James Lind (1753), A treatise of the scurvy – key excerpts

Excerpts from the Lind (1753), with help on the ye olde English from others who have quoted him (Hughes, 1975; Bartholomew, 2002; Weber & De Vreese, 2005).

Lind’s study is sometimes presented as an RCT, but it’s not clear how his patients were assigned to groups, just that the cases “were as similar as I could have them” (see discusison in Weber & De Vreese, 2005). Bartholomew (2002) argues that Lind was convinced scurvy was a disease of the digestive system and warns against quoting the positive outcomes for oranges and lemons (and cider) out of the broader context of Lind’s other work.

Here’s what Lind said he did:

“On the 20th May, 1747, I took twelve patients in the scurvy on board the Salisbury at sea. Their cases were as similar as I could have them. They all in general had putrid gums, the spots and lassitude, with weakness of their knees. They lay together in one place, being a proper apartment for the sick in the fore-hold; and had one diet in common to all, viz., water gruel sweetened with sugar in the morning; fresh mutton broth often times for dinner; at other times puddings, boiled biscuit with sugar etc.; and for supper barley, raisins, rice and currants, sago and wine, or the like.”

Groups (n = 2 in each):

  • “ordered each a quart of cyder a day”
  • “twenty five gutts of elixir vitriol three times a day upon an empty stomach, using a gargle strongly acidulated with it for their mouths.”
  • “two spoonfuls of vinegar three times a day upon an empty stomach”
  • “a course of sea water”
  • “two oranges and one lemon given them every day. These they eat with greediness”
  • “The two remaining patients took the bigness of a nutmeg three times a day of an electuray recommended by an hospital surgeon made of garlic, mustard seed, rad. raphan., balsam of Peru and gum myrrh, using for common drink barley water well acidulated with tamarinds, by a decoction of which, with the addition of cremor tartar, they were gently purged three or four times during the course”

Excerpt from the study outcomes:

  • “The consequence was that the most sudden and visible good effects were perceived from the use of the oranges and lemons; one of those who had taken them, being at the end of six days fit for duty”
  • “Next to the oranges, I thought the cyder had the best effects”


Bartholomew, M. (2002). James Lind’s Treatise of the Scurvy (1753). Postgraduate Medical Journal, 78, 695–696.

Hughes, R. E. (1975). James Lind and the cure of Scurvy: An experimental approach. Medical History, 19(4), 342–351.

Weber, E., & De Vreese, L. (2005). The causes and cures of scurvy. How modern was James Lind’s methodology? Logic and Logical Philosophy, 14(1), 55–67.

Inside every matching study

A potentially useful one-sentence(!) intervention for making a case to run a statistical matching evaluation rather than a randomised controlled trial:

“Matching can be thought of as a technique for finding approximately ideal experimental data hidden within an observational data set.”

– King, G., & Nielsen, R. (2019, p. 442) [Why Propensity Scores Should Not Be Used for Matching. Political Analysis, 27(4), 435–454]


What is a confounder?

‘We thus proposed that a pre-exposure covariate C be considered a confounder for the effect of A on Y if there exists a set of covariates X such that the effect of the exposure on the outcome is unconfounded conditional on (X, C) but for no proper subset of (X, C) is the effect of the exposure on the outcome unconfounded given the subset.’ (VanderWeele & Shpitser, 2013, p. 215)

VanderWeele, T. J., & Shpitser, I. (2013). On the definition of a confounder. The Annals of Statistics, 41(1), 196–220.

Estimating causal effects with optimization-based methods

Cousineau et al. (2023) compared seven optimisation-based methods for estimating causal effects, using 7700 datasets from the 2016 Atlantic Causal Inference competition. These datasets use real covariates with simulated treatment assignment and response functions, so it’s real-world-inspired data, with the advantage that the true effect (here, sample average treatment effect; SATT) is known. See the supplementary material of Dorie et al.’s (2019) paper for more info on how the sims were setup.

The methods they compared were:

Method R package Function used
Approximate residual balancing (ARB) balanceHD 1.0 residualBalance.ate
Covariate balancing propensity score (CBPS) CBPS 0.21 CBPS
Entropy balancing (EBal) ebal 0.1–6 ebalance
Genetic matching (GenMatch) Matching 4.9–9 GenMatch
Kernel balancing (KBal) kbal 0.1 kbal
Stable balancing weights (SBW) sbw 1.1.1 sbw

I’m hearing entropy balancing discussed a lot, so had my eye on this.

