL, supplementation with vitamin D₃ and calcium compared with placebo did not result in a significantly lower risk of all-type cancer at 4 years." even though the observed hazard ratio was 0.7, with lower confidence limit of a whopping 53% reduction in the incidence of cancer.  And the 0.7 was an unadjusted hazard ratio; the hazard ratio could well have been more impressive had covariate adjustment been used to account for outcome heterogeneity within each treatment arm.

Dichotomania

Dichotomania, as discussed by Stephen Senn, is a very prevalent problem in medical and epidemiologic research.  Categorization of continuous variables for analysis is inefficient at best and misleading at worst.  This JAMA paper by VISION study investigators "Association of Postoperative High-Sensitivity Troponin Levels With Myocardial Injury and 30-Day Mortality Among Patients Undergoing Noncardiac Surgery" is an excellent example of bad statistical practice that limits the amount of information provided by the study.  The authors categorized high-sensitivity troponin T levels measured post-op and related these to the incidence of death.  They used four intervals of troponin, and there is important heterogeneity of patients within these intervals.  This is especially true for the last interval (> 1000 ng/L).  Mortality may be much higher for troponin values that are much larger than 1000.  The relationship should have been analyzed with a continuous analysis, e.g., logistic regression with a regression spline for troponin, nonparametric smoother, etc.  The final result could be presented in a simple line graph with confidence bands.

An example of dichotomania that may not be surpassed for some time is Simplification of the HOSPITAL Score for Predicting 30-day Readmissions by Carole E Aubert, et al in BMJ Quality and Safety 2017-04-17. The authors arbitrarily dichotomized several important predictors, resulting in a major loss of information, then dichotomized their resulting predictive score, sacrificing much of what information remained. The authors failed to grasp probabilities, resulting in risk of 30-day readmission of "unlikely" and "likely". The categorization of predictor variables leaves demonstrable outcome heterogeneity within the intervals of predictor values. Then taking an already oversimplified predictive score and dichotomizing it is essentially saying to the reader "We don't like the integer score we just went to the trouble to develop." I now have serious doubts about the thoroughness of reviews at BMJ Quality and Safety.

A very high-profile paper was published in BMJ on 2017-06-06: Moderate alcohol consumption as risk factor for adverse brain outcomes and cognitive decline: longitudinal cohort study by Anya Topiwala et al. The authors had a golden opportunity to estimate the dose-response relationship between amount of alcohol consumed and quantitative brain changes. Instead the authors squandered the data by doing analyzes that either assumed that responses are linear in alcohol consumption or worse, by splitting consumption into 6 heterogeneous intervals when in fact consumption was shown in their Figure 3 to have a nice continuous distribution. How much more informative (and statistically powerful) it would have been to fit a quadratic or a restricted cubic spline function to consumption to estimate the continuous dose-response curve.

Change from Baseline

Many authors and pharmaceutical clinical trialists make the mistake of analyzing change from baseline instead of making the raw follow-up measurements the primary outcomes, covariate-adjusted for baseline.  To compute change scores requires many assumptions to hold, e.g.:

1. the variable must be perfectly transformed so that subtraction "works" and the result is not baseline-dependent
2. the variable must not have floor and ceiling effects
3. the variable must have a smooth distribution
4. the slope of the pre value vs. the follow-up measurement must be close to 1.0

Details about problems with analyzing change may be found here.  A general problem with the approach is that when Y is ordinal but not interval-scaled, differences in Y may no longer be ordinal.  So analysis of change loses the opportunity to do a robust, powerful analysis using a covariate-adjusted ordinal response model such as the proportional odds or proportional hazards model.  Such ordinal response models do not require one to be correct in how to transform Y.

Regarding 4. above, often the baseline is not as relevant as thought and the slope will be less than 1.  When the treatment can cure every patient, the slope will be zero.  Sometimes the relationship between baseline and follow-up Y is not even linear, as in one example I've seen based on the Hamilton D depression scale.

The purpose of a parallel-group randomized clinical trial is to compare the parallel groups, not to compare a patient with herself at baseline.  Within-patient change is affected strongly by regression to the mean and measurement error.  When the baseline value is one of the patient inclusion/exclusion criteria, the only meaningful change score, even if assumptions listed below are satisfied, requires one to have a second baseline measurement post patient qualification to cancel out much of the regression to the mean effect.  It is he second baseline that would be subtracted from the follow-up measurement.

Patient-reported outcome scales are particularly problematic.  An article published 2017-05-07 in JAMA, doi:10.1001/jama.2017.5103 like many other articles makes the error of trusting change from baseline as an appropriate analysis variable.  Mean change from baseline may not apply to anyone in the trial.  Consider a 5-point ordinal pain scale with values Y=1,2,3,4,5.  Patients starting with no pain (Y=1) cannot improve, so their mean change must be zero.  Patients starting at Y=5 have the most opportunity to improve, so their mean change will be large.  A treatment that improves pain scores by an average of one point may average a two point improvement for patients for whom any improvement is possible.  Stating mean changes out of context of the baseline state can be meaningless.

The NEJM paper Treatment of Endometriosis-Associated Pain with Elagolix, an Oral GnRH Antagonist by Hugh Taylor et al is based on a disastrous set of analyses, combining all the problems above. The authors computed change from baseline on variables that do not have the correct properties for subtraction, engaged in dichotomania by doing responder analysis, and in addition used last observation carried forward to handle dropouts. A proper analysis would have been a longitudinal analysis using all available data that avoided imputation of post-dropout values and used raw measurements as the responses. Most importantly, the twin clinical trials randomized 872 women, and had proper analyses been done the required sample size to achieve the same power would have been far less. Besides the ethical issue of randomizing an unnecessarily large number of women to inferior treatment, the approach used by the investigators maximized the cost of these positive trials.

