An engine not a camera: Measuring performative power of online search

Thank you for the thoughtful feedback and comments. We hope to provide additional clarification and address your questions in the following.

W1: Source code. The extension has been published in the Chrome store. The code can be inspected using the developer console in the Chrome browser. We did not include the link for anonymity reasons, but we will add it to the final version. If you wish to inspect the code, we uploaded it to an anonymized repository shared with the AC.

W2: Novelty. The core contribution of our work is to take a theoretical concept and provide a first demonstration for how it can be instrumentalized in a practical scenario. A priori it is unclear how to relate performative power to micro experiments that are feasible to perform on digital platforms. Our experimental design together with the required theoretical assumptions outline a possible avenue for doing this. By relating tools from computer science with a policy relevant question at the heart of a major antitrust investigation our work provides a promising interface between regulatory questions and the expertise of the NeurIPS community.

W3: Choice of interventions. Note that the instantiation of the actions set $\mathcal A$ is part of the performative power definition. Different choices are valid, also larger changes, but they lead to different conclusions about power. So it needs to be instantiated carefully in any given context. In our case we care about the effect of actions the platform has implemented in the past (downranking search results and adding visually appealing elements). Our counterfactuals are designed carefully to give us insights into performative power related to these interventions.

As you pointed out it is important not to interleave experiments with treatments that have a disruptive impact on user experience and behavior, as we want to measure the effects of our interventions under natural interactions of users with the platform. Being exposed to one intervention should not impact the behavior for a subsequent query. We make this requirement explicit in Assumption 1. It is also why we refrained from including larger swaps as an additional treatment group, after feedback from an initial testing phase. All our counterfactuals constitute minimal interventions. As you point out, the largest modification we perform is to move the first search results down by two positions. This is comparable to having two Ads on top of the page and it typically does not move the result out of sight. Based on our own experience and feedback from participants there is no evidence that the extension was noticeable by any of the participants.

It is also important to note that modifications are triggered at random. This offers no structure a user could implicitly or explicitly adapt to. The swap 1-3 only happens with probability ⅛ for any user query (including navigational queries), and for 45% of the queries the extension does not swap results. We checked the behavior in the control group by splitting the data collected before and after November 10. The difference in the average click rate for the first result differs in 0.8% across these two groups (the base rate is 43%) which is significantly smaller than the sampling uncertainty. We will think of a more rigorous experiment to add to the appendix to demonstrate that behavior of participants is stable across the duration of the study.

Triggering a4-a6. Arrangements a4-a6 are triggered each with a fixed probability (p=1/6). If there is no content to hide for this query, a5 solely performs a swap and the other interventions leave the website as is. This ensures that treatment assignment is independent of the potential click outcome which is important to obtain unbiased estimates. On aggregate the effect of hiding Ads will naturally be larger if Ads are present more often.

Latency. The latency refers to the time for loading the search page after entering the search query. A technical report on Google [1] could not find any effect for delays below 100ms on search behavior. Similarly, [2] find that “up to a point (500ms) added response time delays are not noticeable by the users.” Our delay of 40ms is below any of these thresholds and thus not expected to impact our results. We will include these references.

Considering a single click only. As you pointed out we are not making a distinction between follow-up searches and new searches. What we measure is the ability of the platform to steer clicks treating all clicks equal. To analyze a different outcome variable, such as a specific type of click, we would have to adjust the experiment accordingly. However, the scenario you mentioned will still meaningfully affect our measurements. If a user returns to click the second result after clicking the first under intervention a1, this will surface as a reduction in the performativity gap. This leads to the interesting observation that performative power is larger in situations where equally relevant results are being ranked.

Participants tend to give the browser plugin the "benefit of the doubt." There is a bias in the selection of participants, as people who trust us in performing a legitimate scientific experiment and take privacy seriously, are more likely to install the extension. But once they have the extension installed, the experiment is randomized at a query level and we can safely assume that they consume Google search in a natural way. There is no structured change they could respond to. We even deleted the data from the first 4 days after onboarding to be on the safe side and avoid potential biases due to participation awareness.

Please clarify if we misunderstood your last questions. But we hope the additional context is helpful.

References:

[1] J. Brutlag. Speed matters for google web search. Online report by Google. 2009. [2] Arapakis et al. Impact of response latency on user behavior in web search. SIGIR. 2014.

Thank you for the positive feedback on our work. In the following we first discuss your questions and then provide some thoughts on the additional comments below.

