Impact of selection bias in experiments where people treat each other

20 Jun

Selection biases in the participant pool generally have limited impact on inference. One way to estimate population treatment effect from effects estimated using biased samples is to check if treatment effect varies by ‘kinds of people’, and then weight the treatment effect to population marginals. So far so good.

When people treat each other, selection biases in participant pool change the nature of the treatment. For instance, in a Deliberative Poll, a portion of the treatment is other people. Naturally then, the exact treatment depends on the pool of people. Biases in the initial pool of participants mean treatment is different. For inference, one may exploit across group variation in composition.

Sampling on M-Turk

13 Oct

In many of the studies that use M-Turk, there appears to be little strategy to sampling. A study is posted (and reposted) on M-Turk till a particular number of respondents take the study. If the pool of respondents reflects true population proportions, if people arrive in no particular order, and all kinds of people find the monetary incentive equally attractive, the method should work well. There is reasonable evidence to suggest that at least points 1 and 3 are violated. One costly but easy fix for the third point is to increase payment rates. We can likely do better.

If we are agnostic about variable on which we want precision, here’s one way to sample: Start with a list of strata, and their proportions in the population of interest. If the population of interest is sample of US adults, the proportions are easily known. Set up screening questions, and recruit. Raise price to get people in cells that are running short. Take simple precautions. For one, to prevent gaming, do not change the recruitment prompt to let people know that you want X kinds of people.

On balance, let there be imbalance on observables

27 Sep

For whatever reason, some people are concerned with imbalance when analyzing data from randomized experiments. The concern may be more general, but its fixes devolve into reducing imbalance on observables. Such fixes may fix things or break things. More generally, it is important to keep in mind what one experiment can show. If randomization is done properly, and other assumptions hold, the most common estimator of experiment effects – difference in means – is unbiased. We also have a good idea of how often the true estimate will be in the bounds. For tightening those bounds, relying on sample size is the way to go. General rules apply. Larger is better. But some refinements to that general rule. When everyone/thing is the same – for instance, neutrons* (in most circumstances) – and if measurement error isn’t a concern, samples of 1 will do just fine. The point holds for a potentially easier to obtain case than everybody/thing being same – when treatment effect is constant across things/people. When everyone is different w.r.t treatment effect, randomization won’t help. Though one can always try to quantify the difference. More generally, sample size required for a particular level of balance is greater, greater the heterogeneity. Stratified random assignment (or blocking) will help. This isn’t to say that raw difference estimator will be biased. It won’t. Just that variance will be higher.

* Based on discussion in Gerber and Green on why randomization is often not necessary in physics.

Why Were the Polls so Accurate?

16 Nov

The Quant. Interwebs have overflowed with joy since the election. Poll aggregation works. And so indeed does polling, though you won’t hear as much about it on the news, which is likely biased towards celebrity intellects than the hardworking many. But why were the polls so accurate?

One potential explanation: because they do some things badly. For instance, most fail at collecting “random samples” these days, because of a fair bit of nonresponse bias. This nonresponse bias, if correlated with the propensity to vote, may actually push up the accuracy of the vote choice means. There are a few ways to check this theory.

One way to check this hypothesis: were the results from polls using Likely Voter screens different from those not using them? If not, why not? From the Political Science literature, we know that people who vote (not just those who say they vote) do vary a bit from those who do not vote, even on things like vote choice. For instance, there is just a larger proportion of `independents’ among them.

Other kinds of evidence will be in the form of failure to match population or other benchmarks. For instance, election polls would likely fare poorly when predicting how many people voted in each state. Or tallying up Spanish language households or number of registered. Another way of saying this is that the bias will vary by what parameter we aggregate from these polling data.

So let me reframe the question: how do polls get election numbers right even when they undercount Spanish speakers? One explanation is that there is a positive correlation between selection into polling, and propensity to vote, which makes vote choice means much more reflective of what we will see come election day.