The NEJM paper Oral Glucocorticoid–Sparing Effect of Benralizumab in Severe Asthma by Parameswaran Nair et al not only takes the problematic approach of using change scores from baseline in a parallel group design but they used percent change from baseline as the raw data in the analysis. This is an asymmetric measure for which arithmetic doesn't work. For example, suppose that one patient increases from 1 to 2 and another decreases from 2 to 1. The corresponding percent changes are 100% and -50%. The overall summary should be 0% change, not +25% as found by taking the simple average. Doing arithmetic on percent change can essentially involve adding ratios; ratios that are not proportions are never added; they are multiplied. What was needed was an analysis of covariance of raw oral glucocorticoid dose values adjusted for baseline after taking an appropriate transformation of dose, or using a more robust transformation-invariant ordinal semi-parametric model on the raw follow-up doses (e.g., proportional odds model).

In Trial of Cannabidiol for Drug-Resistant Seizures in the Dravet Syndrome in NEJM 2017-05-25, Orrin Devinsky et al take seizure frequency, which might have a nice distribution such as the Poisson, and compute its change from baseline, which is likely to have a hard-to-model distribution. Once again, authors failed to recognize that the purpose of a parallel group design is to compare the parallel groups. Then the authors engaged in improper subtraction, improper use of percent change, dichotomania, and loss of statistical power simultaneously: "The percentage of patients who had at least a 50% reduction in convulsive-seizure frequency was 43% with cannabidiol and 27% with placebo (odds ratio, 2.00; 95% CI, 0.93 to 4.30; P=0.08)." The authors went on to analyze the change in a discrete ordinal scale, where change (subtraction) cannot have a meaning independent of the starting point at baseline.

Troponins (T) are myocardial proteins that are released when the heart is damaged. A high-sensitivity T assay is a high-information cardiac biomarker used to diagnose myocardial infarction and to assess prognosis. I have been hoping to find a well-designed study with standardized serially measured T that is optimally analyzed, to provide answers to the following questions:

1. What is the shape of the relationship between the latest T measurement and time until a clinical endpoint?
2. How does one use a continuous T to estimate risk?
3. If T were measured previously, does the previous measurement add any predictive information to the current T?
4. If both the earlier and current T measurement are needed to predict outcome, how should they be combined? Is what's important the difference of the two? Is it the ratio? Is it the difference in square roots of T?
5. Is the 99^th percentile of T for normal subjects useful as a prognostic threshold?

The 2017-05-16 Circulation paper Serial Measurement of High-Sensitivity Troponin I and Cardiovascular Outcomes in Patients With Type 2 Diabetes Mellitus in the EXAMINE Trial by Matthew Cavender et al was based on a well-designed cardiovascular safety study of diabetes in which uniformly measured high-sensitivity troponin I measurements were made at baseline and six months after randomization to the diabetes drug Alogliptin. [Note: I was on the DSMB for this study] The authors nicely envisioned a landmark analysis based on six-month survivors. But instead of providing answers to the questions above, the authors engaged in dichotomania and never checked whether changes in T or changes in log T possessed the appropriate properties to be used as a valid change score, i.e., they did not plot change in T vs. baseline T or log T ratio vs. baseline T and demonstrate a flat line relationship. Their statistical analysis used statistical methods from 50 years ago, even doing the notorious "test for trend" that tests for a linear correlation between an outcome and an integer category interval number. The authors seem to be unaware of the many flexible tools developed (especially starting in the mid 1980s) for statistical modeling that would answer the questions posed above.

Cavender et all stratified T in <1.9 ng/L, 1.9-<10 ng/L, 10-<26 ng/L, and ≥26 ng/L. Fully 1/2 of the patients were in the second interval. Except for the first interval (T below the lower detection limit) the groups are heterogeneous with regard to outcome risks. And there are no data from this study or previous studies that validates these cutpoints. To validate them, the relationship between T and outcome risk would have to be shown to be discontinuous at the cutpoints, and flat between them.

From their paper we still don't know how to use T continuously, and we don't know whether baseline T is informative once a clinician has obtained an updated T. The inclusion of a 3-D block diagram in the supplemental material is symptomatic of the data presentation problems in this paper.

It's not as though T hasn't been analyzed correctly. In a 1996 NEJM paper, Ohman et al used a nonparametric smoother to estimate the continuous relationship between T and 30-day risk. Instead, Cavender, et al created arbitrary heterogeneous intervals of both baseline and 6m T, then created various arbitrary ways to look at change from baseline and its relationship to risk.

An analysis that would have answered my questions would have been to

1. Fit a standard Cox proportional hazards time-to-event model with the usual baseline characteristics
2. Add to this model a tensor spline in the baseline and 6m T levels, i.e., a smooth 3-D relationship between baseline T, 6m T, and log hazard, allowing for interaction, and restricting the 3-D surface to be smooth. See for example BBR Figure 4.23. One can do this by using restricted cubic splines in both T's and by computing cross-products of these terms for the interactions. By fitting a flexible smooth surface, the data would be able to speak for themselves without imposing linearity or additivity assumptions and without assuming that change or change in log T is how these variables combine.
3. Do a formal test of whether baseline T (as either a main effect or as an effect modifier of the 6m T effect, i.e., interaction effect) is associated with outcome when controlling for 6m T and ordinary baseline variables
4. Quantify the prognostic value added by baseline T by computing the fraction of likelihood ratio chi-square due to both T's combined that is explained by baseline T. Do likewise to show the added value of 6m T. Details about these methods may be found in Regression Modeling Strategies, 2^nd edition

Without proper analyses of T as a continuous variable, the reader is left with confusion as to how to really use T in practice, and is given no insight into whether changes are relevant or the baseline T can be ignored with a later T is obtained. In all the clinical outcome studies I've analyzed (including repeated LV ejection fractions and serum creatinines), the latest measurement has been what really mattered, and it hasn't mattered very much how the patient got there.