Bias was the estimated SATT minus true SATT (i.e., the +/- sign was kept; I’m not sure what to make of that when averaging biases from analyses of multiple datasets). The root-mean-square error (RMSE) squares the bias from each estimate first, removing the sign, before averaging and square rooting, which seems easier to interpret.

Findings below. N gives the number of datasets out of 7700 where SATT could be estimated; red where my eyebrows were raised and pink for entropy balancing and its RMSE:

    Bias   Time
Method N Mean SD RMSE Mean (sec)
kbal 7700 0.036 0.083 0.091 2521.3
balancehd 7700 0.041 0.099 0.107 2.0
sbw 4513 0.041 0.102 0.110 254.9
cbps_exact 7700 0.041 0.105 0.112 6.4
ebal 4513 0.041 0.110 0.117 0.2
cbps_over 7700 0.044 0.117 0.125 17.3
genmatch 7700 0.052 0.141 0.151 8282.4

This particular implementation of entropy balancing failed to find a solution for about 40% of the datasets! Note, however:

“All these optimization-based methods are executed using their default parameters on R 4.0.2 to demonstrate their usefulness when directly used by an applied researcher” (emphasis added).

Maybe tweaking the settings would have improved the success rate. And #NotAllAppliedResearchers 🙂

Below is a comparison with a bunch of other methods from the competition, for which findings were already available on a GitHub repo (see Dorie et al., 2019, Table 2 and 3, for more info on each method).

    Bias   95% CI
Method N Mean SD RMSE coverage (%)
bart on pscore 7700 0.001 0.014 0.014 88.4
bart tmle 7700 0.000 0.016 0.016 93.5
mbart symint 7700 0.002 0.017 0.017 90.3
bart mchains 7700 0.002 0.017 0.017 85.7
bart xval 7700 0.002 0.017 0.017 81.2
bart 7700 0.002 0.018 0.018 81.1
sl bart tmle 7689 0.003 0.029 0.029 91.5
h2o ensemble 6683 0.007 0.029 0.030 100.0
bart iptw 7700 0.002 0.032 0.032 83.1
sl tmle 7689 0.007 0.032 0.032 87.6
superlearner 7689 0.006 0.038 0.039 81.6
calcause 7694 0.003 0.043 0.043 81.7
tree strat 7700 0.022 0.047 0.052 87.4
balanceboost 7700 0.020 0.050 0.054 80.5
adj tree strat 7700 0.027 0.068 0.074 60.0
lasso cbps 7108 0.027 0.077 0.082 30.5
sl tmle joint 7698 0.010 0.101 0.102 58.9
cbps 7344 0.041 0.099 0.107 99.7
teffects psmatch 7506 0.043 0.099 0.108 47.0
linear model 7700 0.045 0.127 0.135 22.3
mhe algorithm 7700 0.045 0.127 0.135 22.8
teffects ra 7685 0.043 0.133 0.140 37.5
teffects ipwra 7634 0.044 0.161 0.166 35.3
teffects ipw 7665 0.042 0.298 0.301 39.0

I’ll leave you to read the original for commentary on this, but check out the RMSE and CI coverage. Linear model is summarised as “Linear model/ordinary least squares”. I assume covariates were just entered as main effects, which is a little unfair. The simulations included non-linearity and diagnostic checks on models, such as partial residual plots, would spot this. Still doesn’t do too badly – better than genetic matching!

Interestingly the RMSE was a tiny bit worse for entropy balancing than for Stata’s teffects psmatch, which in simulations was setup to use nearest-neighbour matching on propensity scores estimated using logistic regression (I presume the defaults – I’m an R user).

The winners were all either regression-based or what the authors called “mixed methods” – in this context meaning some genre of doubly-robust method that combined matching/weighting with regression adjustment. Bayesian additive regression trees (BART) feature towards the best end of the table. These sorts of regression-based methods don’t allow the design phase to be clearly separated from the estimation phase. For matching approaches where this separation is possible, the outcomes data can be held back from analysts until matches are found or weights estimated based only on covariates. Where the analysis also demands access to outcomes, a robust approach is needed, including a highly-specified and published statistical analysis plan and e.g., holding back some data in a training and validation phase before fitting the final model.