The other possible explanation to all this – post-stratification or other posthoc adjustment to numbers, or innovations in how sampling is done: matching, stratification etc. Doing so uses additional knowledge about the population and can shrink s.e.s and improve accuracy. One way to test such non-randomness: over tight confidence bounds. Many polls tend to do wonderfully on multiple uncorrelated variables, for instance, census region proportions, gender, … etc., something random samples cannot regularly produce.

Randomly Redistricting More Efficiently

25 Sep

In a forthcoming article, Chen and Rodden estimate the effect of ‘Unintentional gerrymandering’ on number of seats that go to a particular party. To do so they pick a precinct at random, and then add (randomly chosen) adjacent precincts to it till the district is of a certain size (decided by the total number of districts one wants to create). Then they go about creating a new district in the same manner, randomly selecting a precinct bordering the first district. This goes on till all the precincts are assigned to a district. There are some additional details but they are immaterial to the point of the note. A smarter way to do the same thing would be to just create one district over and over again (starting with a randomly chosen precinct). This would reduce the computational burden (memory for storing edges, differencing shapefiles, etc.) while leaving estimates unchanged.

A Potential Source of Bias in Estimating the Impact of Televised Campaign Ads

16 Aug

Or When Treatment is Strategic, No-Intent-to-Treat Intent-to-Treat Effects can be biased

One popular strategy for estimating the impact of televised campaign ads is by exploiting ‘accidental spillover’ (see Huber and Arceneaux 2007). The identification strategy builds on the following facts: Ads on local television can only be targeted at the DMA level. DMAs sometimes span multiple states. Where DMAs span battleground and non-battleground states, ads targeted for residents of battleground states are seen by those in non-battleground states. In short, people in non-battleground states are ‘inadvertently’ exposed to the ‘treatment’. Behavior/Attitudes etc. of the residents who were inadvertently exposed are then compared to those of other (unexposed) residents in those states. The benefit of this identification strategy is that it allows television ads to be decoupled from the ground campaign and other campaign activities, such as presidential visits (though people in the spillover region are exposed to television coverage of the visits). It also decouples ad exposure etc. from strategic targeting of the people based on characteristics of the battleground DMA etc. There is evidence that content, style, the volume, etc. of television ads is ‘context aware’ – varies depending on what ‘DMA’ they run in etc. (After accounting for cost of running ads in the DMA, some variation in volume/content etc. across DMAs within states can be explained by partisan profile of the DMA, etc.)

By decoupling strategic targeting from message volume and content, we only get an estimate of the ‘treatment’ targeted dumbly. If one wants an estimate of ‘strategic treatment’, such quasi-experimental designs relying on accidental spillover may be inappropriate. How to estimate then the impact of strategically targeted televised campaign ads: first estimate how ads are targeted depending on area and people (Political interest moderates the impact of political ads [see for e.g. Ansolabehere and Iyengar 1995]) characteristics, next estimate effect of messages using the H/A strategy, and then re-weight the effect using estimates of how the ad is targeted.

One can also try to estimate the effect of ‘strategy’ by comparing adjusted treatment effect estimates in DMAs where treatment was targeted vis-a-vis (captured by regressing out other campaign activity) and where it wasn’t.

Sample This

1 Aug

What do single shot evaluations of MT (replace it with anything else) samples (vis-a-vis census figures) tell us? I am afraid very little. Inference rests upon knowledge of the data (here – respondent) generating process. Without a model of the data generating process, all such research reverts to modest tautology – sample A was closer to census figures than sample B on parameters X,Y, and Z. This kind of comparison has a limited utility: as a companion for substantive research. However, it is not particularly useful if we want to understand the characteristics of the data generating process. For even if respondent generation process is random, any one draw (here – sample) can be far from the true population parameter(s).