As long as continuous markers are categorized, clinicians are going to get suboptimal risk prediction and are going to find that more markers need to be added to the model to recover the information lost by categorizing the original markers. They will also continue to be surprised that other researchers find different "cutpoints", not realizing that when things don't exist, people will forever argue about their manifestations.

Improper Subgrouping

The JAMA Internal Medicine Paper Effect of Statin Treatment vs Usual Care on Primary Cardiovascular Prevention Among Older Adults by Benjamin Han et al makes the classic statistical error of attempting to learn about differences in treatment effectiveness by subgrouping rather than by correctly modeling interactions. They compounded the error by not adjusting for covariates when comparing treatments in the subgroups, and even worse, by subgrouping on a variable for which grouping is ill-defined and information-losing: age. They used age intervals of 65-74 and 75+. A proper analysis would have been, for example, modeling age as a smooth nonlinear function (e.g., using a restricted cubic spline) and interacting this function with treatment to allow for a high-resolution, non-arbitrary analysis that allows for nonlinear interaction. Results could be displayed by showing the estimated treatment hazard ratio and confidence bands (y-axis) vs. continuous age (x-axis). The authors' analysis avoids the question of a dose-response relationship between age and treatment effect. A full strategy for interaction modeling for assessing heterogeneity of treatment effect (AKA precision medicine) may be found in the analysis of covariance chapter in Biostatistics for Biomedical Research.

To make matters worse, the above paper included patients with a sharp cutoff of 65 years of age as the lower limit. How much more informative it would have been to have a linearly increasing (in age) enrollment function that reaches a probability of 1.0 at 65y. Assuming that something magic happens at age 65 with regard to cholesterol reduction is undoubtedly a mistake.

Serial Data and Response Trajectories

Serial data (aka longitudinal data) with multiple follow-up assessments per patient presents special challenges and opportunities. My preferred analysis strategy uses full likelihood or Bayesian continuous-time analysis, using generalized least squares or mixed effects models. This allows each patient to have different measurement times, analysis of the data using actual days since randomization instead of clinic visit number, and non-random dropouts as long as the missing data are missing at random. Missing at random here means that given the baseline variables and the previous follow-up measurements the current measurement is missing completely at random. Imputation is not needed.

In the Hypertension July 2017 article Heterogeneity in Early Responses in ALLHAT (Antihypertensive and Lipid-Lowering Treatment to Prevent Heart Attack Trial) by Sanket Dhruva et al, the authors did advanced statistical analysis that is a level above the papers discussed elsewhere in this article. However, their claim of avoiding dichotomania is unfounded. The authors were primarily interested in the relationship between blood pressures measured at randomization, 1m, 3m, 6m with post-6m outcomes, and they correctly envisioned the analysis as a landmark analysis of patients who were event-free at 6m. They did a careful cluster analysis of blood pressure trajectories from 0-6m. But their chosen method assumes that the variety of trajectories falls into two simple homogeneous trajectory classes (immediate responders and all others). Trajectories of continuous measurements, like the continuous measurements themselves, rarely fall into discrete categories with shape and level homogeneity within the categories. The analyses would in my opinion have been better, and would have been simpler, had everything been considered on a continuum.

With landmark analysis we now have 4 baseline measurements: the new baseline (previously called the 6m blood pressure) and 3 historical measurements. One can use these as 4 covariates to predict time until clinical post-6m outcome using a standard time-to-event model such as the Cox proportional hazards model. In doing so, we are estimating the prognosis associated with every possible trajectory and we can solve for the trajectory that yields the best outcome. We can also do a formal statistical test for whether the trajectories can be summarized more simply than with a 4-dimensional construct, e.g., whether the final blood pressure contains all the prognostic information. Besides specifying the model with baseline covariates (in addition to other original baseline covariates), one also has the option of creating a tall and thin dataset with 4 records per patient (if correlations are accounted for, e.g., cluster sandwich or cluster bootstrap covariance estimates) and modeling outcome using updated covariates and possible interactions with time to allow for time-varying blood pressure effects.

A logistic regression trick described in my book Regression Modeling Strategies comes in handy for modeling how baseline characteristics such as sex, age, or randomized treatment relate to the trajectories. Here one predicts the baseline variable of interest using the four blood pressures. By studying the 4 regression coefficients one can see exactly how the trajectories differ between patients grouped by the baseline variable. This includes studying differences in trajectories by treatment with no dichotomization. For example, if there is a significant association (using a composite (chunk) test) between treatment and any of the 4 blood pressures and in the logistic model predicting treatment, that implies that the reverse is true: one or more of the blood pressures is associated with treatment. Suppose for example that a 4 d.f. test demonstrates some association, the 1 d.f. for the first blood pressure is very significant, and the 3 d.f. test for the last 3 blood pressures is not. This would be interpreted as the treatment having an early effect that wears off shortly thereafter. [For this particular study, with the first measurement being made pre-randomization, such a result would indicate failure of randomization and no blood-pressure response to treatment of any kind.] Were the 4 regression coefficients to be negative and in descending order, this would indicate a progressive reduction in blood pressure due to treatment.