No info is provided on CI coverage for the seven optimisation-based methods they tested. This is why (Cousineau et al., 2023, p. 377):

“While some of these methods did provide some functions to estimate the confidence intervals (i.e., balancehd, sbw), these did not work due to the collinearity of the covariates. While it could be possible to obtain confidence intervals with bootstrapping for all methods, we did not pursue this avenue due to the computational resources that would be needed for some methods (e.g., kbal) and to the inferior results in Table 5 that did not warrant such resources.”

It would be interesting to zoom in on a smaller set of options and datasets and perhaps allow some more researcher input on how analyses are carried out.


Cousineau, M., Verter, V., Murphy, S. A., & Pineau, J. (2023). Estimating causal effects with optimization-based methods: A review and empirical comparison. European Journal of Operational Research, 304(2), 367–380.

Dorie, V., Hill, J., Shalit, U., Scott, M., & Cervone, D. (2019). Automated versus Do-It-Yourself Methods for Causal Inference: Lessons Learned from a Data Analysis Competition. Statistical Science, 34(1). 

Variance estimation when matching with replacement

“Matching with replacement induces two types of correlations that must be accounted for when estimating the variance of estimated treatment effects. The first is a within-matched set correlation in outcomes. Matched subjects within the same matched set have similar values of the propensity score. Subjects who have the same value of the propensity score have measured baseline covariates that come from the same multivariate distribution. In the presence of confounding, baseline covariates are related to the outcome. Thus, matched subjects are more likely to have similar outcomes compared to two randomly selected subjects. The second source of correlation is induced by repeated use of control subjects. Failure to account for this correlation and acting as though the matched control subjects were independent observations will likely result in estimated standard errors that are artificially small and estimated confidence intervals that are artificially narrow. Added complexity is introduced by having subjects cross-classified with matched sets such that the same control subject can belong to more than one matched set.”

Austin, P. C., & Cafri, G. (2020, p. 1625). [Variance estimation when using propensity‐score matching with replacement with survival or time‐to‐event outcomes. Statistics in Medicine, 39(11), 1623–1640.]

Baseline balance in experiments and quasi-experiments

Baseline balance is important for both experiments and quasi-experiments, just not in the way researchers sometimes believe. Here are excerpts from three of my favourite discussions of the topic.

Don’t test for baseline imbalance in RCTs. Senn (1994,  p. 1716):

“… the following are two incontrovertible facts about a randomized clinical trial:

1. over all randomizations the groups are balanced;

2. for a particular randomization they are unbalanced.

Now, no ‘[statistically] significant imbalance’ can cause 1 to be untrue and no lack of a significant balance can make 2 untrue. Therefore the only reason to employ such a test must be to examine the process of randomization itself. Thus a significant result should lead to the decision that the treatment groups have not been randomized…”

Do examine baseline imbalance in quasi-experiments; however, not by using statistical tests. Sample descriptives, such as a difference in means, suffice. Imai et al. (2008, p. 497):

“… from a theoretical perspective, balance is a characteristic of the sample, not some hypothetical population, and so, strictly speaking, hypothesis tests are irrelevant…”

Using p-values from t-tests and similar can lead to erroneous decisions of balance. As you prune a dataset to improve balance, power to detect effects decreases. Imai et al. (2008, p. 497 again):

“Since the values of […] hypothesis tests are affected by factors other than balance, they cannot even be counted on to be monotone functions of balance. The t-test can indicate that balance is becoming better whereas the actual balance is growing worse, staying the same or improving. Although we choose the most commonly used t-test for illustration, the same problem applies to many other test statistics…”

If your matching has led to baseline balance, then you’re good, even if the matching model is misspecified. (Though not if you’re missing key covariates, of course.) Rosenbaum (2023, p. 29):

“So far as matching and stratification are concerned, the propensity score and other methods are a means to an end, not an end in themselves. If matching for a misspecified and misestimated propensity score balances x, then that is fine. If by bad luck, the true propensity score failed to balance x, then the match is inadequate and should be improved.”