Applying method to other use cases. This is an interesting point we have not discussed in our work. An important feature of our design is that the complexity of the underlying algorithm does not impact the experimental design. The intervention is implemented at the level of the user interface, rather than the algorithmic system. This means the system does not have to be changed. From a technical viewpoint, changing how results are displayed to users can in principle be applied to any website using a browser extension, independent of how these results are selected by an underlying algorithm. However, one important constraint is that the updates that can be emulated at the display level are limited to the information available on a website. This means, we can swap and hide elements, but not replace them with an alternative that is hidden. Similarly, we can not use any proprietary data the firm might use to determine content allocation. This limits the updates we can emulate. However, for the purpose of lower-bounding performative power, it is sufficient to argue for one feasible update that can be implemented. Evaluating the effect of this update provides a lower bound on the corresponding definition of performative power. Here, the swap of adjacent results usually offers a good proxy for potentially larger updates a firm could implement.

Domains that are harder to study. In light of the constraint mentioned above the design of counterfactuals is harder for settings where the firm offers the user fewer choices, like in the case of the Amazon Buy Box where a single element is selected to be displayed behind a visually appealing button. In such cases natural updates are harder to argue without additional insights into the algorithm, or the alternative options. Large number of items offer the opposite situation which does not seem to be a problem, but we are not entirely sure we understand the question. One interesting aspect of a large number of items is usually that more of them can be relevant, which leads to a stronger effect of ranking and a larger performativity gap. But this would just impact the effect size, not the implementation.

Ecological validity. As the reviewer mentioned, concerns related to ecological validity are unavoidable to some extent. What we can offer is an additional ablation and robustness checks where we remove individual participants from the evaluation to check the sensitivity of the statistics. Results are shown in the supplementary PDF, but error bars are still very small.

Recording query. Thank you for supporting this design choice. Search queries are one of the most sensitive personal data. For our proof of concept it was not necessary to collect this information which is why we refrained from doing it. However, we agree that when inspecting more nuanced policy related questions additional information might be necessary to record, and the benefits may outweigh the privacy costs in a specific case. However, the exact question should come first and guide the corresponding decision. From a technical perspective there is nothing preventing us from recording user queries, we have the information readily available. For a future study we might consider storing an embedding of the search query, but for the current data we simply do not have this information at our disposal.

Why we chose NeurIPS. We agree that this type of experimental work is less typical from the perspective of developing better ranking models. However, from a perspective of causal inference, and algorithmic auditing, directly tackling the measurement problem is quite natural. We also believe that decoupling modeling from empirical measurement is very important for developing investigative tools in the context of AI systems. Modeling behavioral aspects in the interaction of participants with platforms is very complex and this complexity should not prevent us from developing effective monitoring and measurement tools. For additional arguments for why we think our work is interesting for the NeurIPS community and falls under the call for paper can be found in the response to Reviewer 9NWC, but it does not seem that we need to convince you of this.

We hope our rebuttal addresses your questions satisfactorily and we will incorporate additional discussion of the points you raised in a future version.

References

[1] Hardt, Jagadeesan, and Mendler-Dünner. "Performative power." NeurIPS. 2022.

Thank you for the feedback. Let us explain why we see the focus on measurement (rather than qualitative modeling) as an important opportunity of our approach, rather than a weakness.

Qualitative insights. We agree that qualitative insights are highly valuable. However, it is possible to measure and monitor the influence of AI systems on user behavior without the need to understand the complex mechanism behind it. This is an important takeaway of our work in the context of market regulation specifically, as regulators have been struggling with the complexity of digital markets, see e.g., [1]. Our work shows that the complexity to model digital markets should not prevent us from developing effective measurement and monitoring tools.

Countermeasures. Related to the above comment, it is useful to treat measurement separately from the design of countermeasures. Remedies are often context specific and require the balancing of many competing objectives. This goes far beyond measurement. And there are many use cases where measurement is what you primarily care about. This separation is also common in antitrust investigations for example, where there is no need to suggest an effective remedy to run a case. But as a first step towards designing effective remedies, what we can offer is an investigative tool for researchers, regulators, and potentially also platform owners to measure the effectiveness of remedies, as well as setting transparent evaluation criteria.

Sample size. We agree that a larger pool of participants would always strengthen the results, and a larger sample size could be useful specifically to reduce uncertainty on some of the query subset evaluations, where the bootstrap confidence sets are not as tight as for the aggregate results. We can not add additional data at this point, but we have included additional robustness checks in the supplementary PDF, where we evaluate Jackknife error bars with respect to the impact of excluding a random agent from the study. They can not speak to ecological validity, but they can provide an indication for how stable the effect measures are to the observed collection of agents.

References:

[1] Final report: Stigler committee on digital platforms. 2019

Thank you for the feedback. We are glad you enjoyed reading the paper. We hope to clarify your questions by providing additional context related to the comparison points you mentioned. We will incorporate these discussions in the manuscript for a future version.