Returning to the originally stated preferred analysis when blood pressure is the outcome of interest (and not time to clinical events), one can use generalized least squares to predict the longitudinal blood pressure trends from treatment. This will be more efficient and also allows one to adjust for baseline variables other than treatment. It would probably be best to make the original baseline blood pressure a baseline variable and to have 3 serial measurements in the longitudinal model. Time would usually be modeled continuously (e.g., using a restricted cubic spline function). But in the Dhruva article the measurements were made at a small number of discrete times, so time could be considered a categorical variable with 3 levels.

I have had misgivings for many years about the quality of statistical methods used by the Channing Lab at Harvard, as well as misgivings about the quality of nutritional epidemiology research in general. My misgivings were again confirmed in the 2017-07-13 NEJM publication Association of Changes in Diet Quality with Total and Cause-Specific Mortality by Mercedes Sotos-Prieto et al. There are the usual concerns about confounding and possible alternate explanations, which the authors did not fully deal with (and why did the authors not include an analysis that characterized which types of subjects tended to have changes in their dietary quality?). But this paper manages to combine dichotomania with probably improper change score analysis and hard-to-interpret results. It started off as a nicely conceptualized landmark analysis in which dietary quality scores were measured during both an 8-year and a 16-year period, and these scores were related to total and all-cause mortality following those landmark periods. But then things went seriously wrong. The authors computed change in diet scores from the start to the end of the qualification period, did not validate that these are proper change scores (see above for more about that), and engaged in percentiling as if the number of neighbors with worse diets than you is what predicts your mortality rather than the absolute quality of your own diet. They then grouped the changes into quintile groups without justification, and examined change quantile score group effects in Cox time-to-event models. It is telling that the baseline dietary scores varied greatly over the change quintiles. The authors emphasized the 20-percentile increase in each score when interpreting result. What does that mean? How is it related to absolute diet quality scores?

The high quality dataset available to the authors could have been used to answer real questions of interest using statistical analyses that did not have hidden assumptions. From their analyses we have no idea of how the subjects' diet trajectories affected mortality, or indeed whether then change in diet quality was as important as the most recent diet quality for the subject, ignoring how the subject arrived at that point at the end of the qualification period. What would be an informative analysis? Start with the simpler one: used a smooth tensor spline interaction surface to estimate relative log hazard of mortality, and construct a 3-D plot with initial diet quality on the x-axis, final (landmark) diet quality on the y-axis, and relative log hazard on the z-axis. Then the more in-depth modeling analysis can be done in which one uses multiple measures of diet quality over time and relates the trajectory (its shape, average level, etc.) to hazard of death. Suppose that absolute diet quality was measured at four baseline points. These four variables could be related to outcome and one could solve for the trajectory that was associated with the lowest mortality. For a study that is almost wholly statistical, it is a shame that modern statistical methods appeared to not even be considered. And for heaven's sake analyze the raw diet scales and do not percentile them.

Subjective Ranking of Quality of Research by Subject Matter Area

While being engaged in biomedical research for a few decades and watching reproducibility of research as a whole, I've developed my own ranking of reliability/quality/usefulness of research across several subject matter areas.  This list is far from complete.  Let's start with a subjective list of what I perceive as the areas in which published research is least likely to be both true and useful.  The following list is ordered in ascending order of quality, with the most problematic area listed first. You'll notice that there is a vast number of areas not listed for which I have minimal experience.

Some excellent research is done in all subject areas.  This list is based on my perception of the proportion of publications in the indicated area that are rigorously scientific, reproducible, and useful.

Subject Areas With Least Reliable/Reproducible/Useful Research

1. any area where there is no pre-specified statistical analysis plan and the analysis can change on the fly when initial results are disappointing
2. behavioral psychology
3. studies of corporations to find characteristics of "winners"; regression to the mean kicks in making predictions useless for changing your company
4. animal experiments on fewer than 30 animals
5. discovery genetics not making use of biology while doing large-scale variant/gene screening
6. nutritional epidemiology
7. electronic health record research reaching clinical conclusions without understanding confounding by indication and other limitations of data
8. pre-post studies with no randomization
9. non-nutritional epidemiology not having a fully pre-specified statistical analysis plan [few epidemiology papers use state-of-the-art statistical methods and have a sensitivity analysis related to unmeasured confounders]
10. prediction studies based on dirty and inadequate data
11. personalized medicine
12. biomarkers
13. observational treatment comparisons that do not qualify for the second list (below)
14. small adaptive dose-finding cancer trials (3+3 etc.)

Subject Areas With Most Reliable/Reproducible/Useful Research

The most reliable and useful research areas are listed first.  All of the following are assumed to (1) have a prospective pre-specified statistical analysis plan and (2) purposeful prospective quality-controlled data acquisition (yes this applies to high-quality non-randomized observational research).

1. randomized crossover studies
2. multi-center randomized experiments
3. single-center randomized experiments with non-overly-optimistic sample sizes
4. adaptive randomized clinical trials with large sample sizes
5. physics
6. pharmaceutical industry research that is overseen by FDA
7. cardiovascular research
8. observational research [however only a very small minority of observational research projects have a prospective analysis plan and high enough data quality to qualify for this list]

Some Suggested Remedies

Peer review of research grants and manuscripts is done primarily by experts in the subject matter area under study.  Most journal editors and grant reviewers are not expert in biostatistics.  Every grant application and submitted manuscript should undergo rigorous methodologic peer review by methodologic experts such as biostatisticians and epidemiologists.  All data analyses should be driven by a prospective statistical analysis plan, and the entire self-contained data manipulation and analysis code should be submitted to journals so that potential reproducibility and adherence to the statistical analysis plan can be confirmed.  Readers should have access to the data in most cases and should be able to reproduce all study findings using the authors' code, plus run their own analyses on the authors' data to check robustness of findings.