Imai, K., King, G., & Stuart, E. A. (2008). Misunderstandings between experimentalists and observationalists about causal inference. Journal of the Royal Statistical Society: Series A (Statistics in Society), 171(2), 481–502.

Rosenbaum, P. R. (2023). Propensity score. In J. R. Zubizarreta, E. A. Stuart, D. S. Small, & P. R. Rosenbaum, Handbook of Matching and Weighting Adjustments for Causal Inference (pp. 21–38). Chapman and Hall/CRC.

Senn, S. (1994). Testing for baseline balance in clinical trials. Statistics in Medicine13, 1715–1726.

Evaluating What Works, by Dorothy Bishop and Paul Thompson

“Those who work in allied health professions aim to make people’s lives better. Often, however, it is hard to know how effective we have been: would change have occurred if we hadn’t intervened? Is it possible we are doing more harm than good? To answer these questions and develop a body of knowledge about what works, we need to evaluate interventions.

“As we shall see, demonstrating that an intervention has an impact is much harder than it appears at first sight. There are all kinds of issues that can arise to mislead us into thinking that we have an effective treatment when this is not the case. On the other hand, if a study is poorly designed, we may end up thinking an intervention is ineffective when in fact it is beneficial. Much of the attention of methodologists has focused on how to recognize and control for unwanted factors that can affect outcomes of interest. But psychology is also important: it tells us that own human biases can be just as important in leading us astray. Good, objective intervention research is vital if we are to improve the outcomes of those we work with, but it is really difficult to do it well, and to do so we have to overcome our natural impulses to interpret evidence in biased ways.”

(Over here.)


“Randomista mania”, by Thomas Aston

Thomas Aston provides a helpful summary of RCT critiques, particularly in international evaluations.

Waddington, Villar, and Valentine (2022), cited therein, provide a handy review of comparisons between RCT and quasi-experimental estimates of programme effect.

Aston also cites examples of unethical RCTs. One vivid example is an RCT in Nairobi with an arm that involved threatening to disconnect water and sanitation services if landlords didn’t settle debts.

Dealing with confounding in observational studies

Excellent review of simulation-based evaluations of quasi-experimental methods, by Varga et al. (2022). Also lovely annexes summarising the methods’ assumptions.

Methods for measured confounding the authors cover (Varga et al., 2022, Table A1):

Method Description of the method
PS matching (N = 47) Treated and untreated individuals are matched based on their propensity score-similarity. After creating comparable groups of treated and untreated individuals the effect of the treatment can be estimated.
IPTW (N = 30) With the help of re-weighting by the inverse probability of receiving the treatment, a synthetic sample is created which is representative of the population and in which treatment assignment is independent of the observed baseline covariates. Over-represented groups are downweighted and underrepresented groups are upweighted.
Overlap weights (N = 4) Overlap weights were developed to overcome the limitations of truncation and trimming for IPTW, when some individual PSs approach 0 or 1.
Matching weights (N = 2) Matching weights is an analogue weighting method for IPTW, when some individual PSs approach 0 or 1.
Covariate adjustment using PS (N = 13) The estimated PS is included as covariate in a regression model of the treatment.
PS stratification (N = 26) First the subjects are grouped into strata based upon their PS. Then, the treatment effect is estimated within each PS stratum, and the ATE is computed as a weighted mean of the stratum specific estimates.
GAM (N = 1) GAMs provide an alternative for traditional PS estimation by replacing the linear component of a logistic regression with a flexible additive function.
GBM (N = 3) GBM trees provide an alternative for traditional PS estimation by estimating the function of covariates in a more flexible manner than logistic regression by averaging the PSs of small regression trees.
Genetic matching (N = 7) This matching method algorithmically optimizes covariate balance and avoids the process of iteratively modifying the PS model.
Covariate-balancing PS (N = 5) Models treatment assignment while optimizing the covariate balance. The method exploits the dual characteristics of the PS as a covariate balancing score and the conditional probability of treatment assignment.
DR estimation (N = 13) Combines outcome regression with with a model for the treatment (eg, weighting by the PS) such that the effect estimator is robust to misspecification of one (but not both) of these models.
AIPTW (N = 8) This estimator achieves the doubly-robust property by combining outcome regression with weighting by the PS.
Stratified DR estimator (N = 1) Hybrid DR method of outcome regression with PS weighting and stratification.
TMLE (N = 2) Semi-parametric double-robust method that allows for flexible estimation using (nonparametric) machine-learning methods.
Collaborative TMLE (N = 1) Data-adaptive estimation method for TMLE.
One step joint Bayesian PS (N = 3) Jointly estimates quantities in the PS and outcome stages.
Two-step Bayesian approach (N = 2) A two-step modeling method is using the Bayesian PS model in the first step, followed by a Bayesian outcome model in the second step.
Bayesian model averaging (N = 1) Fully Bayesian model averaging approach.
An’s intermediate approach (N = 2) Not fully Bayesian insofar as the outcome equation in An’s approach is frequentist.
G-computation (N = 4) The method interprets counterfactual outcomes as missing data and uses a prediction model to obtain potential outcomes under different treatment scenarios. The entire set of predicted outcomes is then regressed on the treatment to obtain the coefficient of the effect estimate.
Prognostic scores (N = 7) Prognostic scores are considered to be the prognostic analog of the PS methods. the prognostic score includes covariates based on their predictive power of the response, the PS includes covariates that predict treatment assignment.