Even with lots of samples (respondents), we may not be able to say much if the data generation process is variable. Where there is little expectation that the data generation process will be constant, and it is hard to understand why MT respondent generation process for political surveys will be a constant one (it likely depends on the pool of respondents, which in turn perhaps depends on the economy etc., the incentives offered, the changing lure of incentives, the content of the survey, etc.), we cannot generalize. Of course one way to correct for all of that is to model this variation in the data generating process, but that will require longer observational spans, and more attention to potential sources of variation etc.

Representativeness Heuristic, Base Rates, and Bayes

23 Apr

From the Introduction of their edited volume:
Tversky and Kahneman used the following experiment for testing ‘representativeness heuristic’ –

Subjects are shown a brief personality description of several individuals, sampled at random from 100 professionals – engineers and lawyers.
Subjects are asked to assess whether the description is of an engineer or a lawyer.
In one condition, subjects are told group = 70 engineers/30 lawyers. Another the reverse = 70 lawyers/30 engineers.

Results –
Both conditions produced same mean probability judgments.

Discussion:
Tversky and Kahneman call this result a ‘sharp violation’ of Bayes Rule.

Counterpoint:
I am not sure the experiment shows any such thing. Mathematical formulation of the objection is simple and boring so an example. Imagine, there are red and black balls in an urn. Subjects are asked if the ball is black or red under two alternate descriptions of the urn composition. When people are completely sure of the color, the urn composition obviously should have no effect. Just because there is one black ball in the urn (out of say a 100), it doesn’t mean that the person will start thinking that the black ball in her hand is actually red. So on and so forth. One wants to apply Bayes by accounting for uncertainty. People are typically more certain (lots of evidence it seems – even in their edited volume) so that automatically discounts urn composition. People may not be violating Bayes Rule. They may just be feeding the formula incorrect data.

Correcting for Differential Measurement Error in Experiments

14 Feb

Differential measurement error across control and treatment groups or in a within-subjects experiment, pre- and post-treatment measurement waves, can vitiate estimates of treatment effect. One reason for differential measurement error in surveys is differential motivation. For instance, if participants in the control group (pre-treatment survey) are less motivated to respond accurately than participants in the treatment group (post-treatment survey), the difference in means estimator will be a biased estimator of the treatment effect. For example, in Deliberative Polls, participants acquiesce more during the pre-treatment survey than the post-treatment survey (Weiksner, 2008). To correct for it, one may want to replace agree/disagree responses with construct specific questions (Weiksner, 2008). Perhaps a better solution would be to incentivize all (or a random subset of) responses to the pre-treatment survey. Possible incentives include – monetary rewards, adding a preface to the screens telling people how important accurate responses are to research, etc. This is the same strategy that I advocate for dealing with satisficing more generally (see here) – which translates to minimizing errors, than the more common, more suboptimal strategy of “balancing errors” by randomizing the response order.

Against Proxy Variables

23 Dec

Lacking direct measures of the theoretical variable of interest, some rely on “proxy variables.” For instance, some have used years of education as a proxy for cognitive ability. However, using “proxy variables” can be problematic for the following reasons — (1) proxy variables may not track the theoretical variable of interest very well, (2) they may track other confounding variables, outside the theoretical variable of interest. For instance, in the case of years of education as a proxy for cognitive ability, the concerns manifest themselves as follows:

  1. Cognitive ability causes, and is a consequence of, what courses you take, and what school you go to, in addition to, of course, years of education. GSS, for instance, contains more granular measures of education, for instance, did the respondent take a science course in college. And nearly always the variable proves significant when predicting knowledge, etc. This all is somewhat surmountable as it can be seen as measurement error.
  2. More problematically, years of education may tally other confounding variables – diligence, education of parents, economic strata, etc. And then education endows people with more than cognitive ability; it also causes potentially confounding variables such as civic engagement, knowledge, etc.

Conservatively we can only attribute the effect of the variable to the variable itself. That is – we only have variables we enter. If one does rely on proxy variables then one may want to address the two points mentioned above.