Medical journals are reluctant to (1) publish critical letters to the editor and (2) retract papers.  This has to change.

In academia, too much credit is still given to the quantity of publications and not to their quality and reproducibility.  This too must change.  The pharmaceutical industry has FDA to validate their research.  The NIH does not serve this role for academia.

Rochelle Tractenberg, Chair of the American Statistical Association Committee on Professional Ethics and a biostatistician at Georgetown University said in a 2017-02-22 interview with The Australian that many questionable studies would not have been published had formal statistical reviews been done.  When she reviews a paper she starts with the premise that the statistical analysis was incorrectly executed.  She stated that "Bad statistics is bad science."

Damage Caused by Classification Accuracy and Other Discontinuous Improper Accuracy Scoring Rules

In this article I discussed the many advantages or probability estimation over classification.  Here I discuss a particular problem related to classification, namely the harm done by using improper accuracy scoring rules.  Accuracy scores are used to drive feature selection, parameter estimation, and for measuring predictive performance on models derived using any optimization algorithm.  For this discussion let Y denote a no/yes false/true 0/1 event being predicted, and let Y=0 denote a non-event and Y=1 the event occurred.

As discussed here and here, a proper accuracy scoring rule is a metric applied to probability forecasts. It is a metric that is optimized when the forecasted probabilities are identical to the true outcome probabilities.  A continuous accuracy scoring rule is a metric that makes full use of the entire range of predicted probabilities and does not have a large jump because of an infinitesimal change in a predicted probability.  The two most commonly used proper scoring rules are the quadratic error measure, i.e., mean squared error or Brier score, and the logarithmic scoring rule, which is a linear translation of the log likelihood for a binary outcome model (Bernoulli trials).  The logarithmic rule gives more credit to extreme predictions that are "right", but a single prediction of 1.0 when Y=0 or 0.0 when Y=1 will result in infinity no matter how accurate were all the other predictions.  Because of the optimality properties of maximum likelihood estimation, the logarithmic scoring rule is in a sense the gold standard, but we more commonly use the Brier score because of its easier interpretation and its ready decomposition into various metrics measuring calibration-in-the-small, calibration-in-the-large, and discrimination.

Classification accuracy is a discontinuous scoring rule.  It implicitly or explicitly uses thresholds for probabilities, and moving a prediction from 0.0001 below the threshold to 0.0001 above the thresholds results in a full accuracy change of 1/N.  Classification accuracy is also an improper scoring rule.  It can be optimized by choosing the wrong predictive features and giving them the wrong weights.  This is best shown by a simple example that appears in Biostatistics for Biomedical Research Chapter 18 in which 400 simulated subjects have an overall fraction of Y=1 of 0.57. Consider the use of  binary logistic regression to predict the probability that Y=1 given a certain set of covariates, and classify a subject as having Y=1 if the predicted probability exceeds 0.5.  We simulate values of age and sex and simulate binary values of Y according to a logistic model with strong age and sex effects; the true log odds of Y=1 are (age-50)*.04 + .75*(sex=m).   Fit four binary logistic models in order: a model containing only age as a predictor, one containing only sex, one containing both age and sex, and a model containing no predictors (i.e., it only has an intercept parameter).  The results are in the following table:

Both the gold standard likelihood ratio chi-square statistic and the improper pure discrimination c-index (AUROC) indicate that both age and sex are important predictors of Y.  Yet the highest proportion correct (classification accuracy) occurs when sex is ignored.  According to the improper score, the sex variable has negative information.  It is telling that a model that predicted Y=1 for every observation, i.e., one that completely ignored age and sex and only has the intercept in the model, would be 0.573 accurate, only slightly above the accuracy of using sex alone to predict Y.

The use of a discontinuous improper accuracy score such as proportion "classified" "correctly" has led to countless misleading findings in bioinformatics, machine learning, and data science.  In some extreme cases the machine learning expert failed to note that their claimed predictive accuracy was less than that achieved by ignoring the data, e.g., by just predicting Y=1 when the observed prevalence of Y=1 was 0.98 whereas their extensive data analysis yielded an accuracy of 0.97.  As discusssed here, fans of "classifiers" sometimes subsample from observations in the most frequent outcome category (here Y=1) to get an artificial 50/50 balance of Y=0 and Y=1 when developing their classifier.  Fans of such deficient notions of accuracy fail to realize that their classifier will not apply to a population when a much different prevalence of Y=1 than 0.5.

Sensitivity and specificity are one-sided or conditional versions of classification accuracy.  As such they are also discontinuous improper accuracy scores, and optimizing them will result in the wrong model.

Regression Modeling Strategies Chapter 10 goes into more problems with classification accuracy, and discusses many measures of the quality of probability estimates.  The text contains suggested measures to emphasize such as Brier score, pseudo R-squared (a simple function of the logarithmic scoring rule), c-index, and especially smooth nonparametric calibration plots to demonstrate absolute accuracy of estimated probabilities.