Methods for unmeasured confounding (Varga et al., 2022, Table A2):

Method Description of the method
IV approach (N = 17) Post-randomization can be achieved using a sufficiently strong instrument. IV is correlated with the treatment and only affects the outcome through the treatment.
2SLS (N = 11) Linear estimator of the IV method. Uses linear probability for binary outcome and linear regression for continuous outcome.
2SPS (N = 5) Non-parametric estimator of the IV method. Logistic regression is used for both the first and second stages of 2SPS procedure. The predicted or residual values from the first stage logistic regression of treatment on the IV are used as covariates in the second stage logistic regression: the predicted value of treatment replaces the observed treatment for 2SPS.
2SRI (N = 8) Semi-parametric estimator of the IV method. Logistic regression is used for both the first and second stages of the 2SRI procedure. The predicted or residual values from the first stage logistic regression of treatment on the IV are used as covariates in the second stage logistic regression.
IV based on generalized structural mean model (GSMM) (N = 1) Semi-parametric models that use instrumental variables to identify causal parameters. IV approach
Instrumental PS (Matching enhanced IV) (N = 2) Reduces the dimensionality of the measured confounders, but it also deals with unmeasured confounders by the use of an IV.
DiD (N = 7) DiD method uses the assumption that without the treatment the average outcomes for the treated and control groups would have followed parallel trends over time. The design measures the effect of a treatment as the relative change in the outcomes between individuals in the treatment and control groups over time.
Matching combined with DiD (N = 6) Alternative approach to DiD. (2) Uses matching to balance the treatment and control groups according to pre-treatment outcomes and covariates
SCM (N = 7) This method constructs a comparator, the synthetic control, as a weighted average of the available control individuals. The weights are chosen to ensure that, prior to the treatment, levels of covariates and outcomes are similar over time to those of the treated unit.
Imperfect SCM (N = 1) Extension of SCM method with relaxed assumptions that allow outcomes to be functions of transitory shocks.
Generalized SCM (N = 2) Combines SC with fixed effects.
Synthetic DiD (N = 1) Both unit and time fixed effects, which can be interpreted as the time-weighted version of DiD.
LDV regression approach (N = 1) Adjusts for pre-treatment outcomes and covariates with a parametric regression model. Alternative approach to DiD.
Trend-in-trend (N = 1) The trend-in-trend design examines time trends in outcome as a function of time trends in treatment across strata with different time trends in treatment.
PERR (N = 3) PERR adjustment is a type of self-controlled design in which the treatment effect is estimated by the ratio of two rate ratios (RRs): RR after initiation of treatment and the RR prior to initiation of treatment.
PS calibration (N = 1) Combines PS and regression calibration to address confounding by variables unobserved in the main study by using variables observed in a validation study.
RD (N = 4) Method used for policy analysis. People slightly below and above the threshold for being exposed to a treatment are compared.


Varga, A. N., Guevara Morel, A. E., Lokkerbol, J., van Dongen, J. M., van Tulder, M. W., & Bosmans, J. E. (2022). Dealing with confounding in observational studies: A scoping review of methods evaluated in simulation studies with single‐point exposure. Statistics in Medicine.