Category Archives: Statistics

Consider a bank making decisions about loans. For the bank, making lending decisions optimally means reducing prediction errors*(cost of errors) minus the cost of making predictions (Keeping things simple here). The cost of any one particular error — especially, denial of loan when eligible– is typically small for the bank, but very consequential for the applicant. So the applicant may be willing to pay the bank money to increase the accuracy of their decisions. Say, willing to compensate the bank for the cost of getting a person to take a closer look at the file. If customers are willing to pay the cost, accuracy rates can increase without reducing profits. (Under some circumstances, a bank may well be able to increase profits.) Customer’s willingness to pay for increasing accuracy is typically not exploited by the lending institutions. It may be well worth exploring it.

This note is in response to some of the points raised in the Agnoff Lecture by Ed Haertel.

The lecture makes two big points:
1) Teacher effectiveness ratings based on current Value Added Models are ‘unreliable.’ They are actually much worse than just unreliable; see below.
2) Simulated counterfactuals of gains that can be got from ‘firing bad teachers’ are upwardly biased.

Three simple tricks (one discussed; two not) that may solve some of the issues:
1) Estimating teaching effectiveness: Where possible, random assignment of children to classes. I would only do within school comparisons. Inference will still not be clean (SUTVA violations, though they can be dealt with). Simply cleaner.

2) Experiment with teachers. Teach some teachers some skills. Estimate the impact. Rather than teacher level VAM, do a skill level VAM. Teachers = sum of skills + idiosyncratic variation.

3) For current VAMs: To create better student level counterfactuals, use modern ML techniques (SVM, Neural Networks..), lots of data (past student outcomes, past classmate outcomes etc.), cross-validate to tune. Have a good idea about how good the prediction is. The strategy may be applicable to other venues.

Other points:
1) Haertel says, “Obviously, teachers matter enormously. A classroom full of students with no teacher would probably not learn much — at least not much of the prescribed curriculum.” A better comparison perhaps would be to self-guided technology. My sense is that as technology evolves, teachers will come up short in a comparison between teachers and advanced learning tools. In most of the third world, I think it is already true.

2) It appears no model for calculating teacher effectiveness scores yields identified estimates. And it appears we have no clear understanding of the nature of bias. Pooling biased estimates over multiple years doesn’t recommend itself to me as a natural fix to this situation. And I don’t think calling this situation as ‘unreliability’ of scores is right. These scores aren’t valid. The fact that pooling across years ‘works’ may suggest issues are smaller. But then again, bad things may be happening to some kinds of teachers, especially if people are doing cross-school comparisons.

3) Fade-out concern is important given the earlier 5*5 =25 analysis. My suspicion would be that attenuation of effects varies depending on when the timing of the shock. My hunch would be that shocks at an earlier age matter more – they decay slower.

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.

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.

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.

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.

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.

Deliberative Poll proceeds as follows — Respondents are surveyed, provided ‘balanced’ briefing materials, randomly assigned to moderated small group discussions, allowed the opportunity to quiz experts or politicians in plenary sessions, and re-interviewed at the end. The “effect” is conceptualized as average Post–Pre across all participants.

The effect of the Deliberative Poll is contingent upon a particular random assignment to small groups. This isn’t an issue if small group composition doesn’t matter. If it does, then the counterfactual imagination of the ‘informed public’ is somewhat particularistic. Under those circumstances, one may want to come up with a distribution of what opinion change may look like if the assignment of participants to small groups was different. One can do this by estimating the impact of small group composition on the dependent variable of interest and then predicting the dependent variable of interest under simulated alternate assignments.

See also: Adjusting for covariate imbalance in experiments with SUTVA violations

Say there are two datasets—one that carries attitudinal variables, and demographic variables (dataset 1), and another that carries just demographic variables (dataset 2). Also assume that Dataset 2 is the more accurate and larger dataset for demographics (e.g. CPS). Our goal is to weight a dataset (dataset 3) so that it is “closest” to the population at large on both socio-demographic characteristics and attitudinal variables. We can proceed in the following manner: weight Dataset 1 to Dataset 2, and then weight dataset 3 to dataset 1. This will mean multiplying the weights. One may also impute attitudes for the larger dataset (dataset 2), using a prediction model built using dataset 1, and then use the larger dataset to generalize to the population.

Achieving statistical significance is entirely a matter of sample size. In the frequentist world, we can always distinguish between two samples if we have enough data (except of course if the samples are exactly the same). On the other hand, we may fail to reject even large differences when sample sizes are small. For example, over 13 Deliberative Polls (list at the end), the correlation between the proportion of attitude indices showing significant change and size of the participant sample is .81 (rank ordered correlation is .71). This sharp correlation is suggestive evidence that average effect is roughly equal across polls (and hence power matters).

When the conservative thing to do is to the reject the null, for example, in “representativeness” analysis designed to see if the experimental sample is different from control, one may want to go for large sample sizes or say something about substantiveness of differences, or ‘adjust’ results for differences. If we don’t do that samples can look more ‘representative’ as sample size reduces. So for instance, the rank-ordered correlation between proportion significant differences between non-participants and participants, and the size of the smaller sample (participant sample), for the 13 polls is .5. The somewhat low correlation is slightly surprising. It is partly a result of the negative correlation between the size of the participant pool and average size of the differences.

Polls included: Texas Utilities: (CPL, WTU, SWEPCO, HLP, Entergy, SPS, TU, EPE), Europolis 2009, China Zeguo, UK Crime, Australia Referendum, and NIC

Consider the following scenario: control group is 50% female while the participant sample is 60% female. Also, assume that this discrepancy is solely a matter of chance and that the effect of the experiment varies by gender. To estimate the effect of the experiment, one needs to adjust for the discrepancy, which can be done via matching, regression, etc.

If the effect of the experiment depends on the nature of the participant pool, such adjustments won’t be enough. Part of the effect of Deliberative Polls is a consequence of the pool of respondents. It is expected that the pool matters only in small group deliberation. Given people are randomly assigned to small groups, one can exploit the natural variation across groups to estimate how say proportion females in a group impacts attitudes (dependent variable of interest). If that relationship is minimal, no adjustments outside the usual are needed. If, however, there is a strong relationship, one may want to adjust as follows: predict attitudes under simulated groups from a weighted sample, with the probability of selection proportional to the weight. This will give us a distribution — which is correct— as women may be allocated in a variety of ways to small groups.

There are many caveats, beginning with limitations of data in estimating the impact of group characteristics on individual attitudes, especially if effects are heterogeneous. Where proportions of subgroups are somewhat small, inadequate variation across small groups can result.

This procedure can be generalized to a variety of cases where the effect is determined by the participant pool except where each participant interacts with the entire sample (or a large proportion of it). Reliability of the generalization will depend on getting good estimates.