My Journey From Frequentist to Bayesian Statistics

Type I error for smoke detector: probability of alarm given no fire=0.05
Bayesian: probability of fire given current air data

Frequentist smoke alarm designed as most research is done:
Set the alarm trigger so as to have a 0.8 chance of detecting an inferno

Advantage of actionable evidence quantification:
Set the alarm to trigger when the posterior probability of a fire exceeds 0.02 while at home and at 0.01 while away

If I had been taught Bayesian modeling before being taught the frequentist paradigm, I'm sure I would have always been a Bayesian.  I started becoming a Bayesian about 1994 because of an influential paper by David Spiegelhalter and because I worked in the same building at Duke University as Don Berry.  Two other things strongly contributed to my thinking: difficulties explaining p-values and confidence intervals (especially the latter) to clinical researchers, and difficulty of learning group sequential methods in clinical trials.  When I talked with Don and learned about the flexibility of the Bayesian approach to clinical trials, and saw Spiegelhalter's embrace of Bayesian methods because of its problem-solving abilities, I was hooked.  [Note: I've heard Don say that he became Bayesian after multiple attempts to teach statistics students the exact definition of a confidence interval.  He decided the concept was defective.]

At the time I was working on clinical trials at Duke and started to see that multiplicity adjustments were arbitrary.  This started with a clinical trial coordinated by Duke in which low dose and high dose of a new drug were to be compared to placebo, using an alpha cutoff of 0.03 for each comparison to adjust for multiplicity.  The comparison of high dose with placebo resulted in a p-value of 0.04 and the trial was labeled completely "negative" which seemed problematic to me. [Note: the p-value was two-sided and thus didn't give any special "credit" for the treatment effect coming out in the right direction.]

I began to see that the hypothesis testing framework wasn't always the best approach to science, and that in biomedical research the typical hypothesis was an artificial construct designed to placate a reviewer who believed that an NIH grant's specific aims must include null hypotheses.  I saw the contortions that investigators went through to achieve this, came to see that questions are more relevant than hypotheses, and estimation was even more important than questions.   With Bayes, estimation is emphasized.  I very much like Bayesian modeling instead of hypothesis testing.  I saw that a large number of clinical trials were incorrectly interpreted when p>0.05 because the investigators involved failed to realize that a p-value can only provide evidence against a hypothesis. Investigators are motivated by "we spent a lot of time and money and must have gained something from this experiment." The classic "absence of evidence is not evidence of absence" error results, whereas with Bayes it is easy to estimate the probability of similarity of two treatments.  Investigators will be surprised to know how little we have learned from clinical trials that are not huge when p>0.05.

I listened to many discussions of famous clinical trialists debating what should be the primary endpoint in a trial, the co-primary endpoint, the secondary endpoints, co-secondary endpoints, etc.  This was all because of their paying attention to alpha-spending.  I realized this was all a game.

I came to not believe in the possibility of infinitely many repetitions of identical experiments, as required to be envisioned in the frequentist paradigm.  When I looked more thoroughly into the multiplicity problem, and sequential testing, and I looked at Bayesian solutions, I became more of a believer in the approach.  I learned that posterior probabilities have a simple interpretation independent of the stopping rule and frequency of data looks.  I got involved in working with the FDA and then consulting with pharmaceutical companies, and started observing how multiple clinical endpoints were handled.  I saw a closed testing procedures where a company was seeking a superiority claim for a new drug, and if there was insufficient evidence for such a claim, they wanted to seek a non-inferiority claim on another endpoint.  They developed a closed testing procedure that when diagrammed truly looked like a train wreck.  I felt there had to be a better approach, so I sought to see how far posterior probabilities could be pushed.  I found that with MCMC simulation of Bayesian posterior draws I could quite simply compute probabilities such as P(any efficacy), P(efficacy more than trivial), P(non-inferiority), P(efficacy on endpoint A and on either endpoint B or endpoint C), and P(benefit on more than 2 of 5 endpoints).  I realized that frequentist multiplicity problems came from the chances you give data to be more extreme, not from the chances you give assertions to be true.

I enjoy the fact that posterior probabilities define their own error probabilities, and that they count not only inefficacy but also harm.  If P(efficacy)=0.97, P(no effect or harm)=0.03.  This is the "regulator's regret", and type I error is not the error of major interest (is it really even an 'error'?).  One minus a p-value is P(data in general are less extreme than that observed if H0 is true) which is the probability of an event I'm not that interested in.

The extreme amount of time I spent analyzing data led me to understand other problems with the frequentist approach.  Parameters are either in a model or not in a model.  We test for interactions with treatment and hope that the p-value is not between 0.02 and 0.2.  We either include the interactions or exclude them, and the power for the interaction test is modest.  Bayesians have a prior for the differential treatment effect and can easily have interactions "half in" the model.  Dichotomous irrevocable decisions are at the heart of many of the statistical modeling problems we have today.  I really like penalized maximum likelihood estimation (which is really empirical Bayes) but once we have a penalized model all of our frequentist inferential framework fails us.  No one can interpret a confidence interval for a biased (shrunken; penalized) estimate.  On the other hand, the Bayesian posterior probability density function, after shrinkage is accomplished using skeptical priors, is just as easy to interpret as had the prior been flat.  For another example, consider a categorical predictor variable that we hope is predicting in an ordinal (monotonic) fashion.  We tend to either model it as ordinal or as completely unordered (using k-1 indicator variables for k categories).  A Bayesian would say "let's use a prior that favors monotonicity but allows larger sample sizes to override this belief."

Now that adaptive and sequential experiments are becoming more popular, and a formal mechanism is needed to use data from one experiment to inform a later experiment (a good example being the use of adult clinical trial data to inform clinical trials on children when it is difficult to enroll a sufficient number of children for the child data to stand on their own), Bayes is needed more than ever.  It took me a while to realize something that is quite profound: A Bayesian solution to a simple problem (e.g., 2-group comparison of means) can be embedded into a complex design (e.g., adaptive clinical trial) without modification.  Frequentist solutions require highly complex modifications to work in the adaptive trial setting.