Other types of biases. As you pointed out, position bias [6], trust bias [4], presentation bias [3], and other behavioral aspects have been shown to impact the effect of ranking on user clicks. In our work we are not interested in pinpointing any mechanism specifically, rather we are interested in directly quantifying the effect of ranking updates on clicks within the context of a given platform (we call this the performativity gap). The different types of biases will naturally enter such a measurement. We argue that it is not necessary to understand all these complex behavioral mechanisms to measure performative power and monitor algorithmic systems.

In that regard a browser extension is very powerful. It serves as a tool to conduct a controlled experiment and measure the effect of specific algorithmic changes under natural interactions of users with the platform. As a result it implicitly captures trust, display, and other behavioral aspects specific to the platform under investigation.

Methodological differences. Information harvesting, and randomization are methods to explicitly or implicitly exploit interventions to the ranking algorithm to measure their effect on clicks. These methods all get at the fundamental problem of causal inference; the effect of ranking can not be measured from click data alone, due to unobserved feedback and biases. Our work is also a way to gather and exploit interventional data. In contrast to prior work, e.g., the work on data harvesting in [2] where the authors consider interventions to the Arxiv ranking algorithm, the Powermeter design performs interventions at the level of the platform-user interface. We emulate updates to the algorithm without actually touching the algorithm underneath. While the observed effect is equivalent to implementing the corresponding change to the algorithm, it allows us to study the Google search algorithm, without controlling it, which is an important methodological novelty. We are not aware of any such experimental design in the literature.

Finally, you mentioned eye-tracking studies. They are designed to measure the allocation of visual attention, e.g., to support the design of click models, such as cascade models [5]. However, they can not replace click statistics, and are complementary to performing the interventions to study.

Discussion of prior quantitative insights. While our study pursues a different goal than estimating parameters of a click model, some of our intermediate experimental insights can be compared to prior work. While we are not aware of comparable studies related to interventions a4-a6, intervention a1-a3 constitute pairwise swaps routinely used to infer propensities in click models. The most relevant comparison point is work by researchers out of Google from 2010 [3, Figure 1] who published click statistics on FairPairs (adjacent swaps [7]) on Google search. They report an average gain in click counts of 75% when ranked first instead of second under swap 1-2, we observe a gain of 82%. For swap 2-3 they report 48% gain, whereas we see a gain of 66%. Thus, while qualitatively similar the effect size in our results is larger. This might be attributed to changes to the website design since 2009, for example, including the introduction of featured snippets that lead to a larger spatial separation between results, and may increase performativity. While this is only a hypothesis, it demonstrates how effects can change over time even for a fixed platform. With Powermeter we offer a method to reassess such effects within the context relevant for a specific investigation. Beyond swaps, we can provide insights into different counterfactuals that have not been studied before, such as the combination of downranking results and adding visually appealing elements, which is relevant in a regulatory context.

Why NeurIPS? We build on a concept of performative power that has its origin in the NeurIPS community [1], and we offer a first account of its practical applicability which we see as an important contribution to the area of “Social and economic aspects of machine learning" referred to in the CFP. Focusing on neural systems in a broader context is not uncommon for NeurIPS, see work related to auditing and regulation. Similarly, citing again from the CFP: "Machine learning is a rapidly evolving field, and so we welcome interdisciplinary submissions that do not fit neatly into existing categories." While we understand that this is subjective, there is an easy case to be made for why our work is in scope, accessible and relevant for the broader NeurIPS audience. In any case, we believe that the AC/SAC can ultimately make an executive decision about this and we would appreciate if this could be treated independent from the assessment of the quality of our work.

References

[1] Hardt, Jagadeesan, Mendler-Dünner. "Performative power." NeurIPS. 2022.

[2] Fang, Agarwal, Joachims. “Intervention Harvesting for Context-Dependent Examination-Bias Estimation”. SIGIR. 2019.

[3] Yue, Patel, Roehrig. “Beyond Position Bias: Examining Result Attractiveness As a Source of Presentation Bias in Clickthrough Data.” WWW. 2010.

[4] O’Brien, Keane. “Modeling result–list searching in the World Wide Web: The role of relevance topologies and trust bias.” CogSci. 2008.

[5] Craswell, Zoeter, Taylor, Ramsey. “An Experimental Comparison of Click Position-bias Models”. WSDM. 2008.

[6] Joachims et al. “Evaluating the accuracy of implicit feedback from clicks and query reformulations in web search”. TOIS. 2007.

[7] Radlinski Joachims. Minimally invasive randomization for collecting unbiased preferences from clickthrough logs. AAAI. 2006.