I met likelihoodist Jeffrey Blume in 2008 and started to like the likelihood approach.  It is more Bayesian than frequentist.  I plan to learn more about this paradigm. 

Several readers have asked me how I could believe all this and publish a frequentist-based book such as Regression Modeling Strategies.  There are two primary reasons.  First, I started writing the book before I knew much about Bayes.  Second, I performed a lot of simulation studies that showed that purely empirical model-building had a low chance of capturing clinical phenomena correctly and of validating on new datasets.  I worked extensively with cardiologists such as Rob Califf, Dan Mark, Mark Hlatky, David Prior, and Phil Harris who give me the ideas for injecting clinical knowledge into model specification.  From that experience I wrote Regression Modeling Strategies in the most Bayesian way I could without actually using specific  Bayesian methods.  I did this by emphasizing subject-matter-guided model specification.  The section in the book about specification of interaction terms is perhaps the best example.  When I teach the full-semester version of my course I interject Bayesian counterparts to many of the techniques covered.

There are challenges in moving more to a Bayesian approach.  The ones I encounter most frequently are:

1. Teaching clinical trialists to embrace Bayes when they already do in spirit but not operationally.  Unlearning things is much more difficult than learning things.
2. How to work with sponsors, regulators, and NIH principal investigators to specify the (usually skeptical) prior up front, and to specify the amount of applicability assumed for previous data.
3. What is a Bayesian version of the multiple degree of freedom "chunk test"?  Partitioning sums of squares or the log likelihood into components, e.g., combined test of interaction and combined test of nonlinearities, is very easy and natural in the frequentist setting.
4. How do we specify priors for complex entities such as the degree of monotonicity of the effect of a continuous predictor in a regression model?  The Bayesian approach to this will ultimately be more satisfying, but operationalizing this is not easy.

With new tools such as Stan and well written accessible books such as Kruschke's it's getting to be easier to be Bayesian each day.  The R brms package, which uses Stan, makes a large class of regression models even more accessible.

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Interactive Statistical Graphics: Showing More By Showing Less

Version 4 of the R Hmisc packge and version 5 of the R rms package interfaces with interactive plotly graphics, which is an interface to the D3 javascript graphics library.  This allows various results of statistical analyses to be viewed interactively, with pre-programmed drill-down information.  More examples will be added here.  We start with a video showing a new way to display survival curves.

Note that plotly graphics are best used with RStudio Rmarkdown html notebooks, and are distributed to reviewers as self-contained (but somewhat large) html files. Printing is discouraged, but possible, using snapshots of the interactive graphics.

Concerning the second bullet point below, boxplots have a high ink:information ratio and hide bimodality and other data features.  Many statisticians prefer to use dot plots and violin plots.  I liked those methods for a while, then started to have trouble with the choice of a smoothing bandwidth in violin plots, and found that dot plots do not scale well to very large datasets, whereas spike histograms are useful for all sample sizes.  Users of dot charts have to have a dot stand for more than one observation if N is large, and I found the process too arbitrary.  For spike histograms I typically use 100 or 200 bins.  When the number of distinct data values is below the specified number of bins, I just do a frequency tabulation for all distinct data values, rounding only when two of the values are very close to each other.  A spike histogram approximately reduces to a rug plot when there are no ties in the data, and I very much like rug plots.

• rms survplotp video: plotting survival curves
• Hmisc histboxp interactive html example: spike histograms plus selected quantiles, mean, and Gini's mean difference - replacement for boxplots - show all the data!  Note bimodal distributions and zero blood pressure values for patients having a cardiac arrest.

A Litany of Problems With p-values

In my opinion, null hypothesis testing and p-values have done significant harm to science.  The purpose of this note is to catalog the many problems caused by p-values.  As readers post new problems in their comments, more will be incorporated into the list, so this is a work in progress.

The American Statistical Association has done a great service by issuing its Statement on Statistical Significance and P-values.  Now it's time to act.  To create the needed motivation to change, we need to fully describe the depth of the problem.

It is important to note that no statistical paradigm is perfect.  Statisticians should choose paradigms that solve the greatest number of real problems and have the fewest number of faults.  This is why I believe that the Bayesian and likelihood paradigms should replace frequentist inference.

Consider an assertion such as "the coin is fair", "treatment A yields the same blood pressure as treatment B", "B yields lower blood pressure than A", or "B lowers blood pressure at least 5mmHg before A."  Consider also a compound assertion such as "A lowers blood pressure by at least 3mmHg and does not raise the risk of stroke."

A. Problems With Conditioning

1. p-values condition on what is unknown (the assertion of interest; H₀) and do not condition on what is known (the data).
2. This conditioning does not respect the flow of time and information; p-values are backward probabilities.

B. Indirectness

1. Because of A above, p-values provide only indirect evidence and are problematic as evidence metrics.  They are sometimes monotonically related to the evidence (e.g., when the prior distribution is flat) we need but are not properly calibrated for decision making.
2. p-values are used to bring indirect evidence against an assertion but cannot bring evidence in favor of the assertion.  
3. As detailed here, the idea of proof by contradiction is a stretch when working with probabilities, so trying to quantify evidence for an assertion by bringing evidence against its complement is on shaky ground.
4. Because of A, p-values are difficult to interpret and very few non-statisticians get it right.  The best article on misinterpretations I've found is here.

C. Problem Defining the Event Whose Probability is Computed

1. In the continuous data case, the probability of getting a result as extreme as that observed with our sample is zero, so the p-value is the probability of getting a result more extreme than that observed.  Is this the correct point of reference?
2. How does more extreme get defined if there are sequential analyses and multiple endpoints or subgroups?  For sequential analyses do we consider planned analyses are analyses intended to be run even if they were not?

D. Problems Actually Computing p-values

1. In some discrete data cases, e.g., comparing two proportions, there is tremendous disagreement among statisticians about how p-values should be calculated.  In a famous 2x2 table from an ECMO adaptive clinical trial, 13 p-values have been computed from the same data, ranging from 0.001 to 1.0.  And many statisticians do not realize that Fisher's so-called "exact" test is not very accurate in many cases.
2. Outside of binomial, exponential, and normal (with equal variance) and a few other cases, p-values are actually very difficult to compute exactly, and many p-values computed by statisticians are of unknown accuracy (e.g., in logistic regression and mixed effects models). The more non-quadratic the log likelihood function the more problematic this becomes in many cases. 
3. One can compute (sometimes requiring simulation) the type-I error of many multi-stage procedures, but actually computing a p-value that can be taken out of context can be quite difficult and sometimes impossible.  One example: one can control the false discovery probability (incorrectly usually referred to as a rate), and ad hoc modifications of nominal p-values have been proposed, but these are not necessarily in line with the real definition of a p-value.

E. The Multiplicity Mess

1. Frequentist statistics does not have a recipe or blueprint leading to a unique solution for multiplicity problems, so when many p-values are computed, the way they are penalized for multiple comparisons results in endless arguments.  A Bonferroni multiplicity adjustment is consistent with a Bayesian prior distribution specifying that the probability that all null hypotheses are true is a constant no matter how many hypotheses are tested.  By contrast, Bayesian inference reflects the facts that P(A ∪ B) ≥ max(P(A), P(B)) and P(A ∩ B) ≤ min(P(A), P(B)) when A and B are assertions about a true effect.
2. There remains controversy over the choice of 1-tailed vs. 2-tailed tests.  The 2-tailed test can be thought of as a multiplicity penalty for being potentially excited about either a positive effect or a negative effect of a treatment.  But few researchers want to bring evidence that a treatment harms patients; a pharmaceutical company would not seek a licensing claim of harm.  So when one computes the probability of obtaining an effect larger than that observed if there is no true effect, why do we too often ignore the sign of the effect and compute the (2-tailed) p-value?
3. Because it is a very difficult problem to compute p-values when the assertion is compound, researchers using frequentist methods do not attempt to provide simultaneous evidence regarding such assertions and instead rely on ad hoc multiplicity adjustments.
4. Because of A1, statistical testing with multiple looks at the data, e.g., in sequential data monitoring, is ad hoc and complex.  Scientific flexibility is discouraged.  The p-value for an early data look must be adjusted for future looks.  The p-value at the final data look must be adjusted for the earlier inconsequential looks.  Unblinded sample size re-estimation is another case in point.  If the sample size is expanded to gain more information, there is a multiplicity problem and some of the methods commonly used to analyze the final data effectively discount the first wave of subjects.  How can that make any scientific sense?
5. Most practitioners of frequentist inference do not understand that multiplicity comes from chances you give data to be extreme, not from chances you give true effects to be present.

F. Problems With Non-Trivial Hypotheses

1. It is difficult to test non-point hypotheses such as "drug A is similar to drug B".
2. There is no straightforward way to test compound hypotheses coming from logical unions and intersections. 

G. Inability to Incorporate Context and Other Information

1. Because extraordinary claims require extraordinary evidence, there is a serious problem with the p-value's inability to incorporate context or prior evidence.  A Bayesian analysis of the existence of ESP would no doubt start with a very skeptical prior that would require extraordinary data to overcome, but the bar for getting a "significant" p-value is fairly low. Frequentist inference has a greater risk for getting the direction of an effect wrong (see here for more).
2. p-values are unable to incorporate outside evidence.  As a converse to 1, strong prior beliefs are unable to be handled by p-values, and in some cases the results in a lack of progress.  Nate Silver in The Signal and the Noise beautifully details how the conclusion that cigarette smoking causes lung cancer was greatly delayed (with a large negative effect on public health) because scientists (especially Fisher) were caught up in the frequentist way of thinking, dictating that only randomized trial data would yield a valid p-value for testing cause and effect.  A Bayesian prior that was very strongly against the belief that smoking was causal is obliterated by the incredibly strong observational data.  Only by incorporating prior skepticism could one make a strong conclusion with non-randomized data in the smoking-lung cancer debate.
3. p-values require subjective input from the producer of the data rather than from the consumer of the data.

H. Problems Interpreting and Acting on "Positive" Findings

1. With a large enough sample, a trivial effect can cause an impressively small p-value (statistical significance ≠ clinical significance).
2. Statisticians and subject matter researchers (especially the latter) sought a "seal of approval" for their research by naming a cutoff on what should be considered "statistically significant", and a cutoff of p=0.05 is most commonly used.  Any time there is a threshold there is a motive to game the system, and gaming (p-hacking) is rampant.  Hypotheses are exchanged if the original H₀ is not rejected, subjects are excluded, and because statistical analysis plans are not pre-specified as required in clinical trials and regulatory activities, researchers and their all-too-accommodating statisticians play with the analysis until something "significant" emerges.
3. When the p-value is small, researchers act as though the point estimate of the effect is a population value.
4. When the p-value is small, researchers believe that their conceptual framework has been validated.  

I. Problems Interpreting and Acting on "Negative" Findings

1. Because of B2, large p-values are uninformative and do not assist the researcher in decision making (Fisher said that a large p-value means "get more data").